b Contents

OTTO KINNE

Editor

The late Frank H. Rigler

and Robert H. Peters

SCIENCE AND LIMNOLOGY

Introduction (Otto Kinne)

Frank H. Rigler and Robert H. Peters: A Laudatio

(Jürgen Overbeck)

Publisher: Ecology Institute

Nordbünte 23, D-21385 Oldendorf/Luhe

Germany

Robert H. Peters

Department of Biology

McGill University

Montreal, PQ

Canada H3A 1B1

ISSN 0932-2205

No part of this book may be reproduced by any means, or transmitted, or translated without

written permission of the publisher

Printed in Germany

Typesetting by Ecology Institute, Oldendorf

Printing and bookbinding by Konrad Triltsch, Graphischer Betrieb, Würzburg

Printed on acid-free paper

To Ann and Antonella

Contents

Introduction (Otto Kinne) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . XI

Frank H. Rigler and Robert H. Peters: A Laudatio (Jürgen Overbeck) . . . . . . XXI

Prefaces . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . XXIII

Prologue . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1

I WHY READ ABOUT SCIENCE? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5

Some Misrepresentations of Science . . . . . . . . . . . . . . . . . . . . . . . . . . . 5

Some Basic Distinctions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 10

Facts and theories . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 10

Induction and deduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11

Empirical and explanatory theories . . . . . . . . . . . . . . . . . . . . . . . . . 15

The Importance of Science . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16

The Growth of Science . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18

Summary . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19

II A BRIEF HISTORY OF METHOD . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 21

Three Ways to Knowledge . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 21

Aristotle . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 22

Deduction and Induction in the Age of Reason . . . . . . . . . . . . . . . . . . . 25

Logical Positivism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28

On causality . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28

On new ideas . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 30

Sir Karl Popper . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 31

III NORMAL SCIENCE AND PSEUDO-SCIENCE . . . . . . . . . . . . . . . . . . 35

Kuhn’s “Normal” Science . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 35

An historical model of science . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 36

“Pseudo-Science” . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40

Velikovsky . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42

IV THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES . . . . . 47

Science and Ecology . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 48

Non-theories . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 49

The niche . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 49

The competitive exclusion principle . . . . . . . . . . . . . . . . . . . . . . . . 50

Weak Theories . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 54

Evolution by natural selection . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 54

Concepts and measurement of phosphorus fractions . . . . . . . . . . . . 56

V BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE . . . . . . . . 63

Framing Scientific Proposals . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 63

The Reception of Moderately Restrictive Theories . . . . . . . . . . . . . . . . 64

The Pursuit of Ecological Concepts . . . . . . . . . . . . . . . . . . . . . . . . . . . 67

The limiting factor . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 68

Unconcern . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 70

Multiple limitation in the sea . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 70

Inattention to Detail . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 72

The calculation of secondary productivity . . . . . . . . . . . . . . . . . . . . 73

Some Consequences . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 77

VI WHY LIMNOLOGY? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 79

What is Limnology? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 79

What is Science? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 80

Ecological Theories . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 81

The ecosystem concept . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82

Why limnology? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 83

A paradigm shift in limnology . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87

Limnology and marine science . . . . . . . . . . . . . . . . . . . . . . . . . . . . 91

Why limnology — an answer . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 93

VII REDUCTIONISM VERSUS HOLISM:

AN OLD PROBLEM REJUVENATED BY THE COMPUTER . . . . . . . 95

The Place of Philosophical Debates in Biology . . . . . . . . . . . . . . . . . . . 95

Malloy and the principle of trim . . . . . . . . . . . . . . . . . . . . . . . . . . . 96

Vitalism and mechanism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 97

Organicism and holism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 98

Holism and reductionism in ecology . . . . . . . . . . . . . . . . . . . . . . . . 100

What is Systems Analysis? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 101

Some problems with proposed solutions . . . . . . . . . . . . . . . . . . . . . 104

Two Personal Experiences . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 106

The Char Lake Project . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 106

Zooplankton feeding . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 110

The Reality of Systems Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 113

Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 114

VIII SOURCES OF ECOLOGICAL CREATIVITY . . . . . . . . . . . . . . . . . . . . 117

The Challenge of Creativity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117

The Existing Literature as an Inspirational Device . . . . . . . . . . . . . . . . 119

Dissection . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 120

Mechanism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 121

Dichotomies and categories . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 121

Analysis of variance . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122

Extensions, additions and modifications . . . . . . . . . . . . . . . . . . . . . 122

Technologies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 123

Complications . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 123

The Danger of Conventionalism . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 125

Creative Alternatives for Normal Ecology . . . . . . . . . . . . . . . . . . . . . . 126

Syllogisms and analogies . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 126

A return to application . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 127

CONTENTS

IX EMPIRICAL LIMNOLOGY . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129

Social Demands and Scientific Supply . . . . . . . . . . . . . . . . . . . . . . . . . 129

Pessimists and Optimists . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 130

Testing the alternatives . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 131

Holists and reductionists . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 132

What to Predict? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 133

A Research Program in Holistic Empirical Ecology . . . . . . . . . . . . . . . 134

How green is my lake? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134

Phosphorus concentration . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 136

The growing school of empirical limnology . . . . . . . . . . . . . . . . . . 143

Summary — A Future for Ecology . . . . . . . . . . . . . . . . . . . . . . . . . . . . 147

X AN EDUCATION IN SCIENCE: EVALUATION . . . . . . . . . . . . . . . . . . 149

On Advising Teachers . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 149

The Goals of a University Education in Science . . . . . . . . . . . . . . . . . . 150

Strategies for Teaching . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 151

Empowerment by theory . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152

Understanding through explanation . . . . . . . . . . . . . . . . . . . . . . . . . 153

Paradigmatic indoctrination . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 155

Disciplinary description . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 155

An Evaluation of Teaching in Biology and Ecology . . . . . . . . . . . . . . . 156

Nurture or nature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 156

The problem with textbooks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 157

The problem with courses . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 159

Repercussions for graduate training . . . . . . . . . . . . . . . . . . . . . . . . . 160

A lesson from the literature . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 161

XI AN EDUCATION IN SCIENCE: PRESCRIPTIONS . . . . . . . . . . . . . . . . 163

The Undergraduate Program . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 163

The problem of confidence . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 164

De-enrichment and dis-integration . . . . . . . . . . . . . . . . . . . . . . . . . . 166

Hierarchical themes for undergraduate education . . . . . . . . . . . . . . 168

A theoretical typology . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 170

Graduate Education . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 171

The importance of role models . . . . . . . . . . . . . . . . . . . . . . . . . . . . 171

Wise choices in graduate education . . . . . . . . . . . . . . . . . . . . . . . . . 172

Administrative Advice . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 175

XII THE QUESTIONS OF RELEVANCE . . . . . . . . . . . . . . . . . . . . . . . . . . . 177

What Use is Science to Society? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 177

Does science differ from applied research and technology? . . . . . . 178

Does Science Merit Support? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 180

How can we evaluate our science? . . . . . . . . . . . . . . . . . . . . . . . . . . 180

How can ecology merit support? . . . . . . . . . . . . . . . . . . . . . . . . . . . 185

CONTENTS

XIII FUNDING DECISIONS . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 187

The Central Problem for Research Funding . . . . . . . . . . . . . . . . . . . . . 187

Reasonable expectations from research . . . . . . . . . . . . . . . . . . . . . 188

How to gamble with research funds . . . . . . . . . . . . . . . . . . . . . . . . 191

Some realities of ecological research . . . . . . . . . . . . . . . . . . . . . . . 194

The Dream of Multi-Disciplinary Environmental Science . . . . . . . . . . 195

The advantages of team research . . . . . . . . . . . . . . . . . . . . . . . . . . 195

The problems of multi-disciplinary research in ecology . . . . . . . . . 196

Where do we go from here? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 200

XIV DARWIN AND EVOLUTIONARY SCIENCE . . . . . . . . . . . . . . . . . . . . 201

Darwin on the Galapagos . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 202

Critics of Darwin . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 204

The first school: early emotionals . . . . . . . . . . . . . . . . . . . . . . . . . . 204

The second school: directional deists . . . . . . . . . . . . . . . . . . . . . . . 207

The third school: cataclysmic creationists . . . . . . . . . . . . . . . . . . . 208

The fourth school: Popperian purists . . . . . . . . . . . . . . . . . . . . . . . 209

Two other biological schools . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 211

Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 211

XV IS THE FUTURE GRIM? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 213

The Gilt Age of University Research . . . . . . . . . . . . . . . . . . . . . . . . . . 213

The Gathering Challenge to University Science . . . . . . . . . . . . . . . . . . 214

University Responses . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 216

A Policy for the Future: Closing the Aspiration Gap . . . . . . . . . . . . . . 217

Undergraduate teaching . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 217

Graduate training . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 219

Scholarship . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 219

Administration . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 220

Two reservations . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 221

Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 222

Acknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 223

References . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 225

CONTENTS

Introduction

Otto Kinne

Ecology Institute, Nordbünte 23, D-21385 Oldendorf/Luhe, Germany

Science and Limnology is likely to become a milestone in ecological reason-

ing and research. Based to a considerable extent on unpublished thoughts

and notes of Frank H. Rigler, and written by the winner of the Ecology Insti-

tute Prize 1991 in the field of limnetic ecology, Robert H. Peters of McGill

University, Montreal, Canada, the book is enlightening, challenging and

provocative. It is enlightening, because it views science in general and ecol-

ogy in particular from unconventional angles; it is challenging, because it

criticizes many of the ways in which ecologists think and approach their sub-

jects; it is provocative, because the author presents an unattractive picture of

present-day ecology and a harsh assessment of university education and

research. Above all, Science and Limnology is a worthy companion to

previous Excellence in Ecology books: it offers the well-written, concise and

easy-to-read personal views of an outstanding performer in his field of

expertise. Rob Peters has written this book as a professor in the best sense of

that word. He professes his insights, beliefs and convictions with courage

and honesty, and he considers his topics with care and a keen mind. His

views reach far beyond the horizon suggested by the book’s title, far into the

realms of science history, philosophy and methodology; into the relevance of

science to society; and into the centers where science is at home and where

scientists are formed — the universities.

The essence of the message conveyed by Peters is this: ecologists have

collected impressive amounts of observations and facts, but they have failed

to sufficiently identify and formulate theories that go beyond the facts —

theories that can be tested and that can predict. To aid in solving the many

problems which press on modern human societies and in controlling and

restricting the ever-increasing deformation of nature, ecological research

must focus, more so than in the past, on empirical, holistic approaches that

facilitate prediction. Peters insists that the failure of ecologists to produce

useful predictions is not a consequence of the complexity of their subjects,

but of the complexity of their approaches. He believes that his call for a more

empirical, holistic strategy will be heard and accepted by ecologists and that

it will help mankind to preserve itself and to save its environment.

XII INTRODUCTION

For Peters the essence of science is the creation, testing and use of theory.

In the process of creating theory, induction plays an important role. It is here

that inspiration and intuition enter the scene. While theory is the backbone of

research, it can never be beyond doubt. Theories must be tested time and

again. The prediction must be compared to further observation. Since scien-

tific knowledge always remains hypothetical, the ultimate arbiter of scien-

tific research is observation. ‘The main goals of science are to make theo-

ries, to use theories to make predictions and to assess those predictions

against observation’ (p. 21).

Peters defines ecology ‘as the science that predicts the abundance, distri-

bution and other characteristics of organisms in nature’ (p. 81). He deplores

that ecologists have failed to appreciate the nature of their science: ‘... much

of ecology is confused in its goals, uncertain of its thoughts, and inconsistent

in its terminology.’ Chapter V portrays ecologists ‘as nonchalant about their

tests, careless in their measurements, yet closed-minded in considering alter-

natives’ (p. 77).

Turning to his main subject, limnology, Peters points out that the leading

role this branch of science once played in ecological research was lost,

largely because the assumption that ecological theory required an isolated

microcosm was discovered to be a misapprehension. Based on the tools and

information produced over many decades, limnologists are now turning to

empirical theories that predict. Thus, modern limnology is becoming a

leader again, this time showing the way towards predictive ecology.

Examining university research and teaching, Peters identifies shortcom-

ings at every level, but he also makes suggestions for improvements and

offers some practical advice. In regard to teaching science, he stresses again

our failure to appreciate the significance and nature of theory. Reconsidering

and contemplating science should lead to profound changes in research and

in the ways professors teach students: ‘Too much research is done for the

same reason that a mountain is climbed (“because it is there”), and too little

time is spent questioning the motives for doing so’ (p. 179). On the other

hand, deplores Peters, big science and societal power have separated profes-

sors from their ideals and goals, and thus almost destroyed the university as

an intellectual retreat.

XIIIINTRODUCTION

Ecology Institute Prize 1991 in the field of limnetic ecology. Reproduction of the prize

awarding document

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XIV INTRODUCTION

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please give account number and expiration date).

An order for the whole series is accepted at a 10% reduced price.

For book authors, titles and prices, consult pp. XV–XVII.

Nominations for ECI and IRPE Prizes (accompanied by CV, list of publi-

cations, and a statement why, in the opinion of the nominator, the nominee

qualifies for the prize) are invited from research ecologists on a global scale.

They should be sent to the chairperson of the respective ECI Jury, or, alter-

natively, to the ECI’s director, who will then forward them to the chair-

person. Eligible are all ecologists engaged in scientific research (except the

ECI’s director, the Jury’s chairperson, and previous Laureates; Jury mem-

bers nominated will be replaced by other ECI members). The Jury selects

prize winners using the nominations received as well as their own knowledge

of top performers and their own professional judgement.

Nominations for OKF Fellows, addressed to Dr. J. Lom (see above) and

accompanied by a letter of support as well as a documentation of the

nominees’ performance, are invited from ECI members and members of the

Editorial Staffs of the three international Inter-Research journals, Marine

Ecology Progress Series, Diseases of Aquatic Organisms, and Climate

Research.

ECI Prize Winners, Their Major Scientific Achievements

and Their Books

Tom Fenchel (Helsingør, Denmark), ECI Prize winner 1986 in marine ecology.

Quotation of the Jury (Chairman: John Gray, Oslo, Norway)

The Jury found Professor T. Fenchel’s contribution to ecological knowledge in a variety of

research fields to be of the highest international class. In particular, the Jury cites his brilliant

and uniquely important studies on the microbial loop which have opened up a fundamentally

new research field. Professor Fenchel is, in addition, an excellent publicizer in his field of

research with authorship of a number of standard works in marine ecology.

Book 1: Ecolo

gy – Potentials and Limitations. (Published 1987; price DM 67 plus postage

and handling)

Edward O. Wilson (Cambridge, MA, USA), ECI Prize winner 1987 in terrestrial ecology.

Quotation of the Jury (Chairman: Sir Richard Southwood, Oxford, UK)

Professor E. O. Wilson is distinguished for his many contributions to different aspects of ecol-

ogy and evolutionary biology. His life-time love of Nature, a theme explored in his book “Bio-

philia”, has been particularized in his study of ants leading to major new insights on the evo-

lution of castes and the operation of social systems. His seminal “Sociobiology”, derived

from this work, has founded a new branch of science, between ecology and the social sci-

ences. With the late Robert MacArthur he was the originator of the modern theories of island

biogeography that have contributed not only to the understanding of island biota, but to com-

munity and population ecology.

Book 2: Success and Dominance in Ecosystems: T

he Case of the Social Insects. (Published

1990; price DM 49 plus postage and handling)

XVECI PRIZE WINNERS

Gene E. Likens (Millbrook, NY, USA), ECI Prize winner 1988 in limnetic ecology.

Quotation of the Jury (Chairman: William D. Williams, Adelaide, Australia)

Gene Likens is a distinguished limnologist who has made salient contributions to many fields

of limnology. In 1962 he initiated and developed (with F. H. Bormann) the Hubbard Brook

Ecosystem Study in New Hampshire. Comprehensive investigations in this study provided a

model for ecological and biogeochemical studies worldwide. A major finding of the study was

that rain and snow are highly acidic. “Acid rain” is now recognized as one of the major envi-

ronmental hazards in North America, Europe and elsewhere. Elected to the American

Academy of Sciences in 1979, and the National Academy of Sciences in 1981, Gene Likens is

a highly worthy recipient of the 1988 ECI Prize in Limnetic Ecology.

Book 3: T

he Ecosystem Approach: Its Use and Abuse. (Published 1992; price DM 59 plus

postage and handling)

Robert T. Paine (Seattle, WA, USA), ECI Prize winner 1989 in marine ecology.

Quotation of the Jury (Chairman: Tom Fenchel, Helsingør, Denmark)

Robert T. Paine has made substantial and original contributions to marine biology and to

ecology in general. In particular the Jury mentions the discovery of the role of patch forma-

tion and properties of food web structure in shaping communities of sedentary organisms.

These studies (of which several have become classics of marine ecology) have fundamentally

changed the way in which we view marine benthic communities. This work has also served as

an inspiration for innovation in the mathematical description of community processes and has

had a lasting impact on our understanding of “landscape dynamics”, of equal importance to

the development of the science of ecology and to conservation ecology.

Book 4: Mar

ine Rocky Shores and Community Ecology: An Experimentalist’s Perspective.

(Published 1994; price DM 59 plus postage and handling)

Harold A. Mooney (Stanford, CA, USA), ECI Prize winner 1990 in terrestrial ecology.

Quotation of the Jury (Chairman: John L. Harper, Penmaenmawr, UK)

Professor Harold A. Mooney is distinguished for his studies of the physiological ecology of

plants, especially of arctic-alpine and mediterranean species. He has explored the ways in

which plants allocate carbon resources and expressed this allocation in terms of costs, bene-

fits and trade-offs. This has given a quantitative dimension to the study of plant-animal inter-

actions and acted to integrate physiological ecology with population biology, community

ecology, and ecosystem studies.

Book 5: T

he Globalization of Ecological Thought. (To be published soon)

Robert H. Peters (Montreal, PQ, Canada), ECI Prize winner 1991 in limnetic ecology.

Quotation of the Jury (Chairman: Jürgen Overbeck, Plön, Germany)

Professor R. H. Peters’ contributions to the fields of limnology and ecology have been numer-

ous and far reaching. His work on phosphorus cycling in lakes provides examples of excellent

research illuminating a number of important aspects regarding the movement and availabil-

ity of phosphorus in aquatic systems. His book “The Ecological Implications of Body Size”

gives a powerful overview of the utility of allometric relationships for the study of ecological

problems and for building ecological theory.

Book 6: Science and Limnolo

gy. (Published 1995; price DM 74 plus postage and handling.)

Authors: The late F. H. Rigler and R. H. Peters

XVI INTRODUCTION

Dr. David H. Cushing (Lowestoft, United Kingdom), ECI Prize winner 1992 in marine

ecology.

Quotation of the Jury (Chairman: John Costlow, Beaufort, NC, USA)

Dr. David H. Cushing has, for many years, made an enormous contribution to the field of

marine ecology through his numerous publications and his original ideas. His work continues

to be highly influential in fisheries and plankton ecology. Although first published over ten

years ago, his pioneering studies on the dynamics of a plankton patch, the feeding of cope-

pods, the ‘match-mismatch’ theory of recruitment and the climatic influences on plankton and

fisheries remain of central importance.

Book 7: Recr

uitment in Marine Fish Populations. (To be published 1995/96)

Paul R. Ehrlich (Stanford, CA, USA), ECI Prize winner 1993 in terrestrial ecology.

Quotation of the Jury (Chairman: Harold A. Mooney, Stanford, CA, USA)

Dr. Paul Ehrlich’s scientific contributions have been substantial and sustained. The quality

and depth of his interpretation of environmental issues to students, the general public, and to

policy makers is unrivaled. His concern for both environmental quality and environmental

justice has rarely been matched. He has made fundamental contributions to the study of pop-

ulation biology utilizing butterflies as a model system. These studies have had a large impact

on how we view the population structure of organisms and have provided important guide-

lines on the conservation of wild populations.

Book 8: A W

orld of Wounds: Ecology and Human Predicament. (To be published 1995/96)

IRPE Prize Winners and Their Major Scientific Achievements

Colleen Cavanaugh (The Biological Laboratories, Harvard University, Cambridge, MA

02138, USA), IRPE Prize winner 1986 in marine ecology.

Quotation of the Jury (Chairman: John Gray, Oslo, Norway)

The Jury found the research of Dr. C. Cavanaugh on chemosynthesis – initially concerning

hot-vent fauna but extended to other sulphide-rich habitats – to be highly original and to rep-

resent a major scientific breakthrough. Her hypothesis, formulated whilst a beginning gradu-

ate student, met severe opposition from established scientists with opposing views, but never-

theless proved to be correct. The Jury acknowledge Dr. Cavanaugh’s brilliant and

independent research in understanding chemosynthetic energetic pathways.

Karel

Simek (Hydrobiological Institute, Czechoslovak Academy of Sciences, 370 05

Ceské

Budˇejovice, Czechoslovakia), IRPE Prize winner 1991 in limnetic ecology.

Quotation of the Jury (Chairman: Jürgen Overbeck, Plön, Germany)

Dr. Karel Simek belongs to the generation of young limnologists in Eastern Europe who –

despite lack of international information exchange – published, under difficult conditions,

excellent contributions to the field of Aquatic Microbiology. He enjoys a high international

reputation. Under the present, improved conditions Simek is likely to proceed even more

successfully to new professional horizons.

XVIIIRPE PRIZE WINNERS

Richard K. Grosberg (Department of Zoology, University of California, Davis, CA 95616,

USA), IRPE Prize winner 1992 in marine ecology.

Quotation of the Jury (Chairman: John Costlow, Beaufort, NC, USA)

Richard K. Grosberg has not only published extensively on fundamental issues relating to

marine ecology, but has also demonstrated his understanding of marine ecology through

superb teaching of invertebrate zoology to undergraduate and graduate students. He is

acknowledged as a leader in adapting molecular techniques for the study of marine larvae

and in developing information on extraordinarily detailed mapping studies of the genetic

structure of adult populations of marine organisms.

Nikolai V. Aladin (Zoological Institute, Russian Academy of Sciences, St. Petersburg

199034, Russia), IRPE Prize winner 1993 in terrestrial ecology.

Quotation of the Jury (Chairman: Harold A. Mooney, Stanford, CA, USA)

Dr. Nikolai V. Aladin is one of Russia’s most eminent young ecologists. He has researched

environments in the former Soviet Union, particularly in Kazakhstan where he and a small

team have focussed upon the area of the Aral Sea. Dr. Aladin’s studies were performed dur-

ing a period of change, both in the patterns of organismic assemblages and in the political

structure of his country. These studies were undertaken in his own time and at his own

expense. It is only over the past few years that his studies have been officially supported and

their value recognized.

Ecology Institute Staff 1995 (in brackets: year of appointment)*

Director and Founder: Professor O. Kinne, D-21385 Oldendorf/Luhe, Germany

Marine Ecology

Terrestrial Ecology

XVIII INTRODUCTION

Prof. F. Azam, La Jolla, CA, USA (1985)

Prof. H.-P. Bulnheim, Hamburg, Germany (1984)

Prof. S. W. Chisholm, Cambridge, MA, USA

(1993)

Dr. D. H. Cushing, Lowestoft, UK (1993)

Prof. T. Fenchel, Helsingør, Denmark (1985)

Dr. N. S. Fisher, Stony Brook, NY, USA (1985)

Prof. J. Gray, Oslo, Norway (1984)

Prof. B.-O. Jansson, Stockholm, Sweden (1989)

Prof. V. Kasyanov, Vladivostok, Russia (1993)

Prof. E. Naylor, Menai Bridge, UK (1984)

Prof. S. W. Nixon, Narragansett, RI, USA (1989)

Prof. W. Nultsch, Hamburg, Germany (1994)

Prof. R. T. Paine, Seattle, WA, USA (1990)

Dr. T. Platt, Dartmouth, NS, Canada (1984)

Acad. Prof. G. G. Polikarpov, Sevastopol,

Ukraine (1985)

Dr. T. S. S. Rao, Bambolim, India (1985)

Prof. V. Smetacek, Bremerhaven, Germany (1993)

Prof. B. L. Wu, Qingdao, China (1993)

Acad. Prof. A. Zhirmunsky, Vladivostok, Russia

(1988)

*Following their receipt of the ECI prize, laureates are invited to join the institute’s staff

Prof. T. N. Ananthakrishnan, Madras, India

(1984)

Prof. F. S. Chapin, III, Berkeley, CA, USA

(1986)

Prof. J. Ehleringer, Salt Lake City, UT, USA

(1986)

Dr. P. Ehrlich, Stanford, CA, USA (1994)

Prof. M. Gadgil, Bangalore, India (1985)

Limnetic Ecology

Technical Staff (all Oldendorf/Luhe, Germany)

XIXECOLOGY INSTITUTE STAFF

Prof. I. Hanski, Helsinki, Finland (1993)

Prof. J. L. Harper, Penmaenmawr, UK (1986)

Prof. E. Kuno, Kyoto, Japan (1986)

Prof. A. Macfadyen, Coleraine, UK (1985)

Prof. H. A. Mooney, Stanford, CA, USA

(1991)

Dr. M. Shachak, Sede Boker, Israel (1989)

Acad. Prof. V. E. Sokolov, Moscow, Russia

(1986)

Prof. Sir R. Southwood, Oxford, UK (1986)

Prof. S. Ulfstrand, Uppsala, Sweden (1986)

Prof. E. O. Wilson, Cambridge, MA, USA (1988)

Prof. N. V. Aladin, St. Petersburg, Russia (1994)

Prof. J. I. Furtado, Washington, DC, USA (1985)

Prof. S. D. Gerking, Tempe, AZ, USA (1986)

Dr. J. E. Hobbie, Woods Hole, MA, USA (1986)

Dr. E. Kamler, Lomianki, Poland (1993)

Prof. W. Lampert, Plön, Germany (1993)

Prof. G. E. Likens, Millbrook, NY, USA (1989)

Prof. K. Lillelund, Hamburg, Germany (1985)

Prof. R. Margalef, Barcelona, Spain (1986)

Prof. J. Overbeck, Plön, Germany (1984)

Prof. T. J. Pandian, Madurai, India (1985)

Dr. E. Pattée, Villeurbanne, France (1987)

Prof. R. H. Peters, Montreal, PQ, Canada (1992)

Prof. E. Pieczyñska, Warsaw, Poland (1993)

Prof. J. G. Tundisi, São Paulo, Brazil (1990)

Dr. D. Uhlmann, Dresden, Germany (1989)

Prof. W. Wieser, Innsbruck, Austria (1987)

Prof. W. D. Williams, Adelaide, Australia (1986)

J. Austin

G. Bendler

M. Bruns

V. Cleary

C. Fesefeldt

R. Friedrich

B. Fromm

S. Hanson

R. Hooper

J. Hunt

H. Kinne

J. Kunert

M. Masuhr

T. Masuhr

W. Neel

R. Stedjee

H. Witt

Frank H. Rigler and Robert H. Peters:

A Laudatio

Jürgen Overbeck

Max-Planck-Institut für Limnologie, D-24302 Plön, Germany

With the sudden death of Professor Frank Rigler in 1982, we, his friends and

colleagues, lost a distinguished scientist and a leading limnologist with a

broad field of interest and research.

Who was Frank Rigler? Born in London in 1928, he received his Ph.D. in

limnology from the University of Toronto in 1954. He was married and had

5 children. Frank Rigler was Chairman of Biology at McGill University in

Montreal, Quebec, Canada, from 1976 to 1981. His special interests were

predicting the effects of nutrient enrichment on production in temperate and

subarctic lakes. His laboratory was also long concerned with the status of

ecology as a science and the role of ecological knowledge.

My first personal acquaintance with Frank Rigler was at the XIXth

International Limnological Congress in Winnipeg, Canada, in 1974, where

he gave a Plenary Lecture with the title Nutrient Kinetics and the New

Typology. This lecture provoked an extraordinarily controversial discussion.

Rigler began by saying that he doubted that studies on the details of the

phosphorus cycle were really advancing our knowledge at all. There already

existed an embarassingly large accumulation of facts in limnology. But sci-

entific advance comes only when we think up a new theory that overcomes a

difficulty experienced by the old theory. A qualified scientific theory must

be — in the sense of Karl Popper — potentially falsifiable. Starting from

this, Rigler presented, from a holistic point of view, nutritional-production

limnology using the ‘black-box’ approach, which may give us predictive

ability but no real understanding. Models are, by and large, purely empirical

descriptions of correlations between state variables. However, they pose

questions and the work of reductionists may suggest theories to answer these

questions. It was indeed an extraordinary lecture, quite different from the

usual way of presenting ecological results and systems.

Due to his early death, Rigler was unable to publish many of his ideas. In

this connection I will cite a letter of Professor M. L. Ostrofsky, Meadville,

Pennsylvania: “Rigler’s ideas about the nature of science, the requirements

of ‘good’ science, and the role of ecologists in shaping public issues are not

widely known. Rigler’s modesty prevented him from publishing many of his

ideas until late in his career. Many of Rigler’s ideas have been placed before

a larger scientific audience through the work of Dr. Robert Peters, Rigler’s

most articulate student, friend and colleague. It would be of enormous sig-

nificance if the full range of Rigler’s thoughts could be made accessible to a

larger audience. I cannot think of a more timely subject for a book; the recent

literature suggests that ecology is in the midst of a crisis of confidence and

identity. I cannot think of a more appropriate individual to undertake the

task.” The award of the 1991 ECI Prize in Limnetic Ecology to Robert Peters

now offers the unique opportunity for realizing this project. This book,

Science and Limnology, thus has two authors and two prefaces — a junior

author’s preface and a senior author’s preface. Robert Peters approached the

book as a “collaborative exercise, a collage in which Rigler’s enduring ideas

are set within a matrix of my own writing to produce a contemporary essay

about the science of limnology.” The basis of the 15 chapters is over 70 sets

of notes and lectures covering 25 years.

Robert Henry Peters was born in Toronto, Ontario, Canada, on August 2,

1946. He received his Ph.D. in 1972. His doctoral thesis on regeneration of

phosphorus by zooplankton — an issue which is still of great topical impor-

tance — was supervised by Frank Rigler. Highlights of Robert Peter’s

academic career include post-doctoral fellowships in Pallanza (Italy),

1972–1973; in Vienna (Austria), 1973; and in Munich (Germany), 1974. He

became Assistant Professor in 1974, Associate Professor in 1979 and Full

Professor in 1986 at McGill University. He has published 125 papers, notes

and reports, and authored a book on the ecological implications of body size.

His current research interests center on material flow in aquatic ecosystems,

zooplankton behavior, allometric relationships in autecology, and applied

environmental management.

I hope that Science and Limnology will be as inspiring, uncommon and

provoking for its readers as was the Plenary Lecture of Frank Rigler which I

had the pleasure to attend and discuss 20 years ago.

XXII LAUDATIO

Prefaces

Junior author’s preface

To win an international prize is a wonderful and surprising event. A hundred

other researchers could merit most prizes, and many worthy individuals go unre-

warded in any prize-giving. Merton (1968) has called these unrecognized but

worthy colleagues “occupants of the 41st chair”, in reference to the many tal-

ented individuals who never won the honour of a place in the Académie

Française, simply because the Académie is limited to 40 chairs. Deserving new-

comers must await the death of present occupants, and some die before an oppor-

tunity arises, as did Descartes, Molière, Pascal, and Diderot. Because I know the

unlikelihood of winning honours, the decision of the Ecology Institute to award

me its 1991 prize in limnetic ecology was first a surprise, and then a source of

great pleasure. It remains a reason for deep satisfaction and pride, as well as grat-

itude towards Professor Otto Kinne, Director of the Ecology Institute, Professor

Jürgen Overbeck, Chairman of the ECI Jury, the members of the ECI Jury, the

staff of the Institute, and the generous colleagues who lent me their support. Like

most critical scientists, I am prone to self-doubt, and therefore I am all the more

touched that not all of my ideas have been dismissed as either appallingly bad or,

worse, frightfully dull. I am also humbled to find myself in the ranks of previous

laureates whose contributions have been so much greater than my own.

I have an additional personal reason to be pleased with this prize. It has

allowed me to complete a project that I have wanted to do for over a decade: to

prepare the unpublished notes of Frank Rigler for publication. When Frank Rigler

died in 1982, the world of limnology lost one of its leading thinkers. The loss was

all the more tragic because most of his broader views on limnology, ecology and

science were never published. His influence had been a personal one, spreading

through conversation and occasional public lectures. As a summer employer and

undergraduate teacher, as my doctoral supervisor, as my long-time colleague and

close friend, and still as my conscience and model, Frank has been the major

influence on my career and scientific development. He has played a similar role

for other students, at levels ranging from undergraduate to senior scientist. For us

all, conversation with Frank was a treasure, a model of clear thought, logic, pen-

etration, relevance and simplicity. He taught us the nature of science, the power it

gives its followers, and the burdens of responsibility it places upon them. He was

a source of strength and inspiration, and he is sorely missed.

Rigler’s natural modesty stopped him from writing about his larger views for

most of his career. Soon after he finally began to write to a larger audience, his

voice was stilled by cancer. His few philosophical papers (Rigler 1975a, b,

1982a, b) were powerful and controversial, but they exposed only a fraction of his

ideas. Only those who knew his teaching at first hand, whether in university

courses, in scientific lectures, in panel discussions, or in quiet talks, realize how

much went unrecorded.

Rigler’s vision and virtues are even more needed now, but my aim in prepar-

ing this book is not simply to reproduce the text of his lectures and unpublished

notes. His notes were extensive and he was meticulous in preserving that mate-

rial, but even good lecture notes are not publishable as they stand. I have instead

approached the book as a collaborative exercise, a collage in which Rigler’s

enduring ideas are set within a matrix of my own writing to produce a contempo-

rary essay about the science of limnology. This cannot be the book Rigler would

have written, but because his spirit is so much a part of my everyday experience,

it may approach a book we could have written together, had he lived. For me, the

exercise has been profoundly rewarding. I have been able to reexamine the roots

of my own views and to appreciate the rich earth from which they developed. I

also discovered that many ideas I thought my own were actually foreshadowed in

his writings.

I have chosen to write in the first person singular, and therefore I have created

a non-existent author who is neither me nor Rigler, but some amalgam of us both.

Use of the first person preserves that conversational tone of Rigler’s lectures and

confirms this book as a personal document. Use of this chimeric “I” sometimes

results in incongruities since the pronoun clearly refers to only one of the two

authors, but on the whole I like the device. At times, it even allowed me to see my

ideas from a greater distance than I usually can.

The 15 chapters are based on over 70 sets of notes and lectures covering a

quarter century. I have recast and resorted most of the material, but most chapters

can still be appreciated separately. The book is arranged in a roughly chronolog-

ical order based on an intellectual ontogeny or autobiography whose main lines

apply to us both. The first three chapters deal with the development of a coherent

philosophy of science based on the premise that science must tell us something

about the natural world and the realization that not all science is directed to that

goal. In Chapters IV and V, these criteria are used to force recognition that much

of ecology and limnology, our own work included, is wanting. This revelation

fostered a search for alternative models in limnology (Chapter VI), and ecology

(Chapters VII and VIII) that eventually led to our adoption of empiricism (Chap-

ter IX). The success of an empirical research agenda encouraged us to reassess

the role of an education in science (Chapters X and XI), and provided a sharp tool

in the evaluation of the science, whether in the context of society (Chapter XII),

grant reviews (Chapter XIII), or historical analyses (Chapter XIV). The final

XXIV PREFACES

chapter warns that we must be prepared to change the way we do our science.

If we do not, someone else will change it for us.

There is a need for works that translate between the professional philosophers

and the scientific practitioners in different disciplines, and at different levels of

sophistication. The reader interested in the philosophy of biology already has a

number of choices. Excellent reviews of the history of ecological ideas are avail-

able from Kingsland (1985) and McIntosh (1985). David Hull (1974) and

Michael Ruse (1973) are philosophers who have written widely on the philo-

sophy of biology and biological science. Rolf Sattler (1986) is a biologist whose

book describes the important issues that biology presents to the philosopher. I

even have a rather philosophical book of my own about ecology (Peters 1991a).

These texts offer more sophisticated, more advanced, and usually less ecological

treatments than this book.

Science and Limnology is intended to be an easy read. I have purposely used

less referencing and adopted a less dense style than I would in a scientific paper.

Rather than an authoritative review, it is meant to provide ecologists with a ready

access to the history and philosophy of science. I hope it is sufficiently light read-

ing that both the ecological researcher and the student can find a place for it in

their schedules.

Senior author’s preface

This book is a personal essay expressing the

biases of two researchers and promulgating

their faith in an approach to limnological prob-

lems. As such, the book is little more than a ser-

mon, and warrants consideration only if it is a

reasonably good one. By a sermon, I mean an

essay intended to inspire faith in an, as yet,

undemonstrated and perhaps undemonstrable

property of the universe in which the preachers

implicitly believe.

Science and Limnology is not a monograph that presents new data or develops

a new theory, nor is it a text that reviews the field. The writings collected here do

not fall into one of these conventional categories for scientific works. However, if

the reader has interests beyond normal scientific fare, then this contribution may

be worthy of his or her attention.

Let us assume that the reader’s definition of acceptable reading includes

sermons, and evaluate this book as such. A good sermon has three important

XXVPREFACES

F. H. Rigler

characteristics: (1) It must not be too long; (2) it must be internally consistent;

and (3) it must be comprehensible.

Length: Each chapter is short and the different chapters are sufficiently inde-

pendent, so that only a few pages need be read at a time. Part of the price of this

independence is some disarticulation and a modest amount of repetition among

the chapters. As a result, the book loses some impact and is longer than it needs

to be. Unfortunately, the length of this book was entirely out of my hands, and the

junior author must bear full responsibility if he has made a hash of it.

Consistency: I have fewer qualms on this point. We have both striven to main-

tain a logically consistent position throughout the book. Undoubtedly we have

failed in this intention at many points, but we hope we are no less successful than

many other contributions to the literature. In any case, we knew we were unlikely

to succeed in total consistency before we began.

Comprehensibility: In a sermon, the need to keep the story-line clean is more

significant than length or consistency. The message is very simple. The Baptist

preachers (predictive or empirical limnologists) are trying to persuade the

College of Cardinals (other biologists, ecologists and limnologists) that their

lesser sect has its own valid sources of revelation. Since the Roman Catholics of

science have considered themselves to be omniscient for such a long time, it will

take the patience of Job and the logic and clarity of Thomas Aquinas to convince

them that they can learn from others. We can hardly expect a mass conversion,

but we may help prepare the ground for an eventual reformation.

The intent of the book is to convert those whose belief in traditional ecologi-

cal approaches is weak, and to sow doubts in the minds of those whose belief is

stronger. To do so, we show that some freshwater ecologists have achieved suc-

cess by reflecting on the general nature of science and by developing models that

are consistent with those reflections. We anticipate that a similar approach will

apply equally well to other questions and to other systems. Indeed, a successful

response to the environmental degradation of our planetary home depends on the

widespread adoption of just such an approach. Thus, this sermon has an impor-

tant message. It needs to be heard.

XXVI PREFACES

Prologue

I took advantage of being at the seaside to lay in a store of sucking stones. They were

pebbles but I call them stones. Yes, on this occasion I laid in a considerable store. I dis-

tributed them equally between my four pockets, and sucked them turn and turn about.

This raised a problem which I first solved in the following way. I had say sixteen stones,

four in each of my four pockets, these being the two pockets of my trousers and the two

pockets of my greatcoat. Taking a stone from the right pocket of my greatcoat, and

putting it in my mouth, I replaced it in the right pocket of my greatcoat by a stone from

the right pocket of my trousers, which I replaced by a stone from the left pocket of my

trousers, which I replaced by a stone from the left pocket of my greatcoat, which I

replaced by the stone which was in my mouth, as soon as I had finished sucking it. Thus

there were still four stones in each of my four pockets, but not quite the same stones.

And when the desire to suck took hold of me again, I drew again on the right pocket of

my greatcoat, certain of not taking the same stone as the last time. And while I sucked

it I rearranged the other stones in the way I have just described. And so on. But this

solution did not satisfy me fully. For it did not escape me that, by an extraordinary haz-

ard, the four stones circulating thus might always be the same four. In which case, far

from sucking the sixteen stones turn and turn about, I was really only sucking four,

always the same, turn and turn about. But I shuffled them well in my pockets, before I

began to suck, and again, while I sucked, before transferring them, in the hope of

obtaining a more general circulation of the stones from pocket to pocket. But this was

only a makeshift that could not long content a man like me. So I began to look for some-

thing else. And the first thing I hit upon was that I might do better to transfer the stones

four by four, instead of one by one, that is to say, during the sucking, to take the three

stones remaining in the right pocket of my greatcoat and replace them by the four in the

right pocket of my trousers, and these by the four in the left pocket of my trousers, and

these by the four in the left pocket of my greatcoat, and finally these by the three from

the right pocket of my greatcoat, plus the one, as soon as I had finished sucking it,

which was in my mouth. Yes, it seemed to me at first that by so doing I would arrive at

a better result. But on further reflection I had to change my mind and confess that the

circulation of the stones four by four came to exactly the same thing as their circulation

one by one. For if I was certain of finding each time, in the right pocket of my greatcoat,

four stones totally different from their immediate predecessors, the possibility never-

theless remained of my always chancing on the same stone, within each group of four,

and consequently of my sucking, not the sixteen turn and turn about as I wished, but in

fact four only, always the same, turn and turn about. So I had to seek elsewhere than in

the mode of circulation. For no matter how I caused the stones to circulate, I always

ran the same risk. It was obvious that by increasing the number of my pockets I was

bound to increase my chances of enjoying my stones in the way I planned, that is to say

one after the other until their number was exhausted. Had I had eight pockets, for

example, instead of the four I did have, then even the most diabolical hazard could not

have prevented me from sucking at least eight of my sixteen stones, turn and turn about.

The truth is I should have needed sixteen pockets in order to be quite easy in my mind.

And for a long time I could see no other conclusion than this, that short of having six-

teen pockets, each with its stone, I could never reach the goal I had set myself, short of

an extraordinary hazard. And if at a pinch I could double the number of my pockets,

were it only by dividing each pocket in two, with the help of a few safety-pins let us say,

to quadruple them seemed to be more than I could manage. And I did not feel inclined

to take all that trouble for a half-measure. For I was beginning to lose all sense of mea-

sure, after all this wrestling and wrangling, and to say, All or nothing. And if I was

tempted for an instant to establish a more equitable proportion between my stones and

my pockets, by reducing the former to the number of the latter, it was only for an instant.

For it would have been an admission of defeat. And sitting on the shore, before the sea,

the sixteen stones spread out before my eyes, I gazed at them in anger and perplexity.

[...] And while I gazed thus at my stones, revolving interminable martingales all equally

defective, and crushing handfuls of sand, so that the sand ran through my fingers and

fell back on the strand, yes, while thus I lulled my mind and part of my body, one day

suddenly it dawned on the former, dimly, that I might perhaps achieve my purpose with-

out increasing the number of my pockets, or reducing the number of my stones, but sim-

ply by sacrificing the principle of trim. The meaning of this illumination, which sud-

denly began to sing within me, like a verse of Isaiah, or of Jeremiah, I did not penetrate

at once, and notably the word trim, which I had never met with, in this sense, long

remained obscure. Finally I seemed to grasp that this word trim could not here mean

anything else, anything better, than the distribution of the sixteen stones in four groups

of four, one group in each pocket, and that it was my refusal to consider any distribu-

tion other than this that had vitiated my calculations until then and rendered the prob-

lem literally insoluble. And it was on the basis of this interpretation, whether right or

wrong, that I finally reached a solution, inelegant assuredly, but sound, sound. Now I

am willing to believe, indeed I firmly believe, that other solutions to this problem might

have been found, and indeed may still be found, no less sound, but much more elegant,

than the one I shall now describe, if I can. And I believe too that had I been a little more

insistent, a little more resistant, I could have found them myself. But I was tired, but I

was tired, and I contented myself ingloriously with the first solution that was a solution,

to this problem. But not to go over the heartbreaking stages through which I passed

before I came to it, here it is, in all its hideousness. All (all!) that was necessary was to

put for example, to begin with, six stones in the right pocket of my greatcoat, or supply-

pocket, five in the right pocket of my trousers, and five in the left pocket of my trousers,

that makes the lot, twice five ten plus six sixteen, and none, for none remained, in the

left pocket of my greatcoat, which for the time being remained empty, empty of stones

2PROLOGUE

that is, for its usual contents remained, as well as occasional objects. For where do you

think I hid my vegetable knife, my silver, my horn and the other things that I have not yet

named, perhaps shall never name. Good. Now I can begin to suck. Watch me closely. I

take a stone from the right pocket of my greatcoat, suck it, stop sucking it, put it in the

left pocket of my greatcoat, the one empty (of stones). I take a second stone from the

right pocket of my greatcoat, suck it, put it in the left pocket of my greatcoat. And so on

until the right pocket of my greatcoat is empty (apart from its usual and casual con-

tents) and the six stones I have just sucked, one after the other, are all in the left pocket

of my greatcoat. Pausing then, and concentrating, so as not to make a balls of it, I trans-

fer to the right pocket of my greatcoat, in which there are no stones left, the five stones

in the right pocket of my trousers, which I replace by the five stones in the left pocket of

my trousers, which I replace by the six stones in the left pocket of my greatcoat. At this

stage then the left pocket of my greatcoat is again empty of stones, while the right

pocket of my greatcoat is again supplied, and in the right way, that is to say with other

stones than those I have just sucked. These other stones I then begin to suck, one after

the other, and to transfer as I go along to the left pocket of my greatcoat, being abso-

lutely certain, as far as one can be in an affair of this kind, that I am not sucking the

same stones as a moment before, but others. And when the right pocket of my greatcoat

is again empty (of stones), and the five I have just sucked are all without exception in

the left pocket of my greatcoat, then I proceed to the same redistribution as a moment

before, or a similar redistribution, that is to say I transfer to the right pocket of my

greatcoat, now again available, the five stones in the right pocket of my trousers, which

I replace by the six stones in the left pocket of my trousers, which I replace by the five

stones in the left pocket of my greatcoat. And there I am ready to begin again. Do I have

to go on? No, for it is clear that after the next series, of sucks and transfers, I shall be

back where I started, that is to say with the first six stones back in the supply pocket, the

next five in the right pocket of my stinking old trousers and finally the last five in the left

pocket of same, and my sixteen stones will have been sucked once at least in impecca-

ble succession, not one sucked twice, not one left unsucked. It is true that the next time

I could scarcely hope to suck my stones in the same order as the first time and that the

first, seventh and twelfth for example of the first cycle might very well be the sixth,

eleventh and sixteenth respectively of the second, if the worst came to the worst. But

that was a drawback I could not avoid. And if in the cycles taken together utter confu-

sion was bound to reign, at least within each cycle taken separately I could be easy in

my mind, at least as easy as one can be, in a proceeding of this kind. For in order for

each cycle to be identical, as to the succession of stones in my mouth, and God knows I

had set my heart on it, the only means were numbered stones or sixteen pockets. And

rather than make twelve more pockets or number my stones, I preferred to make the best

of the comparative peace of mind I enjoyed within each cycle taken separately. For it

was not enough to number the stones, but I would have had to remember, every time I

put a stone in my mouth, the number I needed and look for it in my pocket. Which would

3PROLOGUE

have put me off stone for ever, in a very short time. For I would never have been sure of

not making a mistake, unless of course I had kept a kind of register, in which to tick off

the stones one by one, as I sucked them. And of this I believed myself incapable. No, the

only perfect solution would have been the sixteen pockets, symmetrically disposed,

each one with its stone. Then I would have needed neither to number nor to think, but

merely, as I sucked a given stone, to move on the fifteen others, each to the next pocket,

a delicate business admittedly, but within my power, and to call always on the same

pocket when I felt like a suck. This would have freed me from all anxiety, not only within

each cycle taken separately, but also for the sum of all cycles, though they went on for-

ever. But however imperfect my own solution was, I was pleased at having found it all

alone, yes, quite pleased. And if it was perhaps less sound than I had thought in the first

flush of discovery, its inelegance never diminished. And it was above all inelegant in

this, to my mind, that the uneven distribution was painful to me, bodily. It is true that a

kind of equilibrium was reached, at a given moment, in the early stages of each cycle,

namely after the third suck and before the fourth, but it did not last long, and the rest of

the time I felt the weight of the stones dragging me now to one side, now to the other. So

it was something more than a principle I abandoned, when I abandoned the equal dis-

tribution, it was a bodily need. But to suck the stones in the way I have described, not

haphazard, but with method, was also I think a bodily need. Here then were two incom-

patible bodily needs, at loggerheads. Such things happen. But deep down I didn’t give

a tinker’s curse about being off my balance, dragged to the right hand and the left,

backwards and forwards. And deep down it was all the same to me whether I sucked a

different stone each time or always the same stone, until the end of time. For they all

tasted exactly the same. And if I had collected sixteen, it was not in order to ballast

myself in such and such a way, or to suck them turn about, but simply to have a little

store, so as never to be without. But deep down I didn’t give a fiddler’s curse about

being without, when they were all gone they would be all gone, I wouldn’t be any the

worse off, or hardly any. And the solution to which I rallied in the end was to throw

away all the stones but one, which I kept now in one pocket, now in another, and which

of course I soon lost, or threw away or gave away, or swallowed.

Samuel Beckett (1950)

4PROLOGUE

I Why Read about Science?

“If, therefore, a scientific civilization is to be a

good civilization it is necessary that increase in

knowledge should be accompanied by increase

in wisdom. I mean by wisdom a right concep-

tion of the ends of life.”

Bertrand Russell

[The Scientific Outlook (1931)]

Scientists and students are busy. When one of them picks up a paper or a

book, it is with the question, “Why should I read this?” That question is par-

ticularly trenchant for Science and Limnology. This book is not a text or

monograph about freshwater ecology. It is a discourse on the relation of some

of the most fundamental questions in the study of human knowledge to one

scientific sub-discipline, freshwater ecology. It therefore offers few theories

or concepts that busy ecologists might apply in their work or cite in an

upcoming paper. Instead, this book addresses questions that most working

scientists rarely ask: What is science? How does my field fit in? Does my

research belong? What research is worth doing? How can I do it efficiently?

Where should I look for ideas? What ideas are worth teaching? This book is

an idiosyncratic and personal account of my struggles with these issues. It

does not pretend to resolve all the problems, but it does outline how they

affect my science. It offers a starting point for the contemplation of science as

I see it. This chapter establishes the need for such contemplation.

Some Misrepresentations of Science

One indication of the need for such a book is the diversity of views among

biologists in general and ecologists in particular about the nature of science.

Some sense of this confusion can be had from the introductions to general

biology texts. These texts provide an overwhelming amount of up-to-date

biological information; that virtue is not in doubt. Introductory biology books

also allow space to a few paragraphs that purport to define science. These

varied descriptions suggest a flawed grasp of the nature of science (Table 1).

The specific weaknesses of the entries in Table 1 will be clearer when the

nature of science has been explored in subsequent chapters. For the moment,

it is enough to signal the confidence, coherence, and regimentation of these

quotations. They seem to show that science is a straightforward, rational pro-

cess following a set of rules embodied in “the scientific method”. What they

really demonstrate is that biology is a naive and immature science that thinks

too little about what it is doing and where it is going.

Since the writers of biology texts are usually respected scientists, we must

hypothesize that biologists can succeed in science without worrying much

about the general nature of their endeavours. Since less than 1% of their texts

are dedicated to the nature of science, it seems fair to hypothesize that these

leading biologists believe the general nature of science to be far less impor-

tant than the thousands of biological details crowding the remainder of each

6WHY READ ABOUT SCIENCE?

Table 1. Some lapses in descriptions of the nature of science in introductory texts in

biology

The major principle underlying the

experimentation step of scientific en-

quiry is that true hypotheses can never

give rise to a prediction that can be

proved false.

(Weisz and Keogh 1982, p. 9)

An annotated historical appendix, unique

to this textbook among zoology and

biology texts, lists key discoveries in

zoology. (Hickman et al. 1984, p. viii)

The pursuit of scientific knowledge must

be guided by the physical and chemical

laws that govern the state of existence

and interactions of atoms, sub-atomic

particles, molecules and so on.

(Hickman et al. 1984, p. 7)

The ultimate goal of science is to under-

stand the natural world in terms of

concepts, interpretations that take into

account results of many experiments and

observations. These concepts are stated

as theories.... The theory of evolution is

one such conceptual theme.

(Mader 1987, p. 14)

Inductive Reasoning: A logical process

in which a generalization is developed to

explain several specific facts. Hypoth-

eses and theories are formed by inductive

reasoning.

(Brum and McKane 1989, p. 38)

Said briefly, a scientist determines prin-

ciples from observations. This method of

discovering general principles by careful

examination of specific cases is called

inductive reasoning. It first became

important to science in the 1600’s in

Europe, when Francis Bacon, Isaac New-

ton and others began to use the results of

particular experiments they had carried

out to infer general principles about how

the world operates.

(Raven and Johnson 1992, p. 3)

A theory is a hypothesis that has been

repeatedly and extensively tested. It is

supported by all the data that have been

gathered, and helps order and explain

those data.

(Keeton and Gould 1986, p. 4)

text. And since these texts are adopted in hundreds of university courses, we

can further hypothesize that most university professors of biology agree that

the details of their science are far more important than science as a whole.

Confusion about the nature of science is not limited to occasional lapses in

the hurried introductions of first year text-books. A review of the introduc-

tions to theses from research universities and of papers published in leading

ecological journals will provide similar evidence. Too many introductions

justify themselves by pointing at some missing information or uninvestigated

phenomenon that then becomes the goal of the research program. Many biol-

ogists therefore act as though “science” consists of reporting previously

unnoticed facts, and “original research” consists of doing something simply

because it has never been done before. As I will argue below, the appropriate

concern of science is instead the creation, testing and use of theory.

If professionals are little concerned with the general nature of their disci-

pline, it is scarcely surprising that the popular press and electronic media are

also confused about the nature of science. Some echo the professionals —

they see science as a vast search for facts. They write as though all facts are

found in one of two piles (Fig. 1). One, a small heap, consists of all known

facts, and represents the present state of scientific knowledge. The other, a

mountainous pile, represents the facts that science has not yet addressed. The

purpose of science is therefore to move facts from the large pile to the small

one until the large one is exhausted and the small one is immense.

Another popular conception depicts science as a sequence of discoveries.

Newton discovered gravity in his orchard, Darwin discovered natural selec-

tion on the Galapagos, and Fleming discovered penicillin in his lab. In the

same vein, the public hopes and expects that future scientists will dis-

cover cures for cancer, Aids, over-population, and depleted resources, and

7SOME MISREPRESENTATIONS OF SCIENCE

Fig. 1. The erroneous view that science consists of collecting previously unknown facts

historians can argue whether Priestly or Lavoisier was the discoverer of oxy-

gen. This view sees science as a treasure hunt wherein important principles,

concepts, theories and facts lie hidden by the artifices of stingy Nature. Par-

ticularly lucky scientists stumble across the truth; astute ones wrench truth

from Nature’s unwilling grasp with the right experiment or with a brilliant

intellectual leap (Fig. 2). Others, the unlucky and the dull, overlook vital

clues and wander into ignominy.

An indication that even scientists see science as the discovery of a pre-

existing natural order is provided by the basic protocol of many laboratory

exercises in university teaching. A piece of apparatus is made available to a

student and a question is posed. The student is required to do an experiment

and is prompted to discover the law. The law to be discovered is one posited

by a famous, usually long-dead, scientist. This protocol presents the experi-

ment as the key that unlocks one of nature’s secret boxes. When the box is

opened, the principle pops out and the student makes the one discovery that

was inevitable. If something else is found, the student has failed to repeat the

great scientist’s act of discovery, and (needless to say) the student is wrong.

8WHY READ ABOUT SCIENCE?

Fig. 2. Two versions of the erroneous view

that science consists of discovering the

truth about nature either through good luck

or hard work

Still another view sees science as the application of the scientific method.

Under this conception (Fig. 3), a scientist begins with a series of observations

or facts, and the careful consideration of these facts results in an hypothesis.

This process is called “induction”. The scientist then deduces other facts from

the hypothesis and “tests” the hypothesis by determining if the deduced facts

are actually observed. If the observations differ from the expectation, the

hypothesis is abandoned. If observation agrees with expectation, the scientist

places a little more faith in the hypothesis and tests it further. As confirma-

tions accumulate, the hypothesis gains in status, becoming first a theory and

finally a natural law.

9SOME MISREPRESENTATIONS OF SCIENCE

Fig. 3. An erroneous version of the scientific method, one that develops true theories

and confuses fact with theory

This description is the treatment that appears in introductory texts. It

seems a serviceable starting point, but it has a number of faults. In practice,

the different elements in the scientific method are much more variable and

much less methodical. For example, scientists often start with an hypothesis

instead of observation; the inductive step may be no more logical than

whimsy; many tests are often biased and flawed; negative evidence likely

exists for every hypothesis, theory and law, but scientists ignore it; most sci-

entists are never aware of a point in time when they made a discovery and

many productive, important researchers are not aware of discovering anything

at all; no theory can be considered “true” or above the threat of disproof in

future tests; and falsification is rarely, if ever, unquestionably complete. To

look at these seeming problems in more detail, I will have to define the basic

elements of the scientific method.

Some Basic Distinctions

Facts and theories. First it is essential that we distinguish between facts

and theories. If we do not do so, we will never understand science. Many

scientists confuse the two. If we look at books or journals, we often see dis-

coveries and laws treated as facts, as suggested in Fig. 3. For example, most

biologists act as if evolution and the elemental table are facts, when they are

really theories.

A fact is an observation, a datum or sense impression which has not yet

been consciously interpreted and about which no scientific claim is being

made. By itself, a fact is empty and useless, because it gives no basis for

action. Parenthetically, one may object that such a pure fact probably cannot

exist, that all observations are interpreted through our biological and cultural

biases as soon as they are sensed. In other words, all facts are “theory-laden”.

A stricter interpretation would define a fact so that, as soon as it became more

than empty and useless, the fact would be termed a theory. I accept this, but

will not complicate discussion further for the time being.

A theory is a generalization that goes beyond the facts. It therefore makes

predictions which are statements about facts we do not yet know. Consider a

simple example. If I were to rise in a scientific meeting to state “it is not a fact

that animals need food to grow”, most of the audience would dismiss me as a

lunatic. Nevertheless, it is not a fact that animals need food to grow. It is far

more important. It is a theory. The facts are that the effect of starvation of a

few individuals of a few species has been studied. Each of these individuals,

when deprived of food, failed to grow, and instead wasted away and died. We

do not know that other individuals of the same species would do the same. We

10 WHY READ ABOUT SCIENCE?

can never know what every individual of every species that ever lived would

do. Therefore, we are going far beyond the facts when we claim that all ani-

mals need food to grow. When we state a theory, we make a statement that we

can never show to be true. We can however demonstrate that a theory is prob-

ably false as we shall see in the next section.

Induction and deduction. Deduction is the derivation of specific in-

stances of a generalization. In simpler terms, deduction is the process by

which we decide what predictions a theory makes. For example, suppose that

we are interested in the growth of babies, that we measured and weighed a lot

of them (Table 2) and that we had erected a theory (Fig. 4, overleaf) to

describe the relationship between the weight (in kg) and length (in cm) of

babies:

Weight = 0.0002(Length)

(1)

Perhaps few would be willing to say we have made a discovery, but by

developing an equation relating length and weight, we have created a theory,

albeit a very simple and trivial one. There are other theories that would

describe the data just as well; some of those may be much more comprehen-

sive than Eq. (1), and they may offer deeper explanations, but I will postpone

discussion of those complications. It is sufficient for the reader to accept that

one characteristic of a scientific theory is that a theory offers the power to pre-

dict about specific cases on the basis of a more general statement. Most

authorities concede the point.

The equation is a theory for two reasons. First we did not measure all

babies, so we are claiming that we can extrapolate from our observations to

babies we have never seen. Second we did not measure all sizes, even of the

babies we did measure; so we are claiming that we can interpolate the weights

that these babies had or will have at lengths we have not observed. When we

go beyond the facts by extrapolating or interpolating, we have made a theory.

11SOME BASIC DISTINCTIONS

Table 2. Some facts about the lengths and weights of some babies

Baby Length (cm) Weight (kg)

Vic 39 11.864

Sarah 30 5.400

Eva 25 3.125

Adrienne 32 6.554

Mike 29 4.878

Julian 22 2.130

Elisa 37 10.131

The theory in Fig. 4 makes some very definite predictions. It says that for

any baby we measure, there will be one, and only one, possible weight, that

predicted by Eq. (1). This weight is a deduction from the theory. It is the log-

ical consequence or implication of the generalization or theory. The impor-

tant point is that a given theory makes specific predictions about unobserved

instances, and that anyone who uses the theory will make exactly the same

predictions. The theory may be wrong, because not all babies behave as it

suggests, but that would not affect the claim that the relation is a theory.

Deductions allow us to test the theory to see if the predictions are correct.

Given a theory, like Eq. (1), and some additional specific cases that were not

used to build the theory, say Anna or Kate, we can make the required mea-

surements of the babies’ lengths, and calculate or deduce their expected

weights. We can then test these predictions by observing the babies’ weights

and comparing them to our expectations. If Anna or Kate is lighter or heavier

than we predicted, we would have falsified our theory and therefore we would

have to revise it.

In describing the creation of a theory, I skipped over one of the most con-

tentious parts, induction. Induction is the process by which we move from a

set of facts to a theory or generalization. This is where intuition or inspiration

enters science. The scientist looks at the facts and they, in some mysterious

way called induction, suggest a generality to the scientist. Induction is not a

logical process. It does not lead inevitably to one conclusion, but instead

could lead to an infinity of possible theories.

12 WHY READ ABOUT SCIENCE?

Fig. 4. A theory about the size of babies

The point that the same set of facts could inspire different researchers to

entirely different theories seems hard for many people, including some scien-

tists, to accept. I will therefore develop a ridiculously simple illustration

(Fig. 5). The example will again deal with growing babies but this time, just

for variety, we shall develop a theory about how fast babies grow. We will

again begin by making a few measurements of weight (W, in kg) and age (X,

in months), and after one month’s work we might find:

Age Weight

Now I need only sit back, contemplate the data and wait for an inspiration.

After some time, I might hit on a more general pattern and propose a theory

to describe the growth of a baby:

W = X (2)

13SOME BASIC DISTINCTIONS

Fig. 5. The development of alternative theories about the effect of age on the weight of

babies

A more sophisticated, or at least more mathematically competent, ob-

server might instead propose another observation on the basis of the same

observations:

W = e

0.346X

(3)

In fact there is an infinite series of relations, each representing a theoreti-

cal generalization, that could describe these data.

Logic will never tell us which of these simple theories best describes the

growth of a baby, but we can logically deduce the consequences of the two

competing theories. If Eq. (2) is correct, then W = 3 kg when X = 3 months.

But if Eq. (3) is correct then W = 4 kg when X = 3 months. Assuming that we

still have our baby, we need only wait until it is 3 months old to take the

observation that will allow us to determine which theory makes the better pre-

diction. If we find that W = 4 at X = 3, we can reject W = X as the less useful

theory. We thus know that W = X is wrong, but we cannot therefore claim that

W = e

0.346X

is correct. Someone else might look at the three pairs of data

points and induce that:

= X + W

X–1

(4)

where the subscripts indicate weight at the ages of X and X–1 months.

Since Eq. (4) fits the available data as well as Eq. (3), we cannot tell which

of these two competitors, or of a host of other possible theories connecting

the points, is right or wrong or even better. However, once again we can

deduce the logical consequences of the competing theories. When X = 4,

Eq. (3) suggests that W

= 8, but Eq. (4) would instead suggest that W

= 7.

Once again, we must wait a month and make more observations to test these

alternatives. Obviously, we will never reach the end of this process. We could

postulate various wavy lines or step functions implying varying growth rates

within each month, or an infinity of other possibilities that could join the four

weights of the growing baby. In fact, no matter how many points there are,

there will still be an infinite number of relations that could connect them

together, and because we always use induction to arrive at the theory to

describe these points, there can never be any guarantee that we have found the

right one. In other words, we can never know if we have found the truth and

therefore we should never claim that a theory is true in the sense that it is

beyond doubt.

This is a profound discovery. It is one that Aristotle never made, Galileo

rejected, and Newton dismissed. The widespread acceptance of the principle

that we can never be sure of anything in science is one of the most revolu-

tionary changes of the 20th century.

14 WHY READ ABOUT SCIENCE?

Empirical and explanatory theories. The theories I have used to illus-

trate this discussion are modest statements of trend that describe some data

and could be used to predict future observations of the same kind. Many sci-

entists are unwilling to call these statements “theories”. I see this as only a

problem of definition.

Like many who have considered the problem, I call any statements that

make predictions “theories”. This single term embraces two general types

which I call “empirical theories” and “explanatory theories”. Empirical theo-

ries are simple relationships based on observed patterns (e.g. allometric

relations, species-area curves, the second law of thermodynamics) that

make predictions by assuming that the future relations among the variables

will resemble those in the past. Explanatory theories are grander, more

comprehensive statements that not only make predictions, but also offer a

comprehensible explanation of the phenomenon being predicted, like the

size-efficiency hypothesis of Brooks and Dodson (1965), the trophic cascades

of Carpenter et al. (1985), Darwin’s theory of evolution by natural selection,

and various theories of creation, like the big-bang hypothesis. Both empirical

and explanatory theories play important roles in science.

The history of scientific achievement shows that theories develop in a

characteristic sequence. First the scientist surveys the subject matter of inter-

est, looking for patterns that might allow a prediction. This might be the

swirling of stars in the night sky, or the occurrence of rain, or the production

of certain chemicals in the lab. This search seems a simple step but it is just

the opposite. The patterns we are seeking are invariably set among a vast col-

lection of confusing and unrelated facts. These irrelevant observations often

obscure the regularity of the system under study.

Once the scientist has perceived a regularity in the objects of study, and

expressed this pattern unambiguously, an empirical theory has been pro-

duced. Empirical theories may be complex, but they are more likely to be

simple X-Y relationships because such relations are so easy to perceive and to

define. Thus the relations describing the weight of a baby from its age or

length are theories. They are theories because they generalize from our obser-

vations and allow the prediction of weight from any value of age or length.

Empirical theories can be useful, but they have limitations. First, they

make predictions only about the correlated variables. Thus, they can never

generate unexpected predictions about other aspects of these entities or about

other phenomena. They remain theories of relatively low generality. Second,

they do not satisfy our desire to explain our environment; this sense of under-

standing seems to be a bodily need, at least for some researchers.

Empirical theories stimulate other scientists to explain why the theories

work. With luck, someone will eventually replace the original empirical

15SOME BASIC DISTINCTIONS

theory with an explanatory theory. Because this new theory relates the

observed variables to other observations, it may make more predictions and

thus be more useful. Given the limited predictive power of empirical theories,

many scientists underplay their importance in science. Nevertheless, the his-

tory of scientific development shows that empirical theories are a crucial step

toward explanation.

In summary, science is not about collecting facts or observations. It is the

process of identifying, testing and organizing generalizations or theories that

go beyond the observed facts and, in some sense, explain these facts as

instances of a general pattern. Both empirical and explanatory theories are

created by induction, an inspired guess that leads us to postulate some regu-

larity in the universe. They are then tested by deduction that allows us to

know what the theory predicts so we may compare its predictions to further

observations.

The Importance of Science

Why should we care what science is? The reasons are clear. As citizens,

we expect science to give us some grasp of the risks that we face and some

measure of control over our fate. As taxpayers, we ultimately fund research,

and so we must learn to scrutinize the growing demands of modern science

for money and resources. As teachers and students, we need to know what

science is so that we can teach and learn what is scientifically important, and

disregard what is trivial. As scientists, we need a better knowledge of what we

are doing, so we can use our resources well to confront the problems of sci-

ence and humanity, so we can promote our vision to the rest of society, and so

we can defend it from unjust criticisms. We cannot afford to be ignorant of the

nature of science any longer. Society must learn what it can expect from sci-

ence, and what it cannot.

There seems little call for a detailed defense of the thesis that science

plays an important role in our civilization and therefore that the nature of

science should be better appreciated. Like it or not, our food, shelter, health,

our ways of life depend on science and technology. We may deplore this

dependency as unnatural, dangerous, and unstable, but we cannot change the

situation. Science has helped create the problems of the 20th century, but

to throw away science at this stage in civilization would be a fatal error.

We now depend on science so much that the solution to our dilemma will be

scientific, whether it is civilized or catastrophic. We must use science for

good, because we must use science. That will be easier if we know what

science is.

16 WHY READ ABOUT SCIENCE?

Many humanists have taken the trouble to discover what science is. They

often do a better job of explaining science than do the scientists. It may rankle

scientists to turn to humanists to discover the nature of science. However,

there is no reason to disdain their help.

The prologue to this book is an allegory of scientific research. It shows

that the novelist and playwright, Samuel Beckett, had a keener appreciation

of the nature of scientific enquiry than many scientists. There is science in

Molloy’s struggles with the problem of the sucking stones, in his abandon-

ment of the vaguely felt, yet fundamental principle of trim, and in the

inelegant (but sound) solution whose elaboration marked the end of both

enquiry and interest. In all of this, Molloy gives a better picture of science

than most introductory biology texts.

Jacques Barzun is another humanist who has concerned himself with sci-

ence. His Science: The Glorious Entertainment is a milestone. In addressing

C. P. Snow’s (1963) concept of two cultures, Barzun writes about the need to

appreciate science:

The new science is for the public a Delphic mystery; it keeps the western

intellect troubled but unenlightened, except for the practitioners them-

selves. Here we touch upon the grim deficiency of the scientific culture,

which is also the first lesson to be drawn from our historical review: the

fundamental lack in our mental and spiritual lives does not come from

the trifling division between scientists and humanists, or between scien-

tists and the whole of the laity; it comes from the fact that science and the

results of science are not with us an object of contemplation.

By common consent the sciences are taught in school and college;

but everyone admits that this teaching is wasted on three fourths of those

who are forced to endure it. For all the use or interest they find in “the

science requirement” they might as well be required to take Greek or

Latin: science remains to them a dead language. The belief persists that

if sciences were better taught they might prove to be more titillating, but

there is little agreement on how to teach them. And one reason for this is

that to the teachers and practising scientists themselves science is rarely

an object of contemplation. They teach therefore as if to intending

professionals. (Barzun 1964)

Barzun’s condemnation is well deserved. Somehow in a society that

depends on science, we manage to turn off most students. How do we do it?

We teach as we were taught, and we were taught “as to intending profession-

als.” Given a choice, few professors would elect to teach any students other

than those concentrating in biology, and most of us prefer to teach the details

of our own narrow specialities. If instead we want to instruct a larger fraction

17THE IMPORTANCE OF SCIENCE

of the general population about science, we must escape the traditions of our

own training. We must find ways to make science meaningful to more people,

without necessarily recruiting them to the profession. We must teach science

as an object worthy of contemplation. I feel our only hope of doing so is to

understand something about the nature of science. We scientists must step

back from the welter of detail that bemuses us in our daily work and learn

from enlightened humanists. If we can do so, we may be able to talk across

the gulf that sometimes separates humanist and scientist, and across those

that separate us from our students, our public patrons and our colleagues.

The Growth of Science

Derek de Solla Price (1986) dedicated much of his career to measuring the

size of science. He showed that whether one measures science by the number

of scientists engaged, the number of papers produced, the number of journals

published or the number of dollars spent, one reaches the same conclusion:

for the past 300 years, science has doubled in size every 10 to 20 years. In

other words, science doubles about twice as fast as population (Fig. 6). This

has some remarkable implications. One is that over 85% of all the scientists

who ever lived are still alive. Another is that the scientific literature increases

18 WHY READ ABOUT SCIENCE?

Fig. 6. A comparison of the growth rates of science and population in the United States.

(Modified from Price 1986)

by about ten times over the course of an individual’s career and has done so

since its inception; we have always been awash with new work and we always

will be. A third implication is that science has grown by encroaching on the

rest of society.

The growth of science has demanded accommodation from working sci-

entists. For example, we assemble in multi-disciplinary teams of specialists to

teach and do research, we insist that scientists write, and that students read,

even longer text-books, and we use the power of the computer and other

machines in our data collection, data analysis, writing and publication. Many

of us work nights, weekends, and holidays. We may focus our efforts more,

and hone our interests to narrower specialties. Some ruthlessly excise erst-

while non-professional interests from their lives — hobbies, friends, family.

Many scientists I know have already done these things, but we have not

resolved our difficulties. We may only have made things worse. Science is

growing faster than we can handle.

Obviously, science cannot grow faster than society forever. For example,

if science does not slow down, every man, woman, and child in North Amer-

ica will have a Ph.D. by the year 2200. Whom, or what, will we teach then?

Research now consumes 2 to 4% of the gross national product of most devel-

oped countries. If science were to continue to grow at present rates, this will

increase to between 4 and 8% in another generation, and between 16 and 32%

in another 100 years. There must be an upper limit and the explosive growth

of science must eventually slow as that limit is approached. Since science

already commands a large share of resources, we should expect to see the

reduction in growth in the near future.

A slower rate of growth will present new problems, and require some hard

decisions. For example, it is unlikely that society will fund all future mega-

projects of all the disciplines, or meet all the demands of all the researchers.

Eventually, choices will be made among many seemingly incomparable

proposals. For example, we may have to decide if science is better served by

a space station, a biotechnology complex, a mass accelerator, or an oceano-

graphic vessel. We may have to compare the desirability of research into

biodiversity with that into chemical pollution or crop yields. We may have to

decide among sub-atomic physics, molecular biology, astronomy and limnol-

ogy. To do that, we will likely have to know what science is, not just what

interests its sub-disciplines.

Summary

I can now return to the question in the title of the chapter: Why read about

science? First, a growing literature shows that science can be appreciated and

19THE GROWTH OF SCIENCE

understood as a process, rather than simply as a body of information, so that

we can expect our reading to be profitable. Second, there are many indica-

tions that science is not properly appreciated. Introductory texts and graduate

theses show that many biologists are unsure of the nature of science and the

role of the scientist; I believe that an appreciation of science would make us

better teachers and produce better students. There is also evidence that the

fundamental components of research — facts, theories, tests, induction and

deduction — are poorly understood by many members of society; a better

grasp of these basics would allow the citizen to function better in a society

that funds and depends on scientific research. It may also allow scientists to

do their jobs better. Finally, we should learn what science is and what it is not,

because the dynamics of growth of humanity and science imply that the

traditional relations between science and society will soon change. Modern

researchers and citizens are about to experience interesting times, and I

believe that an appreciation of the nature of science will help them find a way

out of the gathering confusion.

20 WHY READ ABOUT SCIENCE?

II A Brief History of Method

“The great scientists ... represent to me a simple but

impressive idea of science.... This, then, for me is

science. I do not try to define it, for very good rea-

sons. I only wish to draw a simple picture of the

kind of men I have in mind, and of their activities.

And the picture will be an oversimplification.... My

criterion of demarcation between science and non-

science is a simple logical analysis of this picture.”

K. R. Popper

[The Problem of Demarcation (1934)]

Much of this book is premised on Karl Popper’s distinction between scientific

theory and non-scientific concept, his criterion of demarcation. According to

Popper a construct qualifies as a scientific theory if it makes a potentially

falsifiable statement or set of statements. These statements are called “pre-

dictions”. The main goals of science are to make theories, to use theories to

make predictions and to assess those predictions against observation.

Although Popper’s views are widely known, they are not universally

accepted even by philosophers, and their relevance is even less appreciated by

many working scientists. For example, I was raised in a tradition that science

discovers the truth, that only a scientist can understand science, and that

philosophers and historians had nothing to tell the researcher. I came to real-

ize the folly of that position through a consideration of the history of biology,

a history that often reflects the stages of my own philosophical development

and often those of other scientists. This chapter therefore uses an historical

overview of biological thought as a device to appreciate Popper’s criterion of

demarcation.

Three Ways to Knowledge

For all the variety of human thought and endeavour, there are only three

methods of gaining information about the universe: the intuitive method, the

metaphysical method, and the scientific method. Each method is character-

ized by certain assumptions about nature and by criteria for judging insights

that the methods produce.

The intuitive method is the oldest way of discovery. It assumes that no

laws govern the behaviour of natural objects or, if there are laws, they can be

repealed at any time by some greater organizing being or force. Given the

fickleness of observable phenomena, the intuitive method puts little faith in

observation. Instead, it holds that the only way to gain knowledge of lasting

value is through revelation. Truth will be revealed to us if we put ourselves in

so receptive a frame of mind that the organizing force can reveal its inten-

tions. It is a corollary of this view that humans, by their own efforts, cannot

gain any real understanding of the universe or hope to predict future events.

The second method, the metaphysical method, has been favoured by many

philosophers. It assumes that the behaviour of natural objects is governed by

a set of laws and that people can discover these laws by their own efforts.

This method emphasizes the power of the human mind to see these laws. It

begins with the search for premises that are obviously true and, by the use of

logic, deduces natural laws from these axiomatic truths. Both the intuitive

and metaphysical methods justify their insights by interpreting appropriate

observations as instances of the perceived general truths.

Finally, the scientific method shares the metaphysicians’ assumptions that

the universe functions according to laws. Scientists differ from metaphysi-

cians in that they rely not only on thought, but also on observation to define

these laws. Science may therefore begin with observations, as suggested in

Fig. 3, or with an idea. Wherever the method begins, scientists use their

brains to produce a theory or law. Then they move to test the implications of

theory against new observations. If the theory fails to predict well, the theory

is changed and the new theory is tested in its turn.

The essential difference between the scientific method and the others is

that the statements of science need not be truths. Science does not require its

practitioners to perceive truth directly, nor does it accept that others can do

so. In science, knowledge is always hypothetical, so the ultimate arbiter in

science should be the testimony of observation, not the fervour of belief.

The three methods of enquiry are not necessarily applied separately. Time

has allowed hybridization, and the history of science can be very usefully

interpreted as the history of the interplay of these three methods.

Aristotle

We begin with Aristotle (384–322

BC) because science arguably began

with the Greeks and Aristotle was the most influential of the Greek scientists.

22 A BRIEF HISTORY OF METHOD

We are only interested in his method of finding out about nature. When we

look at how Aristotle did that, we find a curious blend of metaphysics and

science.

Aristotle should be considered a scientist because he insisted on the

importance of observations. For example, 2300 years ago it was commonly

believed that the human embryo nourished itself by grasping the mother’s

flesh with its mouth and sucking. Aristotle ridiculed this idea because “any-

one who takes the trouble to look” will see that the embryo is completely

enclosed in a fluid filled bag; it could not possibly suck the mother’s flesh

(Bodenheimer 1953). Aristotle concluded that nourishment must enter via

the placenta and umbilical cord (Fig. 7A, overleaf). This is what we still

believe today.

Aristotle’s argument for placental nutrition, although it concerned a small

point, was a piece of science. He built on one theory — that all animals need

nutrition — and one observation — that the fetus is enclosed in the amniotic

sac — to conclude that the prevailing theory was false. He then drew on a fur-

ther observation — that the umbilical cord passed from mother to fetus — to

produce a generalization that concerned all human embryos: the embryo is

nourished through the placenta and cord.

In considering the problem of placental nutrition, Aristotle appears to

have thought very much as scientists do today. However, elsewhere in his

writings, we encounter arguments that are almost meaningless to us. At those

points, Aristotle blends science with his now strange metaphysics. A com-

mon property of all these now meaningless arguments is that they derive from

“intelligible principles”.

Aristotle’s intelligible principles were really general statements, or if you

wish theories, that seemed to be self-evidently true or axiomatic. They are

like the obvious truths that characterize the metaphysical method of studying

nature. For example, for Aristotle it was an intelligible principle (a) that the

universe is perfect, and on a less general scale (b) that the circle is the perfect

geometrical form. A consequence of these principles is that we should find

circles everywhere. Aristotle did (Fig. 7B). He saw instances of these princi-

ples in the paths of the planets, in the cycle of birth, life and death and, since

evolution or extinction would disrupt this perfect cycle, in the permanence of

the species. Given this bias, Aristotle would not look for extinction or evolu-

tion of living species, and would probably have disregarded any observations

relevant to those processes. As a result, he used his principles to deduce that

species are permanent.

The argument for placental nutrition seems essentially scientific even

today, but that for the permanence of the species is almost ludicrously incom-

prehensible. I have described these two instances of Aristotle’s science to

23ARISTOTLE

24 A BRIEF HISTORY OF METHOD

Fig. 7. (A) Aristotle’s use of the scientific method in developing the theory of placental

nutrition. (B) Aristotle’s use of the metaphysical method in arriving at the theory of the

permanence of the species

contrast the metaphysical and scientific methods of enquiry Aristotle used to

understand the universe.

In both cases, Aristotle was confronted by theories of uncertain origin.

Some, like the theory that the embryo sucked the mother’s flesh, were pre-

sumably common-sense beliefs of the time. Others, like the theories that the

universe and the circle are perfect, arose from his mind as intelligible princi-

ples. We cannot reject a theory because of its origins. We insist that the the-

ory make predictions, but predictions can be deduced from both theories in

Fig. 7. Both methods moved Aristotle to make other observations and to

develop other theories, like those regarding placental nutrition and the per-

manence of the species.

The difference between the scientific and metaphysical methods lies in the

way different practitioners link prediction to observation. Aristotle the scien-

tist looked for observations that could be inconsistent with prediction. When

they were inconsistent, he rejected the theory as false and moved to create a

better theory. Aristotle the metaphysician looked for observations that were

consistent with the theory because he wanted to illustrate the truth of his

intelligible principles. Because the principles were not under test, he saw con-

trary evidence not as falsifying but as irrelevant. Since the intelligible princi-

ples were not open to change, the induction of the permanence of the species

was not intended to be tested, but to extend the whole complex of theory and

observation so that as much “knowledge” as possible would be consistent

with the intelligible principles.

This explains why Aristotle’s work is alternately meaningful and mean-

ingless to us. When guided by intelligible principles, his work seems crazy,

because it reflects the world view of a brilliant man who lived in an almost

unimaginably different time and culture. Whenever he is free of these princi-

ples, whenever he saw no connection between the theories and the principles,

his use of observations becomes “scientific” and valuable.

Deduction and Induction in the Age of Reason

Throughout the dark ages, Aristotle’s ideas, beliefs and observations were

accepted almost without question. In a sense, both his observational science

and his metaphysics were treated as indubitable principles, so the distinction

between the two methods of enquiry became blurred. When science began to

emerge in the 16th century, there was a strong reaction against this meta-

physical science. This reaction went in two diametrically opposed directions.

One faction is associated with Francis Bacon (1561–1626), an English

philosopher and visionary, who also served as Lord Chancellor to James I.

25DEDUCTION AND INDUCTION IN THE AGE OF REASON

Bacon recommended that we first purge our mind of wild theories and intel-

ligible principles, and then carefully and systematically collect a mass of

observations relevant to the subject of interest. From this material, Bacon

thought we would induce a general theory, or two or three theories that could

explain the observations. He supposed that we would then disprove and elim-

inate the wrong theories by careful observations and experiments. Bacon’s

method was characterized by its absence of intelligible principles and its

emphasis on observation and induction. Subsequently, the Baconian method

has been associated with the less tenable opinion that induction proceeds log-

ically and certainly from masses of systematic observation to truth, but that is

a perversion of his more complex views (Eiseley 1973).

Another approach was taken by the French philosopher and mathemati-

cian, René Descartes (1596–1650). Descartes was impressed by the certainty

of mathematics, which advances step-by-step from one indisputable conclu-

sion to another. Any claim to true knowledge outside of mathematics seemed

dubious. He therefore concluded that we must bring order into chaos by

applying the clear and certain deductive method of mathematics to philoso-

phy and science.

Deductive science would only be possible if the deductions started from

one or more very general and true theories. Descartes saw that the intelligible

principles of Aristotle and his medieval followers had led only to confusion,

and so devoted himself to a search for indisputable axioms that could form

the basis for a true science. By rigorous thought, he arrived at two proposi-

tions he considered indubitable: I think, therefore I am; and God exists.

Descartes’ radicalism got rid of a lot of the spurious truths that had directed

the science of Aristotle and his successors. However, Descartes also left us a

one-sided view, still dependent on intelligible principles and still limited to

deduction.

Both Descartes and Bacon greatly influenced subsequent views of science.

Two schools of thought developed around their teachings. One tells us that

knowledge is obtained by induction and the other relies on deduction. The

resulting methodological debate eventually led to the newer and much greater

question of whether it is possible to obtain true knowledge in any way at all.

This terrible question undercut a basic assumption about the quality of

knowledge and the goals of understanding. This was a turning point for

science and humanity.

David Hume and Immanuel Kant both sought to answer this new question.

In doing so, they came to very different answers. Each was extremely influ-

ential and each founded a philosophical tradition based on his answer.

David Hume (1711–1776) was a Scottish philosopher and writer. Interest-

ingly (and somehow reassuringly) he thought his major philosophical treatise

26 A BRIEF HISTORY OF METHOD

was a failure that “fell stillborn from the press” (Popper and Miller 1983).

Before Hume, mathematics was considered a science, so analogies between

the two were used to support the belief that science yields true knowledge.

Hume instead separated the two, and so made that argument for the truth of

science untenable. Hume then showed that induction did not give us certain

knowledge.

I can only approximate the reasoning that led him to this belief. Philoso-

phers differ about his arguments and I have no reason to suppose that I can do

better than the professionals. Hume started with the demonstration that we

know nothing about the external world. All we have are sensory impressions.

Therefore we do not know that events in the external world regularly follow

one another. We only know that certain sensory impressions follow each

other in time.

For example, if a sequence of two events, P then Q, happens in the exter-

nal world, we can never know it. All we experience, all we know, is a succes-

sion of sensory impressions, p then q. From these impressions, we infer the

occurrence of the corresponding sequence of real events, P then Q. However

this inference is a guess or induction. Because it is not certain, we can never

know that the real events exist. We all sometimes experience this uncertainty

when we become confused about whether a memory occurred in reality or in

a dream. If we cannot know what events are real, we can similarly never

know if there is a causal connection between P and Q. If there is no causal

connection, then we can never be sure that Q or q will follow P or p. No

matter how many instances of p then q we experience, we can never claim

that we are sure that the next p will be followed by q. We have even less

reason to believe that Q will necessarily follow P.

Hume concluded that the only systems about which we have true knowl-

edge are artificial, like mathematics, and that we can never know when we

have true knowledge about the universe. In the terms I have been using, there

is no logical basis for believing that induction will ever lead us to a true

theory about nature.

The great German philosopher Immanuel Kant (1724–1804) led the clas-

sical backlash to Hume. Kant argued that our knowledge of the external world

does not merely come from Hume’s sensory perceptions. For Kant, knowl-

edge has two sources. There is empirical or a posteriori knowledge that

comes after the fact, through our senses, as Hume agrees. But there is also a

priori knowledge which is supplied by our consciousness independently of

all experience. Of these two, a priori knowledge is by far the more important

source.

In his Critique of Pure Reason, Kant argued that the most basic laws of

nature can be discovered a priori, that is before the fact. Thus, discovery does

27DEDUCTION AND INDUCTION IN THE AGE OF REASON

not require science or empirical observation, it could be achieved by pure

reasoning alone. In fact, Kant held that if we did not have these a priori laws

for perception to play upon, we could not have any experience of the world at

all.

With Hume and Kant, there appears to be a clear schism. Hume argues that

the only source of knowledge is empirical but that it is not reliable, whereas

Kant, Descartes and Aristotle found that reason is the most reliable, and per-

haps the only, source of knowledge. Philosophers have not resolved this

dichotomy, but natural scientists have tended to follow Hume. His denial of

the possibility of certain knowledge was at first devastating, unacceptable,

and even incomprehensible, but if scientists had instead followed Kant, they

might have had to abandon observation and then they could scarcely claim to

be natural scientists.

Logical Positivism

The philosophical direction that developed from Hume reached one ex-

treme in the writings of Ernst Mach and his associates. These philosophers

were known as the Vienna circle and their philosophy subsequently became

known as logical positivism. Their history and ideas are explored by Phillipp

Frank in his Modern Science and its Philosophy (1949) and his The Philo-

sophy of Science (1957) upon which I depended in writing this section. At one

time, I was deeply influenced by their writings. I no longer believe that they

represent an end-point to philosophical development, because their philo-

sophy is so extreme as to be completely unacceptable for many scientists.

However, some of the findings of logical positivism still address contempo-

rary issues in biology and so serve to show how thinking about science can

help scientists to do their work. Just as importantly, the extremity of logical

positivism prepares us to accept the more recent and useful position of Sir

Karl Popper.

Hume viewed observations as only sensory impressions and held that the-

ories suggested by these observations need not bear any relation to the laws

of nature. Logical positivism suggested the situation might be far worse:

Maybe there are no natural laws at all, for how would we know if there are?

The regularities we perceive, and the explanatory theories we build around

them, may be nothing more than a product of the scientists’ minds. Perhaps

the human mind demands the existence of laws, and scientists work in such a

way as to satisfy that need. If so, the laws of nature may be no more than a

definition of how scientists’ minds work.

On causality. As an example of this argument, I will develop Phillipp

Frank’s attack on causality. Many scientists see causality as the cement of

28 A BRIEF HISTORY OF METHOD

the universe; they hold causal connection among events to be the basis for

meaningful pattern in the universe and contend that the description of these

connections is the goal of science and the basis of theory. Frank attacks this

fundamental assumption because, if he can topple that, the rest of our self-

assurance about science and reality should follow.

Frank tried to show that the law of causality only exists because scientists

act in such a way as to preserve it. In everyday words, we could express this

law as “every event or effect has a specific cause”. Frank states the law more

rigorously: “If a State A of the universe is once followed by a State B, then

whenever A occurs again, it will be followed by B”. This pure form of the law

can find no application in science because we can never know the state of the

whole universe. But if we do not know the state of the whole universe, we can

never be sure that some additional factor will not modify the State A so that

State C follows instead. Frank feels that what we do is to reformulate the law

as a more useful approximation: “If in a finite region of space, State A is once

followed by State B and at another time by State C, we can make State B as

similar to State C as we wish by increasing the size of the region of space we

consider”. This reformulation is more meaningful if we translate it into the

everyday language of experiment: “If State A once appeared to be followed

by State B and another time by State C, then our results were spoiled by an

unknown and uncontrolled variable”. To paraphrase Frank further, when we

apply the law of causality to a finite biological system, the number of vari-

ables we control and the number of organisms we sample are determined by

the amount of agreement we demand among our replicates, that is by how

similar we require B and C to be.

Once he showed that the law of causality is rigorously valid only for an

infinite system, Frank proceeds to a second argument. Even if we suppose the

law to be valid for small, finite systems, there is still reason to doubt that it is

really a natural law. Science begins with data and these data are sensory

impressions. Our statements and generalizations must always refer to some-

thing we sense. We must be able to see them, touch them, smell them or

something. Our laws and theories must therefore be translated, or at least

translatable, into terms that have meaning in relation to what we observe.

Whatever version of the law of causality we choose, the law refers to the state

of the system. Frank defines this state in sensory terms as the sum of all per-

ceptible properties of the system. However, when we find that some observa-

tion apparently violates the law, we invent unperceived, even imaginary,

properties of the system to explain the contradiction.

Frank provides an example. Imagine two pairs of identical iron rods on a

table. Both pairs are in State A. One pair simply sits there, that is State B. The

other pair move towards each other — State C. To satisfy the law of causal-

29LOGICAL POSITIVISM

ity, we say that the latter pair of rods had an imperceptible property called

magnetism. Thus we conclude that the initial states were only apparently the

same, and in doing so we preserve the law of causality. If we act this way, the

law of causality will always be obeyed because whenever a system does not

obey the law we invent as many fictitious properties as necessary to preserve

the law.

Frank concludes that the law of causality no longer looks like a law. It is

simply a definition. It defines the way we will interpret any situation in which

A is not inevitably followed by B. If we treat causality as a law, we merely

introduce a modern intelligible principle to science.

On new ideas. Frank’s ideas on causality seem radical. After all, we have

used the concept of magnetism since we were children, whereas discussion of

States A, B, C and causality is unfamiliar and highly philosophical. Many

biologists might be tempted to dismiss logical positivism as empty intellectu-

alism. If this is so, an examination of Frank’s views about how we convince

ourselves of the truth of intelligible principles and general theories is appro-

priate.

His thesis is that a theory, when first introduced, is incomprehensible. We

do not understand it and do not use it unconsciously as a premise in our think-

ing. Therefore, when a theory is new, we treat it as a theory should be treated,

as a construct that may be “scientifically valid, but philosophically false”. It

is scientifically valid in that it makes more and better predictions than com-

peting theories, and it is philosophically false because we do not believe it

represents an eternal and self-evident truth. As we become more accustomed

to the theory we begin to have more faith in it. Finally, we come to take the

generality for truth.

Frank illustrates his point by reviewing how thinkers’ attitudes to New-

ton’s laws changed with time. Shortly after Newton published his theory of

gravitation, the Irish philosopher and cleric George Berkeley (1685–1753)

objected to it. He felt that scientists take a lot of trouble to apply, use and test

their theories, but do not try hard enough to understand them. How can a the-

ory be valid if we do not understand it? Berkeley saw that Newton’s laws

made good predictions, but found them incomprehensible. They were scien-

tifically valid, but philosophically false.

The German philosopher and scientist Gottfried von Leibniz (1646–1716)

also objected to Newton’s theory. He wondered how a moving body could

keep its direction and velocity with respect to empty space, and how bodies

can exert a force on one another through empty space. For Leibniz, both

experience and Aristotelian physics tell us that these elements of Newton’s

theory were in conflict with our perception of reality. For Berkeley and

Leibniz, Newton’s theory was philosophically false because it offended both

30 A BRIEF HISTORY OF METHOD

reason and common sense. However, it was scientifically valid. Conse-

quently, it was used by scientists and technologists for generations. It still is.

With the passage of time, Newton’s theory was built into the thoughts of

philosophers, scientists and educated laymen. It became assimilated and by

the late 18th century, it had become philosophically true. For example,

Immanuel Kant claimed to show that the law of inertia could be derived from

pure reason and believed that, unless we accept the law of inertia as true, we

will never understand nature.

In a few generations, Newton’s laws changed from being philosophically

false to being philosophically true. They eventually became a necessity of

thought. This internalization was so complete that when Einstein showed that

Newton’s laws were scientifically incomplete, and even false, it was a stun-

ning blow to the concept of scientific truth.

Sir Karl Popper

Logical positivism leaves us with the conclusion that science is not about

the real world at all. It is a description of the way that scientists’ minds orga-

nize sequences of sense impressions. As a philosophy of life and work, I do

not find this very attractive. It removes many misconceptions, but offers little

that one can use to improve one’s science. However, it is a powerful device to

free us of our own intelligible principles and to prepare us accept a different

philosophy. Logical positivism helped us escape the view that science dis-

covers the whole truth about nature. In doing so, it prepared the way for the

views of Sir Karl Popper.

Popper was born in 1902 and trained as a physicist. In Vienna, he came to

know the members of the Vienna circle and their ideas. His most influential

work was The Logic of Scientific Discovery, first published in German in

1930 and in expanded form in English in 1959. He moved to England to

escape Nazism and has since published many books and papers in English.

Good summaries of the vast corpus of his works are available in reviews by

Magee (1973) and Pera (1980), and in an anthology of his writings edited by

Miller (1985).

Popper’s contribution was to give scientists a beautifully simple scheme

for recognizing and evaluating science. He accepts much of logical posi-

tivism, including the conclusion that a theory can never be shown to be true.

Knowledge therefore cannot be a true understanding of natural laws; it is only

the ability to look into the unknown to predict as yet unobserved events.

These predictions are achieved by constructs that we call theories. Because

science is the activity that generates such theories, science is the only source

of such knowledge. Most importantly, the only good theory is one that has the

31SIR KARL POPPER

potential to be wrong. If no conceivable observation could show the theory

wrong, then the theory must predict every possibility and therefore would tell

us nothing. In other words, to qualify as a scientific theory, a statement or set

of statements must be potentially falsifiable. For example, the statement that

human babies will weigh less than 15 kg could be wrong, so it is a theory. The

statement that human babies will weigh something is not.

For Popper, scientists begin by creating a theory. It is irrelevant where this

theory came from: principle, observation, revelation, intuition, induction, or

simply a lucky guess. What is important is whether the theory identifies any

potential future observations or facts as inconsistent with the theory, because

the theory makes a prediction by telling us what facts will not be observed.

We can then test the theory by comparing future observations with those

facts. If unexpected observations are made, the theory has been falsified. If

the facts agree with the predictions, we would be justified in using it again.

Popper’s work has given us a clear working description of theories and

facts. The former are the devices we use to make predictions and the latter are

the instance that the theories predict. This great clarification should allow us

to communicate better with both scientists and non-scientists, and to do better

science. Because it is a scheme that deals only with the relation between

theory and observation, and not with intelligible principles or philosophical

axioms, we can use it, regardless of future philosophical changes. Indeed,

much of the philosophical debate that has subsequently focused on Popper’s

work seems irrelevant to me as a working scientist. Popper has freed us from

the philosophical fashions that make so much of Aristotle and other philoso-

phers incomprehensible.

For me, Popper’s work was a revelation. I was troubled by Hume’s argu-

ment that induction was fallible and verification impossible, and could see

no escape from the answer of logical positivism, that science was simply the

creation of our minds to describe their own workings. I was not satisfied with

science or philosophy.

Popper accepted the reality of the philosophical difficulties that I could not

escape, but he also saw that these things did not matter. Science works regard-

less. What makes it work is its method and central to that method is

falsification. As a working scientist I need no longer worry about being

wrong, because it is irrelevant to ask if my theory is a true representation of

the external world. I no longer need to ask if this theory is more true than that

theory. I need only ask:

(1) Does it predict anything?

(2) Does it predict more than its rivals?

(3) Can I show that the theory is wrong?

32 A BRIEF HISTORY OF METHOD

Furthermore, I can do my science knowing that I have profited from a long

philosophical tradition and that I base my thoughts on a current philosophy

whose fundamental characteristics are not likely to change. Contemplation of

the nature of science has made me a happier and better scientist.

33SIR KARL POPPER

III Normal Science and Pseudo-Science

“It is the normal practise of scientists to ignore evidence

which appears incompatible with the accepted system of

scientific knowledge, in the hope it will eventually prove

false or irrelevant. The wise neglect of such evidence pre-

vents scientific laboratories from being plunged forever

into a turmoil of incoherent and futile efforts to verify false

allegations.”

Michael Polanyi

[Personal Knowledge (1958)]

Popper’s approach has many virtues, but his science is an abstract ideal.

When Popper illustrates his ideas, he uses heroic figures like Newton and

Einstein. Popper therefore gives a goal to strive for, but not a picture of what

most real scientists do. His prescriptive definition of science must be tem-

pered with a descriptive one that reflects better the reality of science as a

human activity. Thomas Kuhn has provided one such description.

Real scientists, those who do day-to-day science, are also real people.

They want recognition, they feel the pressures of society, and they suffer var-

ious limitations of intellect, temperament, resources, and opportunity. Such

people probably comprise 99.9% of all scientists who ever lived, and this

chapter examines their work. It begins with a review of the masterful work of

Kuhn on the nature of everyday science, and ends by considering the recep-

tion of challenges to the scientific community, in light of Kuhn’s ideas. This

book, like many contemporary essays in the field, uses the word “science” in

both Popper’s prescriptive and Kuhn’s descriptive senses, but the context

should make my intention clear.

Kuhn’s “Normal” Science

In 1962, Thomas Kuhn published what might be one of the most important

books about science in this century, and certainly one that has had a continu-

ing influence on me since I first read it in 1968. The Structure of Scientific

Revolutions continues the process of uprooting our faith in science as an

austerely intellectual search for greater truth about more phenomena. But

instead of a reanalysis of the philosophy behind the scientific enterprise,

Kuhn offers an historical reanalysis.

Many histories of science treat past research either as unsuccessful

attempts to reach, or as necessary intermediary steps to achieve, contempo-

rary ideas. Kuhn rejected that approach. Instead, he provides a new and

unflattering model about what scientists actually do and have done.

An historical model of science. Kuhn posits that any branch of science

cycles between long periods of “normal science” when scientists follow a

dominant tradition or “paradigm” and short periods of crisis and revolution-

ary change when the paradigm is shaken and ultimately replaced. Kuhn also

postulates an early pre-paradigmatic stage before the discipline emerges.

That phase seems an appropriate beginning for a review of his model (Fig. 8).

Pre-paradigmatic science. The earliest members of a scientific discipline

are at a considerable disadvantage, because the discipline cannot yet be well

defined. There are no text-books to describe the material of the discipline, no

courses to provide model answers to model questions, no scientific societies

to identify the proud tradition that contemporary members of the discipline

should respect and advance, no manuals of methods, nor any reviews of

important questions.

The founders of a field are free of both the guidance and the constraints of

tradition. As a result, there is usually a great deal of confusion and flounder-

36 NORMAL SCIENCE AND PSEUDO-SCIENCE

Fig. 8. A schematic representation of Kuhn’s model of scientific revolutions

ing in the fledgling discipline. Terminology is inconsistent, methods are

suspect and even the relevance of various observations is questionable. More

positively, the field is very open because there is no constraining tradition.

Different schools of thought compete and intellectual ferment is real. In the

absence of specialists, researchers are drawn from many existing disciplines.

To talk to one another, they must disseminate their new ideas in accessible

language, and since contributions cannot assume a common intellectual base,

books are an honoured device for communication. Relevant observations are

often so simple, that the new discipline is even open to educated laymen.

Normal science. Eventually, researchers reach some modicum of agree-

ment on the nature of the field. They embrace some view about how their cor-

ner of the universe works, at least in general terms, and this view dictates

reasonable avenues of investigation. Working within this world-view, prac-

titioners develop standards for education, research, and reporting. They come

to accept certain questions as significant, and to ignore others as irrelevant.

They produce intellectual leaders, text-books, courses, and learned societies,

and these promote specific theories, applications, instrumentation, and

methods.

In Kuhn’s terminology, these common scientific traditions represent a

paradigm or series of paradigms for the new field. Paradigms are what we

refer to when we speak of Copernican astronomy, or Newtonian physics, or

evolutionary biology. These paradigms not only tell scientists what to expect

of the world, they also define legitimate subjects for future research and the

methods for that research. In Kuhn’s view, textbooks serve to propagate the

paradigms of the field, and the purpose of scientific training is to indoctrinate

a new generation of scientists to think and act like their teachers. Once the

paradigm is so established that the practitioners in the field have a well

defined research program, the field may be said to enter the phase of “normal

science”.

Before Kuhn, the accepted view was that science advances as a struggle

between competing theories (Platt 1964). A winning theory is consistent with

all relevant facts, whereas the loser is not. Kuhn instead argues that contrary

evidence is available for every theory at all times, but that scientists unite

behind their favourite anyway. Normal science therefore engenders agree-

ment among researchers, not confrontation. One might wonder why science

does not grind to a stop. The answer to this question sets Kuhn apart from

other observers of science.

Kuhn suggests that an emerging paradigm is very limited in scope and

precision. It is often more successful than alternatives only in solving those

problems that a group of scientists have recognized as particularly acute. It

out-competes the opposition and becomes established, not necessarily

37KUHN’S “NORMAL” SCIENCE

because it solves more problems, but because it promises to solve more. The

allure for scientists is that the new theory provides more questions for them to

address.

Kuhn’s normal science is a mop-up operation as scientists attempt to real-

ize the promise of their paradigm. “Normal scientists” are those who try to

squeeze nature into the conceptual mould provided by their paradigm.

Because no theory is perfect, they must often ignore, dismiss or simply not

see anomalous observations. Thus normal scientists often seem to be striving

to confirm their theories, not to test them. Kuhn suggests that even great

figures act as normal scientists for most of their careers, and only rarely as

revolutionaries. He believes that good scientists must always maintain an

“essential tension” between conservatism and radicalism (Kuhn 1977). As a

result, normal science is the business that occupies most scientists for most of

their lives.

Kuhn identifies three classes of activity that typify normal science. Some-

times researchers who seem to be testing the theory are really looking for

confirmatory instances and trying to show how useful the paradigm is. Other

times they may be observing certain phenomena more carefully and precisely

than ever before, because the paradigm suggested that such efforts may lead

to new discoveries. For example, after Newton, more exact measurements of

the position of the stars and planets allowed the discovery of other heavenly

bodies; after Dalton, more exact estimates of atomic weights allowed the

discovery of isotopes; and after Darwin, careful study of heredity led to

genetic theory. The third activity in normal science seeks to resolve the

theory’s initial ambiguities and failings.

According to Kuhn, normal scientists do not revolutionize the field, and

likely are never famous. Kuhn’s answer to the obvious question about why

they do their work is disturbing, yet it echoes Barzun’s view of science as

entertainment. Kuhn’s normal scientists do their work because they enjoy

puzzle-solving. They have a question which is certified as valid by the

paradigm, they have a set of rules for solution that the paradigm has also

specified, and they have a large part of the solution that the paradigm has

again supplied. The motivation for science is the same as that for art, history,

music and all the other activities that keep humanity occupied: our own dis-

interested curiosity, perhaps the one truly human activity.

Crisis and revolution. Kuhn’s normal science sows the seeds of its own

destruction. Eventually normal science ceases to provide us with interesting

enough puzzles, so some scientists point to previously ignored anomalies as

an indication that the old paradigm is in crisis and begin to look elsewhere for

gratification. During this period of uncertainty, the anomalies may provide

fodder for research within the old paradigm, so some workers rearticulate

38 NORMAL SCIENCE AND PSEUDO-SCIENCE

theory and practice to account for the now troublesome anomalies. Neverthe-

less, as more scientists become interested in observations that do not fit, the

old paradigm begins to fragment. An alternative approach or paradigm even-

tually promises more fertile ground for future research. The old paradigm is

abandoned, the new one takes its place, and a new generation of normal

scientists begin the cycle again.

Kuhn ends with the question of scientific progress. In a Kuhnian scientific

revolution, some problems that the old paradigm addressed may be dropped

from consideration as uninteresting. Kuhn interpreted these shifts in interest

as indications that different paradigms are incommensurate. Thus successive

paradigms cannot be compared fairly, and there is no basis to claim that new

paradigms are better than the old ones.

Kuhn’s model makes science a very human subject, and very different from

the intellectual discipline of the philosophers. His science is only “what sci-

entists do”, and is much closer to our everyday use of the word than Popper’s

heroic examples. Nevertheless, the differences between Kuhn and Popper are

smaller than they may seem (Kuhn 1977). In particular, Kuhn’s model is con-

sistent with the philosopher’s conclusion that we cannot recognize truth in sci-

ence. Indeed, given the scepticism of modern scientific philosophy, we prob-

ably feel less that we understand nature than did most of our predecessors.

Criticisms of Kuhn’s model. Despite the richness and even genius of

Kuhn’s book, some aspects of his model seem less sound. Although it is not

my intent to review his position fully, I cannot leave the topic without point-

ing to some shortcomings.

The model implies that all sciences pass through a pre-paradigmatic stage.

However, such a phase would be very difficult to identify in any area of

human interest. Theories and paradigms existed in most areas long before the

emergence of science. For example, before there was an evolutionary biology

or a uniformitarian geology, there was a creationist paradigm, and there

seems to have been some such paradigm since the dawn of humanity. Perhaps

a pre-paradigm phase is only an illusion that one sees in retrospect.

Another criticism focuses on Kuhn’s use of the scientific papers of normal

scientists as evidence for his thesis. These papers often contain confirmatory

tests of dominant paradigms. The authors’ words suggest that they are

pleased that their tests support the paradigm and that they did their

work to protect that paradigm. However, when researchers write a paper, the

rationale may have to be rephrased to fit the results. The introductions there-

fore present an idealized and flattering picture of scientific foresight, because

any other introduction would confuse the purpose of the paper and confound

the reader. If a scientist wanted desperately to overturn a paradigm but failed,

the finished paper would almost certainly describe the work as a successful

39KUHN’S “NORMAL” SCIENCE

test of the dominant ideas in the field (Medawar 1990). Kuhn may have over-

interpreted these politic misrepresentations as indicators of unthinking sup-

port for the dominant paradigm among scientists.

My final criticism is more general. Kuhn’s book is short and readable, but

this was achieved in part by excluding examples. Tests for his ideas are there-

fore difficult to devise because he provides so few models. Indeed, when one

tries to identify a paradigm, a crisis, a pre-paradigm stage, or even a field of

normal science, Kuhn’s intuitively attractive concepts prove surprisingly

difficult to apply. We discover that paradigms exists within paradigms, that

hierarchies of normality, crises and revolutions make any identification of

the current phase of a science ambiguous. Seemingly consistent episodes are

therefore easy to find because the model is slippery and the observations

malleable. For similar reasons, critical tests are rare (Cohen 1985).

Kuhn’s model is therefore not without problems. Perhaps that is appropri-

ate for a potential paradigm of the nature of science. After all, initial prob-

lems are what the model predicts.

“Pseudo-Science”

Kuhn’s analysis helps resolve one of the continuing challenges to scien-

tific researchers. It explains why most of us dedicate our lives to the resolu-

tion of apparently minor details of nature, rather than addressing glamorous

questions of broad interest to society. Why do we not leave our laboratory

benches to study alien abductions, holistic medicine, extra-sensory percep-

tion, or spectral apparitions? Kuhn’s answer is that our scientific tradition

identifies research on these topics as inappropriate. Such material can be

called “pseudo-science”, even if it passes Popper’s criterion of demarcation,

because it falls outside the Kuhnian model whereby science is largely what

normal scientists do.

In this sense, pseudo-science is anything that purports to be science, but

that the established scientific community does not accept as such. So defined,

pseudo-science is not the delusional domain of a lunatic fringe. For example,

Gregor Mendel spoke to the Brünn Natural History Society on two occasions

in 1865 about his experiments with inheritance in plants; he published this

work the next year and informed the leading scientist Karl von Naegli about

the importance of the work in 1867. Nevertheless, as far as the world of sci-

ence was concerned, Gregor Mendel did not exist. No one paid any attention

to his work until 1900 when it was rediscovered simultaneously by three

botanists (De Vries, Tschermak, and Correns) and Mendel became the father

of Genetics.

40 NORMAL SCIENCE AND PSEUDO-SCIENCE

What I am suggesting is that from 1865 to 1900, Mendel’s work was

pseudo-science, because it was treated as pseudo-science. For 35 years no one

recognized it as science. It was simply ignored. There is nothing unusual

about the treatment Mendel received. Most new ideas about science are

ignored. No one gets excited about them, no one cites them, they just disap-

pear unnoticed. That is the fate of most pseudo-science.

A further example demonstrates the other extreme of the scientific

response to pseudo-science. In 1910, the German meteorologist Alfred

Wegener became convinced that, 200 million years ago, all the continents

were joined into a single super-continent he called Pangaea. Wegener pro-

moted this theory for many years and it excited considerable debate amongst

geologists until 1929. That year, at the Geological Congress, Wegener’s

theory was officially declared to be false, and so became pseudo-science for

the geologists. Curiously, there was widespread, if tentative, acceptance of

Wegener’s views among biologists, even after it had been rejected by geolo-

gists; so a theory could be pseudo-science under one tradition while it was

still science under another. There may be no right or wrong in science, but a

very similar distinction is maintained between what the majority of scientists

declare as interesting or uninteresting. That is the point of these examples of

pseudo-science.

The year after his theory was declared false, Wegener himself disappeared

in Greenland where he had gone to test his theory. The theory did not die. A

number of new discoveries, like the lack of sediment in parts of the ocean

floor and the mirror images of fossil magnetism on either side of the mid-

oceanic ridges, eventually forced a complete re-appraisal. Today, the ‘new’

theory of plate tectonics is universally accepted.

This cruel and unfair treatment of new hypotheses is just what one should

expect. According to Kuhn, we scientists spend most of our careers trying to

patch up our leaky theories, modifying and mending them in the hope that

they will one day fit the facts. As long as the theory holds the promise of

being patchable, as long as it continues to provide interesting puzzles to keep

us amused, there is no chance that the majority of scientists will reject it. We

will cling to the established paradigm as tenaciously as a child clings to a

favourite toy.

We will not reject a favourite theory simply because someone shows us a

few embarrassing facts. Neither will we accept a new theory simply because

some rebel champions it. There is a time for new theory, and that time is when

our old theory has ceased to entertain us by generating new, but soluble,

puzzles. This forces us to look to the anomalous observations that we had pre-

viously ignored as pseudo-science. Thus Mendel was a pseudo-scientist in

1865, but by 1900 his time had come. We were ready for a new toy.

41“PSEUDO-SCIENCE”

The reverse of this reaction to a new theory is also part of the reception of

pseudo-science. As long as we are content with the dominant paradigm, the

theory it represents moves gradually towards acceptance as a universal truth.

As such, the paradigm tells us what sort of experiments we can do, what

methods we should use, what canons of evidence we will accept, and what

form of publication we should use.

The initial reaction to the theories of Mendel or Wegener could be

discounted as near-sighted conservatism that was eventually put right by

forward thinkers. In that case, the examples would show the adequacy of

scientific self-correction, despite the relativism of scientific truth and the

dominance of the paradigm. This alternative explanation seems to posit that,

although science was always wrong in the past (because no past theory has

survived unchanged), modern science is right. I prefer the relativistic expla-

nation, not just because it avoids hubris, but because it renders the scientific

conservatism of the past more rational and comprehensible. The conserva-

tives were not benighted disciples of error, but conscientious scientists work-

ing under other premises than those we use today. The lesson we should learn

from Mendel and Wegener is to be more tentative in our conclusions about the

validity of scientific theories.

Velikovsky. My last example of pseudo-science has not enjoyed the re-

habilitation of Mendel or Wegener. It has always been considered pseudo-

science and seems likely to remain so. My purpose in introducing such mate-

rial is not to champion a failed cause, but to illustrate the resistance of science

to new paradigms, the advantages and disadvantages of such resistance, and

some of the mistakes that characterize a failed scientific revolution.

Immanuel Velikovsky was born in Russia in 1895. He studied abroad, but

returned to Moscow to take a medical degree and subsequently practised

medicine and psychiatry in Tel Aviv. After 15 years, he began a study of

Akhenaton, Oedipus and Moses, during which similarities in the legends of

different civilizations convinced him that a global catastrophe took place

about 1450

BC. While seeking the cause of such an event, he discovered that

neither Babylonian nor Hindu astrologers ever made mention of Venus

among the planets, even though it is one of the brightest objects in the sky. He

concluded that Venus did not exist during early human history.

The theory. From these and many more observations, all derived from

ancient texts, Velikovsky developed the following theory and published it

in Worlds in Collision (Velikovsky 1950). Our solar system originally had

one less planet than it does now. Sometime before 1500

BC, a violent explo-

sion on Jupiter gave birth to a massive comet that eventually became the

planet Venus. About 1450

BC, this comet passed close to the earth, producing

enormous tides, global heating, electrical discharges and a rain of hydrocar-

42 NORMAL SCIENCE AND PSEUDO-SCIENCE

bons. These events are associated with the exodus of the Jews from Egypt.

The comet then disappeared into space, only to return around 747

BC, when it

collided with Mars. This collision brought the comet into planetary orbit as

Venus but so perturbed the orbit of Mars that in 687

BC, Mars almost collided

with Earth, causing one or more new global catastrophes. Although they may

not have been so devastating as the upheaval of 1450

BC, they were enough to

tilt the earth’s axis by 10°.

According to Velikovsky, this theory explains many myths and legends,

explains the absence of Venus from early astronomical records, and explains

some of earth’s petroleum deposits (as hydrocarbons from the planet’s tail).

He also believed that the theory predicted that (a) Venus would be hot, (b) its

atmosphere would contain hydrocarbons, and (c) Jupiter would emit radio

waves. Neither these predictions nor others are very clearly stated in the

book. Nevertheless, Velikovsky believed that he had made these and other

predictions, and that all of them proved correct (Anon. 1972).

Velikovsky followed Worlds in Collision with a second book, Earth in

Upheaval (Velikovsky 1955), in which he gathered together a large number of

biological and geological observations that he believed were consistent with

his theory. He places before the reader a whole series of both well-known and

obscure facts about vast bone heaps in the Arctic, about whale skeletons on

hilltops, about erratic boulders found hundreds of kilometres away from their

parent bedrock, about the food in the mouths of quick-frozen mammoths

in Siberia, etc. These observations serve three purposes. First, Velikovsky

wanted to convince us that many observations do not fit existing geological

theory. Second, he wants us to accept that there was a recent world-wide cata-

clysm, and to change the date of the last ice age so that it will be consistent

with the hypothesized approach of Venus in 1450

BC. Finally he wants to

convince us that biological evolution could not have taken place by mutation

and natural selection as Darwin supposed, but that it arose through mass

extinctions caused by the cataclysms, followed by rapid speciation through

multiple mutations caused by heat and radiation associated with the cata-

clysms.

The reception of Velikovsky’s theory. At the time, Velikovsky appeared

even more radical than he does now. His theories about rapid speciation pre-

dated the contemporary interest in discontinuous rates of speciation called

“punctuated equilibrium” (Eldredge and Gould 1972) by a generation. His

belief that single celestial events might control major turning points in terres-

trial natural history predated current theories about mass extinction and mete-

orite impacts (e.g. Melosh et al. 1990) by 30 years. And his explanation of

events in human history as the result of dramatic changes in their non-human

environment was equally far ahead of its time.

43“PSEUDO-SCIENCE”

Velikovsky managed to challenge the fundamental paradigms of four

fields simultaneously. Not surprisingly, he was not well received. Most scien-

tists simply and totally ignored his work. Some wrote damning criticisms of

his book. Five of these critics had never read it. Other scientists brought such

pressure to bear on his publishers (MacMillan) that they transferred the rights

to the book to Doubleday and Company which was less easy to pressure

because it published no textbooks. The unseemly condemnation of the author

and his ideas by the scientific and academic establishment (de Grazia et al.

1966, Rose 1972, Stove 1972) made Velikovsky something of a hero during

the 1960’s. His book sales made him a millionaire, and eventually he was

appointed to the Princeton Institute for Advanced Studies, where Einstein

had worked. But he never found scientific respectability for himself or his

theories.

Why did Velikovsky’s theory fail to win support? If we accept Thomas

Kuhn’s view of science, it is clear that Velikovsky made a number of fatal

mistakes. He failed to present scientifically acceptable evidence, he failed to

present his work in the proper form, and he tried to revolutionize fields that

were not ready for change.

Velikovsky’s data sources were ancient texts, including the Bible. For him,

observations like the parting of the Red Sea by Moses and the fall of manna

on which the Israelites fed were anomalous facts that the dominant paradigm

could not explain. For most scientists, these stories were simply irrelevant;

they were not facts at all. Most scientists saw the history of their discipline

partly as a liberation from such ideas. Scientists did not cite holy books; they

used the theories of physics, the concepts of mathematics, and the resolving

power of fine spectroscopes and powerful telescopes. Velikovsky’s sources

seemed a long step backwards. A serious work of science would be packed

with tables, graphs and equations, but Velikovsky wrote 400 pages without

any. By the standards of science, but not his own, Velikovsky presented no

data at all.

Velikovsky also failed to examine any other explanation for the observa-

tions he presented. Although we scientists cannot hope to be unbiased

towards our intellectual creations, we are expected to vet these ideas as care-

fully as possible by considering alternatives. Velikovsky passed this onus to

the reader and thus sacrificed his own credibility.

Velikovsky also used the wrong style to present his ideas. Compared to

the dry, impersonal writing of the professional researcher, his prose looks

like sensational journalism. Moreover, Velikovsky chose to publish in popu-

lar books, rather than in scientific journals. Scientists have developed formal

standards for communication, the scientific paper and the monograph (Kinne

1988), and are deeply suspicious of those who ignore those standards.

44 NORMAL SCIENCE AND PSEUDO-SCIENCE

Not only did Velikovsky fail to present his theory effectively, he also

chose to present it at the wrong time. According to Kuhn, a new theory can

only be effective when the old paradigm has entered a state of crisis, when it

has ceased to provide a bounteous supply of soluble puzzles. Unfortunately

for Velikovsky, his books appeared when traditional sciences had more puz-

zles than they had scientists to solve them. Astronomy was still ecstatic about

the giant telescope at Mount Palomar, and radio-telescopes were in the offing;

the theory of stellar evolution was still fresh, the nuclear furnace was new,

and the consequences of the red shift were being explored. Geologists were

also delighting in a surfeit of new tools: deep-drilling for stratigraphy, mag-

netometry, seismographic surveys, and soon satellite pictures and remote

sensing; intellectually, they dealt with the evolution of rock types and the

discovery of new minerals, and were on the brink of the new theory of plate

tectonics, a theory which would eventually address many of Velikovsky’s

objections. Biology was even healthier. Chromatography and the electron

microscope soon led to the development of molecular biology; evolutionists

were pursuing the possibilities of the new synthesis between genetics, natural

history, selection and molecular biology. Scientists felt no need for a radical

new paradigm, when normal science offered so much.

Finally, and perhaps most importantly, Velikovsky failed to give a clear

and unambiguous description of his theory. He hints at its beauty, like a

dancer behind seven veils, but the veils are never lowered. The theory is

never apprehended. By any scientific standard, such vagueness is unaccept-

able.

Testing Velikovsky’s theory. Kuhn’s model explains the lack of interest in

Velikovsky’s theory, but not why the theory was ridiculed rather than being

subjected to scientific tests. I therefore raise two further questions: “Can

Velikovsky’s theory be falsified?” And if so, “Why was it not tested?”

I believe that Velikovsky’s theory can be tested and that if it had been

tested, it would have been falsified. In a discussion of tree-rings in relation to

the catastrophism, Velikovsky tries to convince the reader that no trees sur-

vived the cataclysm of 1450

BC and that there had been violent climatic

changes in 747 and 687

BC. To achieve his first objective, he describes the dat-

ing of the giant sequoias of California, and concludes that “the most ancient

of these started life after the year 1300 before the present era”. This is

advanced as evidence that no tree survived the “great catastrophe of the

middle of the second millennium”. He dismissed from consideration the

oldest tree of all — the General Sherman — on the grounds that it had not

been cut down. However, everyone knows that you can age a tree without

cutting it down. In fact, the General Sherman tree had been aged in 1946 and

its germination date estimated as 1550

BC ± 500 years. Thus there is a

45“PSEUDO-SCIENCE”

good chance that this tree antedated Velikovsky’s great cataclysm. Since

Velikovsky published, even better evidence against the great cataclysm has

been found. A number of bristlecone pines have been aged and appear to have

begun life between 2050 and 2950

BC.

A second category of tree-ring data can be used to test Velikovsky’s

theory. Annual growth varies with climate, so dramatic changes in the width

of the annular rings might indicate climate change. Velikovsky found evi-

dence for such changes that might represent the cataclysms of 747

BC and

687

BC (Douglas 1919), but failed to mention that even greater changes

occurred many times in the life of these trees. Furthermore, he neglected to

mention that very large annual fluctuations in tree growth are correlated with

very slight differences in mean temperature and precipitation in the recent

record. Thus we must conclude that there is no evidence for any major distur-

bances over the entire period from 750 to 660

BC. Similar evidence for the

absence of cataclysms can be had from the record left in lake sediments.

If Velikovsky’s theory can be falsified with observations like this, one

must wonder why it was not done. I cannot speak for others. For myself I did

not bother to publish these tests or to devise others because these ideas

seemed so futile. Why would anyone want to disprove something that no one

believes (at least, no one whose scientific opinion is worth having)? If some-

one claimed that Mars was made of Edam cheese, what joy would scientists

have in disproving the theory? What place would they win in the estimation

of their peers or in the history of science? As Polanyi suggested, the normal

practice of scientists is “wise neglect”.

46 NORMAL SCIENCE AND PSEUDO-SCIENCE

IV The Ecologists’ Disease: Two Personal Examples

“In dealing with any aspect of limnology, as perhaps

any other branch of science, it is impossible to avoid

the thought that no work is perfect and that the

greater proportion of published investigations are

very imperfect indeed. Every one of us is at fault in

some way or another, every one of us must attempt to

achieve progressively higher standards in accuracy,

scope and imagination.”

G. E. Hutchinson

[The Prospect Before Us (1966)]

Ecologists have known for over a generation that something is wrong with the

earth. There are too many people, too few wild places, too much waste, too

little clean water, too many chemicals, too little food. These troubles make

the life of an ecologist interesting, if depressing. We have been dragged from

the quiet of academia to help solve the global problems of over-exploitation

and over-population.

We have tried to respond effectively. Everywhere, universities and col-

leges have produced courses, programmes, chairs, institutes and faculties to

deal with “human biology” and “environmental science”. Some ecologists

spend their evenings in legal challenges to proposed developments, political

movements, and preaching to the public. Ecological researchers offer a dizzy-

ing array of new techniques, concepts and instruments to address our prob-

lems. A suite of learned societies have been formed and a host of new journals

are being published. This is an exciting time because society desperately

needs the services of good ecologists, drawn from the full range of science

and beyond.

Nevertheless, for many ecologists, ecology has not provided the quest we

sought. We entered the science because we felt a love for nature and the

beauty of natural things, and because these things are under threat. Then, as

soon as we were trapped in our careers, teachers confronted us with theoreti-

cal models, multivariate statistics, simulations and hypothetico-deductive

frameworks. Our colleagues express horrified disbelief when we admit

ignorance of eigenvalues, matrix algebra or Laplace transforms, and we

naturalists hide our inadequacies like guilty secrets. It sometimes seems that

we can only save the things we love by abandoning them in our work.

Even as we accept our inadequacy, we make another horrifying discovery.

Different experts are equally confident, but they all have different ideas. At

this point, we should feel bewildered.

My own bewilderment first caused me pain, but then it led me to wonder

how much of what we call ecology can be considered scientific. Other ecolo-

gists are also questioning the relevance of ecological research, asking if their

work is useful, and if they could be more effective. These questions spring

from a deep disillusionment with the present paradigms of ecology. I am

encouraged by such questions, because the present confusion is a sign that

better times may be in store for us. I think ecology is ready for a Kuhnian sci-

entific revolution (Kuhn 1962) and I see criticism as the goad that will push

us to change (Peters 1991a).

I contend that the body of ecology is infected by a strange disease. The

infection is not new, but its extent was unappreciated until our troubles were

brought into the open by a set of unusual circumstances. Just as a heavy snow-

storm reveals a blockage in the coronary artery of the hapless shoveller, the

environmental crisis has revealed the unhappy state of ecology. The disease

of ecology is that it is a science that lacks theories it thought it had. When we

are asked to predict the impact of a new dam, or of an oil spill, or of chronic

chemical contamination, we cannot do it.

This diagnosis can be illustrated with examples from the greater literature,

but such critiques are available elsewhere (Peters 1991a, Schrader-Frechette

and McCoy 1993), so I need not repeat that information. This chapter dwells

on questions of lesser generality which arose in my own work. In part, I do

this because I know that work better, so I can criticize it more easily. I also

have a more subtle reason for self-criticism. I want to show that all ecologists

carry the infection and to encourage others to be at least as critical of them-

selves as they are of others.

Science and Ecology

Our problems arise because ecologists do not seem to appreciate fully

what a science should do. The job of science is to produce and examine a set

of one or more statements, called theories. A scientific theory is a tool that

specifies which of an infinite range of possible states are likely to occur, and

which are not (Fig. 9). In other words, a scientific theory is a statement that

makes a prediction and so tells us what we can expect to observe.

48 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

The most informative theories identify the likely future observations of the

system precisely and completely. To do this, they must exclude most

possibilities as unlikely. Thus the best theories are highly restrictive, and the

worst are slightly restrictive. Constructs that place no restrictions on the

future states of the system make no predictions at all and should not be called

theories.

We may want to do more than predict. For example, we may want to

explain or to understand nature. We may claim that we can do more, but those

claims only demonstrate our naivety. Science cannot do more. The only way

that we can demonstrate our understanding of nature is with predictive

power; all else is opinion and posture. By ignoring that basic limitation of

science, ecologists guarantee failure in their great endeavours, and direct

attention away from what science can do, prediction.

Non-theories

Some ecological constructs are called theories because they tell us what

might happen, even though they fail to identify what might not. As a result,

every observation is either consistent with the general construct or irrelevant

to it; no observation will falsify it. Such constructs are not theories at all. That

they are given this status by ecologists reflects our failure to think about

science.

The niche. The niche as a multi-dimensional volume in environmental

hyperspace (Hutchinson 1959) is a familiar example of non-theory. This

concept provides a model whereby we could order our observations about a

49NON-THEORIES

Fig. 9. A classification of putative scientific theories in terms of the degree to which

they eliminate possible future states of the system as improbable

species’ occurrence, or performance, as a function of some of an infinite

number of environmental factors. Because the hypervolume has no definite

shape, any form of the response will do. Because there is no minimum or

maximum number of factors to be specified, any set of appropriate observa-

tions can fit. Because there are always other axes to establish, the niche can

never be fully described, so seeming overlap between different species is not

unexpected. And because the significance of any degree of overlap on any

measured axis is unspecified, one is free to interpret overlap in any way one

wishes. In short, any observation is consistent with the construct, and none is

excluded. The multi-dimensional niche is wholly unrestrictive.

To assess a theory we must ask not “What facts are consistent with the

theory?”, but “What observations would be inconsistent with it?” That is

Popper’s criterion of falsifiability. If we focus where a theory may fail, we are

more likely to find its failings, to seek improvements and eventually to

develop better theories. But if we are interested only in showing how well a

theory performs, we will focus on confirming instances and entrench that the-

ory in the science, excluding alternatives and stultifying scientific advance.

We must remember that an infinite series of relations (i.e. of theories) can fit

any finite pool of data equally well (Chapter I), so confirmation is relatively

uninformative about the validity of a theory. As scientists, we must seek the

weaknesses of existing theory, so we can move to offer a better theory.

The competitive exclusion principle. The competitive exclusion princi-

ple provides a second case of an ecological non-theory. This principle goes

under several names, but most students of ecology are exposed to it in the

Lotka-Volterra equations. These equations ostensibly deal with the fate of

two competitors, Species A and Species B, occupying the same habitat. The

principle tells us that if you put two potentially competing species together

either A will be eliminated, presumably by competition, or B will be elimi-

nated, also by competition, or A and B will coexist, by sharing the habitat. A

final case, where both A and B die out, is implicit but uninteresting. The prin-

ciple is consistent with all possible outcomes; therefore it cannot be falsified

and provides no information.

Hardin (1961) recognized that the competitive exclusion principle was

unfalsifiable long ago, but he defended the principle as an aid to thought. For

example, it has caused generations of ecology students to puzzle through the

abstract algebra of the Lotka-Volterra equations, it has focused our thoughts

and research on examples of coexistence of similar species, and it allowed us

to organize observations of these examples within a common rationale, deter-

mining the resources over which competition is most intense, the likely

mechanisms of competitive exclusion, or those differences in resource use

that allow coexistence.

50 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

I pursued this example in my own work on the co-occurrence of calanoid

copepods in Ontario lakes. Calanoids are minute crustaceans that constitute a

major component of the zooplankton in most lakes, and in the sea. Hutchin-

son (1961) recognized that the co-occurrence of two or more species in the

homogeneous habitat presented by the open water of lakes represented a

major challenge to the exclusion principle. Co-occurrence of such similar

animals in such a simple environment should lead to exclusion, but it does

not. This “paradox of the plankton” became a classic example for limnologi-

cal applications of ecological ideas (Hutchinson 1951).

My first approach to the problem was to establish its reality. To do this,

samples were collected in over 100 lakes to determine the extent of coexis-

tence among calanoid copepods in Ontario. Calanoids were found in 95 lakes

and different species co-occurred in almost 3/4 of these. The animals were

represented by four genera: Senecella, Limnocalanus, Epischura and Diapto-

mus (Table 3).

We first used the principle to rationalize and simplify our observations.

The principle deals with competitive exclusion, but Senecella and Epischura

are thought to prey on other zooplankton; we therefore eliminated those gen-

era from consideration. As disciples of Darwin we had no difficulty in posit-

ing that ecological competition is a universal phenomenon or in accepting

Darwin’s statement that competition between closely related species is likely

more severe. We therefore further limited our analysis to the most common

and speciose genus Diaptomus, on the grounds that the others may be suffi-

ciently distinct phylogenetically that they no longer compete with Diapto-

mus. This had the further advantage of directing our attention away from Lim-

nocalanus whose little known food habits might include predation.

Diaptomus is considered a filter-feeding herbivore, although its food habits in

nature have actually been little studied. Subsequently, the genus has been

divided into several genera. I will not use this taxonomic nicety, but it could

be invoked to save the hypothesis.

51NON-THEORIES

Species Lakes Species Lakes

Diaptomus minutus 70 D. birgei 2

D. oregonensis 69 D. ashlandi 1

D. sicilis 9 Epischura lacustris 49

D. reighardi 4 Limnocalanus macrurus 11

D. sanguineus 2 Senecella calanoides 5

Table 3. The number of lakes in southern Ontario in which each species of calanoid was

found

After eliminating other genera from consideration, 92 lakes remain in the

sample; these contain seven common species of Diaptomus, and these con-

geners frequently co-occur (Table 4). D. oregonensis and D. minutus occur

together in about half the lakes, occasionally with a third species (D. sicilis in

six lakes, D. sanguineus in two, and D. ashlandi in one). D. birgei or D.

reighardi occasionally co-occur with D. minutus. This completed the first

phase of study. Directed by the competitive exclusion principle, potential co-

occurrence among congeners had been established and a scientific puzzle had

been generated.

The second part of the study was directed at the mechanisms by which this

co-occurrence was achieved, or equivalently, at the way species in the same

lake divide their habitats so that apparent co-occurrence is not real. I will only

give an impression of these results (Rigler and Langford 1967). Fig. 10 shows

that the most common putative competitors, Diaptomus oregonensis and D.

minutus, differ in their depths of maximum abundance, although there is con-

siderable overlap and in some lakes their vertical distribution is virtually

indistinguishable. When a third species is present, it consistently inhabits a

deeper stratum than either D. oregonensis or D. minutus, although it may

sometimes overlap with the two common species.

Our results are therefore consistent with the competitive exclusion princi-

ple: coexisting competitors do seem to divide their resources. However, we are

not yet justified in concluding that spatial separation is sufficient to allow co-

existence. The overlap between Diaptomus oregonensis and D. minutus seems

great, yet these species co-occur in half of our lakes. We should therefore

expect further differences between these species. Sandercock (1967) showed

52 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

Type of association

ABCDEFGH I J

D. minutus X XXXXXX

D. oregonensis XX XXX

D. sicilis XX

D. reighardi XX

D. sanguineus X

D. birgei XX

D. ashlandi X

No. of lakes 36 24 19 6213112

Table 4. Frequency of associations in which the various species of Diaptomus were

found to coexist

that the species are also temporally separated both in breeding and in diurnal

migration. These differences are more substantial, and again lead to the con-

clusion that the two species coexist because they have divided their resources.

In short, our investigation of competitive exclusion in Diaptomus ended

like all other investigations of the issue. Whenever two coexisting species are

studied, we find ecological differences between them, and thus we support

the competitive exclusion principle. When we find no difference, as when D.

oregonensis and D. minutus had similar vertical distributions, we cannot con-

clude that the principle was wrong. That observation, like the supposition that

both species use oxygen and phytoplankton, is irrelevant because the princi-

ple allows co-occurring species common use of many resources, provided

they divide at least one.

The problem is not yet finished. We have not yet shown that these differ-

ences are enough to prevent competition. We might make further observa-

tions to determine other differences in resource use, we might determine

limiting resources for Diaptomus, or we could manipulate the abundance of

53NON-THEORIES

Fig. 10. Vertical distributions of co-occurring species of the calanoid copepods (genera

Diaptomus, Senecella, Limnocalanus, Epischura) in several Ontario lakes. The length

of the horizontal bars at the base of each polygon gives the scale since each is propor-

tional to 5 copepods l

–1

one species to see how the other responds. The principle suggests much more

work we might do. It acts as a fruitful paradigm.

I do not believe that any further studies would disprove the principle of

competitive exclusion. In every case, the results would be confirmatory, or

irrelevant. This is a serious flaw. When we deal with a predictive theory, we

must be able to specify the observations that would be inconsistent with the

theory. In the case of competitive exclusion, this is not possible. Our study,

designed in light of the principle, could not have shown the competitive

exclusion principle to be false.

Ecologists seem to like constructs that fit all relevant observations. Like

Aristotle and his intelligible principles, we use observations to demonstrate

the applicability of our ideas, to shore them up against criticism, and to

extend them to new phenomena. As “theories”, these generalities are com-

pletely safe, and completely uninformative. Unlike Aristotle the scientist, we

do not use the general constructs to identify critical observations that might

cause us to change our general ideas. Indeed, we cannot do so because the

constructs are not susceptible to test. If we followed the simple rules of sci-

ence, non-predictive constructs like these would have been eliminated years

ago, and ecology would be less cluttered with nonsense.

Weak Theories

The best theories are those that tell us exactly what will happen by identi-

fying only one future state among many as probable. In doing so, they iden-

tify the many other future states as improbable. We can call these highly

desirable constructs “restrictive theories” (Fig. 9), because they restrict or

limit the range of possible futures to a narrow range of probability. Such pre-

cise predictions are not common in ecology, but they can be found where a

system is highly controlled or where the experimental manipulation is very

large.

Ecology contains many theories which are only slightly restrictive. They

might identify one or two future states that would be inconsistent with the

theory. Other weak theories are simply quantitatively inexact. They predict

trends: neonate size increases with maternal weight; species number de-

creases at higher latitudes; algae increase with nutrients; etc. These theories

are predictive, but their predictions are so uninformative that the theories are

virtually useless. They survive because ecologists do not demand better.

Strong science recognizes that falsifiability and predictive power are relative,

so each advance raises the standards for acceptable predictive power.

Evolution by natural selection. Other weak theories address only a lim-

ited range of phenomena, but are misleading because we act as though they

54 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

addressed many more. For example, the theory of evolution by natural selec-

tion may be only weakly predictive. I say “may be” because I want to be gen-

erous. The principle may not be a theory at all (Slobodkin 1968, Peters

1991a).

Natural selection is characteristically invoked to explain or rationalize the

variety of animals inhabiting the earth and their exquisite fit to their environ-

ments. In those contexts, there are four possible observations: maladaptation

and extinction, adaptation and survival, descent with modification, and an

evolutionarily stable state. These alternatives exhaust the possible future

states, but no general statement of the theory of evolution allows one to pre-

dict what will occur in a given case, or the average response in a set of cases.

Respecifications of the general theory may exclude some of these possibili-

ties and therefore seem to offer predictions, but close analysis of those cases

reveals only a narrower range of possibilities tautologically entailed by the

particularities of the case (Peters 1976).

The theoretical status of natural selection apparently depends on some

minor implications. Darwin thought that his theory would be shown false if

any organ were found which existed for the benefit of another species. Ruse

(1982) suggests that the theory of evolution predicts that some animals will

be difficult to classify and that palaeozoic mammalian fossils will not be

found. Whether or not these are predictions from the general theory is not

under debate here (see Peters 1991a). Instead I want to point out that the

absence of altruistic organs or the problems of taxonomists are not phenom-

ena that interest evolutionary biologists. If the generality of evolutionary

theory does not predict the phenomena of major interest, it is not theoretically

relevant to those interests.

A construct is not valuable just because it can be made to yield a predic-

tion. That only meets formal requirements of a scientific theory. Constructs

can be theories and still fail to tell us anything we want to know. Popper’s

demarcation is only a bare minimum.

Weak theories are misapplied when they are used in situations where they

eliminate no possibility. Like non-predictive constructs, concordances of

weak theories and data are used to organize or “explain” unpredictable ob-

servations in terms of the generality, and to extend the sway of these non-

predictive generalities. The frequency of such concordance is then used to

defend the general construct in areas where its predictive power is negligible.

The increasing popular technique of “hypothesis testing” in ecology (Fretwell

1975) often exploits this confusion to warrant weak theory, rather than to pro-

mote predictive power. The only protection against such abuse is to ask in

every instance where a theory is invoked, “What observation would have

falsified the theory?”

55WEAK THEORIES

Concepts and measurement of phosphorus fractions. Because ecolo-

gists are uncertain about the nature of theory, they often seem to confuse

theory with fact. Established, or merely familiar, theories are treated as if they

were true, and therefore no longer worthy of the tests and scepticism that are

the due of every theory. Alternative theories are regarded as contrary to facts,

and falsifying facts are seen as erroneous theories. The effect is to entrench

error and to slow the pace of scientific response and growth.

I became aware of my own confusion of fact and theory in an analysis of

the various fractions that comprise phosphorus in lakes. Phosphorus fractions

are traditionally identified operationally (Fig. 11). To measure the “total

56 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

Fig. 11. The operations by which different fractions of phosphorus in lake water are

characterized

phosphorus concentration” in a water sample, the organic material in the sam-

ple is burnt away by wet oxidation. All the phosphorus in the sample is thus

converted to a soluble, inorganic form that reacts quantitatively with an acid

molybdate reagent to yield a blue compound. The concentration of this blue

compound is proportional to that of reactive phosphorus, so phosphorus

concentration can be measured spectrophotometrically (Griesbach and Peters

1991).

If the sample is filtered before analysis, the phosphorus in the filtrate is

taken to measure “dissolved” or “soluble” phosphorus in the lake water. Solu-

ble phosphorus is analyzed in two different ways. If the sample undergoes wet

oxidation before exposure to acid molybdate, the concentration of “total solu-

ble phosphorus” is estimated. If the sample is exposed to acid molybdate with-

out oxidation, the concentration of “soluble reactive phosphorus” is measured.

The difference between total soluble phosphorus and soluble reactive phos-

phorus is the amount of soluble phosphorus liberated by oxidation and may be

called “soluble unreactive phosphorus”. The difference between total phos-

phorus and total soluble phosphorus is a measure of “particulate phosphorus”.

Each of these fractions is subject to varying interpretations, but the most

common are as follows. Because ortho-phosphate (also called PO

or inor-

ganic phosphorus) also reacts with acid molybdate, without oxidation, solu-

ble reactive phosphorus is usually considered to be PO

; because ortho-

phosphate is a prime plant nutrient, soluble reactive phosphorus is usually

taken as a measure of available algal nutrient. Similarly, because soluble

unreactive phosphorus is not ortho-phosphate, it is often considered to repre-

sent biologically unavailable forms of dissolved organic phosphorus. Particu-

late phosphorus is thought to be a mixture of the phosphorus bound to living

and dead particles. Fresh water researchers now focus on total phosphorus

(Chapter IX), but many workers still see soluble reactive phosphorus as

particularly meaningful. Such considerations were apparent in the early work

at the Experimental Lakes Area in Ontario (Armstrong and Schindler 1971),

and still prevail in work by marine biologists and public health officers

(APHA 1989).

I became interested in these fractions when I began to wonder about the

biological availability of organically bound phosphorus, and sought a lake

with high concentrations of soluble unreactive phosphorus for my experi-

ments. The prevailing theory at the time was that soluble unreactive phos-

phorus concentrations were disproportionately high in tea-coloured lakes.

Hutchinson (1957) had advanced this hypothesis to explain differences in the

proportion of soluble organic phosphorus reported in lakes in Connecticut,

Michigan and Wisconsin (Table 5, overleaf). However, when I tested this

theory in Ontario lakes with different degrees of colour, I found similar

57WEAK THEORIES

proportions of soluble unreactive phosphorus in all lakes, despite changes in

colour (Table 6).

When I was unable to produce the expected colour effects, I looked for

alternative explanations, and noticed that previous studies had used different

techniques to isolate soluble and particulate phosphorus. Juday and Birge

(1931) had used a Foerst continuous centrifuge, Tucker (1957) had used three

layers of Whatman filter paper and Hutchinson (1957) “a 35-second mem-

brane filter”. I postulated that the reported differences in the amount of solu-

ble unreactive phosphorus might reflect these different methods, and tested

my hypothesis by applying different techniques to water from the same lakes.

I found that one could have almost any concentration of soluble organic phos-

58 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

Wisconsin Michigan Linsley Pond, Ontario*

Connecticut

(Juday and Birge 1931) (Tucker 1957) (Hutchinson 1957) (Rigler 1964)

Soluble inorganic 13 11 9.5 5.9

Soluble organic 61 48 28.5 28.7

Particulate 26 41 62.5 65.4

*Grenadier Pond was excluded

Table 5. The proportion (%) of total phosphorus in different soluble fractions and in

particulates as reported for lakes in Ontario and the literature. (From Rigler 1964)

Lake Total P % of total P in each form Colour

(µg l

–1

) (Pt units)

SRP SUP PP

Grenadier Pond 133 4.8 12.5 82.7 12

Heart 44 4.8 27.8 64.7 23

Teapot 33 5.0 29.6 65.2 42

Mary 27 6.8 25.0 68.2 11

Eos 18 4.8 28.1 67.1 162

Costello 12 7.2 28.8 64.0 30

Opeongo (South Arm) 7 5.5 31.7 62.8 20

Lake of Two Rivers 7 5.3 28.9 61.8 24

Found 5 7.8 30.0 62.2 6

Table 6. Water colour and the proportion of phosphorus in different fractions in Ontario

lakes. SRP: soluble reactive phosphorus; SUP: soluble unreactive phosphorus; PP:

particulate phosphorus. Colour is measured by comparison to the colour of platinum

solutions measured in mg l

–1

. (From Rigler 1964)

phorus one wished by using the appropriate technique (Table 7). Apparently,

the proportion of “particulate” or “soluble” phosphorus in a lake depends on

the technique used, presumably because a continuum of small particles and

colloids prevents any sharp distinction between the two fractions.

I had a very similar experience with soluble reactive phosphorus. Because

soluble reactive phosphorus reacts with acid molybdate as if it were PO

, it

was assumed to be the major form of nutrient phosphorus in lakes. When I

wanted to investigate the possibility that soluble organic phosphorus, mea-

sured as soluble unreactive phosphorus, was also a nutrient, I tried to strip the

from filtered lake water with an ion exchange column. To determine the

efficiency of the column, I added a small amount of radioactive phosphate to

the water before passing the water through the exchange column. When I ana-

lyzed the elutriate, I had a surprise. Retention of soluble reactive phosphate

was high only when elutriate volumes were very small. When large volumes

of water passed through the column, more soluble reactive phosphorus

appeared in the elutriate. This did not seem to reflect exhaustion of the reten-

tion capacity of the column, because the efficiency of retention of

remained high. Soluble reactive phosphorus behaved more like soluble unre-

active phosphorus than like PO

(Fig. 12, overleaf). This behaviour suggested

that soluble reactive phosphorus was not a measure of available inorganic

nutrient, and that the soluble phosphorus in lake water was almost all unavail-

able, despite its lability with acid molybdate, and the opinion of ecologists.

A further anomaly supported the view that soluble reactive phosphorus

was not available to algae. When a small amount of PO

is added to lake

water, it is rapidly taken up by the seston (Einsele 1941, Rigler 1956). Even-

tually, a steady state is established with 90 to 98% of the label in particles and

59WEAK THEORIES

Method of Heart Mary Thompson Average

separation 8 Jul 9 May 9 Dec

(38 µg l

–1

) (16.5 µg l

–1

) (18.2 µg l

–1

)

Foerst centrifuge 66 55 85 69

3-layer No. 44 Whatman filter 34 40 37 37

5.0 µm Millipore filter 32 42 52 42

1.2 µm Millipore filter 34 38 40 37

0.45 µm Millipore filter 21 39 40 33

0.22 µm Millipore filter 16 28 20 21

0.1 µm Millipore filter 15 26 13 18

Table 7. Effect of the method of separating seston from water on the percentage of total

phosphorus appearing as soluble organic phosphorus. Values in parentheses are total P

concentration in the lake. (From Rigler 1964)

the rest in solution. This process (Fig. 13) is most parsimoniously described

as a two-compartment exchange between a small soluble compartment repre-

senting PO

in solution and a large particulate compartment representing the

labile fraction of the total particulate phosphorus. This exchanging particulate

compartment seems to consist of bacteria (Currie 1990) and might be pre-

sumed to represent 10 to 20% of the total phosphorus. If

is added to the

soluble compartment, then at equilibrium, the ratio of radioactive tracer in

particles to that in solution (

part

sol

) should be the same as the ratio

between the pools of exchanging particulate phosphorus and ortho-phosphate

exchange

:PO

). This identity allows us to calculate the size of the exchanging

particulate pool from the equilibrium distribution of tracer and the concentra-

tion of soluble reactive phosphorus (SRP), as an estimate of ortho-phosphate

concentration:

exchange

= SRP × (

part

sol

) (5)

However, when these calculations are made, the concentration of exchange-

able particulate phosphorus is too large, sometimes several times larger than

the total phosphorus concentration in the water. One of the measured values

60 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

Fig. 12. Retention of soluble unreactive phosphorus (SUP), soluble reactive phosphorus

(SRP), and radioactively labelled inorganic phosphorus (

P-PO

) when different vol-

umes of filtered lake water are passed through an ion exchange column. SRP

behaves like SUP and not like PO

must be in error, and the most likely source of this error is that soluble reac-

tive phosphorus does not represent PO

Subsequent experiments showed that the accepted technique vastly over-

estimates biologically available phosphate in lake water (Rigler 1966) and a

number of authors have reached similar conclusions (Lean 1973, Peters 1977,

Tarapchak and Herche 1988, Bentzen and Taylor 1991, Taylor and Lean

1991, Karl and Tien 1992). It appears that in phosphorus-limited systems,

soluble reactive phosphorus is an irrelevant measure of nutrient phosphorus.

Nürnberg has shown that the two are similar only where concentrations are

high, above 10 to 30 mg m

–3

(Nürnberg and Peters 1984).

This re-evaluation of various phosphorus fractions is not simply a history

of methodological improvement. I see instead a typical programme of normal

science whereby concepts, like available free nutrient, soluble but unavailable

organically bound nutrient, and nutrient that is already biologically con-

sumed, emerged from a dominant paradigm to set puzzles for the scientist.

We wondered how we were to measure these concepts, and we assumed that

the quantities we measured had the properties of the concepts: reactive phos-

phorus is available to algae or phosphorus that passes a fine filter is in solu-

tion. Working within the paradigm, I showed some inadequacies of current

techniques, but did not question current concepts.

61WEAK THEORIES

Fig. 13. A two-compartment exchange model to describe the plotted data showing rapid

uptake of radioactive phosphate by seston in lake water, in the absence of any change

in ambient level of PO

as measured by SRP concentration

Although I was pleased with the tests as pretty bits of science, I now

recognize that the programme of research they represented was flawed. The

programme confused the things I measured (e.g. soluble reactive phosphorus)

with the concepts they represented (e.g. PO

and free nutrient) and the theo-

ries in which they were involved (e.g. algae can only use PO

), until my mind

slipped easily back and forth between fact, concept and theory, confounding

and confusing these very different entities. I was trying to find a measurement

that would correspond perfectly to a perceived truth, a paradigmatic concept,

without realizing that I had no way of recognizing this correspondence if I

found it. Apparently, I felt that the theory would arise almost automatically

from the data, once the concepts were perfectly measurable. I now believe

that those years of research, for all that they were interesting to me and pro-

ductive of publications, would have been better spent if I had instead asked

myself what theories could be built around the measurements I could make

and what predictions these theories would yield. I might then have discovered

much earlier that there was no theory waiting to use the concepts I was

studying.

62 THE ECOLOGISTS’ DISEASE: TWO PERSONAL EXAMPLES

V Broader Symptoms of The Ecologists’ Disease

“The environ is a device to truncate the infinite time regres-

sions and progressions propagating, respectively, inward

toward and outward from the holon center. The truncation

occurs at the border of the system to which the defining

holon belongs, and hence the environ is also relative to this

system. Accordingly, an environ is defined as a holon

together with its associated within-system environment.”

B. C. Patten

[Environs: Relativistic Elementary

Particles for Ecology (1982)]

Confusion of concept, theory, and fact has made any assessment of ecology

difficult, because the criteria on which scientific assessments should be

made are obscured. The resulting fuzziness makes research proposals hard to

judge, bewilders potential students, and obfuscates the few useful theories in

ecology.

This chapter continues the examination of ecology that began in Chap-

ter IV, and thus illustrates the disorder of ecology by pointing out some of the

symptoms. I begin by discussing our difficulty in posing large questions that

can be answered scientifically, because I believe that this difficulty has led to

our interest in relatively uninteresting minor problems that can be easily

addressed. I then examine the dissatisfaction, even contempt, that some ecol-

ogists seem to have for imperfect theories, for probabilistic statements and

simplifications. Next, I consider our tendency to let untestable concepts grow

unchecked and the characteristic lack of concern for scientific rigour in eval-

uating the theories we have. Finally, I consider the seeming incapacity of

ecologists to use quantitative theory effectively. In all these examples, the

underlying theme is that in ignoring the criterion of falsifiability, scientists

discard or fail to grasp the touchstone of scientific quality. This fault has

ramifications for the entire scientific enterprise.

Framing Scientific Proposals

I have generated two realistic, but artificial, introductions to research pro-

posals or scientific papers to illustrate how easily we let slip the opportunity

to pose relevant scientific questions (Table 8). These introductions might

have introduced the two personal research topics discussed at length in the

previous chapter. Both proposals begin by appealing to some large, generally

desirable goal, like feeding the hungry or understanding secondary produc-

tion. But both end by proposing a highly specific study whose relation to the

grand goal is obscure.

Given this mode of operation, whereby the projected work does not strive

to resolve the specified problem, almost any generally recognized societal or

scientific problem will suffice as background for a scientific project. Instead

of identifying a testable theory about the larger issue, typical ecological intro-

ductions point out that we need to understand, or that we are ignorant of,

some component. We cannot know if this component is really important,

because no theory specifies it as a critical element. Often there is only an allu-

sion to some shared belief and that allusion allows one to introduce a specific

topic (e.g. the relation between SRP and PO

, or the distribution of Diapto-

mus in Ontario) under the aegis of a grand one (e.g. feeding the hungry).

The jump from grand science to little science is hidden by reference to our

“ignorance” or our “need to understand”. Such phrases are like the black-out

of a theatre stage between scenes, for they allow a change of topic without

any logical inter-connection. If that intellectual sleight-of-hand is not obvi-

ous, it shows us to be enured to such tricks. We no longer find them surpris-

ing or disruptive. We no longer question what they might mean. If we are

actually ignorant, we cannot know enough to mount a scientific investigation.

If we seek understanding, we should specify how we will know when this

understanding has been achieved.

Once we accept the Popperian criterion of falsifiability, we know we are

not ignorant because we can specify one or more theories that restrict the

states that we are likely to observe. We would know when we have tested the

original hypotheses because we can compare observed and predicted states.

We would know when we have improved our original hypotheses, because

we could specify states considered likely under the old theories that are

unlikely in the new ones. And we would know that we have increased our

understanding when these new hypotheses survive further rigorous tests. In

the absence of hypotheses, introductions like those in Table 8 only indicate a

topic that interests the proponent.

The Reception of Moderately Restrictive Theories

Ecology has a number of empirical theories which are only moderately

restrictive. For example, given the average concentration of phosphorus in a

64 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

65THE RECEPTION OF MODERATELY RESTRICTIVE THEORIES

Introduction

The world is hungry for animal protein. Most protein for human consumption is grown

on land, but this is inefficient, because farm animals compete with food crops for space

and because of inefficiencies in the conversion of fodders to homeothermic tissue. The

sea covers 70% of the planet but as yet produces only 10 kg of food per ha. Canada may

have five million lakes that are even less productive. Intensive aquaculture can yield

100 times more food. There is thus great potential, if the factors that limit productivity

in either fresh or salt waters can be relaxed. Of the two types of system, tractability and

small scale argue that it would be more efficient to first assess the determinants of sec-

ondary productivity in lakes, and then to use these results as models with which to

approach the limitation of productivity in the sea.

Proposal I

Nutrients usually limit the productivity of aquatic systems, yet the process by which a

given quantity of free nutrient is transformed into consumable flesh is virtually

unknown. Understanding this process will be the work of many scientists for many

years, but an important first step is the accurate assessment of available nutrient. In

lakes, phosphorus typically limits productivity and free phosphate is measured as solu-

ble reactive phosphate (SRP) by exposing filtered lake water to acid molybdate reagent.

A growing body of evidence suggests that SRP overestimates bioavailable phosphorus.

This project reassesses the relation of SRP as a measure of free phosphate.

Proposal II

Calanoid copepods form the base of pelagic marine food chains and are arguably the

most abundant organisms on earth. Yet they are only very imperfectly understood. In

large part, our ignorance reflects the difficulty in sampling and studying wild popula-

tions across thousands of square kilometres of open ocean.

Lakes can be studied more intensively and at less cost. Since calanoid copepods are

also important in lakes, the approximation involved in studying limnetic models of the

marine system is not extreme. We can therefore use lakes to develop and test initial

hypotheses about the structure and function of calanoid communities. Promising

hypotheses will eventually be tested in marine systems, but initial probing and sorting

of data and theories can be more efficiently followed in lakes than in the sea itself.

This programme will determine how congeneric species divide up a seemingly

homogeneous environment. We will survey a large number of lakes to establish the

degree to which species co-occur in different lakes and the amount of spatio-temporal

overlap in their distribution within lakes. If co-occurrence is as prevalent as anecdotal

and scattered literature accounts suggest, we will determine the likely factors that per-

mit these animals to share their simple habitats.

Table 8. Justifications for two programmes of normal scientific research in ecology.

After an ethically strong introduction, we can justify almost any study by invoking our

ignorance, the use of model systems, and the importance of understanding some funda-

mental part of the system. In neither proposal is it clear how the work will solve the

important problem in the common introduction

lake, it is possible to predict the mean chlorophyll concentration (Dillon and

Rigler 1974a) to within an order of magnitude, and given the body weight of

a Daphnia, one can make a similarly approximate estimate of its respiration

rate (Peters 1987). These moderately restrictive theories predict a range of

states, so the information they provide is probabilistic.

Probabilistic theories are good as far as they go, but we wish they went

much further. If we are planning a picnic, we want to be told that there is no

chance of rain, not that the chance is only 25%. Nevertheless, in the absence

of alternatives, such moderately restrictive theories have their place. They tell

us how well our science currently performs (as the explained variance), and

they indicate how much more we have to do (as the unexplained variance).

Moderately restrictive theories are not viewed as useful by all ecologists.

Some lament that the predictions are only approximate. For example, Shapiro

(1978) and Benndorf (1987) focus on the uncertainty of chlorophyll concen-

trations predicted from phosphorus concentration in lakes. They are con-

cerned because the chlorophyll concentration for a specific lake could lie

well off the value implied by the mean trend, and still be consistent with the

theory.

Others hold that such moderately restrictive, empirically based theories

are too simple. For example, the abundance of zooplankton, planktivorous

fish, piscivorous fish and spatial refuges can all be expected to affect chloro-

phyll development (Carpenter et al. 1985), yet they are not represented in pre-

dictive theories used for lake management (Chapter IX). The feeling that a

model is insufficiently complicated also reflects the confusion between what

contemporary science can offer and what we want. The critic posits the exis-

tence of a grand theory that describes the entire lake ecosystem and therefore

predicts chlorophyll effectively. This dream is compared to our present lim-

ited predictive power. If one discards the existing theory when it loses to a

phantom competitor, one is left with no theory at all.

These criticisms assume that explanatory theories spring fully formed

from the mind of their creator. That is not the lesson of experience. In de-

veloping their theories of astronomy and gravity, Copernicus, Newton and

Einstein drew on a tradition of recorded observation that dates back to the

beginning of history. The table of the elements was basically the description

of pattern in chemical behaviour; and the modern theory of the atom arose

from painstaking measurements of absorption spectra. Theory begins with a

search for pattern within the field of interest, passes to a rigorous description

or quantification of that pattern and, finally, to the incorporation of the pattern

into an explanatory theory. The idea that science can begin with comprehen-

sive explanatory theories betrays ignorance of how science has always

worked.

66 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

Still other critics complain that moderately restrictive theories do not tell

us everything about the lake. For example, a theory that predicts mean sum-

mer chlorophyll tells us nothing about bio-accumulation of mercury (Lehman

1986a). Such complaints indicate a healthy desire for more and better theo-

ries. Such complaints are also disturbing because they indicate a general fail-

ure of ecologists to appreciate the nature of science and scientific theory. No

theory can do everything. A theory that predicts chlorophyll will not predict

contaminant burdens or algal taxonomy. A theory that predicts planetary

motion cannot predict the natural fall of a feather nor the flight path of the

bird that dropped it.

None of these counter-points to criticism should suggest that our current

empirically derived, moderately restrictive theories approach perfection.

They do not; replacements are needed and the current generation of theories

should be discarded as soon as better alternatives are available. The moder-

ately restrictive theories we have are only a step in the identification of pat-

tern (Fig. 14). But if we do not make some first step, we will never reach the

distant goals of better prediction and understanding for which so many of us

yearn.

The Pursuit of Ecological Concepts

Science progresses towards better theories by comparing the abilities of

competing theories to predict observations in critical experiments (Platt

1964). To make such comparisons, one must identify competing theories,

and devise experiments that provide sound tests. In ecology, critical tests of

competing theories are rare. Existing ecological theories are so little appre-

ciated that most ecologists would be unable to identify one theory to predict

67THE RECEPTION OF MODERATELY RESTRICTIVE THEORIES

Fig. 14. At present, empirical ecological theory is far from where we hope to go, but it

is a first step. (From Rigler 1982a)

a given phenomenon, much less two or more competitors. Unfortunately the

response to this deficiency has not been a search for ecological theories and

patterns.

Science uses theories to pinpoint observations of importance, and uses

observations to test theories. Ecologists rarely think in these terms. Instead,

we direct our thoughts towards abstract concepts that represent elements of

a sophisticated (but incomplete) mental model of the system we want to

study. If observations are used at all, they serve to confirm that the concepts

act in nature. Ecologists thereby abandon the practice that distinguishes sci-

ence and non-science, and our science suffers as a result. For example, that

approach identified free nutrient as a critical component in the phosphorus

cycle, and led me to two decades of work trying to measure a variable for

use in a future theory (Chapter 4) rather than testing a theory. The pursuit of

concept instead of theory is not just a personal failing. I share it with many

colleagues.

The limiting factor. The history of ecology is filled with abstract discus-

sions substituting for theoretical development. The concept of the limiting

factor is a case in point. In 1840, Justus Liebig proposed his famous “law of

the minimum”. He was concerned with the growth of plants and had observed

that a plant needs many different nutrients from the soil. If one of these nutri-

ents was absent, the plant would not grow. He formalized his observations in

the law of the minimum:

... if one is present in minimal supply, growth will be minimal. This is true

no matter how abundant the other foodstuffs may be. Growth is then

dependent on the amount of foodstuff present in minimal proportion.

At its inception, the limiting factor concept was applied only to the effect of

mineral nutrition on the growth of individual plants.

The next step was taken by F. F. Blackman in 1905 who was also con-

cerned with the factors controlling the metabolic responses of plants. How-

ever, he extended the concept beyond growth by considering other processes,

like respiration, and non-mineral factors, like temperature. Moreover, Black-

man described cases where high levels of the factor limited respiration, as

high temperatures reduced plant respiration. Thus, in Blackman’s work the

initial concept of the limiting factor began to expand and change. It got

muddled.

Shelford (1911) picked up Blackman’s concept and applied it to the distri-

bution of species: “The geographic range of a species is limited by the fluctu-

ation of a single factor (or factors) beyond the limit tolerated by that

species.” Shelford thus extrapolated the concept from a factor constraining

68 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

individual metabolism to one determining species’ distributions. This exten-

sion may seem to offer wider application, but it also further inflates the con-

cept and renders any precise use of the term increasingly difficult. Elton

(1927) analyzed the geographic distribution of species more carefully than

Shelford and concluded that “biotic limiting factors” could act in conjunction

with abiotic limiting factors. Under that interpretation, a multiplicity of fac-

tors could act together, so the concept means little more than that the organ-

ism is affected by its environment.

F. E. J. Fry (1947) recognized the confusion gathering around the concept

of limiting factors. The concept seemed ready to treat all environmental

factors and all aspects of physiological and biogeographical response. To

address the problem, he reintroduced some rigorous terminology. For Fry, a

“limiting factor” was an environmental variable which regulates the

metabolic rate of an organism by virtue of its operation within the metabolic

chain. Thus nutrients, light, and oxygen could all be limiting factors, as

Liebig had suggested, but Blackman’s temperature, like pH, salinity, and

humidity, could not. Fry called these factors “controlling factors” which were

characterized by their ability to affect maximum and minimum rates, and all

rates in between. Finally, Fry recognized “lethal factors” that operated at the

extremes by killing the organism.

Fry’s redefinitions were rigorous and rational but they did not stem the

proliferation of conceptual meanings associated with the term. Eugene Odum

(1954) also began with a definition: “Any condition which approaches or

exceeds the limits of tolerance is said to be a limiting factor.” Thus Odum’s

limiting factors are equivalent to Fry’s lethal factors, and are nothing like

Liebig’s factors. However, when Odum uses the term limiting factor he obvi-

ously has many other definitions in mind. Sometimes his usage is consistent

with his definition: “Fire is ... an extremely important limiting factor”; but at

other points, his usage is similar to Fry’s: “In the geological and physiologi-

cal sense, the low concentration of CO

now existing is limiting to all land

plants.” Sometimes, he accepts that multiple limiting factors are at work, like

Elton, suggesting that “in lakes, oxygen, nitrate and phosphate are limiting.”

Later he introduces a new conception of limiting factors by claiming that “on

land ... wind exerts a limiting effect on the activities ... of organisms” and

illustrates the point with an experiment where the growth form of an alpine

plant was altered by a wind shield.

The limiting factor concept has continued to evolve. Hairston et al. (1960)

apply the term to an environmental influence that determines the maximum

population of a species. Limnologists refer to phosphorus as the factor that

limits primary productivity of a whole trophic level, or the secondary pro-

ductivity of a whole community. A glance at most contemporary ecology

69THE PURSUIT OF ECOLOGICAL CONCEPTS

texts reveals simultaneous use of multiple concepts. Each application of the

concept may be tied to observations, but these observations serve as confirm-

ing instances, not tests.

The end point of this development is that we can never hope to measure

“the limiting factor”. Ecological thinkers have associated so many meanings

and ideas with a single term that no measurable property could ever corre-

spond to all, and many different observations could correspond to one or

more ideas. Such a multi-facetted concept cannot play a role in theory, and

any construct that uses the concept, without rigorous redefinition and consis-

tent subsequent use, cannot be a theory.

This history of limiting factors is not an isolated case. Conceptual expan-

sion leading to terminological confusion and ending in unoperational concept

clusters is the common fate of many ecological ideas (Peters 1991a). As a

result, models that use such concepts cannot play a role in the formulation or

test of ecological theory. Ecologists who work with these concepts are exiled

to an untestable shadow-world that exists only in the imagination. The way to

avoid this limbo is to insist that the entities we discuss be measurable com-

ponents of predictive scientific theories.

Unconcern

Despite the developments outlined in the preceding section, some versions

of the limiting factor concept are among the most cherished simple theories in

ecology. Liebig’s law of the minimum says that the growth of an organism is

limited by only one substance at any one time. If more of that substance is

added, growth will increase, but if any other substance is added growth will

be unchanged. Extrapolation of the law to whole communities has had useful

consequences for eutrophication abatement programs: tertiary sewage treat-

ment and legislated changes to detergent composition have substantially

reduced phosphorus loads to lakes and rivers. The law of the minimum has a

strong intellectual appeal because it simplifies the theoretical problems of

complex systems.

Multiple limitation in the sea. In 1974, Theodore Smayda, a highly

respected oceanographer, published a paper in Limnology and Oceanogra-

phy, the foremost journal in his field. This paper challenged the law of the

minimum by concluding that in the nearshore waters of the western Atlantic

Ocean, as many as five factors could concurrently limit the growth of a single

clone of the planktonic alga Thalassiosira pseudonana.

Although Smayda’s paper claimed to falsify a theory that had been ac-

cepted for 150 years, it generated no excitement. It went almost as unnoticed

70 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

as Gregor Mendel’s paper on inheritance. Each year, I look at the Science

Citation Index to see how many times the paper has been cited and why. And

each year it gains a modest few citations, a total of 40 by 1992, but no one

seems to appreciate that the paper challenges one of the dominant paradigms

in ecology.

Smayda’s paper is an example of the fate of heretical ideas raised at the

wrong time. Although Smayda’s credentials, choice of journal and style of

exposition followed accepted norms, Smayda’s analysis was received with

the same indifference as Velikovsky’s (Chapter III). This was to be expected

(Polanyi 1958, Kuhn 1962). Normal ecologists have quite enough puzzles to

keep themselves busy, and see no need to upset the world-view that justifies

those puzzles as scientifically interesting. Yet one would have hoped that

some supporters of the law of the minimum would have rallied to defend their

paradigm, if only because the prestige of the author and journal gave the con-

trary view some credibility. But no one cared.

There is an irony in this anecdote. If defenders of orthodoxy had attacked

the paper, they would have discovered a fatal flaw. I chanced to study the

article particularly carefully because I planned to use it in class as an

example of a sound bioassay. When I examined the data, I found only one

limiting factor, nitrogen. The paper compared growth rates in cultures where

all nutrients were in excess with those from cultures where all nutrients but

one were in excess, and found that the absence of any one of several nutri-

ents might reduce growth below the rate where all nutrients are present in

excess. Unfortunately, that finding is irrelevant to limitation in the field. The

proper comparison is with controls to which no nutrients were added.

Except for treatments where some toxicity was evident, growth rate in-

creased above that in the no-nutrient controls control whenever nitrogen was

added. If no nitrogen was added, growth rate was similar to those of the con-

trols despite the addition of other nutrients (Fig. 15, overleaf). Here is an-

other reason to suppose that the paper would have attracted serious atten-

tion, but again no one cared.

Most ecologists can point to other examples of flaws in experimental

design or interpretation. This example is therefore only one among many. I

do not intend to blame or discredit authors who have made mistakes in

their scientific careers. We all do that and should expect to do so. I am

instead concerned about a science which does not move to correct mistakes,

that offers no resistance to challenges to its principles, and that does not

read its own literature critically. Such nonchalance suggests a science deep

in normality and far from revolution. If we need a revolutionized ecology to

meet the environmental crisis, this evidence suggests that we are far from

ready.

71UNCONCERN

Inattention to Detail

Because ecologists are not used to working with theories, they often do

not realize that strong theories and predictions provide important checks on

poor measurements and miscalculations. If theory predicts one value for

some fact and observation yields a different value, there is an anomaly. Such

anomalies are fruitful. One might check the validity of the prediction, by

recalculation, and the observation, by repetition of the measurement. This

comparison allows us to identify human errors in both processes. If the

anomaly persists, one has a potential falsification of existing theory and the

basis for future scientific work.

In the absence of prediction, observational errors often go unnoticed and

the necessity for theoretical development is hidden. Under these conditions,

scientists lack a measure of validity, they may become sloppy and science

may stagnate.

72 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

Fig. 15. Growth rate, expressed as a percentage of the maximum observed growth rate

of the alga Thalassiosira pseudonana (clone 13-1) exposed to sea water amended

with varying nutrient mixtures. Cultures which received all nutrients except nitrogen

(All – N) grew no better than control cultures (None), whereas cultures that received

nitrogen grew much better, regardless of deficiencies in other minerals. The variations

among cultures that received nitrogen may indicate other deficiencies that are ex-

pressed only when nitrogen is available in excess. TM = trace metals, VITS = vitamins.

(Data from Smayda 1974)

The calculation of secondary productivity. I became aware of this in-

attention in preparing a review of the methods of calculating secondary pro-

duction (Rigler and Downing 1984). This section is a precis of that review.

Secondary production has fascinated ecologists for much of this century

(Downing 1984). Many theories have been advanced to explain it and many

methods have been used to measure it. The basic concepts and techniques are

simple. Nevertheless, I found myself amazed at the total confusion that sur-

rounds these simple calculations. I worked through the literature in a futile

search for good examples of production studies. All I found was one error

after another.

I believe these errors arose because production biologists have been con-

fused by the many complicated and sometimes erroneous methods described

in the various instruction manuals and review papers to which they go for

guidance. I suggest that if we were to address ourselves to the simple princi-

ple underlying the calculation we would not make so many mistakes. Fur-

thermore, we would have more mental energy left over to devote to really

difficult and interesting problems.

The production of a population is the total amount of tissue that population

synthesizes during some interval of time. This production is a rate and has the

dimensions of mass or energy per unit of time. A year is often taken as the

unit of time, and for mass we might use fresh weight, dry weight, ash-free dry

weight, carbon content, nitrogen content, etc.

To illustrate the principle of calculating production, let us consider a single

cohort of an imaginary population (Fig. 16A, overleaf). It begins with a pop-

ulation of 10 individuals each weighing W

. After an interval of time t

, one of

these individuals, now weighing W

, dies. Its lifetime production is therefore

– W

. At a later time, t

, another animal weighing W

dies, and its lifetime

production may be calculated as W

– W

. This process will continue until the

last individual dies at t

and its production W

– W

is calculated. The total

production of the cohort over the interval from t

to t

is then the sum of the

final weights (∑W

) less the initial weight of the population (10 × W

P = (∑W

– 10 × W

)/(t

– t

) (6)

That is all there is to it.

Why then do we find whole books written on the subject of production,

and within them a whole series of different calculations? There are a number

of reasons that ecologists make such heavy going out of productivity calcula-

tions. One is that natural populations cannot be known as well as the imagi-

nary cohort in Fig. 16A. As a result, we must replace individual animals with

size classes, approximate the number of individuals in each size class and

73INATTENTION TO DETAIL

approximate the size limits of the class. The problems of approximation are

real and merit thought.

A second reason for our difficulties in treating secondary production is

that production ecologists erroneously believe there are three fundamentally

different methods of calculating production from these data:

(1) increment summation

(2) mortality summation

(3) the Allen curve.

These methods are essentially identical. They differ only in the way they sum

the weight increment over time (Rigler and Downing 1984). Each requires

74 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

Fig. 16. (A) The exact calculation of secondary production by animals of known initial

and final weights. When the first animal dies, the production of the cohort is the area of

rectangle abcd; when the second animal dies, the cohort production is increased by the

area of rectangle defg, and so on until all the animals are dead, and the total area under

the curve is known. (B to D) Three variants in calculating secondary production of the

cohort in panel A. Dots indicate four observations of population size and individual

weight taken over the course of the cohort’s existence and represent the means in a size

class or over a time period. Heavy lines indicate the areas which are used to calculate

total production and shaded areas are errors in estimation

that the population be divided into a number of size classes, and that for each

size class one know N

(the average number of animals entering size class i),

min.i

(the mass of the average animal entering the size class), and W

max.i

(the

mass of the average animal leaving that size class; this is also the mass of the

average animal entering the next size class). Production is then calculated as

P = ∑N

max.i

– W

min.i

) (7)

At this point, the interesting problems begin. Most real populations do not

produce cohorts. When we measure the number of animals in a size class over

time, we do not see a regular decline in numbers (Fig. 17), but a more or less

erratic pattern of peaks and troughs as animals are born, grow and die. If the

animals can be aged, they can be sorted by age class and treated as if they rep-

resented a cohort. If this is not possible, then production can be estimated

from the number of animals in the size class (N

), the upper and lower size

limits of the class (W

min.i

, W

max.i

) and the average duration of that size class

P = ∑N

max.i

– W

min.i

)/D

(8)

75INATTENTION TO DETAIL

Fig. 17. Approximation of the production of a cohort, age- or size-class, or population

based on a single estimate of N, estimates of minimum and maximum size (W

min

and

max

), and estimated duration of the size class (D). The magnitude of the errors in this

calculation depends on the schedules of mortality and growth over the period D, as well

as on how representative the estimates of D and population size are

This equation is really an extension of the model in Fig. 16 pushed to the

bare minimum of sampling effort (Fig. 17). It is an approximation to the

extent that Eq. (8) departs from Eq. (6). For example, Eq. (6) assumes that the

timing of growth and mortality are known for every animal, but Eq. (8)

assumes that they can be approximated by averages. In fact, changes in the

scheduling of mortality and growth over the interval D

could cause signifi-

cant errors in estimating production. For example, the production of animals

that died before sampling to estimate N

is left out of Eq. (8), and if these are

many, then the equation underestimates production. Conversely, the equation

assumes that animals alive at sampling survive to reach maximum size, and to

the extent that they die soon after sampling, the equation will overestimate

production. Finally, Eq. (8) assumes a linear growth curve, but if growth is

exponential, most of the production will occur towards the end of D

, when

population is smallest; and again Eq. (8) will overestimate.

For fish or clams or humans or trees, D

is easily measured, but for the host

of tiny invertebrates that dominate aquatic ecosystems, this determination is

not easy. Consequently, a number of so-called methods of calculating pro-

duction are really disguised attempts to avoid measuring D

. These attempts

almost always lead to error and add to our confusion. I will give only one

example: the size-frequency or Hynes method.

The Hynes method really excited stream ecologists because they could

never sample their animals well enough to calculate D

and, even when they

had their samples, they could not identify the species. They were accordingly

very pleased when offered a method that required neither D

nor identification

of species. This method is based on two implicit assumptions: that total devel-

opment time equals one year for all species and that the development time of

each size class or instar, D

, is a constant. That is to say, the method assumes

that animals spend the same amount of time in each size class. The

Hynes method therefore does not overcome difficulties, it merely ignores

them. But you cannot avoid measuring N

, D

, and (W

max.i

– W

min.i

). If you try,

you will go wrong and confuse everyone else. More problems are discussed

in Rigler and Downing (1984).

Let me summarize this section. Production has been considered important

by a generation of ecologists. The method of calculating production is so

incredibly simple that a child in elementary school could be taught it. Yet

almost every zoologist who has calculated secondary production has done it

incorrectly. There are similar errors in calculating primary production, and

probably in most quantitative treatments in ecology. We can take a lesson

from this example and that lesson contains both good news and bad.

First the good news. Ecologists are still frightened by the most elementary

mathematics. Consequently we use the literature like a cook book: we look up

76 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

a method and use it without understanding the principle behind it. I know

personally that when I have to look at an equation and try to understand it, I

usually fail. I give up, feeling frustrated and stupid. The lesson in this section

is that if one has really tried to understand a paper and failed, the reason for

failure may not be that one is stupid, but that the paper is wrong.

Now for the bad news. I think the persistence and frequency of error in the

secondary production literature and in the rest of ecology shows that, by and

large, ecologists do their research superficially and carelessly. We act as if we

do not care about the validity of our results. We do not care because we are

not testing theory, so that any value will do. This is a sign of the sickness in

ecology.

We should all take pains to remove error and nonchalance in our own

work. However, we should also be concerned with the cause of these symp-

toms. If we could understand their source, we would make an enormously

greater contribution to our discipline. For me, the root of our problems is our

disinterest in prediction. Predictive theories require accurate measurements

to provide adequate tests and to avoid spurious anomalies.

Some Consequences

This chapter suggests that much of ecology is confused in its goals, uncer-

tain of its strengths, and inconsistent in its terminology. It portrays ecologists

as nonchalant about their tests, careless in their measurements, yet closed-

minded in considering alternatives. It claims that ecologists do not recognize

the few good theories they have, preferring to pass their time with weak theo-

ries and non-theories that substitute a form of explanation for prediction. It

also claims that ecologists rarely try to make predictions, believing that some

special property of their systems makes the common model for building and

testing theories inoperable.

This is an unattractive picture. It is one in which few ecologists see them-

selves. Yet I believe it is the face we turn to the public, to the granting agen-

cies, and to our students — with devastating results. In each case, a poten-

tially friendly and supportive audience is baffled by arcane subject matter.

Many turn away, feeling bored, frustrated, stupid, embarrassed and incapable.

I submit that the fault is not with them; they have sensed the real nature of

much of contemporary ecology.

Some students have such interest in ecology that they refuse to drop out.

Those few survive to become professors and researchers. Unfortunately, they

often do so by making the illogical jump from grand concerns to picayune

experiments. When they do so, they become part of normal science. They

77SOME CONSEQUENCES

accept the dominant paradigms of ecology and no longer see its anomalies

and failures. They become us.

This process of acculturation explains the failure of ecologists to appreci-

ate the nature of their science. We have all been brain-washed. To escape, we

must step outside the comfortable limits of normal science to see what needs

to be done, and to look back at what we are doing. We have to contemplate

our science.

78 BROADER SYMPTOMS OF THE ECOLOGISTS’ DISEASE

VI Why Limnology?

“There is nothing — absolutely nothing — half so

worthwhile as simply messing about in boats.”

K. Grahame

[The Wind in the Willows (1966)]

Science has a way of overwhelming its participants. Fields of interest that fit

within our scope during periods of youthful exuberance double in size every

ten to fifteen years (Price 1986), and even rare demonstrations of personal

competence invite additional duties. To succeed in their research, most con-

temporary scientists therefore have to dedicate themselves to the tasks at

hand: experimental design, observation, data analysis, publication and read-

ing in their specialty. One result is that scientists have little time to address

philosophical generalities or to worry about how their efforts contribute to the

larger body of science.

Our behaviour is justified if we believe that science is sufficiently self-

correcting: a proper overall direction arises automatically from the process of

thousands of researchers “doing science”. A similarly blissful ignorance fos-

ters the view that because any piece of scientific information is intrinsically

valuable, there is no need to fit the piece we study into a larger picture. We

may recognize the value of the long view, but too often our response is sim-

ple regret that we have not the time to think about it. None of this is accept-

able. We must reject the notion that scientific forethought is an unnecessary

luxury. To do otherwise is to deny the most fundamental of scientific tenets:

that humanity can achieve some power over our destiny by thought and

observation.

In this essay, I contemplate my own branch of science by trying to answer

a question that has bothered me for some time: Why teach or study limnol-

ogy? My answer is still only preliminary. I hope that by asking it, I will

encourage others to complete the process of analysis for limnology and to

extend that analysis to other branches of ecology, biology, and science.

What is Limnology?

Limnology is the scientific study of fresh waters. Within that limitation, its

subject matter is broad. Limnologists may be physicists, chemists, mathe-

maticians, geologists, hydrologists, engineers, or any of a host of other

specialists. Limnology could involve studies of the evaporation rate of water

collected by a pitcher plant, the thermal stratification of Lake Michigan, the

chemistry of iron, etc. For biologists, like me, limnology is more restricted:

limnology is the study of living organisms that inhabit fresh water. I will

restrict it further and deal only with living organisms in lakes. The reason for

this second restriction is partly personal, and partly convenient. I work with

lakes and like them, and if I demonstrate that studying the biota of lakes has

value then I will have demonstrated that limnology as a whole has at least that

same value.

There are obvious practical reasons to study fresh water. Water is one of

our most important and valuable resources. In Canada, many of us live in one

of the most famous lake districts in the world: five of the world’s largest lakes

lie at our doorsteps, and millions of smaller lakes dominate the landscape of

the Canadian shield and condition our lives. In the country as a whole, gov-

ernment figures suggest that fresh waters add 10 to 20 billion dollars to the

economy every year (Science Council of Canada 1988). In the United States,

extensive irrigation has allowed the deserts to bloom and feed a hungry

world. In England, a tenth of the waters of the Thames passes down domestic

drains on its way to the sea and at least as much again is used industrially. In

the developing world, water-borne diseases are major killers. At a practical

level, the need for limnology is obvious: fresh water is critical to industry,

agriculture, health, and nature, yet it is in short supply and its quality is

increasingly compromised. We must learn how to improve, to conserve and to

use this precious resource (Likens 1992). That is the practical challenge for

limnology.

Practical considerations are critically important, but they are not of central

concern in this chapter. Practical issues are not used in universities to justify

hiring a limnologist or offering a course in limnology. As university students

and teachers, we should be primarily interested in science, and the reasons for

hiring and teaching should hinge on the scientific value of the discipline. As

students, we should be asking “What is science?” As teachers, we should be

trying to answer that question. And as scientists, we should all be trying to

make a contribution to the development of science.

What is Science?

Before we can ask “Why limnology?”, we have to ask “What is this thing

called science?” Since I have discussed the point in earlier chapters, I can

answer arbitrarily here. Science is the process of making, testing and using

80 WHY LIMNOLOGY?

theories. These theories are verbal or mathematical statements that make pre-

dictions, and thereby give a functional description of the world in which we

live. I say “functional” because our theories need not give a “true” description

of the world. In fact, philosophers have shown very convincingly that science

cannot hope to give a true picture of the universe.

Our job as scientists is to produce a set of statements or theories that are

consistent with each other and which make good predictions about future

events and observations. In other words, the essence of science is in its theo-

ries, and the justification for any and every piece of research lies in its rela-

tion to a particular theory. If someone asks what you do, it is useless to

answer, “I am an entomologist”, or “I am a limnologist”, as this describes

only the tools of research. Insects and lakes are only the material used to test

theories. A better answer would be “I am interested in gene theory” or “I

study competition theory”, because this describes the ideas you wrestle with

in your research. I define ecology as the science that predicts the abundance,

distribution and other characteristics of organisms in nature. Biological lim-

nologists, as freshwater ecologists, seek to predict these characteristics of

organisms inhabiting fresh water. If limnology is to interest other ecologists,

it must show them how the study of lakes relates to the tests and problems of

other fields.

Now we can return to our original problem: “How do we justify limnol-

ogy?” We now know that we can justify it only by showing how limnology

allows us to test a scientific theory or a group of theories. In effect, we now

know what to look for among all possible justifications and our search will be

much shorter. We are looking for theories related to the study of organisms in

their natural environment, and I will argue that lakes are a particularly good

place to test those theories.

Ecological Theories

There are many theories waiting to be tested in ecology. We have theories

about how individuals use their resources, about how predators interact with

their prey, about how populations compete, about how food webs are orga-

nized, about how higher trophic interactions affect plants and about how

variations in plant nutrients affect predators. In short, we have many, many

theories about how organisms interact with their environment.

Where will we test these theories? What constitutes the environment?

How extensive is the population? or the community? Do we consider the

assemblage of species in the whole world as “living together”? Are there

practical limits to the system we wish to study? Perhaps it is hard to imagine

81ECOLOGICAL THEORIES

that an Australian earthworm and a North American beaver share any res-

ources, but does this mean we should treat continents as our units? If not, how

do we carve the world up into ecological units? Are we actually justified in

dividing it up at all? These questions have always been thorny ones for ecol-

ogists and they show no sign of resolution. Modern chaos theory has given the

problem new respectability as “the butterfly effect” whereby small causes

may have grand effects, as the reverberations from a butterfly’s wing in

Africa may determine weather patterns half a world away (Gleick 1987).

The ecosystem concept. Ecologists believe that we can and, in fact, must

divide the world up in order to study it. We call this “the ecosystem concept”.

The idea that we could identify lakes as discrete ecological units was formu-

lated back in 1887 by Steven Forbes in The Lake as a Microcosm. This article

had such a strong influence on amateur as well as professional biologists, that

it was reprinted at least twice and is still cited in the literature. Forbes begins

his paper:

A lake is to the naturalist a chapter out of the history of a primeval time,

for the conditions of life there are primitive, the forms of life are, as a

whole, relatively low and ancient and the system of organic interactions by

which they influence and control each other has remained substantially

unchanged from a remote geological period.

The animals of such a body of water are, as a whole, remarkably iso-

lated — closely related among themselves in all their interests but so far

independent of the land about them that if every terrestrial animal were

suddenly annihilated it would doubtless be long before the inhabitants of

the lake would feel the effects of this event in any significant way. ...It

forms a little world within itself — a microcosm within which all the ele-

mental forces are at work and the play of life goes on in full, but on so

small a scale as to bring it easily within the mental grasp.

Forbes makes a number of interesting points in this short section of his

paper, but I want to draw attention to only two: organisms in a lake are un-

affected by those on the land; and the ecological processes in a lake are so

primitively simple and the scale of these processes is so small that the lake

system can be easily comprehended.

These two ideas have been very influential. They have attracted many

ecologists to work on lakes, and convinced many limnologists that the study

of lakes is more likely to be rewarding than the study of streams. If the organ-

isms in the lake are isolated from events and organisms on the surrounding

land, then characteristics of the lake alone must determine the properties of

the lake system. If lakes are simple systems, they will allow us to see general

ecological principles in action. Thus a lake provides ecologists with a simple

model system in which to test their ideas.

82 WHY LIMNOLOGY?

Forbes and his followers saw that it was possible to divide up the bio-

sphere into little, self-contained units in which all ecological processes could

be observed. He called this unit a microcosm, but many terms have been used

for this concept. Nowadays, everyone uses the term ‘ecosystem’. English-

speaking writers usually attribute the term to Tansley (1935), but Remmert

(1980) mentions that it was introduced by R. Woltereck a decade earlier and

the concept is older still.

An ecosystem is an ecological unit comprising living and non-living com-

ponents interacting to produce a stable system. An ecosystem might be a

forest, an area of grassland, a stretch of desert, an oceanic island, a temporary

pond, an alpine meadow, a lake, or any other piece of the biosphere. The

ecosystem has become a basic unit for ecologists, just as the atom is a basic

unit for chemists and the species is a basic unit of taxonomists. Since the

ecosystem is considered to be the smallest unit in which all ecological pro-

cesses occur, it may be the functional unit of the biosphere (Odum 1971). If

so, ecologists must eventually test their theories in ecosystems, and until a

theory has been shown to be relevant in a real ecosystem, its relevance to

ecology is speculative.

Why limnology? Now we can return to our original question: Why study

limnology? And since I have explained why we should study the ecosystem,

our original question can be resolved to

“Why study this particular ecosystem?” Why not offer a course in grass-

land biology, forest biology or even urban biology? The answer, if there is

one, should be that the lake has properties that make it a more suitable eco-

logical tool than other ecosystems. At least at first sight, lakes offer many

advantages for testing theory, and I believe that these advantages explain

much of the early interest in limnology by ecologists. So let us now look at

some characteristics of a lake that make it a better model ecosystem than

many others.

A terrestrial ecosystem. Instead of looking at lakes in isolation, let us first

consider a wood bordered by grassland (Fig. 18, overleaf) to see the limita-

tions of terrestrial ecosystems as objects of study. The wood seems a self-

contained ecosystem; it includes a whole assemblage of plant species not

found in grassland, and many mammals and birds found there do not enter

surrounding grassland. Within this woodland, nutrients are cycled, energy is

fixed and degraded, predators prey and plants reproduce. It is an ecosystem.

But let us look more closely. Ask how the oak interacts with the beech. Do

they share nutrients or energy? Would removal of beech affect the oak in any

way? One can always argue that there might be an effect. Perhaps some squir-

rel that depends on nuts from both trees is hiding them together so their off-

spring compete. My point is not whether there are or are not interactions, but

83ECOLOGICAL THEORIES

only that some of these interactions appear weak and tenuous. It is easy to

imagine that interactions within the woodlot are no stronger than those

between the beech tree and the nearby shrubs or grasses at the edge of the

adjacent grassland ecosystem.

Now consider large herbivores or predators associated with our ecosys-

tem. How do we handle the fox that hunts mice and insects in the wood, the

grassland and the adjacent woods across the valley? What do we do about the

male robins that come from miles around to spend each night in a bachelor

tree, leaving behind little heaps of concentrated nutrient? We seem to be run-

ning into problems with our terrestrial ecosystem. Its boundaries have be-

come so blurred that we begin to wonder if it is really there at all.

Finally, consider the practical problem of sampling a terrestrial ecosystem.

Except in the very special cases where the researcher can count and measure

each individual, every ecological study begins by sampling the populations of

some species. In a forest, this is not easy, for each group requires special tech-

niques. Plants are not evenly distributed and must be sampled in randomly

selected quadrats, deer may be sampled by aerial surveys, mice by capture-

recapture with live traps, soil invertebrates by Berlese or Tullgren funnels,

moths by night-lighting, and other insects by sweep-sampling or ground-

sheets. Estimates for mobile species are often affected by emigration and

immigration, and some measures of abundance are only indices that cannot

be compared to each other.

This hypothetical example and its suite of rhetorical questions highlight

the problems of applying the ecosystem concept to real ecosystems. Interac-

tions, such as the sharing of energy and nutrient, between any two organisms

within same ecosystem are sometimes less than those between two organisms

84 WHY LIMNOLOGY?

Fig. 18. A woodland ecosystem

in adjacent systems. Animals migrate from one system to another and we

must decide where they belong. The transition from forest to grass may be so

gradual that it is difficult to say where one ecosystem begins and the other

ends. An added difficulty is that the assemblage of species in the oak-

dominated hilltop differs from that in the beech-maple forest lower on the

slopes; one is always tempted to divide the single ecosystem further.

A limnetic ecosystem. The confused and complex situation of the terres-

trial ecosystem contrasts sharply with the apparent simplicity of a lake

(Fig. 19). The first difference is that the lake has definite boundary: a step in

one direction puts you in, and a step back gets you out. Some animals, like

kingfishers and frogs, cross the boundary, but because conditions change so

abruptly at the water’s edge, most do not. Boundary-crossers are much less

common than on land.

The second difficulty we encountered with a terrestrial ecosystem was that

it is sometimes more difficult to show interactions between individuals within

one ecosystem than between individuals in adjacent systems. Now look again

at lakes and see if this difficulty exists (Fig. 20, overleaf). The lighted, well-

mixed, surface layer of a lake is called the epilimnion. It is here and in the

upper portion of the next layer (the metalimnion) where most photosynthesis

takes place. The photosynthesizers in this ecosystem are not trees, but minute

algal cells, 1 to 200 µm in length. Now consider cells at two positions (A and

B) in the epilimnion, and ask if we can expect interaction. Because the wind

continuously stirs the epilimnion, the algal cells there can be compared to

lumps of vegetable in a stew. Each leaks organic material into the medium

and each absorbs the flavour of the others. If you stir long enough each lump

will bump into every other lump. We can therefore conclude that interactions

are potentially very strong and that all cells compete for nutrients and energy.

A related advantage to this stirring is that it imposes considerable horizontal

uniformity on the system. Just as we have less trouble distinguishing bound-

aries, we are also less tempted to divide the system further.

The third difficulty concerned sampling terrestrial systems. Now consider

lakes. The plants are microscopic, many cannot swim against the current and

85ECOLOGICAL THEORIES

Fig. 19. A lake ecosystem

their horizontal distribution will usually be sufficiently uniform that a single

vertical series of samples will give a good estimate of biomass (Hanna and

Peters 1991). Zooplankton are more mobile and may be affected by wind so

vertical samples must be taken at different positions in the lake (Langford and

Jermolajev 1965, Prepas and Rigler 1982), but this is still a simple procedure.

Sampling fish is a more onerous exercise, but because migration is negligible,

the method of capture-recapture is probably valid.

There are other advantages to lakes as systems of study. Aquatic commu-

nities are dominated by minute organisms with short lifespans; such organ-

isms can respond almost instantaneously (at least to the human observer) to

disturbance, so the influences of an unknown history are presumably much

less than in terrestrial communities, and the likelihood of encountering a

quasi-steady state seems larger. If we avoid the discontinuities associated

with the surface and the mud, the lake community is more homogeneous than

the forest or grassland, so that sampling can be less intensive. Horizontal

changes are small and existing vertical gradients in light, temperature and

oxygen are gentle and predictable.

I will stop here because my object is not to convert all ecologists to lim-

nologists. I am not proselytising for limnology, but for a way of approaching

research. A scientist’s job is not to make measurements that no one has made

before, it is to construct and test theories. Science always begins with theory,

whether with a theory that needs testing or with groups of facts that should be

related by a theory. You should try to discover where your interests fit into the

scheme of things in science by showing how your pet theory is related to

other theories. When you test predictions of your theory, look for the system

— whether a cell, a species or an ecosystem — that makes your job simpler.

A difficulty arises because aesthetics almost always enter into biological

research. We are biologists because animals or plants happen to please us.

One researcher likes fish and finds them beautiful, but hates birds; another is

86 WHY LIMNOLOGY?

Fig. 20. Gradients in light and temperature in the lake ecosystem. A and B are two

distant points in the epilimnion

just the opposite. Personally, I find lakes and the organisms they contain

aesthetically pleasing. Obviously, one should not try to test a theory with

inappropriate material, however fascinating you think it to be; but equally

obviously, we will not give up the subject we like to work on for one we find

repulsive, just to test a theory. If we begin with the subject matter, we must

ask what biological theory or theories can best be tested with that pet mate-

rial. Thus we still look for the theory before we start making measurements.

Ecological theories relate an object of particular interest to its environ-

ment. In lakes, both the object and its environment are easily defined. This

practical detail, coupled with the theory that the lake ecosystem is easier to

understand, made the lake ecosystem an important tool in the search for and

the testing of ecological theory.

A paradigm shift in limnology. This argument for limnology explains the

interest of early ecologists in limnology, but not its current role. Some of us

still see limnology as a vital field, providing leadership to the rest of ecology.

However, for many scientists both inside and outside limnology (Jumars

1990, Wetzel 1991), limnology has lost its central position in ecology. There-

fore I want to end this eulogy to my beloved science with a further sugges-

tion.

The early lead that Forbes gave to limnologists allowed us to discover the

limits of the ecosystem concept before other ecologists. The idea of the lake

as a microcosm now threatens to be restrictive rather than instructive. Lim-

nologists who have gone beyond that paradigm are now poised to enter a new,

more powerful phase of scientific development in which limnology will once

again be a major branch of ecology.

The lake is not a microcosm. In Europe, limnologists were less influenced

by the beauty of Forbes’ English (Elster 1958). Some held similar views

(Pearsall 1932), but others disagreed. Thienemann (1926) stressed the role of

lake morphometry in determining the composition and abundance of organ-

isms in lake communities. A deep lake would be unproductive and rich in

oxygen; shallow lakes were instead productive and their deeper waters were

deficient in oxygen. Both types of systems would have the flora and fauna

appropriate to their respective conditions. Naumann (1930) instead argued

that lake properties were determined by the geology of their basins.

At first, limnologists on both sides of the Atlantic were little concerned

with the impact of the land on lakes or with the evolution of lakes under these

impacts. Because the life of lakes is long relative to our own, we first thought

of lakes as we first thought of species, as permanent. Then paleobotanists

began coring bogs to reconstruct the history of terrestrial vegetation, and

found that bog sediments contained the remains of open-water algae. This

discovery forced us to extend our time scale and to admit that lakes change

87ECOLOGICAL THEORIES

and die. We began to think of the evolution of lakes as similar to the life of a

star: A lake is created in a catastrophic event such as the advance and retreat

of a glacier; it develops strength as it slowly accumulates nutrients; it ages as

sediments accumulate; it gradually fills, becoming shallower and richer; and

it finally dies in a eutrophic burst of productivity before it is transformed into

a meadow of sedges and grasses. This view of lake evolution was basically

consistent with the ideas of Thienemann.

As the human population increased, human observers first on the shores of

Swiss lakes (Ambühl 1960, Thomas 1969) and then on the shores of North

American lakes (Beeton 1969, Edmondson 1969) began to see changes within

their own lifespans. We had to admit that the evolution of a lake was not so

slow as we once thought. In fact, only a few lakes, like Baikal, Titicaca, and

the African Rift Valley lakes, antedate the pleistocene. The rest are only

10000 to 100000 years old. The inhabitants of these lakes cannot be the rem-

nant from a distant past. Moreover, we had to admit that climate and human-

ity could hasten the aging process and affect the properties of the evolving

lake. We began to realize that lakes were not isolated systems. They were very

much influenced by what happened on land. We became interested in pre-

dicting these processes, and much of the current support for limnology is

directed to predicting the effects of development in the drainage basin on the

properties of the lake.

Evidence against the hypothesis that lakes are isolated ecosystems is now

everywhere. The watershed and airshed bring nutrients that set the limits of

biomass and production (OECD 1982) but also bring mercury (Håkanson et

al. 1990), lead (Evans and Rigler 1985), PCB’s (Macdonald and Metcalfe

1991, Taylor et al. 1991) and acid (Neary and Dillon 1988). In most lakes,

planktonic primary production is insufficient to meet the energetic demands

of even the plankton, let alone the benthos and fish (del Giorgio and Peters

1993), so energy subsidies are required from the littoral or the catchment. The

modern lake is not a microcosm.

From Forbesian microcosm to empirical holism. Limnologists had elected

to follow what Forbes calls “the a priori road” whereby we begin with bold

conjectures about nature. There is no harm in such a first step. Problems arose

because we did not see this process as only a first step to the identification of

hypotheses for testing. We instead treated some conjectures as inspired

guesses at intelligible principles for ecology. Such principles were accepted

as true. Since they did not need to be tested, they were above the scrutiny of

scientific criticism. With hindsight, we can be more critical; what we see is

that many of the positive attributes of lakes as study sites were illusory. No

measurements showed that the lake was more isolated than a forest or grass-

land, that its inhabitants were more primitive, that its interactions were sim-

88 WHY LIMNOLOGY?

pler, or that its scale was smaller. We had accepted our conjectures as descrip-

tions of reality, rather than hypotheses for testing, and we built and tested

hypotheses within the framework of that preconception. In other words, we

confused our most fundamental theories about the environment with facts.

The change in perception that saw limnology move from the view that

lakes are isolated microcosms to the view that they are part of a larger unit

including their drainage basin and airshed represents a shift in the paradigm

of limnology. Eventually, the old paradigm failed because it could not address

the new problems of pollution, so its initial flaws became more obvious. This

change should entail reassessment of the advantages of lakes for the testing of

ecological theory.

The loss of limnology’s privileged position among ecological testing

grounds also has another, more hopeful message for limnologists. The Forbe-

sian view that lakes were specially appropriate for ecological study because

they were distinct ecosystems was also a trap. The rationale that led us to

expect to see the principles of ecology more clearly in lakes also implies that

the lessons learned in lakes would not easily apply to other ecosystems. This

limitation was not a problem because limnologists found few principles and

because the premise that all ecosystems were similar was not treated as a

theory, but as a metaphysical doctrine. In any case, we can now see that lakes

may not differ from other ecosystems, so our limnological experience may

have broader relevance.

It is counterproductive to think of paradigms as right or wrong. For all its

faults, the old Forbesian paradigm played an important role in the evolution of

limnology. For many years, it attracted scholars to work on lakes and it

allowed these researchers to treat lakes in a consistent and characteristic way.

Because the lake was seen as a homogeneous entity, limnologists came to char-

acterize the ecosystem with a few state variables. In the water, we measured

phosphorus concentration, chlorophyll concentration, zooplankton biomass,

conductivity, and pH. In the sediments, we measured organic content, redox

potential, metal levels and density of macrobenthic invertebrates. Such data

represent the measurements made by a whole generation of limnologists.

Regardless of the status of the lake ecosystem concept, we can use past

measurements to construct new theories about lakes. When we do this, we use

the time-honoured approach that scientists have always used: we identify a

system of interest, we look for regularities in the behaviour of the state vari-

ables describing that system, we express this regularity qualitatively, and then

we may seek to explain these patterns.

For example, Richard Vollenweider (1968) sought patterns in lake

eutrophication. He saw a pattern in the loading of nutrients (P and N) to a lake

and the degree of eutrophication, and developed a simple model to describe

89ECOLOGICAL THEORIES

the pattern. This approach has since been used repeatedly to provide simple

empirical descriptions of nature (Peters 1986, Seip and Ibrekk 1988). For a

small group, this process has become a new paradigm, based on empirical

holism and called “ecometrics” (Håkanson 1991) or “predictive ecology”

(Peters 1986; Chapter IX).

If lakes are no more isolated than other ecosystems, there is no reason to

suppose that this approach is limited in its effectiveness to lakes. It should

and does apply to forests (Box 1981), grasslands (East 1984, McNaughton et

al. 1989), seas (Nixon 1988, Iverson 1990) and rivers (Morin and Peters

1988, Hoyer and Canfield 1991). It should apply everywhere we take the

trouble to measure state variables, to examine those measurements for pattern

and to express those patterns quantitatively (e.g. Fig. 21). Since robust pat-

terns beg explanation, the last step to explanatory theory will follow almost

automatically. Limnology continues to give leadership to ecology, because it

has demonstrated that ecology can be a predictive, empirical science.

90 WHY LIMNOLOGY?

Fig. 21. Relation between plant biomass and primary production in terrestrial and

aquatic systems. One regression applies to both the upper panels. Both it and the re-

gression for forest and woodlands are reproduced in the panel for aquatic systems.

(From Peters 1980)

Plant Biomass (t ha

–1

)

Primary Production (t ha

–1

)

Limnology and marine science. I hypothesize that limnology achieved

its current predictive power (e.g. Table 9) because it passed through a Forbe-

sian period whereby different systems were characterized by a few measure-

ments. We have now forsaken the idea that lakes are isolated ecosystems, but

in doing so, we discovered that those measurements have an independent

value. The importance of limnology’s Forbesian past can illustrated by com-

paring the developments in limnology and oceanography.

Oceanographers have typically led limnologists in breaking new ground,

rather than vice versa. For example, in my own fields of interest, oceanogra-

phers developed techniques to measure phosphorus (Atkins 1923), identified

zooplankton feeding as worthy of study (Pütter 1909), and provided the first

effective techniques and estimates of filter-feeding (Gauld 1951). Therefore

if limnology has stolen a step on oceanography, it is not because freshwater

scientists are usually first off the mark.

Differences in the evolution of the two subdisciplines are not imposed by

the nature of their material. Marine systems offer most of the practical advan-

tages as lakes. Their boundaries are distinct, much of the biota consists of

minute organisms in a homogeneous, three-dimensional habitat with little

structure and few gradients. They are sampled in similar ways and similar

measurements are compiled. The open sea even appears more isolated from

91ECOLOGICAL THEORIES

Dependent variable Units Equation r

[Chlorophyll] mg m

–3

Y = 0.073TP

1.4

0.96 77

Transparency m Y = 9.8TP

–0.28

0.22 87

[Phytoplankton] mg wet wt m

–3

Y = 30TP

1.4

0.88 27

[Nanoplankton] mg wet wt m

–3

Y = 17TP

1.3

0.93 23

[Net plankton] mg wet wt m

–3

Y = 8.7TP

1.7

0.82 23

[Blue-green algae] mg wet wt m

–3

Y = 43TP

0.98

0.71 29

[Bacteria] millions ml

–1

Y = 0.90TP

0.66

0.83 12

[Crustacean plankton] mg dry wt m

–3

Y = 5.7TP

0.91

0.72 49

[Zooplankton] mg wet wt m

–3

Y = 38TP

0.64

0.86 12

[Microzooplankton] mg wet wt m

–3

Y = 17TP

0.71

0.72 12

[Macrozooplankton] mg wet wt m

–3

Y = 20TP

0.65

0.86 12

[Benthos] mg wet wt m

–2

Y = 810TP

0.71

0.48 38

[Fish] mg wet wt m

–2

Y = 590TP

0.71

0.75 18

Average primary prod. mg C m

–3

–1

Y = 10TP – 79 0.94 38

Maximum primary prod. mg C m

–3

–1

Y = 20TP – 77 0.95 38

Fish yield mg wet wt m

–2

–1

Y = 7.1TP

1.0

0.87 21

Table 9. Selected regressions describing the relationships between total phosphorus

concentration (TP, mg m

–3

) and other lake characteristics; n: number of lakes. (From

Peters 1986)

the land. Of all the ecological sub-disciplines, marine biology seems the most

likely to resemble limnology, yet in some respects the two sub-disciplines are

poles apart.

There are differences between lakes and oceans. The sea is salt, the scale

of the oceans is greater, sampling is more expensive, biological diversity is

higher and so on, but none of these differences seems crucial. A more impor-

tant distinction between lakes and oceans is the number of discrete sites.

There are vast numbers of lakes. My home province of Quebec has a million

lakes larger than 10 ha in area and, next door, Ontario has half a million more.

There may only be seven seas.

The great number and small size of lakes offer the advantage that limnol-

ogists can manipulate lakes to test our theories (Schindler and Fee 1974; Elser

and Carpenter 1988). In the sea, one could use estuaries, bays (Håkanson and

Wallin 1991) and fjords (Aure and Stigebrandt 1990) as natural units for

replicated measurements and experimentation, but this approach has only

proven popular in the marine littoral (Paine 1977).

The large number of lakes is a misleading statistic. That alone need not

impose different frames of reference on fresh and salt water researchers.

There are more lakes than seas, but those many lakes cover less than 1% of

the area of the oceans, contain less than 0.01% of the ocean volume, and are

spread less evenly across the earth’s surface. In some important ways, the

ocean offers more sampling sites than lakes. Even the discreteness of lakes

may be more apparent than real, for most lake districts bind their lakes

together by common patterns of geology, climate, and land use. In any case,

the distinctness of lakes and the inter-connectedness of the seas are relevant

only as properties of our theories about these systems. If the theories do not

work, then the properties are irrelevant.

Because oceanographers could not delimit small distinct areas to study,

many of them adapted a different form of the ecosystem concept. Rather than

characterize each area with a few state variables, they tended to treat each

study area as a unique assemblage that required detailed description of its

components, likely in terms of a simulation model. Oceanographers felt the

collapse of the microcosm view less. They did not normally work at the level

of the ecosystem, but at a lower level of organization, with ecosystem com-

ponents. They experienced neither the discomfort of paradigm change nor the

benefits of a fresh outlook. Instead, marine biologists continued to treat their

material as an aggregate of many sub-systems, each of which has to be indi-

vidually described. This view is discussed in the next chapter. For the present,

it is enough to note that, without the Forbesian frame of reference, marine

ecologists could not see their data as state variables characterizing a system,

and therefore their systems remained difficult to characterize or to compare.

92 WHY LIMNOLOGY?

Why limnology — an answer. In summary, limnology originally played

a leading role in ecology because limnological systems seemed optimal for

testing contemporary ecological theory. The suggestion that the limnetic

pelagial might be a microcosm attracted some of the brightest minds in ecol-

ogy to consider limnological examples. Terrestrial ecologists were less drawn

to the approach because their ecosystems were less clearly connected inter-

nally; marine biologists were not attracted because their potential ecosystems

were less obviously isolated from other parts of the ocean. Neither group was

able to agree on how to identify the system they should study or on what

measurements characterized their systems. Confident in the definition of their

ecosystems, limnologists moved ahead to describe their ecosystem with state

variables that characterized the whole.

Subsequent development revealed anomalies and flaws in the limnological

paradigm, and many of the concepts it encouraged have been shown to be

untestable or erroneous. If limnology is no longer leading all of ecological

theory, it is because its earlier success was premised on the misapprehension

that tests of ecological theory required an isolated microcosm. Since this is no

longer tenable, ecological theories are equally testable in many systems and

limnology has lost some pride of place. Thus to much of ecology, limnology

seems to have slipped from its once pivotal position (Jumars 1990, Wetzel

1991).

Some limnologists learned from the experience to move beyond the micro-

cosm concept. The information and tools that developed under the old

paradigm allowed researchers to step boldly into a new phase of growth based

on measurable state variables and prediction of whole system properties.

Although our original conceptions of lake system limits were flawed, and

although we are uncertain what the new limits should be, the holistic mea-

surements we took still describe our lakes. Even if we can no longer define

the system, our holistic measurements function as the basis of empirical theo-

ries to predict lake characteristics.

Science does not depend on what we think about reality or about the state

variables we use. Science depends on how well these variables function in

theories to make predictions. Some limnologists learned this when their

paradigmatic conception of reality crumbled, but related empirical theories

continued to predict. Predictive limnology is a flourishing sub-discipline

(Peters 1986, Seip and Ibrekk 1988), and limnology is once again showing

the way, this time towards a new science of predictive ecology. And that is

why we should teach and study limnology.

93ECOLOGICAL THEORIES

VII Reductionism versus Holism:

An Old Problem Rejuvenated by the Computer

“The meaning of this illumination [...] did not

penetrate at once, and notably the word trim [...]

long remained obscure.”

Samuel Beckett

[Molloy (1950)]

The subject of this chapter has been ignored for such a long time that the

key words in the title are nearly meaningless to most biologists. These

words may even give the impression that I will deal with the history or

philosophy of biology rather than with its science. That is not my inten-

tion at all, for I am neither an historian nor a philosopher. My only rea-

son for being interested in the history and philosophy of science is that

these disciplines may teach me to do my science, ecology, more effec-

tively.

Ecology is a branch of science that is, or at least ought to be, very impor-

tant to society. We need ecological predictions and we need them now, yet

ecology has failed to produce the predictive theories we need. If asked why,

most ecologists explain away our failure by the extreme complexity of our

subject matter and the youth of our discipline. I do not deny these explana-

tions. They may be right. However, the intractability of our subject matter is

not the only barrier to ecological progress. There is also something peculiarly

unproductive about the approach we ecologists have taken to study our sub-

ject matter.

The Place of Philosophical Debates in Biology

The theme of this chapter is that we ecologists have been working ineffi-

ciently because we ignored philosophical debates that involved a few biolo-

gists a century ago. We working scientists ignored the biophilosophers

because we never understood what they were talking about. Indeed, they did

not understand it themselves. The advent of the computer has re-invigorated

some of these old, semi-philosophical questions, and forced us to restate them

in such a way that they become meaningful to experimental ecologists. I will

illustrate the problems this creates with some of my own work with ecosys-

tem ecology in the high Arctic and with the autecology of zooplankton feed-

ing. Finally I will suggest that if we learn the lesson such examples provide,

we may become more effective. The point of the chapter is to suggest that the

discovery of ecological systems and the introduction of the technique of sys-

tems analysis into biology require us to reevaluate the ecologists’ approach to

science.

Molloy and the principle of trim. Before describing the history of our

debates I will give an example of what I mean by saying that we did not

understand our own arguments. This statement would seem strange to

philosophers and historians because they work with words, and are expected

to use them rigorously. However, scientists tend to be less interested in

words than in phenomena. Consequently, when a scientist looking at nature

gets a brilliant idea, the immediate problem is to express the idea in words.

Until this is done, there will be no convincing others of the brilliance of the

idea.

My illustration comes from the writings of Samuel Beckett — a writer

most remembered for his deep understanding of the human tragedy. I believe

he had an equally deep understanding of science, as shown beautifully by the

incident of the sucking stones in his novel Molloy, which forms the prologue

to this book.

Molloy, crippled, destitute and lost, rests (to the extent that he could ever

rest) on the sea shore. There he sucks wave-washed pebbles to relieve the

pangs of hunger and thirst. Yet he is totally engrossed in the problem of dis-

tributing his sixteen sucking stones among his four pockets such that he can

suck them each in rotation. He goes through several unsatisfactory solutions

until finally he has an insight. He can obtain his goal if he sacrifices “the prin-

ciple of trim” and distributes the stones unevenly among his pockets. At this

phase in his research, Molloy exemplifies my point, that scientists have trou-

ble expressing their discoveries, in the quotation that begins this chapter.

Molloy was convinced he had made a great discovery and he expressed his

discovery in a word: “trim”. However, for a long time he did not know what

he had discovered, nor why it was aptly described as “sacrificing the princi-

ple of trim”.

This inadequacy did not deter Molloy. Neither does it deter the biologist

who has found something great but cannot explain it. This I believe was the

situation with a few biologists who took part in the debates of the 19th cen-

tury. Their insights were important, but unfortunately the words they used left

the great mass of working biologists unmoved.

96 REDUCTIONISM VERSUS HOLISM

Vitalism and mechanism. The debate I want to discuss is the debate

between the holists and the reductionists. Because this debate has become

incredibly confused, I will also give some of its history and show how it

evolved.

Aristotle is again a good starting place. Among his many ideas about the

nature of living things, he believed that the difference between living and

non-living things was due entirely to the fact that the living things possess a

soul. A simple consequence of this belief is that we cannot expect to learn

anything about life by studying a dead body. Neither can we learn anything

about life by studying a hand or a liver or some other organ removed from a

living body. This philosophy (perhaps “faith” is a better word) was called

vitalism (Table 10).

Vitalism dominated biology until the 18th and 19th centuries, by which

time physiologists had wrought a slow, initially unnoticed, change. Incited by

René Descartes (1596–1650), they began to treat living things as if they were

physico-chemical machines. For example, Hermann Boerhaave (1668–1738)

and George Martine (1702–1741) argued that the vital warmth of the human

body is produced by the friction of red corpuscles rubbing on the walls of

arterioles. A century later, Gustav Magnus conducted experiments with blood

removed from the body, analyzing the results of his experiments as if blood

were merely a physical fluid (Mendelsohn 1964). Theodor Schwann

(1810–1882) extracted the active principle of gastric juice from the lining of

the stomach with acid, and then showed it could be precipitated as if it were

simply a chemical substance (Bodenheimer 1953).

97THE PLACE OF PHILOSOPHICAL DEBATES IN BIOLOGY

Vitalism: Life depends on the presence of a soul.

Mechanism: Living organisms are simply complex physico-chemical machines.

Organicism: Life depends on organisation; each level of increasing complexity of

organisation can only be described in terms of laws appropriate to

that level.

Reductionism: The proper approach to the study of complex phenomena, like life, is

to decompose this complexity to simple components. In many cases,

these components can then be shown to be instances of general phys-

ical and chemical laws.

Holism: Complex systems must be treated as whole systems, because the

process of analysis inherent in reductionism destroys the basis of

their integrity.

Table 10. Fundamentally different approaches to the study of biology

The story of vitalism ends in France in the middle of the 19th century

in a little cellar in Paris, where the great physiologist Claude Bernard

(1813–1878) had a table which he called his laboratory. Bernard did a very

simple experiment. He killed a dog and removed its liver. He then inserted a

tube into the hepatic portal vein and perfused water through the liver. He ana-

lyzed the water emerging from the liver for sugar and found glucose, but in

time no more sugar came out. He had washed out all the available sugar.

He then left the liver in a warm place for several hours, once again perfused

it, and found more sugar. Bernard concluded that the liver could make

sugar from another compound and he called this hypothetical precursor

“glycogen”.

This experiment was terribly important in its day. It showed that animals

can change one compound into another, it helped Bernard develop the idea of

internal control, which became one of his greatest contributions to science,

and it showed that an organ can have more than one function (Larner 1967).

The experiment was even more important because biologists of the time

accepted it as valid.

Bernard had drawn conclusions about the functioning of a living organism

from an experiment done with a part of that organism separated from the rest

of the body. For the two thousand years after Aristotle, this approach had

been totally unacceptable to most biologists. Everyone had known that the

only difference between a living organism and a dead organism is the soul,

which conferred life and left the body at death. Thus a dead animal or animal

part could tell us nothing about life.

By Bernard’s time, biologists were no longer unanimous on this point. A

growing number were treating organisms as highly complicated machines.

The biologists promoting this new approach were the mechanists who saw

life as a complicated physico-chemical process, and Bernard’s experiment

marked the triumph of this scientific revolution. The real significance of

Claude Bernard’s experiment was that it was the last shot in the battle. With

this experiment, the mechanists won the war and vitalism was never again an

acceptable paradigm for biologists. With Claude Bernard, the revolution was

over and most biologists rejected vitalism for mechanism.

Organicism and holism. Our story does not end with the mechanistic

revolution. It begins there. Some biologists accepted that biology could best

progress without postulating a soul, but not that living things were only per-

ambulating bags of chemicals. These biologists argued that the components

of living things are organized into living systems, and that the properties of

these systems could not be predicted from a study of their parts. This new idea

was a modification of vitalist thought. It differed from vitalism by substitut-

ing organization for soul and by asserting that we could learn to understand

98 REDUCTIONISM VERSUS HOLISM

living things, but only if we studied them intact. This view came to be called

organicism. The organicists produced the idea that is central to this chapter.

The new trend began with Xavier Bichat (1771–1802) who was obsessed

by the variability of living systems. Physico-chemical systems were depend-

able and their behaviour reproducible, but biological material was unreliable

and variable. From this hypothesis, he argued that biological systems must

have something extra. Their behaviour must be governed by new, still

unknown, peculiarly biological laws (Mendelsohn 1964, Hall 1969).

Lloyd Morgan (1923) improved on Bichat by inventing the idea of “emer-

gent properties” whereby each level of complexity has its own laws. An

important consequence of this idea is that if we want to develop theories

about matter at a particular level of complexity — like a cell, an organ or a

whole organism — then we must study the cell, the organ or the whole organ-

ism, not its parts. This is because the whole cell (or organ or organism) has

properties that its component parts lack.

At the beginning of the 20th century, the opposing forces had regrouped

and the mechanists had changed their names. The descendants of mechanism

became “reductionists”, because they believed in breaking up the system they

intended to study. The battles that raged, unnoticed by most biologists, were

first between the vitalists and mechanists and then between the mechanist-

reductionists and organicists. It was the organicists who had something to say

but were unable to find a way of saying it. Just as “trim” meant something to

Molloy, “emergent properties” meant something to the organicists. Unfortu-

nately, it meant nothing to most working biologists.

In the 20th century, their words began to gather more meaning and began

to be applied not just to living organisms but to ecological work as well. The

first advance was made by Ludwig von Bertalanffy (1950, 1952) who sug-

gested why living systems might have emergent properties. Von Bertalanffy

said the important characteristic of organisms is that they are systems, that is

to say they comprise “a complex of elements in mutual interaction”. The

behaviour of a system depends on all interactions amongst all the parts, and

so the interactions are as important as the parts. If one part is removed, the

interactions between it and other parts are broken. This was much more con-

vincing than the vague talk about emergent properties, and in recognition of

the advance we changed the names of the protagonists for the last time to

holists and reductionists.

Reductionists and holists were debating a real and significant question

about scientific knowledge, but we hear little about their dispute today. I

believe biologists lost interest because the opposing forces were just too

unequal to make a battle worth fighting. The holists were few and far

between, so the reductionists just ignored them. Consequently, most of us are

99THE PLACE OF PHILOSOPHICAL DEBATES IN BIOLOGY

reductionists by default. We accepted an approach to which we were condi-

tioned without ever questioning our belief or knowing that there is another

viewpoint.

Holism and reductionism in ecology. Most ecologists were oblivious of

these questions. We were mostly concerned with predicting and controlling

the abundance of particular species, because we wanted to know, for example,

if fishing would deplete fish-stocks, or how different forms of pollution affect

organisms we care about. Our interests were therefore largely directed to

individual species, and we hoped that a single factor would be of overwhelm-

ing importance for each species.

Many ecologists behaved as if the distribution and abundance of a species

could be predicted from physical and chemical factors alone, and early field

work was largely directed at the relations between individual members of a

species and their physical or chemical environment. Researchers therefore

sought to establish the response of an organism to temperature, humidity, pH,

salinity, etc. Given this emphasis, it is scarcely surprising that autecology was

a major branch of ecology or that the limiting factor was the most popular

concept. The emphasis on autecology even allowed plant and animal ecology

to develop as separate disciplines in different university departments, as if

animals and plants did not interact.

The autecological approach was appealingly simple, but it did not work

well enough. Researchers therefore increasingly emphasized biological inter-

actions, like competition and predation. This interest marked an implicit

recognition that biological interactions can be more important than physico-

chemical factors.

The American botanist F. E. Clements (1916) moved decisively beyond

autecology when he wrote about plant communities as superorganisms. He

has since been thoroughly abused for this. I think the attacks against him were

unjust, but I recognize that he made two fatal mistakes: he was suffering from

the Molloy syndrome and he was too far ahead of his time. If Clements had

“penetrated the meaning of his illumination” and if he had read von Berta-

lanffy, he would have said something like this: “The community is a system,

and in this respect, it resembles an organism. But it is more complex. It com-

prises the interactions among many organisms, and in that sense, the commu-

nity is at a higher level of organization than an organism. This is what I mean

by superorganism”. Similar ideas are currently accepted as elements in hier-

archical thinking (Allen and Starr 1982, O’Neil et al. 1986). But, alas for

Clements, he did not say it right, and he has been a bogey-man for politically

correct ecologists ever since.

Nevertheless, gradually and unconsciously, we began to change. We ad-

mitted the food chain among our fundamental concepts, and when faced with

100 REDUCTIONISM VERSUS HOLISM

results like Hardy’s (1924) study of the complex feeding relations of the her-

ring, we admitted that the food chain was unrealistic and changed to food

webs, implicitly accepting the idea of multiple interactions. We stopped sep-

arating plant and animal communities, and began to talk about ecosystems.

We slowly came to realize that in ecology we are not dealing with isolated

entities but with one or more highly organized systems in which the parts

interact with and depend upon one another.

The concept of the ecosystem led to a problem. Most ecologists had devel-

oped a tradition of studying bits and pieces, but had no idea of how to fit our

bits and pieces together. Then, two developments outside of ecology made it

possible for us to deal with complex systems. These were systems analysis

and the computer.

What is Systems Analysis?

I can explain systems analysis best with a simple example (Fig. 22). Take

a tumbler of water containing plant nutrients. Shine a light on it. Put in some

algal cells and add a few water fleas to eat the algae. This is a system: algae,

nutrients and Daphnia all living together and dependent on each other. If we

know the quantity of each component and the interactions between all the

101WHAT IS SYSTEMS ANALYSIS?

Fig. 22. A simple system consisting of an external energy source (light), a primary pro-

ducer (algal cells), herbivores (Daphnia) and their interactions

components, then we can use a computer to do an incredible amount of sim-

ple arithmetic and so calculate the amount of each component or “state of the

system” at any time in the future. This approach was taken by many ecolo-

gists who accepted that ecology deals with complex systems. It is called

“systems” analysis because it seeks to decompose the working natural system

into parts for study, and then to recreate that system as the sum of these inter-

actions. In the example of Fig. 22, the interactions I must measure are feeding

rate as a function of animal size and algal abundance, uptake rate of plant

nutrients as a function of nutrient concentration, and the rate of nutrient

excretion by the animals.

There is a catch. To succeed, I must measure all components and all inter-

actions. If I leave out Daphnia or omit excretion, or if I measure one interac-

tion erroneously, my model will not work any better than a watch without its

tiniest cog-wheel. To do otherwise, to presume that we can either leave some

elements out of our model or model only the significant interactions, presup-

poses that we can somehow identify the important processes a priori.

Failures since the time of Aristotle should have taught us that appeals to

“intelligible principles” or the “a priori road” of assumptions about nature are

not effective. If we are to dismiss some interactions as unimportant, we must

first study those interactions in detail. Unfortunately, that effort is exactly

what we are trying to avoid. Moreover, partial representations involve a pos-

sible contradiction because the appeal of mechanism and reductionism is

their capacity to represent “what’s really happening”, so that we will “under-

stand what’s going on”. If we ignore much of what is really happening, then

the apparent strong point of the reductionist-mechanist position is already

lost. Any argument would only be a methodological debate about how thor-

ough the holist position should be.

Even in a simple system, the possibility of modelling all the interactions is

small. For example, we perhaps should consider the excretion of different ele-

ments or compounds separately. Perhaps our model should have a place for

the bacteria in the daphnid’s gut and the epibiotic organisms living on its

shell. Perhaps the modifying effects of time of day, or light levels or temper-

ature or age of the culture should be considered. Perhaps there are important

interactions among the algal cells. Neither these specific problems nor the

general question of when we should stop analyzing the system has been

resolved.

We are not satisfied with systems consisting of a few species and their

physico-chemical environment. We need to describe large ecosystems, and to

do so we must gather larger and larger teams of scientists and technicians to

work on each ecosystem. For example, in Russia, a team of 150 scientists

worked on a single reservoir for three years. This trend to more ambitious

102 REDUCTIONISM VERSUS HOLISM

projects is also exemplified by large scale international programs, like I.B.P.

(The International Biological Programme) of 1965 to 1975, or the contempo-

rary JGOFS (The Joint Global Ocean Flux Study) and WOCE (World Oceans

Circulation Experiment).

To appreciate the difficulties that systems analysis presents in the treat-

ment of these large systems, we must consider the data that ecologists are

gathering and the uses to which these data are put. Imagine the moderately

simple ecosystem represented by the biota of a temperate lake. In round num-

bers, this might include 200 species of plants, 100 species of herbivores, 100

species of carnivores, 50 species of bacteria, 200 animal species that cannot

be attributed to any trophic level, and 100 species of detritivores. This com-

munity of 750 species is simpler than it might be. Likens (1992) estimates

that there are at least 850 species in Mirror Lake, New Hampshire (USA) and

Elton (1966) suggested that Whytham Woods in England might contain 5000

species of metazoans. To model such systems we must describe these com-

munities. Such a description might take the form of a compilation of the

biomass, the rates of birth, growth, and death for each species, and the inter-

actions (predation, competition, etc.) among these species. We might further

describe the effect of variations in light, temperature, nutrients, etc. on these

components and their interactions. We could then build these parts of the sys-

tem into a model system in our mind (Fig. 23, overleaf).

The arrows in Fig. 23 show only the predator-prey interactions. In a real

description of the system, every component potentially interacts with every

other one. Therefore if the number of components (n) equals the number of

species, n = 750 and the potential number of interactions = n(n–1). This aver-

age lake has 561 750 potential interactions among its components. (The cal-

culation assumes that the effect of Species A on Species B must be described

separately from the effect of Species B on Species A, because that situation

seems more plausible to me; if the interaction is instead bidirectional, the

number of arrows will be halved.) Now imagine that we have our system

arranged in our minds where all 561 750 interactions are indicated by arrows.

The human mind cannot keep track of all these interactions. To predict the

effect of any disturbance on our system, we have to use the technique of sys-

tems analysis and its characteristic tool, the computer. What should we do

next to make this possible?

There is no need for details. It is sufficient to note that systems analysis

requires us to quantify every interaction, under the entire range of environ-

mental conditions that we expect to encounter. If each interaction requires

only one person-year of effort, this description will require centuries even for

a large team. In passing, I note that I spent over four years developing a

theory that describes only 50% of the variation in a part of a single inter-

103WHAT IS SYSTEMS ANALYSIS?

action: phosphorus excretion rate by Daphnia rosea (Peters 1972, Peters and

Rigler 1973). Other arrows linking zooplankton, their food and the resources

upon which that food depends were studied almost as long with almost as

limited success by other doctoral candidates in the same laboratory (Cham-

berlain 1968, Confer 1969, 1972, Haney 1970, Lean 1973). I conclude that

full description of an entire ecosystem is so great an effort that we will never

complete the task. In fact, we won’t even try. The job is just too big.

Some problems with proposed solutions. The previous section estab-

lished that it is impossible to specify the current state and interactions of the

components of complex ecological systems. The problem is not a philosoph-

ical issue but a purely practical limitation (Wimsatt 1980). Simplification

seems a practical solution, but a few moments’ reflection shows that this is

not the case.

Identifying the components. Most biologists prefer to work on individual

species, and when systems models have been built, they normally depend

104 REDUCTIONISM VERSUS HOLISM

Fig. 23. A hypothetical lake ecosystem consisting of 200 species of primary producers,

100 species of herbivores and 100 species of carnivores. Arrows indicate potential

trophic interactions, and not shown are 50 species of bacteria, 100 species of detriti-

vores, 200 species that could not be classified to a single trophic level, and all non-

predatory interactions

heavily on autecological work done at the species level. Unfortunately, we

do not know the number of species in any natural ecosystem. Study after

study has shown that the harder and longer one searches, the more species

one will find. Thus we can never know how many components comprise the

system.

One can seem to address this problem in a number of arbitrary ways. For

example, one could propose that the system is characterized well enough

when the rate of increase in species number per unit of additional effort falls

below some specified value. Unfortunately, approximations like that will not

do. There are many cases in which obscure components play important roles

in structuring their communities: Opuntia, the prickly pear cactus, is held in

check by the now rare Cactoblastis moth in Australia; in Africa, intestinal

parasites of tse-tse flies apparently protect the Serengeti from over-exploita-

tion by debilitating human agriculturalists with sleeping sickness. Currently

small or rare members of the ecosystem cannot be excluded from a systems

analysis on the grounds that such components never play an important role.

Aggregation. One way to simplify the system is to lump different species

of similar organisms into a smaller, more tractable number of functional

groups. The trophic level approach (Lindeman 1942) is one such attempt. The

description of the planktonic community of primary producers in terms of

chlorophyll concentration might be another. Unfortunately, aggregation is

rarely easy or effective in systems analysis. To determine which organisms

are functionally similar members of a community, we must determine their

relations to the rest of the community, but this was the difficulty we were try-

ing to escape. Whether we aggregate the data or not, we are required to create

a tiny theory for each member of our system in which we hypothesize how

that member relates to every other component. Since we can hardly expect to

create 561 750 correct theories, we must build error and approximations into

the systems analysis model. Since these errors will be propagated with each

calculation (Beck and Halfon 1991, Peters 1991a, van Straten and Keesman

1991), we cannot expect that the model will work.

Interactions. We have not seen it all yet. One last problem poses even

more difficulties than either simplification or aggregation. Consider how the

ecologist usually quantifies interactions between system components. Occa-

sionally these are estimated in situ, but more often than not this is impossible.

Therefore the two interacting components to be studied are isolated and their

interactions are measured in the laboratory. For example, when we measure

the feeding rate of a water flea as a function of the abundance of its food, we

isolate the flea and one type of food in a beaker where we can easily vary the

food supply. Then we take the rates we measured and apply them in our

model.

105WHAT IS SYSTEMS ANALYSIS?

This procedure is effective only if no component of the natural system acts

directly on the interaction we are measuring. If there is such a component, our

lab values will not apply to the natural system. Obviously such modifying

interactions are common: the presence of noxious algae may cause the water

flea to reduce its ingestion rate of palatable species (Burns and Rigler 1967,

Burns 1968), the absence of vitamins may make the water flea less capable of

utilizing assimilated food (Provasoli et al. 1970), and feeding rates change

with temperature and time of day (Haney and Hall 1975). Since most interac-

tions are modified by the environment in which they occur, we must study the

animals in situ, and we must study each interaction intensively. We cannot

escape the massive work-load that systems analysis of any natural ecosystems

imposes (Rigler 1982a). But since we cannot do that much work, the applica-

bility of systems analysis is so limited as to require reassessment of the

approach.

Two Personal Experiences

The impossibility of really analyzing a system and of synthesizing the

parts into a computer model is rarely appreciated. Most of our research is

designed to allow us to analyze the bits of a natural system that interest us,

leaving the remainder for others and assuming that someone else will solve

the problems of putting the big picture together. I no longer accept this view

because I have seen the magnitude of the problem of creating a system anal-

ysis model. I encountered these difficulties in many aspects of limnology,

but I will illustrate the problems with two aspects of my work which dif-

fered very much in scale: the Char Lake Project and the analysis of zoo-

plankton feeding.

The Char Lake Project. Some years ago I became involved in the study

of one of the simplest lake ecosystems in the world, Char Lake located on

Cornwallis Island in the Canadian High Arctic. This study was not under-

taken because the lake seemed an ideal site for systems analysis, but we

justified our research with a conceptually similar argument. We hoped that we

could exploit the simplicity of Arctic systems (Table 11) to increase our

chances of learning something about lakes in general. In retrospect, this

justification seems lame, but at the time it was quite convincing.

The Char Lake Project also represented part of Canada’s contribution to

the International Biological Programme in which 50 countries participated in

over 140 different projects. Each project involved a team of biologists work-

ing together for up to five years. At the time, IBP provided an unprecedented

level of funding, international communication and communality of purpose.

106 REDUCTIONISM VERSUS HOLISM

In many ways and despite its eventual shortcomings, the period of the IBP

was a golden age in ecological research.

The ostensible reason for the IBP was to determine the limits of produc-

tivity of the earth and thus to determine its capacity to meet human needs.

Teams of scientists were to measure productivity all over the earth, and the

composite of their results was to represent this global overview. Most of us

felt that this was too simple a goal and sought to measure primary, secondary

and tertiary production and the associated biomasses and energy flows as

well. We hoped that by focusing our attention on this previously little studied

set of properties, and by standardizing our techniques as much as possible, we

might discover a theory relating these properties to others such as light, tem-

perature or nutrients. This hope now seems naive.

Regardless of the reality of our hopes, the same data were to be used both

to estimate production and to try to understand production processes. A large

team was required for this work because the objective was to study every-

thing in the system.

Only a few members of the IBP were directly involved in simulation mod-

elling. The others sought to identify the components of the system, and then

to quantify each component and interaction. When these had been measured

in sufficient detail, the various components were to be pieced together as a

predictive model in a computer simulation.

There are reasons for comprehensive data collection, other than systems

analysis. Indeed, the larger part of the IBP teams doubted that systems analy-

sis would resolve the problems of ecosystem ecology. That group acted as

though ecology (and presumably science) consists in the organized and sys-

tematic collection of data that the scientific community considers important.

Presumably few members of IBP were pure Baconians, subscribing to the dis-

credited view that theories arise automatically from a sufficient quantity of

107TWO PERSONAL EXPERIENCES

Group Number of species

Char Lake A temperate lake

Vertebrates 1 20

Planktonic crustaceans 1 10

Planktonic rotifers 1 15

Diptera 7 150

Nematodes 24 ?

Other benthos 13 100

Table 11. The depauperate fauna of a high Arctic lake, Char Lake, relative to that

typical of a temperate lake

good data. However, many would have accepted the view that the collection

of good data is justification enough.

Other researchers may have joined a team project because they believed

that they were working on the single critical and tractable component of the

ecosystem. The subject of their interest would repay study because, when this

component was understood, we would be able to predict the observations that

other members of the team had conveniently made (Fig. 24). A corollary of

this egocentric view is that the subjects studied by others would prove less

easy or valuable. The weak point in this argument is the lack of consensus

about which process was the controller, and the individual assurance that each

of us had chosen to study the critical interaction whether that be nutrient load,

primary production, excretion, predation, or whatever.

Regardless of its rationale, the team approach made reductionists of us all,

even if we did not know the term, because the team was trying to assess the

108 REDUCTIONISM VERSUS HOLISM

Fig. 24. A subjective view of the interactions among lake processes studied by different

reductionists in the same team. (From Rigler 1975a)

whole, but the individuals were studying the parts. The approach also made us

all systems analysts, whether we touched a computer or not, because we

could not hope to put all our studies together except in some form of com-

puter model.

Problems in the components of reductionism. The problems of building a

computer model for an ecosystem are rarely apparent to anyone except the

modellers. The present generation of models is so complex that a description

of all the adjustments, guesses and theories that went into model development

cannot be given in the space of a scientific paper. As a result, these presenta-

tions are usually impossible to assess (Rigler 1976). Instead, I will simply

describe some of the results from our own work that made the simulation of

Char Lake impossible.

So far, I have written as though the species was the smallest component

that one would include in a systems model. However this is a gross over-sim-

plification. For example, although all the fish in Char Lake are Arctic char

(Salvelinus alpinus), these animals are not all equivalent. A few were canni-

balistic giants, whereas the rest of the population fed largely on benthos. The

single crustacean zooplankter, Limnocalanus macrurus, has 11 different

instars or developmental stages, some of which are so different that they were

once classified as a separate genus, all of which differ in their feeding capac-

ities. Thus the complexity of the system is not necessarily reflected in its

species list.

If we could identify the components of the ecosystem, we would then seek

to estimate their biomass. Such estimates have preoccupied ecologists for

many years. Most of us recognize that the size of a wild population can rarely

be estimated within 50% at any one point in time and that population size nor-

mally fluctuates by an order of magnitude over time (Connell and Sousa

1983, Peters and Wassenberg 1983, Schoener 1985, Pimm and Redfearn

1988). For example, when we used nets to make a capture-recapture estimate

of the fish population in Char lake, we estimated a population of 15 000 char.

However, when we counted the fish on the spawning beds, our estimate rose

to 50 000. Apparently, marked fish were more easily recaptured than

unmarked fish, so our recapture rate was high and our population estimate

low. Although we are justified in claiming that the initial estimate was low,

we cannot assume that our spawner count was right.

Finally, our modelling, whether conceptual or computed, required esti-

mates of the various rates of energy flow through the members of the com-

munity. In a general sense, this was unsatisfactory because each component

was analyzed to a different degree and with different methods. A great deal of

effort was directed to the zooplankton, largely because the plankton were the

simplest part of this simple system and because many of us were primarily

109TWO PERSONAL EXPERIENCES

planktologists. Unfortunately, most of the energy flow in this system went

through the benthos, which was less studied and more difficult. For example,

none of the 24 species of nematode could be cultured and there were no in situ

methods for these organisms. The energy budgets of our most speciose taxon

could not be studied.

Some holistic successes within the Char Lake Project. These many diffi-

culties should not obscure the successes of the project, but because most have

been reviewed elsewhere (Rigler 1978), I will only mention some examples

here. At the level of the whole system, Welch (1974) was able to measure

community metabolism by using the ice-covered lake like a huge dark bottle

through the dark Arctic winter. Welch and Kalff (1974) developed techniques

to measure bryophyte-dominated benthic production in the lake and showed

that 80% of all primary production in this lake was benthic. They also showed

that nutrients limited algal biomass in the Arctic, just as they do in more tem-

perate regions (Kalff and Welch 1974). At a smaller scale, work with rotifers

(Rigler et al. 1974), chironomids (Welch 1976), Mysis (Lasenby and Lang-

ford 1972) and char (Holeton 1973) showed that these Arctic populations

were not especially well acclimated to their cold environment, but behaved

like southern representatives of the same species at the same temperature; this

finding is a major challenge to a generation of autecology. With respect to

zooplankton feeding, careful examination of the guts of the crustacean zoo-

plankton showed that these calanoids did not digest diatoms, unlike their

marine counterparts (Kibby and Rigler 1973). Careful use of well-designed

sediment traps showed that Limnocalanus produces only one faecal pellet per

instar; contrary to general belief, the faeces of this animal are not bound into

a pellet and so most of the faeces might not have been lost from the water

column, but rather resuspended.

The common thread through these results is that all address different sys-

tems of interest. The lake, the benthos, the animals, and the faecal pellet were

treated as separate systems, albeit systems of very different scales. Thus suc-

cessful projects focused on a phenomenon for its own sake and not because

the phenomenon was the sum of its component processes or because the pro-

cess played a role in a larger system too. Holistic analyses by individuals or

small teams succeeded, whereas systems analysis of the entire project based

on reducing the whole to parts that were studied separately failed.

Zooplankton feeding. My experience with zooplankton feeding seems

poles apart from the scale of the Char Lake Project. However, decades of

research into this single element in the systems analysis of any lake show con-

clusively that estimations of the parameters for transfers among different lake

compartments are uncertain. I can illustrate this point best with research on

zooplankton feeding, because I know that work well. Indeed, I believe that

110 REDUCTIONISM VERSUS HOLISM

zooplankton feeding rate estimates are among the best measured of all

ecological rates (Rigler 1971, Peters 1984). Unfortunately, even the best

estimates leave much to be desired as system parameters.

Individual variation. If one measures the rates of ingestion of a number of

animals, whether these be Limnocalanus in Char Lake or Daphnia in the lab,

one finds that the animals do not all behave in the same way. Some eat at a

very high rate, others at a much lower rate, and others are in between (Fig. 25;

Turner et al. 1993). When we try to describe these data we often use the aver-

age rate, assuming that our experimental conditions captured nature effec-

tively and that the most representative rates are somewhere in the middle of

our measurements. Alternatively, we could decide that the experiment some-

times disturbs the animals, and that the correct rate is the maximum observed

in the experiments. There is however convincing evidence that some experi-

mental protocols starve the animals before feeding, and that starving animals

feed at greater than normal rates. Perhaps the low values are most appropri-

ate. In any case, we do not know the rates at which animals feed, so the rates

we use in our simulations are hypothetical and uncertain.

Environmental factors and their description. There are other problems.

Early work on zooplankton assumed that they filtered food from a constant

volume of water per unit time. If this was so, filtering rate would have been a

constant, and ingestion rate would rise directly with food concentration

(Gauld 1951). Subsequent studies showed that filtering rate was constant

111TWO PERSONAL EXPERIENCES

Fig. 25. The effect of size on filtering rate in laboratory study of Daphnia. (Peters un-

publ. data)

only at low food levels (McMahon and Rigler 1965) and declined at increas-

ingly higher food concentrations. Ingestion rate is instead roughly constant

when food is abundant, and varies with food levels when they are low. Many

different curves can relate ingestion rate to available food, but three are pre-

ferred (Fig. 26) because they relate to three basic types of predator functional

response identified by Holling (1959). The differences among these curves

are critical to some systems analysis models, but the data for zooplankton

have never been good enough to distinguish which model is best. Indeed,

where enough data and enough statistics have been brought to bear on the

problem, the best fit can support any of these three curves, and more besides

(Downing 1981).

Lab measures and field applications. Even if zooplankton feeding in the

laboratory could be effectively described, application of the description to

nature would still be problematical. For example, Haney (1973, Haney and

Hall 1975) has shown that in nature animals follow a marked diurnal cycle in

feeding rate, and approach rates measured in the lab only around dusk and

dawn; so our lab rates may be even poorer approximations of field behaviour

than we all fear.

Still another source of error is the use of relations and measurements in the

literature to convert measured lengths and counts into estimates of population

biomass. Schmidt (1968) has shown that variations in food level can change

112 REDUCTIONISM VERSUS HOLISM

Fig. 26. The effect of food concentration on ingestion rate of Daphnia. (From Porter et

al. 1982)

an animal’s weight two-fold, and many of the discrepancies in estimates of

weight specific rates in the literature might represent no more than the error

due to an inappropriate length-weight relation. I once surprised myself by

generating negative weights for Daphnia simply by “correcting” my mea-

sured weights for the egg mass, in turn estimated as the product of egg num-

ber and an average value for egg weight. Egg size can vary considerably with

age and food level (Glazier 1992), so no such easy step is justified.

Other organisms. One last example can demonstrate the problem of

employing these rates in a simple model. Jassby and Goldman (1974) mea-

sured potential and actual growth of phytoplankton, and calculated mortality

by difference. They then estimated mortality due to sedimentation and to

grazing and found that the sum of these two processes was much less than the

calculated total mortality. They concluded that natural cell death is the main

cause of phytoplankton mortality. If they are correct, their analysis demands

a complete revision of the way we think about lakes. But is it right?

If we look more closely at their grazing calculation, we see that they took

data for the filtering rates of individual cladoceran and calanoid zooplankton

and summed these to get community grazing rate. This process ignores yet

another odd discrepancy in feeding studies. Haney (1971, 1973) developed a

technique to measure the grazing rate of zooplankton communities and indi-

vidual crustacean zooplankton in situ. He found that the measured total graz-

ing rate is much higher than the summed total of the individuals. Apparently,

rotifers, nauplii, protozoans, and other organisms ignored in the analysis of

Jassby and Goldman (1974) are responsible for much of the phytoplankton

mortality. We cannot leave inconvenient animals out of our analyses simply

because they are less studied and therefore presumed to be less important.

I could go on, but I think I have given enough examples to show that every

aspect of feeding behaviour of zooplankton is uncertain. I conclude that,

although the data are uncertain enough to encourage more study of zooplank-

ton feeding, they are not nearly good enough to be used in systems models.

Ecologists have developed a flourishing scientific sub-discipline to address

the feeding behaviour of zooplankton, and this work by and large treats the

animals as wholes, not as the sum of many mechanisms. However, that excel-

lent work cannot be combined reliably into reductionistic models of lake

ecosystems.

The Reality of Systems Analysis

Systems thinking now dominates ecology. It has convinced us quite

rightly that a reductionist theory must embrace all significant components of

113THE REALITY OF SYSTEMS ANALYSIS

the system and all significant interactions between these components. We

should also recognize the futility of trying to measure all those components

and interactions. Those who attempt to quantify them (as opposed to those

who build the interactions into a simulation model) will be overwhelmed by

the number of phenomena that need to be described quantitatively long before

the simplest ecosystem can be modelled.

Modellers have accepted this limitation and are usually content to fill the

gaps with interactions patterned after Michaelis-Menten kinetics, with arbi-

trary but reasonable constants, and empirical relations. Patten (1975) even

argues that we do not need good data for systems analysis, because the mod-

els work perfectly well without good data, so long as we refrain from testing

them against observation. However, if we wish to apply the model, we always

take short-cuts, replacing reductionistic descriptions with arbitrary rules or

empirical relations of at least some components. When we do so, we imply

that reductionism is inadequate.

One result of our recognition of these limits is the disorientation of exper-

imental ecologists. We do not have enough faith in the systems analysis mod-

els. On the other hand, we have lost our traditional, if naive, belief that there

is a key interaction and the ecologist fortunate enough to stumble on it would

produce the theory we seek. We have lost faith in our ability to generate use-

ful theories. Consequently, there is a large element of ‘going through the

motions’ in contemporary studies of ecological interaction.

This raises some interesting questions. Why do we do it? Why are zoo-

planktologists satisfied with bad estimates of every vital parameter? And

why are other ecologists similarly satisfied? I think the reason we expect

so little from science is that we have not yet realized that our job is to pre-

dict not to describe. We have not yet come face-to-face with our failure to

do effective ecological science. If we had effective, interesting, ecological

theories we could be testing them, and they would dictate the accuracy

required of our measurements. In the absence of theories, we can be as

careless as we like.

Conclusions

Now I think we can see what the computer has done for us. It has turned a

vague, semi-philosophical question of apparently little relevance to the work-

ing biologist into a practical, methodological problem. The computer gave

reductionists the tools required to approach an ecosystem as the sum of its

parts, and it allowed us all to discover that these tools are, and will always be,

inadequate. When ecologists realize what has taken place, they will take

114 REDUCTIONISM VERSUS HOLISM

renewed interest in the long-forgotten debate between holism and reduction-

ism, and this time the debate should have a different resolution.

There are two morals to my story. First, if ecology is to develop quickly

into a science that develops by testing its theories, we must recognize the

limitations of reductionism and put more effort into the holistic approach to

living systems. To make predictions about the future states of a system, we

must study the properties of that system, not those of its parts. Secondly,

philosophers and historians of science could play an important role in the

development of science. But to play this role, they must learn to communicate

with working scientists. They must find the right words with which to convey

their insights. This may mean that they must learn enough about day-to-day

science to convert their insights about the methodology of science into a

language scientists understand.

115CONCLUSIONS

VIII Sources of Ecological Creativity

“Science proceeds by revolution and not by

addition, pure and simple.”

Claude Bernard

[Le Cahier Rouge (1860)]

Philosophers of science have long distinguished between “the context of dis-

covery” of theory and “the context of justification”. The former, which is the

topic of this chapter, is concerned with the sources and modes of scientific

creativity. The latter deals with the evaluation of existing theories. Although

both phases are important to science, most writers treat questions about justi-

fication, rather than questions about the nature of scientific discovery.

Justification has received more attention for two reasons. First, it is the

public phase of science (Peters 1991a). Scientists are obliged to provide

scrupulously honest accounts of the tests of their hypotheses, but they need

not explain what inspired those tests or hypotheses. In fact, the rational devel-

opments of an hypothesis or test described in the introductions of scientific

papers are usually part of the context of justification and bear little relation to

the actual events surrounding the creation of the theory (Caws 1969). As a

result, the scientific literature does not lend itself to the study of creation.

Second, justification has received more attention because it has attracted and

yielded to the great philosophers of science, from David Hume to Karl

Popper. The same thinkers have placed far less emphasis on creativity, allow-

ing that discovery is a personal matter best left to the individual scientist and

his or her muse (Popper 1934).

The Challenge of Creativity

This uneven emphasis on creation and justification should be a matter of

some concern for working scientists. The evaluation and application of exist-

ing theories is relatively straightforward. We are by and large competent

technicians, distinguished by some modest originality, above average intelli-

gence, and a highly specialized education. This combination allows us to

function effectively in the context of justification. Our problem is more likely

to be the creation of clearly stated theories that are interesting enough to

warrant the effort of justification.

The problems of how to identify the hypotheses that will receive the

weight of our highly developed evaluative abilities should be addressed by

those philosophers who deal with the context of discovery, but that literature

is not very helpful in practice. Many of the writers who treat scientific cre-

ativity are visionaries who think that the object of their studies is too sublime

to be fully grasped (Caws 1969). As a result, their writing deals with concepts

that are too ill-defined for application. For example, we learn from Koestler

(1969) that there is a ripeness to ideas, but we are given no advice about how

we are to find these ideas or how we can compare maturities of ideas once

they are found. Koestler also tells us that we may expect a creative flash of

insight, but not how we can precipitate such a “Eureka act”. Most accounts of

scientific creativity give space to genius, imagination, and intuition (Morris

1966). The problem for working scientists is not that we mistrust the value of

these intangibles, but that an appeal to them is no help in our day-to-day work

(Caws 1969). Like most scientists, I recognize I have too little of these

virtues, and I gain nothing on being told I need more. What would be useful

are instructions about how to make my little store of imagination grow, or at

least how to use it effectively. The metaphors are simply unhelpful in that

regard.

Sociologists of science have approached the problem of creativity by plac-

ing science and scientists under the microscope and examining creation as a

phenomenon. They examine the lives of distinguished scientists to determine

if some similarity of education or environment might explain their stature.

From such studies, we learn that Nobel laureates tend to come from the mid-

dle class, studied with other Nobel laureates and worked at only a select few

universities (Zuckerman 1977). Francis Galton (1875), one of the first to

work on this topic, noted that distinguished scientists tended to be the eldest

child, had lost one parent before the age of ten, and had become strongly

attached to the other. Galton also emphasized the role of family and heredity

in genius. There is some indication that left-handedness may be more com-

mon among great scientists. Unfortunately, this information comes too late

for most of us. Our genetic dispositions, childhoods and formal educations

are already set in an unredeemable past.

There are some hints as to what we might do to be more creative. Caws

(1969), following Galton, suggests that creative scientists are critical of cur-

rent views in the science and suspicious of dogma. Koestler (1969) suggests

that we not resist new ideas, but try to prepare our minds to accept them. We

should consider alternatives (Chamberlin 1890, Platt 1964). The notable suc-

cess of scientists who switch fields suggests that periodic changes in research

118 SOURCES OF ECOLOGICAL CREATIVITY

topic are likely beneficial too. These steps are suggestive, but far from a cook-

book for creativity.

In considering this literature, I came to the conclusion that it has limited

meaning for most scientists because it deals primarily with scientists of

heroic dimensions: Galileo, Newton, Einstein, and Darwin. Even the sociolo-

gists of science limit themselves to such distinguished individuals that the rel-

evance of the conclusions for the rest of us must be suspect. For example,

Zuckerman (1977) deals with Nobel laureates, but figures in Price (1986)

show that only one in every one to ten thousand scientists can hope for such

achievement. What are the rest to do?

It can be argued that the research of the bulk of scientists simply does not

contribute to their science (Glaser 1964, Cole and Cole 1972). Statistics show

beyond the shadow of a doubt that the literature is dominated by a relatively

small number of scientific authors. These are the leaders who write most of

the papers, fill most of the best journals and receive most of the citations. At

the other extreme, there are a large number of authors who write but one or a

few papers, who are never cited, and who are relegated to lesser journals with

tiny readerships (Price 1986). The rest of us, mid-level career scientists,

could accept that we are unlikely to contribute creatively (Cole and Cole

1972) and resign ourselves to the important role of the audience that gives the

great scientists the recognition they have earned (Merton 1968). However,

most scientists legitimately hope to do more.

The Existing Literature as an Inspirational Device

Medawar (1967) suggested that scientists almost always draw their inspi-

ration from the literature of their science and their own scientific observa-

tions. Falling apples, swinging chandeliers, and slopping baths are therefore

as atypical as instances of scientific insight as Newton, Galileo, and Archi-

medes are atypical of scientists. Most of us do not write revolutionary papers

that redimension our sciences, and even scientific revolutionaries do so

rarely. Instead, most research is directed to solution of “puzzles” thrown into

relief by the paradigms of our sub-disciplines (Kuhn 1962, 1970).

Most of the remainder of this essay elaborates Medawar’s position using

the ecological literature. My concern is to provide models for scientific cre-

ativity that are more familiar and more functional for the majority of working

scientists, by providing more typical and more prosaic examples of the dis-

covery of pattern in nature. Although I have no authority to judge their appli-

cability beyond ecology, I would be surprised if scientific creativity in other

disciplines were remarkably different.

119THE EXISTING LITERATURE AS AN INSPIRATIONAL DEVICE

Dissection. The most common approach to the identification of relevant

problems in ecology has been the dissection of large things into manageable

parts. For example, the literature identifies many processes as important: the

phosphorus cycle in lakes, the productivity of forests, and the interaction

between plants and herbivores. Since these topics are too vast for a single

research project, we study some component of the total process that is inter-

esting and that we are competent to handle — plankton in a beaker, stomatal

gas exchange, or the feeding preferences of moose.

Fig. 27 provides a model of the rationalization for such studies (Rigler

1982a). The model provides a rationale for an almost limitless number of

small studies providing bits of previously unknown information about the

world around us. It can be used over and over again so as to help scientists

find new topics for research, and so continue playing the game. Science of

120 SOURCES OF ECOLOGICAL CREATIVITY

Fig. 27. The safe and easy game of ecology. Scientific research programs can be iden-

tified by choosing some population, species, community or ecosystem as X, and then

selecting the appropriate words and phrase in brackets. (From Rigler 1982a)

X is a very

abundant community

unusual type of species .

important ecosystem

species

Although similar communities have been studied,

ecosystems

as have some aspects of X

(references, to demonstrate knowledge of the literature) ,

feeding

production

X’s physiology has not.

Pb content

et cetera

Therefore I chose to study

one of the last set .

this sort is not particularly challenging, but it may be essential for normal

science.

Mechanism. Mechanism is a special case of dissection. Mechanistic anal-

ysis arranges other components of the system explicitly in flow diagrams and

simulation models, or implicitly as a mental construct in the minds of the pro-

ject directors. The object of study is important only because it is an essential

part of the whole. This device was effective in realizing the aims of NASA

and the Manhattan project, where a final, tangible goal was well recognized

and the parts were developed for this application.

Mechanistic analysis has also produced a number of fine descriptions of

various ecosystems (e.g. as part of the International Biological Program). It

seems to have been less successful in this area, perhaps because the problems

the ecological teams were to confront were less clear than bombing the

enemy or walking on the moon.

Although this essay is most concerned with indicating some of the ways

that working ecologists find their problems, the preceding chapter obliges me

to point out a difficulty with mechanism. The rationale assumes that the

importance of the process does not lie in the isolated parts, but in the whole.

If the program is to succeed, someone must eventually put the disconnected

parts together. This synthesis has proven remarkably difficult (Brown 1981).

Dichotomies and categories. Dissection and mechanism are reductionis-

tic approaches to theory building in ecology, but there are holistic alterna-

tives. One of these involves a thorough classification of the phenomena and

subsequent hypothesis about the characteristics of the classes. For example,

Robert MacArthur repeatedly identified extreme behaviours and then used

these extremes as dichotomous categories for the classification of less

extreme behaviour of the same type (Schoener 1972, Kingsland 1985). Thus

we have opportunist and equilibrium species, generalist and specialists, and

coarse- and fine-grained environments. A similar approach takes the

extremes as the poles of an axis, as in the r–K continuum in life history

theory. In all cases, the approach involves two steps: first an identification of

the defining categories or axis, then an examination or comparison of the

different characteristics associated with the resulting categories or ranks.

There is no reason to limit this approach to dichotomous categorizations.

Southwood (1988) advocates a trichotomous division of the habitat in terms

of disturbance, adversity, and biological interaction. MacArthur (1972)

believed that future developments in ecology would depend on a two- or

three-way categorization of the habitat and its potential inhabitants such that

ecological theory would take the form: in environments of type B, organisms

of type X will have characteristics P, Q, and R. The biome approach goes

further still.

121THE EXISTING LITERATURE AS AN INSPIRATIONAL DEVICE

Analysis of variance. Categorization is often qualitative, but an analo-

gous quantitative approach is available. This uses the power of common

statistical procedures to identify tentative patterns which can then be evalu-

ated by further tests. Again one selects a significant topic from the literature,

but now interest is limited to quantitative estimates of the process of interest.

For example, primary production may represent the productivity of lakes and

fish catch that of the sea. One then collects as many estimates as possible and

estimates the variance. The variance quantifies the extent of our ignorance

and is addressed by determining what other factors explain a significant frac-

tion of this variation. Qualitative factors are assessed by expressing these

variables as simple categorical variables and applying analysis of variance

(ANOVA) to determine the explanatory power of the categorization. The

effects of continuous variables can be estimated by regression techniques,

which are themselves minor variants of ANOVA, and mixed models with both

categorical and continuous variables can be developed with analysis of

covariance (ANCOVA). Downing (1991) found that 50 % of the statistical

comparisons between ecosystems used one of these variants; a further 40 %

relied on visual inspections of graphs or tables, which are simply the non-

statistical analogues of ANOVA. This empirical approach has been particu-

larly effective in developing nutrient response models in limnology (Peters

1986) and allometric models in autecology (Peters 1983, Calder 1984).

Extensions, additions and modifications. Almost all relations in ecology

are unsatisfying because the uncertainty of prediction is too large, because the

domain of the relation is too small, or because the original work suffers some

potential bias or other shortcoming. These limitations have long been fruitful

areas for new research. For example, the phosphorus-chlorophyll relation

first proposed by Sakamoto (1966) was improved by Dillon and Rigler

(1974a) who expressed the relation statistically, showed that it applied out-

side Japan, added more lakes to the data base, and, following Vollenweider

(1968), related it to the problem of phosphorus abatement. Since then, more

than 60 relations (Peters 1986) have been added to show that the relation

holds or to modify it for use under a variety of conditions or regions. Such

modifications suggest different mathematical forms for the relation

(Strasˇkraba 1980, McCauley et al. 1989, Prairie et al. 1989), different param-

eters (OECD 1982), different measures of algal biomass (Nicholls and Dillon

1978), and additional variables (Smith 1982, Canfield et al. 1984). Some

authors have concentrated on developing the largest possible data set (Can-

field and Bachman 1981), others on explaining the variation in the existing

sets (Carpenter et al. 1985).

Similar developments have occurred in allometry. Beginning with Rub-

ner’s study of respiration in dogs (Kleiber 1961), there has been a consistent

122 SOURCES OF ECOLOGICAL CREATIVITY

tendency to increase the range of weights, the number of species, and the

number of higher taxa represented (e.g. Benedict 1938, Brody 1945, Hem-

mingsen 1960, Pagel and Harvey 1988). Robinson et al. (1983) considered

temperature as well as size; McNab (1980) has suggested that life styles and

food habits be considered too. Some few champion other models (Economos

1979, Smith 1980, Seim and Saether 1983) and many have argued for differ-

ent statistical treatments (Zar 1968, Jolicouer and Heusner 1971, Harvey and

Mace 1982, Ricker 1984, Pagel and Harvey 1988). Moreover, successful

models, like the phosphorus-chlorophyll models and size-metabolism

models, have encouraged the development of similar models predicting other

responses from the same independent variables or from correlates of these

variables (Peters 1983, 1986).

The amazing fertility of extension, addition and modification is not lim-

ited to large scale regression analyses. Indeed, limnologists have so long

insisted that each lake and each species is different, that we can safely claim

to be doing science simply by repeating earlier research in a previously unin-

vestigated region, or with a slightly different organism, or at a different time

of year. Extensions to new domains, additions of new variables, and modifi-

cations to existing analyses and models are all implicit elements in the model

for normal research in ecology in Fig. 27.

Technologies. The application of a new technology to the traditional prob-

lems of aquatic ecology is another way to generate a research problem in

ecology. This allows us to profit from advances in our sister sciences includ-

ing the traditional areas of electronics, analytical chemistry, mathematics, and

statistics, but also molecular biology, bioengineering, and computer science.

For example, we can now work at higher levels of sensitivity in the analysis

of the contaminants of our waters, we can identify the genetic structure of our

study populations, and we can collect and analyze data at a rate which was

unimaginable only a few years ago. We can only expect these fruitful inter-

actions to grow. Those ecologists who are technologically competent can

therefore look forward to long, profitable, and potentially much cited careers

dedicated to the translation of advances outside of ecology to ecological

applications.

Complications. Still another mode of creation in ecology has involved the

further complication of existing theoretical models by allowing greater com-

plexity. The history of the logistic curve and its descendants provides an

example (Hutchinson 1978, May 1981). The logistic is itself a modification

of the equation for exponential growth over time (t) of a population contain-

ing N individuals, where r is the growth rate constant:

δN/δt = rN (9)

123THE EXISTING LITERATURE AS AN INSPIRATIONAL DEVICE

The logistic sets an upper limit to this population by assuming that population

growth may be described as sigmoid growth to an asymptote (K) so that the

rate of increase slows as the asymptote is approached:

δN/δt = rN(1 – N/K) (10)

When it became apparent that few populations grew according to this for-

mula, the formula was complicated by the addition of other terms to include

other factors. Thus, the basic equation could be modified (Hutchinson 1978)

to accommodate the lag whereby population growth at time t is a response to

population size at time t –1:

δN/δt = rN(1 – N

t–1

/K) (11)

Alternatively, one could presume that the asymptote varied in time and

thereby replace K with a function of time, or a function of resource supply.

This was developed further by Lotka and Volterra to treat the effects of a

predator population (containing P individuals):

δN/δt = Nr(1 – N/K) – α NP (12)

δP/δt = –Pd + β NP (13)

where α NP describes the decline in prey growth as a result of predator-prey

encounters. The growth of the predator population is instead assumed to

represent a balance between the predator death rate, d, and some positive

function of predator-prey encounters, β NP. These equations can be elabo-

rated much further (May 1981).

A further set of equations based on this model were developed by Volterra

to describe population growth of the ith species as a function of both its own

population size and the effect of 1 to j competing species, each characterized

by a competition coefficient α

δN

/δt = r

(1 – N

– ∑

) (14)

This led to the very rich conceptual developments of MacArthur, Levins, May

and others, treating communities as matrices of mutual competition coeffi-

cients.

Since an infinite number of equations could replace the simple relations of

Verhulst, Lotka and Volterra, these developments could go on indefinitely.

Moreover, since there are also an infinite series of alternatives to these simple

models, we could expect to see creative programmes in ecology eventually

developing parallel to the logistic mainstream.

Not all complications need be so mathematical. Some can be largely

qualitative. For example, models of zooplankton filtering rate (Chapter VII)

124 SOURCES OF ECOLOGICAL CREATIVITY

began with the assumption that the animals were simple pumps and filters.

Gradually researchers have uncovered a far greater range of complications

showing that the feeding rate is sensitive to temperature, pH, oxygen, food

particle concentration, particle size, particle type, experimental methodology,

animal feeding history, age, size and so on (Peters 1984, Lampert 1987). Sim-

ilar developments could be sketched for any physiological process. Another

limnological example, but one which invokes community ecology, is pro-

vided by the size efficiency hypothesis (Hall et al. 1976, Peters 1991b, 1992)

which began as a rather straightforward case of predator-mediated competi-

tion between large and small animals (Brooks and Dodson 1965), but which

has subsequently been developed, extended, and complicated by considering

the effects of invertebrate predators and their vertebrate predators (Dodson

1970), of food particle size, of starvation resistance in juveniles (Tessier and

Goulden 1987), of interference due to larger particles, and of differential

capacities to avoid entanglement (Webster and Peters 1978, Gliwicz and

Siedlar 1980, Porter and McDonough 1984). The paradigm has built on the

original broader base of Hrbácˇek et al. (1961) to include a host of top-down

effects (McQueen et al. 1986) and may be considered a forerunner of bio-

manipulation (Shapiro and Wright 1984). Ecologists thrive on complication

and therefore an easy step to creativity is to develop still another flourish for

the existing models.

The Danger of Conventionalism

It is not my intention to describe all the ways that ecologists come to their

new ideas. Instead of developing this list further, I want to end by considering

a problem that results if these are the only models for creative developments

in ecology and to point to a potential solution to that difficulty.

The flaw is that these developments are all based on the overriding

paradigms and dogmas of contemporary ecology. If we use any of these mod-

els we further entrench prevailing ideas. Therefore before we continue any

line of development we should invoke our critical capacities to determine if

that line merits development. In some cases, including limnological models

of lake nutrient-response models and autecological models based on allome-

try, I think a fair evaluation would encourage such development. These are

good theories with considerable promise for growth and application. In other

cases, the logistic and competition theory being two, conventional creativity

has led to many publications and citations, but not to predictive power or the

resolution of problems that such power allows. I suspect that the normal cre-

ative modes of ecology sometimes simply extend the life of constructs which

125THE DANGER OF CONVENTIONALISM

have not borne fruit in the past (Brown 1981) and are unlikely to do so in the

future.

The traditional questions and topics of our science can be fruitful sources

of inspiration for new research. They can also be intellectual traps. We risk

entrapment when we allow the science to become so self-defined that the only

interesting questions are those which we have always asked, but failed to

resolve. This is the final retreat to scholasticism, it is part of what Pramer

(1985) called “terminal science”, and it is the opposite to Medawar’s (1967)

conception of science as “the art of the soluble”.

Creative Alternatives for Normal Ecology

If we are to escape from the trap of terminal science, we need a means of

introducing new questions. At first, this may seem to require a higher level of

creativity than the techniques mentioned above, but there are some ways of

finding new questions which need not lie outside normal science.

Syllogisms and analogies. One spectacularly successful technique to

encourage creativity is that of Hutchinson (1978; see Kingsland 1985 for

discussion). This consists in the identification of a syllogism — that is of

some logical, usually algebraic or graphical, model — from some area out-

side of ecology, and application of this syllogism to a problem in ecology

which is hypothesized to be analogous. This approach appears in analogies of

ecology with economics, game theory, physics and genetics. It is frequently

used in competition theory, optimality theory, and evolutionary theory, and

has been characteristic of the powerful school of ecological thought domi-

nated by Hutchinson, MacArthur, and their intellectual descendants (Fretwell

1975, Brown 1981). It is especially useful for those who have interests and

abilities which extend beyond ecology.

The process has two relatively independent phases. The logical implica-

tions of the model are elaborated in a deductive phase. Since this elaboration

is a purely logical question, this phase requires no empirical input and there-

fore this is a major activity for theoretical ecologists. Once the deductive

phase is well advanced, the research enters a hypothetical phase in which the

model is hypothesized to apply to some ecological phenomenon. Identifying

such a phenomenon may prove difficult or impossible, and some of these log-

ical models leave the theoretician with a solution in search of a problem, like

the logistic and its descendants.

Because this approach is based on analogy and metaphor (Oster 1981), it

is only as good as the degree to which the analogy holds. In practice, the anal-

ogy is rarely perfect and considerable ingenuity may be required to fit some

126 SOURCES OF ECOLOGICAL CREATIVITY

ecological observations to the logical model (Maynard Smith 1972). How-

ever, even if the model cannot be applied to nature, its logic may become a

part of theoretical ecology. For example, this seems to have happened to the

theory of limiting similarity, whose terms cannot be applied to nature (Brown

1981) but which remains a favourite point of discussion for theoretical ecol-

ogy (Abrams 1983). Sometimes, as in optimal foraging theory (Beatty 1980,

Stephens and Krebs 1986, Gray 1987), one may be in a position to decide

which model applies to a particular case only after making the observations

that the models purport to predict. Such models only tell us what we already

know.

The syllogism has proven a useful prod to ecological creativity, but it has

also introduced a series of logical arguments into ecology which are either

impossible to apply to nature, or can only be applied after the fact. These are

the tautologies that confound ecological texts, courses and journals, and slow

the development of a powerful science (Peters 1976, 1991a).

A return to application. There is another way to stir the creative juices of

ecologists and thereby help them to isolate appropriate research problems.

This also involves material from outside the traditions of the science, but it

has been less widely recognized than syllogism and analogy.

I suggest that we step back from our library desks and lab-benches, that we

put aside our field notes and learned journals, and instead take a long look at

our lakes, our seas, our forests and our fields. We should ask ourselves what

are the most obvious, first questions that we would put to such a system. We

might wonder, for example, if the water in a lake is good to drink or if it is

warm enough for swimming. We might wonder what fish live there, where in

the lake they are found, how many we can catch, and if they are safe to eat.

We may have other concerns like how much water we can drain from the lake

for agriculture or how the fish will respond to water level controls, industrial

development, and acid rain. There are a host of questions like this, questions

we once asked, but of which we lost track in the course of the professional-

ization and professorization of the science.

Often, we have turned our backs on these obvious questions to ask ques-

tions like “How many eggs does a copepod carry?”, ”What is the successional

sequence of algal species in the lake?”, “What are the names of the animals

which the fish have in their stomachs?”, “How fast is radioactive phosphate

absorbed by the plankton?”, and “How much does a water flea excrete?”.

These may be important questions. We may need to know these things to

answer the obvious questions. Whether this is so or not, we have lost the con-

nection between these obvious questions that first attracted many scientists to

ecology and many contemporary ecologists to their specialities, and those

which our scientific training has subsequently encouraged us to pose.

127CREATIVE ALTERNATIVES FOR NORMAL ECOLOGY

The benefits of practice are widely recognized. De Solla Price (1986)

made the point in a general context in his last paper, On Sealing Wax and

String. Box (1976) argued that the interchange of theory and practice was an

essential element in the genius of R. A. Fisher. Vollenweider (1968) showed

that it is possible to contribute powerfully to limnology, while ignoring the

traditions of the science. Application is more scientifically valuable, more

socially essential, and more intellectually challenging (Rigler 1975a, 1982a,

b) than most of normal science.

Therefore my last suggestion to increase our creativity is a simple one. It

is to return to the questions of the layman, or better to the questions of a child.

In doing so, we may be able to see our subjects with fresh eyes, lighting again

the creativity that effective science demands, and simultaneously helping

confront the ever-growing problems of humanity.

128 SOURCES OF ECOLOGICAL CREATIVITY

IX Empirical Limnology

“No scientist is admired for failing to solve problems

that lie beyond his competence. The most he can

hope for is the kindly contempt earned by Utopian

politicians. If politics is the art of the possible,

research is surely the art of the soluble. Both are

immensely practical-minded affairs.”

Sir Peter Medawar

[The Art of the Soluble (1967)]

In previous chapters, I defined science and theory to emphasize the impor-

tance of theory in telling us what the world is like. According to Popper, sci-

ence does this by telling us what the world is not, so that we can discount

logically possible observations that the theory tells us are unlikely to occur. I

then detailed my growing unease as I searched for such theories in ecology

and instead discovered that many ecological constructs were not very infor-

mative in this sense. I looked for guidance to my speciality and to the general

field, but was again disappointed. They did not seem to measure up, either to

Popper’s criterion of demarcation or to the growing environmental challenge.

Initially, my disillusionment was profoundly disquieting, but eventually it led

me to resolve the issue by putting aside the traditional topics of my research

to focus on socially relevant, holistic, empirical studies of lakes. That change

in approach is the topic of this chapter.

Social Demands and Scientific Supply

For many years, eminent ecologists have warned that the present course of

society will lead to certain disaster for civilization. For the most part, society

has ignored them.

I was never an eco-preacher — I am much too selfish about research

time — but generally I support that mission and I have wondered why the

excellent arguments of our leading ecologists were ignored. I resolved the

issue, at least in my own mind, by recognizing that the questions ecologists

were answering differed from those society was asking. The eco-preachers

made predictions about the fate of the biosphere, but society was asking ques-

tions about populations and ecosystems. Ecologists would eagerly argue for

global restructuring of the economy, culture and politics, but were often mute

in discussions about cleaning a river or managing a fish stock. The ecologists

argued, with some justification, that biospheric questions were more impor-

tant. Society wondered, equally legitimately, why it should accept ecologists’

solutions to big questions, when it was apparent that ecologists could not

resolve local issues.

This ecological credibility gap grew when society realized that most ecol-

ogists had not been trained as biospheric experts. Ecologists trained to

address much smaller questions, yet, when asked to make a specific predic-

tion about a particular population or ecosystem, we could rarely do it. Even

more rarely did we agree with one another.

The standard reply to a request for advice was in effect, “Give me

$100 000 per year for twenty years to study the issue and I’ll tell you what

happened.” Society caught onto this trick pretty quickly. Instead of asking

one ecologist, it asked a suite of n ecologists, and out of the n different

guesses that resulted, it picked the guess that was most economically or polit-

ically expedient. This tactic simply obfuscated the process of finding scien-

tific solutions to societal problems, delaying science by confusing both

researchers and society.

My discovery that ecologists’ answers were mismatched with society’s

questions led me to a personal choice to start predicting what society wanted

to know. My decision to change research directions after many years was

hard, but I found it even harder to develop useful theories. I could, with mod-

est intellectual effort and considerable hand-waving, invent a new theory, but

I could not guarantee its success in application. I therefore focused on finding

the approach most likely to create a “useful” theory. In this context, “useful”

means predicting what society wanted to know.

Pessimists and Optimists

There seemed to be two distinctly different methods of attacking a scien-

tific problem, which I shall call, for the present, the way of the optimist and

the way of the pessimist. They can be distinguished by the way they address

difficult scientific problems. The optimist says “I am going to solve it.” The

pessimist says “It is not soluble in its entirety, therefore I will solve a little bit

of it.”

Imagine that each school wanted to predict when an alarm clock would go

off so that they might control this device to their advantage. The optimist

130 EMPIRICAL LIMNOLOGY

would study the behaviour of the clock under a variety of conditions and look

for regularities or patterns. The pessimist, believing that the clock could

never be really understood that way, would instead offer to take the clock

apart: “I will study each screw, and each cog wheel. I will take apart the cogs

and see how they are made, I will study the shape of the teeth, and the

scratches on the casing; I will look at the structure of the brass, steel and lead.

Then I will begin to study the interactions between and among these parts,

and slowly, painstakingly, I will come to understand the clock.” Given the

information at hand, we have no way of knowing which approach is better.

The scenario supposed that we could not predict the clock’s behaviour, and as

long as this is so, we cannot judge the success of the different approaches.

Any choice between them is whimsical, unless we can appeal to a broader

experience. We need a theory of scientific development.

Testing the alternatives. Luckily for me, I once taught a course on the

history of biology, and I was able to cast my mind over examples of the

invention of past theories. To my delight, I discovered that they all came

about in the same way.

If we were to look over the history of branches of science that have

achieved successful theories, we would discover a remarkably consistent

story. It runs as follows:

(1) identify the system about which you want to make predictions;

(2) observe the behaviour of that system and look for pattern;

(3) express the pattern rigorously and, if possible, quantitatively to yield

an empirical theory;

(4) try to explain why the theory works, with an analytical or explanatory

theory.

Thus Copernicus built on patterns that had been observed by astronomers

from Babylonia to Tycho Brahe, and Newton “only” completed the quantita-

tive description of those patterns begun by Kepler and Galileo. That arche-

typical scientific advance did not reach the status of explanation until a new

generation saw it as philosophically true (Chapter III). Dalton saw that chem-

icals combined in fixed ratios, Mendel tended his peas, and Darwin visited

the Galapagos. Even the most elegant analytical theories began as humble

empirical patterns.

This is not to say that the discoverers of pattern had no preconceptions or

working hypotheses. They undoubtedly did. Nevertheless, the initial work

was observational and the first achievement was the identification of patterns

in those observations. Consequently, most of the creative approaches of nor-

mal ecology (Chapter VIII) aim to detect pattern. That is an appropriate focus

for a young science.

131PESSIMISTS AND OPTIMISTS

One of our problems in ecology is that many ecologists have decided that

this standard scientific strategy is inappropriate for ecological systems. Ecol-

ogists have placed their trust in alternatives. Perhaps the most popular has

been reductionism or mechanism, whereby we dissect a system we see as too

complex and study the parts in isolation. An alternative technique, less used

but still much honoured, is the “a priori road” (Forbes 1887) whereby we

intuit bold hypotheses for subsequent test. Still another technique creates

elaborate intellectual universes and ecosystems of concept or algebra and

then seeks parallels between those intellectualisms and the real world. These

approaches are popular and attractive, but the weakness of ecological theory

in the face of the environmental crisis argues tellingly against them.

Holists and reductionists. I have made two important points. Successful

investigators did not begin by dissecting the system of interest; and the origi-

nal theories did not pretend to convey understanding. In other words, histori-

cal evidence suggests that the way to construct theories has been holistic and

empirical. There is really only one way to create new theory and that is the

way of the optimists.

My perception that there were two ways to create theory was based on a

misapprehension. The source of this misapprehension was also revealed by

our collective experience in building ecological theories. After a pattern had

been identified empirically, other investigators were inspired to explain why

this holistic theory worked. They might tear the system apart and relate the

behaviour of the whole to the behaviour of the parts. They might attempt to

rephrase the theory in words that conveyed understanding, and if successful,

they might gain far more credit than the empiricist who first described the

pattern. The pessimists then were not trying to build a new theory or to offer

useful new predictions. They were trying to explain theories that already

existed. Like many ecologists, I had confused the two processes and now see

my early years in research as a misapplication of the pessimist’s piecemeal

approach to the creation of new theory, rather than to the explanation of exist-

ing theory.

In more conventional terms, the ecological optimists are called “holists”

and the pessimists “reductionists”. In general, scientists are much happier

with a reductionist, explanatory theory than with an empirical, holistic theory,

even though both may be equally predictive. As a result, most researchers

approach their material as reductionists. However, since I was concerned with

producing predictions that contemporary ecological theory could not give,

there was no reason for me to work like a reductionist. My decision was there-

fore to reject the reductionist approach and to become a holist and an empiri-

cist. Thus after twenty years, I stopped being a scientific pessimist and

became an optimist.

132 EMPIRICAL LIMNOLOGY

What to Predict?

Once I had decided to hunt for a theory, I had to decide what the theory

was going to be about. What system would I study and which of its proper-

ties would I predict? The system would clearly have to be a lake, because I

had no expertise about anything else. At the time, there were a number of

questions people asked about lakes: Is it green? Does it smell? Are there fish

in it?

At first, I balked at the idea of addressing topical issues in society. The

professor in me, the old scientist, grey, wrinkled, and paunchy, wanted to

say “No, you must stick to pure science because only basic research yields

new theories.” The concerned scientist, interested in society’s problems and

society’s image of ecologists, countered by asking how I could hope to close

the credibility gap if I insisted on making predictions that were irrelevant to

society.

Luckily, history again came to the rescue. The old professor was wrong.

Many contributions to scientific theory come from attempts to answer soci-

ety’s questions. Astronomical theory arose from our perceived need for a

calendar. The earliest chemical theory arose from our desire for eternal life

and for the ability to convert base metals to gold. More recently, the germ

theory of disease and our theory of spontaneous generation arose because

Louis Pasteur was hired to find ways to cure diseases of grapes and wine.

Claude Bernard, motivated by a desire to cure diabetes, developed our

theory of homeostatic internal regulation. The best examples of useful theo-

ries in ecology that I knew were models developed to predict commercial

fish catch by D. S. Rawson (1955) and later by Dick Ryder (1965, 1982).

Thus we have plenty of evidence to show that new theories can come from

applied problems.

The problem of which property to predict remained. Society wants pre-

dictions about many properties of lakes: taste, toxicity, algal abundance,

oxygen levels, contaminant fates, fish harvest, and so on. How does one

select amongst these properties? An answer to this question was given most

succinctly by the Nobel laureate P. B. Medawar (1967) in a review of Arthur

Koestler’s book, The Act of Creation. Medawar answered Koestler’s ac-

cusation that scientists ignore the important questions by saying that these

questions are too difficult. Successful researchers deal with soluble prob-

lems. Here was the answer I was looking for. I should try to make predic-

tions about the easiest problem I could identify. For a variety of reasons,

most of which concern personal competence and logistic support, the most

tractable problem of societal interest was the problem of predicting algal

abundance.

133WHAT TO PREDICT?

A Research Program in Holistic Empirical Ecology

How green is my lake? I had decided that we needed predictions. The his-

tory of biology showed that the holistic, empirical approach was most likely

to produce the requisite theory. Algal abundance looked easy, so that was my

first target and I did not mind in the least that society was interested in that

result. My approach would be to search for repetitive patterns in the algal

abundance of lakes and then to correlate these patterns to other lake proper-

ties, so that in future we would be able to predict algal abundance from those

properties.

The twin perils of complexity and reality. At this point, I had to be careful

not to fall into a dangerous trap. I must not allow myself to be distracted by

all the fascinating complexities of the system. For example, it was tempting to

start by counting all the species and races of algae in a series of lakes; or I

might have instead begun to speculate about the relation between the property

I wanted to predict and other equally unpredictable properties, like the rela-

tion between zooplankton and algae. These questions, and many others, are

quite capable of engaging armies of limnologists for generations.

To avoid such traps, I very quickly decided that the measure of algal abun-

dance for my purposes was the concentration of chlorophyll a. This choice

seems dangerously simplistic to the modern limnologist who knows that dif-

ferent algal divisions contain different pigments, and that the chlorophyll:

biomass ratio can vary enormously within a single algal species (Nicholls and

Dillon 1978). Indeed the choice is even more simplistic because we are not

even measuring chlorophyll a. All that I was trying to predict was the absorb-

tion of a particular wavelength of light by the pigments extracted from the

particles collected in a sample of lake-water.

The decision to study chlorophyll extracts put me in danger from another

trap, that I might become stalled in a lengthy consideration of the reality of

my measurements, just as I had once studied the reality of phosphorus frac-

tions. I escaped both pitfalls by applying a holistic, empirical approach. The

holist avoids dissection of the problem (i.e. the prediction of total algal abun-

dance) into its components (e.g. the prediction of algal species abundance).

The empiricist focuses on measurable properties. The amount of green colour

to be extracted from lake-water by a rigorously defined method is a measur-

able property of the lake. To keep my mind focused on the right approach, it

would probably have been useful to say that I was trying to predict greenness

rather than algal abundance. Not surprisingly, that was what society wanted

to know because that is what people see.

Success — the phosphorus-chlorophyll relation. I was now ready to look

at the data and find patterns in the greenness of lakes. Whenever one starts

134 EMPIRICAL LIMNOLOGY

such a search for pattern in nature, the obvious place to begin is the published

literature. When I did so, I discovered the problem was even more easily

solved than I hoped, because much of the work was already in the literature

waiting to be used.

In a study of 40 Japanese lakes, Sakamoto (1966) showed that, where the

ratio of total nitrogen concentration to total phosphorus concentration was at

least 12:1, chlorophyll concentration is closely correlated with total phospho-

rus. I immediately began looking for other lakes to test this relationship. I

found work by Deevey (1940) in Connecticut, by Edmondson (1969, 1972) in

Lake Washington, and by others elsewhere in North America. All of them fit

very well on Sakamoto’s plot. Peter Dillon (1973) confirmed the applicability

of this relationship in a further series in Ontario, and Wolf Scheider (1978)

did the same in a series of much smaller lakes. All the data fit the same rela-

tionship (Fig. 28).

Twenty years ago, the phosphorus-chlorophyll relation was a revolution-

ary discovery, so counter-intuitive (Elster 1958) that for a time it seemed

unpublishable. Since then, the basic positive response has been confirmed so

many times that the relation is taken for granted. Some even say that the rela-

tion is tautologically true, although I have never seen the deductive proof that

claim implies. Instead, I think the imputation of tautology indicates that the

135A RESEARCH PROGRAM IN HOLISTIC EMPIRICAL ECOLOGY

Fig. 28. The phosphorus-chlorophyll relationship in lakes. (From Dillon and Rigler

1974a)

relation is now considered self-evident. The phosphorus-chlorophyll relation

has become philosophically true, because it now is what we expect.

Phosphorus concentration. At first, we misinterpreted the data in Fig. 28

as a correlation between total phosphorus concentration at spring overturn

and mean summer chlorophyll, but now we would see this as a relation based

on seasonal mean of the phosphorus concentration. In either case, this is not

a particularly useful relationship because it is as much work to measure phos-

phorus as it is to measure chlorophyll and because there is no indication in the

correlation that we could manipulate chlorophyll by manipulating phospho-

rus. However, if we could predict phosphorus concentration from some other

easily measured property we might be getting somewhere; and if we could

relate mean phosphorus concentration to the quantity of phosphorus entering

a lake or something similar, it would be more useful still.

Vollenweider’s basic model. In 1969, Richard Vollenweider published a

model for substance budgets in lakes that purported to predict the concentra-

tion of any substance in lake water. The model is extremely simple. It treats

lakes as if they are open systems, each consisting of a single compartment in

steady state (Fig. 29). For the present discussion, the model can be specified

to predict average lake phosphorus concentration ([TP], in mg m

–3

[TP] = L/(q

+ σ z

) (15)

where L (mg m

–2

–1

) represents the annual load of phosphorus to the lake’s

surface, and the other terms may be thought of as correction factors for other

processes. Mean depth (z

, in m) corrects for the depth over which the load

must be distributed; the term for areal hydrological load of water to the lake’s

surface (q

, in m

–2

–1

or m yr

–1

) corrects for loss of phosphorus through

the outlet, and the sedimentation coefficient (σ, yr

–1

) corrects for the sinking

of phosphorus from the lake water to the bottom. If it worked, this model

could be combined with the phosphorus-chlorophyll regression (Fig. 28) to

predict the effects of phosphorus abatement and enrichment on the greenness

of lakes.

Modifications and reformulations. Vollenweider’s model appeared to

work very well for total phosphorus in relatively unproductive lakes, but not

in highly eutrophic lakes. However, the model had a more important flaw. It

required an estimated sedimentation coefficient to describe the net rate of

phosphorus sinking, and this constant is very difficult to measure directly.

Our solution was to reformulate the model slightly, replacing the hard-to-

measure sedimentation coefficient with a “retention coefficient” so that all

terms were measurable (Dillon and Rigler 1974b). If the total amount of

phosphorus entering the lake from all sources is J (the phosphorus load in

mg yr

–1

), and the total amount of phosphorus leaving the lake via the outflow

136 EMPIRICAL LIMNOLOGY

is J

out

(also in mg yr

–1

), the retention coefficient (R) is defined as the frac-

tional loss

R = (J – J

out

)/J (16)

R is therefore the net fraction of the incoming phosphorus which is apparently

lost to the sediments.

Given R, J and an estimate of the net amount of water flowing into the lake

from all sources (the hydrological load, Q, in m

–1

), one can predict [TP]

in the lake water as

[TP] = (J/Q)(1 – R) (17)

Eq. (17) simply states that lake phosphorus concentration is equal to the

volume-weighted mean phosphorus concentration of all sources of water and

phosphorus (J/Q), corrected for net loss of phosphorus (1 – R). Dillon (1973,

Dillon and Rigler 1974b) then showed that this formulation could effectively

predict phosphorus concentration in lakes. These results were subsequently

confirmed in a set of smaller lakes by Scheider (1978).

137A RESEARCH PROGRAM IN HOLISTIC EMPIRICAL ECOLOGY

Fig. 29. The lake interpreted as a simple continuously stirred mixed reactor in which the

internal concentration at steady state is the result of a single source, the inlet, and

two sinks, the outlet and the sediments. (From Reckhow and Chapra 1983)

Predicting the components of the model. Unfortunately, the model de-

scribed by Eq. (17) is useless for many practical purposes. Because estimates

of J, Q and J

out

require vast field programmes, they are far more expensive

and time consuming than measurements of [TP]. An estimate of Q requires

estimates of the sum of the annual flows of all the i tributaries to the lake (Q

, ..., Q

), the sum of the water inputs from each of j “precipitation events”

, Q

, ..., Q

), less evaporation (E) from the lake surface:

Q = ∑Q

+ ∑Q

– E (18)

An estimate of J requires estimates of the total phosphorus concentration

associated with these various inputs from tributary streams ([TP

]) and pre-

cipitation including dry fallout [TP

J = ∑Q

[TP

] + ∑Q

[TP

] (19)

And estimates of R require all this plus an estimate of [TP] and water flow

in the outflow. Obviously, the approach would be much more useful if we

had a way to predict these components of the phosphorus mass balance. If

this were possible, we might be able to predict how green a lake would be

with minimal field work, perhaps without even visiting the lake. This be-

came our goal (Dillon and Rigler 1975).

Q was the easiest of all the components of the budget to estimate. Because

the quantity of water in streams is important for many purposes, hydrologists

had been measuring water flows for years and government sources were able

to provide maps describing the average annual flows of water per unit area of

drainage basin for all of Canada. The same sources provide estimates of evap-

oration from and precipitation onto lake surfaces. Analogous agencies can

provide the same information for other jurisdictions. We simply had to

assume that future flows would resemble past ones and we were able to pre-

dict the components of Eq. (18).

Predicting the phosphorus concentrations associated with this water was

more difficult, because that characteristic had been measured less frequently.

However, Dillon and Kirchner (1975) were able to collect enough estimates

from the literature to provide average figures for the amount of phosphorus

exported per unit area of watershed, given contrasting patterns of land use

and geology (Table 12). The values were only averages, the scatter is high,

and some land uses are not addressed, but the data were then the best avail-

able. As this approach eventually proved powerful, subsequent authors

(Reckhow and Simpson 1980, Prairie and Kalff 1986) have improved and

extended it.

Because P load is calculated as the product of hydrological load and phos-

phorus concentration, Eq. (19) requires estimates of the phosphorus in pre-

138 EMPIRICAL LIMNOLOGY

cipitation and dry fall (Q

[TP

]). Dillon (1973) estimated an average value for

this “aeolian input” (77 mg m

–2

–1

), and we were surprised to find that in

many of our lakes rain, snow and dust could be the major source of nutrient

(Rigler 1974). Because there were many opportunities for error in our esti-

mates of aeolian input, Renata Gomolka (1975) took a much more careful

look at the phosphorus associated with rain and dust. Her work showed that

much of the phosphorus collected by shore-based funnel traps overestimated

the amount that falls on the lake surface. Nevertheless, her estimate (37 mg P

–2

–1

) still identified the air as the major source of phosphorus for many

undeveloped lakes with small catchments. This still seemed counter-intuitive,

but subsequent work has confirmed both the magnitude of this input and its

biological reactivity (Peters 1977).

Eq. (19) has no adjustment for the number of people living in the lake’s

drainage basin, yet we know from physiological studies that animals the size

of human beings release about 0.5 kg P yr

–1

. In other words, each additional

human occupant of the drainage basin has the same effect on phosphorus load

to the lake as an additional 10 ha of undisturbed watershed. Thus, to adjust for

the phosphorus in human sewage in occupied watersheds, one must add

0.5 kg P per occupant to the sum in Eq. (19). If the population uses high phos-

phate detergents, the per capita phosphorus load should be increased to 1 kg

per person per year. These same values allow us to calculate the effect of pro-

posed developments and cottaging on the phosphorus load to a lake. The

effectiveness of the approach has been confirmed in subsequent studies relat-

ing the number of people living in a catchment and phosphorus output

(Mosello et al. 1978, Dillon et al. 1994).

Precept and observation in models of retention. Although we might be

able to predict J and Q, the annual loads of phosphorus and water respec-

tively, we could not use Eq. (17) to predict total phosphorus concentration

without an estimate of the retention coefficient, R.

139A RESEARCH PROGRAM IN HOLISTIC EMPIRICAL ECOLOGY

Geology Dominant land use

Forests Forests + pasture

Igneous 4.7 (0.7–8.8) 10.2 (5.9–16)

Sedimentary 12 (6.7–18) 23.3 (11–37)

Table 12. Phosphorus export coefficients for contrasting bedrock geologies and land

use patterns. Listed values are the means and ranges, in mg m

–2

–1

, of observed

annual losses of phosphorus in all forms expressed per unit area of drainage basin.

(From Dillon and Kirchner 1975)

To predict retention, Kirchner and Dillon (1975) first fit a regression

model to estimates of R from the whole lake phosphorus budgets in Dillon’s

doctoral work and the literature. The model described R as a complex func-

tion of the annual hydrological load expressed per unit of lake area (q

= Q/A,

in m yr

–1

). Although the regression fit the data as well as possible, extrapola-

tion beyond the data set suggested that retention would be less than 100% in

lakes with no outflow (q

= 0). Since this seemed impossible, they chose a

second, semi-empirical model that was consistent with the expected retention

of 100% when q

was zero, at the cost of a slightly poorer fit to the data:

R = 0.426 exp(–0.271q

) + 0.574 exp(–0.00949q

) (20)

Dillon and Kirchner’s model made sense, but it did so by sacrificing

descriptive power for preconception. Such trade-offs may sometimes be nec-

essary. However, in this case the semi-empirical model (Eq. 20) proved less

effective in predicting retention in lakes with low values of q

(Fig. 30).

Ostrofsky (1978) developed a series of empirical models that performed bet-

ter, although they did not predict 100% retention where outflow was zero:

R = 0.201 exp(–0.0425q

) + 0.574 exp(–0.00949q

) (21)

Ostrofsky succeeded by sacrificing preconception for descriptive power.

Other retention models. Subsequent authors have developed a series of

regressions and other models to handle phosphorus retention, either explicitly

like Eqs. (20) and (21), or implicitly in variations on Eq. (17). For example,

the widely recognized international program of eutrophication research sum-

marized by Richard Vollenweider and Joseph Kerekes (OECD 1982) recom-

mends:

[TP] = (J/Q)/(1 – τ

0.5

) (22)

where τ is the lake turnover time (yr) calculated as lake volume divided by

annual hydrological load (τ = V/Q). In other words, 1 – R = 1/(1 – τ

0.5

). Nürn-

berg (1984) compared a series of possible models and settled on:

R = 15/(18 + q

) (23)

Nürnberg also showed that existing models performed poorly in lakes that

developed anoxic deep waters, apparently because anoxia increases the rate

of phosphorus release from the sediments. For such lakes, Eq. (23) should be

corrected by an additional term for internal phosphorus load (J

int

) calculated

as the product of the area of anoxia, the duration of anoxia, and the rate of P

release from anoxic sediments:

[TP] = J(1 – R) + J

int

/Q (24)

140 EMPIRICAL LIMNOLOGY

Holistic tests of the predictions. All the theories predicting the concentra-

tion of phosphorus in lakes would count for nothing if lakes did not respond

to higher phosphorus concentrations by becoming greener, and by developing

other symptoms of eutrophy. When I changed my research directions to pre-

141A RESEARCH PROGRAM IN HOLISTIC EMPIRICAL ECOLOGY

Fig. 30. The failure of precept as a guide in empirical modelling. (A) The model for re-

tention of Kirchner and Dillon (1975) made sense in that it was required to predict

100% retention of phosphorus in lakes with no outflow, but it overestimates retention

(B) where hydrological load is small (Ostrofsky 1978)

dictive limnology, a considerable body of evidence already suggested that

lakes eutrophied in response to phosphorus, but much of that work was open

to criticism and re-interpretations. For example, the classic work of Edmond-

son (1970, 1972, Edmondson and Lehman 1981) detailed changes in Lake

Washington, including phosphorus and chlorophyll reductions, after sewage

was diverted away from the lake. These observations could be interpreted as

the parallel effects of some common, but unmeasured, cause. The bulk of lab-

oratory work suggested that phosphorus was limiting, but there were excep-

tions and the problems of scale hampered the transfer from lab to lake.

Some whole-lake studies appeared to support the role of phosphorus in

the eutrophication of lakes. Schindler’s dramatic experiments with nutrient

addition to lakes showed that massive additions of phosphorus made a lake

green (Schindler 1971, 1974, 1978). In Sweden, early implementation of

phosphorus abatement programs began to yield positive results (Forsberg

1987), and projects elsewhere also showed promise (Sas 1989). However,

fortunes were at risk, both to the public purse in terms of the cost of tertiary

treatment, and to the soap and detergent industry which had invested heavily

in the production of high phosphate detergent, so phosphorus abatement met

active resistance.

I recognized the need for more whole-lake tests of the models, but I was

generally unable to convince my traditional sources of funding that such

money would be well spent. Twenty years ago, Canadian agencies, that is to

say my peers in science, had such faith in the necessity and efficacy of tradi-

tional approaches that they saw little of value in whole-lake experiments and

were appalled at the costs of field surveys that sought patterns among many

lakes. This attitude still prevails at the world’s most important source of

research funds, the National Science Foundation of the United States. As a

result, American ecologists are actively discouraged from empirical, holistic

research in ecology. Since American scientists are among the best supported

and best respected in the field, this antipathy is one of the greatest stumbling-

blocks to the development of effective ecological theory.

Interestingly, applied branches of government in Canada were less reluc-

tant to accept the lessons of our research. Indeed, we were startled at the

speed with which our results were implemented in phosphorus abatement

programs. As dusty academics, we had always believed that government and

politicians ignored our advice out of perversity, ignorance or self-interest.

Instead, the public clamour for action on eutrophication was so loud that

politicians were desperate for applicable solutions. As soon as we had some-

thing concrete to offer, they proved more than ready to listen and to act.

In the past, ecologists had failed to give advice that could be applied. For

example, our traditional advice on eutrophication was essentially to reduce

142 EMPIRICAL LIMNOLOGY

phosphorus loads to zero. Since that goal was impossible, our advice was

ignored. The new models allowed cost-benefit comparisons and showed that

effective abatement was practicable.

I eventually succeeded in finding support for whole-lake experiments,

but only from an unconventional source, The Department of Indian and

Northern Affairs, and then only under the condition that I work in the Cana-

dian Arctic. The department wanted a scientific basis for land use regula-

tions in the north. Since I was now committed to the idea that lakes fit a

common pattern, I saw little immediate need for remote testing, but I was

prepared to make a virtue of necessity by testing the applicability of south-

ern models on lakes lying in permafrost. In this work, we essentially re-

peated Schindler’s whole-lake phosphorus addition experiments, but rather

than raising phosphorus concentration an order of magnitude in a single

lake, we added only enough phosphorus to double the initial phosphorus

concentration of several different lakes. To our delight, the lakes responded

like southern lakes. Our initial surveys showed that the phosphorus-chloro-

phyll relation in these lakes was no different from those established in

southern lakes. Phosphorus addition to some of these waters resulted in

higher phosphorus concentrations, and the chlorophyll levels responded by

increasing as expected (Smith et al. 1984).

The growing school of empirical limnology. According to Kuhn (1962),

programmes in science succeed because they generate more puzzles for sci-

entists to solve. Thus, to predict the greenness of lakes, my group was led to

predict phosphorus concentration of lakes. Those studies in turn led us to

predict retention and the components of the phosphorus and hydrological

budgets, and eventually to test the corpus of existing theory with experiments

on Arctic lakes. It proved a fertile area of research.

The Arctic work was more novel than I had anticipated. The limestone

basins of the area held a surprise: the hydrological budget depended so much

on subsurface flows that Q could not be estimated. As a result, models like

Eq. (17) have limited application in such sites. There is still work to do there,

and at every other stage of the research.

I do not think that our success with the prediction of chlorophyll is a lucky

fluke. I see it as a successful test of the theory that science begins with hol-

istic study and empirical identification of patterns in nature. The same

approach should work elsewhere, on other problems in ecology and limnol-

ogy, and so it has. I will therefore conclude this section with some further

tests of the efficacy of holism and empiricism in producing simple ecological

theories.

Hypolimnetic oxygen deficit. Trout (Salvelinus), whitefish (Coregonus)

and walleye (Stizostedion) are among the most prized game-fish in Canadian

143A RESEARCH PROGRAM IN HOLISTIC EMPIRICAL ECOLOGY

lakes. Because these fishes prefer cold temperatures, they are often confined

to the deeper water of lakes during the summer months. Because they are

adapted to well oxygenated waters, they die if the oxygen concentration falls

below 2 to 3 mg l

–1

, and because eutrophication often results in hypolimnetic

deoxygenation, fish-kills are among the most noticeable and unwelcome

effects of eutrophy. As a result, there was a particular need for models that

predicted oxygen concentrations in lakes. In addition, because anoxia

enhances phosphate release from the sediments, a model to predict the extent

of anoxia should allow improved predictions of internal load. Welch (1974)

and Lasenby (1975) had already developed relations for oxygen concentra-

tions under the ice on frozen lakes, and Jan Barica (1984) had developed

models to predict fish-kills in hypertrophic prairie lakes and sloughs. We still

needed relations for stratified lakes in summer.

At the time, limnologists depended on ideas developed by the founders of

limnology: Thienemann, Strøm and especially Hutchinson. They had devel-

oped three hypotheses about the development of the hypolimnetic oxygen

deficit:

(1) Hypolimnetic oxygen consumption is the result of oxidation of organic

material settling out of the surface waters.

(2) The quantity of this organic material is directly proportional to the rate

of organic production in the surface waters.

(3) The rate of hypolimnetic oxygen consumption is proportional to the

amount of organic matter settling into the hypolimnion.

Since hypolimnetic oxygen consumption depended on the amount of material

settling through the upper surface of the hypolimnion, the rate of hypolim-

netic oxygen consumption was expressed as the average rate of decrease in

the mass of dissolved oxygen under a square meter of the hypolimnetic sur-

face. This is called the areal hypolimnetic oxygen deficit (AHOD, in mg O

–2

–1

The three hypotheses listed above were generally accepted in limnology,

and were supported by a series of estimates of hypolimnetic oxygen con-

sumption in lakes of different trophic state by Hutchinson (1938). Unfortu-

nately, no limnologist was able to confirm Hutchinson’s results for other

lakes. Forty years later, Jack Cornett, a graduate student at McGill, succeeded

where other limnologists failed. He showed why no one had been able to

reproduce Hutchinson’s results, he falsified the model under which Hutchin-

son had worked, and he pinpointed the source of this failure as the third of the

listed hypotheses.

Cornett was able to do so for two reasons. He doubted the premises of

Hutchinson’s model, whereas others accepted them without reservation; and

144 EMPIRICAL LIMNOLOGY

he used the absolute retention of phosphorus (calculated as R × J) as an index

of the amount of organic material falling into the hypolimnion. The second

point is important because it allowed Cornett to estimate organic load in many

more lakes than would otherwise have been possible. Cornett’s model (Fig.

31) shows that the AHOD is a function of the absolute retention of phospho-

rus, the mean temperature of the hypolimnion, and the mean depth of the

hypolimnion.

Cornett did not stop at this point. He recognized that AHOD was not really

what we wanted to know. The hypolimnion is not homogeneous with respect

to oxygen concentration. If we wanted to know what part of the hypolimnion

was anoxic and what part was still habitable by fish, we had to estimate the

volumetric oxygen deficit (VOD) in each stratum. Apparently we had agreed

to look at a substitute variable (AHOD), even if this was not what we wanted

to know, and for many years we were content with this substitution because it

showed what determined hypolimnetic oxygen in principle, even if not in

practice. Eventually, Cornett was able to develop a model which did predict

VOD and therefore could predict the concentrations of oxygen in the water,

the variable in which we are actually interested (Fig. 32, overleaf).

Other phosphorus response models. A number of workers reasoned that if

phosphorus influenced chlorophyll so profoundly, it should affect other com-

145A RESEARCH PROGRAM IN HOLISTIC EMPIRICAL ECOLOGY

Fig. 31. Predicted vs observed estimates of areal hypolimnetic oxygen deficit. R

= ab-

solute retention of phosphorus, T

–

= mean temperature of the hypolimnion (°C),

–

= mean depth of the hypolimnion (m). (From Cornett and Rigler 1979)

ponents of the lake community too. No doubt some of this work is simply an

analogue of the existing regressions, whereas others are based on a deep con-

viction about how lakes function. The source of the researchers’ beliefs is not

at issue in theory creation. What is noteworthy is that such general success

has been achieved in developing empirical, holistic theories, that the ecologi-

cal characteristics of lakes are more predictable than those of any other com-

munity.

I would need a much larger review than this to do justice to all of pre-

dictive limnology. I can, however, briefly indicate the scope of that work.

Models now exist to predict fish standing stock (Hanson and Leggett 1982),

zooplankton biomass (Hanson and Peters 1984, Pace 1986, McCauley et al.

1988), bacteria (Bird and Kalff 1984), benthos (Rasmussen and Kalff 1987,

Rasmussen 1988), and the distribution and biomass of epiphytes (Cattaneo

1987) and macrophytes (Chambers and Kalff 1985, Duarte and Kalff 1990).

Other models predict primary production (Smith 1979), planktonic respira-

tion (Ahrens and Peters 1991, del Giorgio and Peters 1993) and fish harvest

or yield (Hanson and Leggett 1982, Downing et al. 1988, Godbout and Peters

1988). Antoine Morin developed models to predict the biomass (Morin and

146 EMPIRICAL LIMNOLOGY

Fig. 32. Predicted vs observed volumetric rates of oxygen consumption in different

hypolimnetic strata. T = temperature (°C), R

= absolute retention of phosphorus,

V:SA = ratio of stratum volume (m

) to sediment area (m

) contacting that volume.

(From Cornett 1989)

Peters 1988), production (Morin et al. 1988a) and ingestion (Morin et al.

1988b) of black flies living in streams. Still other general relations exist to

predict the production of aquatic invertebrates and fish (Downing et al. 1988,

Plante and Downing 1989, Morin and Bourassa 1992). Other models predict

characteristics of sediments (Rowan et al. 1992), macrophytes (Chambers and

Kalff 1985, Duarte and Kalff 1990), and periphyton (Cattaneo 1987).

None of these relations are perfect, but none of us expected perfection.

What is far more surprising is the speed and the ease with which empirical

theories were developed for a broad range of limnetic phenomena. This rapid

success gives me hope that many ecological questions can be similarly

resolved, and that useful, credible ecological theory is generally possible. If

so, we may see a generation of applied ecologists who, like physicians and

engineers, have valuable skills to offer, and a generation of ecology texts that

are more similar to engineering handbooks than to philosophical treatises.

Perhaps then humanity will be worthy and capable of the planetary steward-

ship we have assumed.

Summary — A Future for Ecology

In summary, the failure of ecology to produce useful predictions was due

not to the complexity of the subject, but to the complexity of our approach. It

took me twenty years to become dissatisfied with the traditional approach and

to identify an alternative. However, when I changed course, it took less than a

decade to see the results of the new approach put into practice and to see the

rapid success of the approach in addressing a whole range of limnological

phenomena. The process has just begun and I am fully confident that the field

will continue its rapid expansion for many years to come. After all, even the

best of the current models leaves great room for improvement. Eventually,

these patterns may be ready for the next step in science, reductionistic expla-

nation, but for the time-being our needs are such that I am still putting my

faith and my effort in theory creation. I am optimistic that an empirical, holis-

tic approach will be widely embraced by ecologists because society needs

help to preserve itself and its environment, because ecologists want to be use-

ful, and because the empirical, holistic approach is the approach that works.

147SUMMARY —A FUTURE FOR ECOLOGY

X An Education in Science: Evaluation

“The instruction at Edinburgh was altogether by

lectures, and these were intolerably dull...”

Charles Darwin

[The Autobiography of Charles Darwin (1876)]

The thrust of my argument to this point has been that scientific knowledge is

knowledge of a special sort. It uses theory to identify which of the possible

observations are unlikely. The ecology we teach and learn often fails to meet

that criterion, yet there is an alternative. Predictive ecology uses an holistic,

empirical approach to identify pattern in nature. This search for pattern has

been an early step in the development of all scientific theory. Better still, the

identification of pattern is a simple process that uses time-honoured scientific

tools and that lies within the grasp of most working scientists. Even without

genius, we can create a more incisive ecology by thinking about the science

we do.

One element in this introspection is thinking about the way we teach ecol-

ogy and biology. Because one generation of scientists teaches the next, it is

imperative that we consider our present paradigms and methods of teaching,

their past success and their future place in education. We have to teach better

than we were taught or have taught.

On Advising Teachers

Perhaps the most arrogant act a teacher can commit is to advise others how

to teach. What is merely a weakness on the part of a student, parent or admin-

istrator is a sin for the teacher because the teacher alone knows how much

harder it is to teach well than to give good advice. We teachers know how eas-

ily a lesson, conceived like a beautiful dream in the solitude of our office,

becomes a nightmare when presented in class. And although we can dash off

an eloquent description of our philosophy, methods and objectives in an

evening, we rarely, perhaps never, produce a course that actually achieves

those objectives. As a teacher, I should know better than to give advice about

teaching. Nevertheless, I yield to the temptation to do so because I believe

that it is time for a change in the teaching of ecology, of biology, and of sci-

ence. The curriculum we inherited from 19th century Britain is no longer

appropriate to producing the scientists we need.

Even as I set aside my aversion to advice about teaching, I still face daunt-

ing questions like “Is it possible for us to become better science teachers than

we are now?”, “Have we reached the limits imposed by our own ability and

education?”, and “What remains to be said about a subject that has been

worked and reworked by generations of professional educators?” I cannot

answer these questions with authority. When I teach, I merely profess my

beliefs about science to a small group of select students. I therefore have

neither the training nor the experience one expects from a teacher of peda-

gogy. I only have faith — faith that there is always more to be said and faith

that we can always do better. Secondary schools could do a better job of

preparing students for science programs at university, and universities could

do a better job with the students they get. Those of us who are teachers must

ask how this can be achieved.

The Goals of a University Education in Science

To begin, we should ask what we are supposed to be doing for our stu-

dents. In other words, what is the purpose of a university training in science?

I see only two purposes for scientific education, one a question of practical

detail and the other a question of general grasp, but I recognize that these are

stressed differently by different people.

The first purpose is practical. Students expect the university to prepare

them for a career and therefore they want what they call a marketable degree.

Legislators and taxpayers want the university to produce the technicians and

managers necessary to keep a highly industrial, technological society running

smoothly. The objectives of both interest groups can be met by providing stu-

dents with a certain number of specific skills, by giving them the ability to

learn new skills and by instilling in them the confidence to use their abilities.

University teachers sometimes reject the practical demands of students or

society because we think them inconsistent with the goals of a true university.

We therefore spend little time explicitly teaching students the details of doing

things. Instead, we seek to develop a general understanding of the field, pre-

suming that the practical skills needed to solve specific problems will some-

how follow automatically. Unfortunately, the evidence for this coupling of

general grasp with specific capacity is not strong, and many graduates are

frustrated that their general education gives them so little ability to do any-

thing concrete.

150 AN EDUCATION IN SCIENCE: EVALUATION

Our disinterest in teaching people how to do things reflects a long-

standing tradition that science is an aesthetic and contemplative activity, not

a practical one. Many thinkers in ancient Greece eschewed experiment, per-

haps because their manufacturing skills were too rudimentary to test their

sophisticated ideas or because manual labour was appropriate only for slaves

(Macaulay 1852, Russell 1931, Medawar 1984). In the great British universi-

ties, the traditions of scientific thought and discussion grew out of the human-

ities and arts. Applied science and engineering were left to more practical

men outside of academia (like James Watt or Josiah Wedgwood), so that man-

ual skills were undervalued. Until this century, many English scientists were

independently wealthy gentlemen who saw the study of nature as purely intel-

lectual. They devised and used experiments, but the labour and critical tech-

nical skills were provided by unsung technicians (Price 1986). The contem-

plative tradition in science has a long and noble lineage, but it was an error.

We are wrong to treat science only as a matter for the mind.

Universities have always had some pedestrian, practical goals and always

will. Now, when the doing and teaching of science are more expensive than

ever before, universities depend totally on society. University teachers must

therefore serve the state and the students. We must teach them how to do

things. As a bonus, we will find that we also produce better scientists,

because we will produce people who can do their science, not just think and

talk about it.

I do not mean to suggest that the university is nothing but a service insti-

tution. It is and must be a subversive element in society. Its professors should

preach an anti-materialist, anti-establishment, and sometimes anti-religious

doctrine. As the university trains students to be useful tools of society, it

should also tempt them with a vision of total self-indulgence: a life in science,

a life dedicated to inquiry into the workings of the material world. As we train

our students, we should try to change their values, to make them more inter-

ested in the generalities of nature than in the details of making money.

Since our subversion rarely succeeds, university scientists were much

happier teaching the violent rebels of the 1960’s than the docile herds of the

late 70’s and 80’s. Students in the 1960’s seemed so much less interested in

the demands of society, that we teachers thought we had at last succeeded in

our subversive agenda.

Strategies for Teaching

The teacher tries to provide an overview of major findings of the contem-

porary discipline, to initiate the student into the paradigms of science, and to

151STRATEGIES FOR TEACHING

show the student how the findings of the discipline apply to relevant obser-

vations. Some of these strategies will teach students about the theories of the

science, but others can conflict both with that intention and with the expecta-

tions of student and society. Yet, because university teachers rarely specify

either the goals or the strategies of education, they lack explicit guides in the

preparation and presentation of their material. Instead, teachers try to do

everything simultaneously and science courses become self-contradictory,

confused, and confusing. It is therefore a useful exercise to consider what

strategies might achieve the various goals of education.

Empowerment by theory. Theories allow anyone to derive identical de-

ductions from the same, specified information. They have to be used with

care, because they provide the power of science to control our environment

and our lives. However, they are not statements that should be kept out of

the hands of the unwary or the uninitiated (i.e. the students). Instead, an ini-

tiation into the use of theory should be the core of an effective education in

science.

In practice, the application of science is necessarily a question of detail.

It requires a knowledge of theories of very low generality to select appropri-

ately among competing constructs, to choose the appropriate techniques to

monitor a particular situation, to use these techniques well, to assess the

results of this monitoring, and to find alternatives that offset any adverse

effects suggested by assessment. Part of our education should teach this

process through paradigmatic examples of good practice and ecological

success.

Students also need to learn theories of greater generality. Grand theories

provide models for less general theories and contexts for specific actions.

Students must therefore learn the grand theories of science, like the laws of

thermodynamics or gravity. There are also theories of intermediate generality

that link the grand theories to observation and that provide broader, less pre-

cise predictions about the phenomena of nature for non-specialists. The stu-

dent should master some of these intermediate theories too.

A scientific education also transmits the traditions of searching for and

testing theories. It describes some of the successes of theoretical discovery

and application, and outlines the failures of current theory. In Kuhn’s (1962)

phrase, it provides paradigms for future practitioners.

An education in science should teach students how to use some subset of

existing theory, provide them with the skills needed to find other extant theo-

ries, and cultivate their abilities to build, apply, disseminate and judge future

theories. If we taught our students about theory and theories, our graduates

would find they have skills to sell, society would find they have the requisite

technicians, and science would find it has a new generation of able practi-

152 AN EDUCATION IN SCIENCE: EVALUATION

tioners. A student who has had such an education would know some of what

has been done and what remains to do, would know a series of examples of

good scientific practice, would see how techniques condition and interact

with theory, and would have a basic set of theories that allow application of

knowledge to some of the problems of society. Such a student would have

been empowered by his or her scientific education.

Understanding through explanation. Scientific knowledge is predictive

and theories are the constructs that make predictions. I would like to be able

to claim that an education in ecology is based on theory, but no such claim is

justified.

If one searches the indices and tables of contents of current ecology texts

for references to “theory”, one is struck with how rarely the word is used.

When it is used, the word almost invariably denotes a highly academic con-

struct which makes few, if any, predictions. Most ecology courses, texts and

teachers try to describe the contemporary science, and therefore do not stress

the role of prediction and theory. Because ecologists often do not recognize

the central role of theory in science, we do not yet have the theories we need,

we do not teach the few theories we have, and our students would be unable

or unwilling to learn them if we did. In short, courses teach what ecology is,

not what it does or should be.

Many ecology teachers have adopted a strategy designed to produce a

sense of understanding, rather than a mastery of ecological theory. In provid-

ing a sense of understanding, science makes us feel “at home” in the universe

and so performs a role similar to that of religion, art, and an assortment of

other human activities. These activities succeed by giving us the feeling that

we understand and control events in our lives, even if this is not so. In reli-

gion, the rituals associated with the winter solstice appear to bring longer

days and, eventually, spring. In art, the irrationality of poetry may seem to

explain events and feelings we do not understand at all, like love, beauty,

laughter, and grief. And in science, an educated student can expound at length

about the causes of the weather, the impact of pollution, and the future of

AIDS, even though the phenomena may be totally unpredictable. In all fields,

the importance of understanding is not whether we actually control events,

because we certainly do not, but to make us feel less at the mercy of unknown

powers and forces.

To promote understanding, teachers try to explain relevant aspects of the

universe using the constructs of their discipline. In principle, these explana-

tions should demonstrate that a given observation could have been pre-

dicted, and thus that the observation was an instance that could have been

deduced from a more general theory (Hempel 1962). In practice, the

elements of explanation are a hodge-podge (Peters 1991a). By offering

153STRATEGIES FOR TEACHING

alternatives to predictive theory, the search for understanding usurps the

rightful place of whatever theories we have, and hides our ignorance with

word-play.

Putative explanations based on non-predictive statements are no more than

post hoc rationalizations. Because the human mind can explain any finite set

of observations in many ways, such explanations are always possible and

plausible. Given the advantage of hindsight, post hoc explanations can fit the

available facts exactly, whereas predictions from theory are unspecific state-

ments of probability. So long as we only compare explanations for data that

have already been observed, post hoc rationalizations appear more precise

and attractive than scientific explanations.

To distinguish post hoc rationalization from scientific explanation, one

must ask if any observation would have invalidated the explanation. Because

post hoc rationalizations are specific and complex, they need only explain

what occurred. Alternative observations are easily explained away by differ-

ences in the details of each case. In contrast, scientific theories not only pre-

dict some observations, they also prohibit others. The theory would be

falsified if these other observations were made. This asymmetry has the

regrettable consequence that post hoc rationalizations are difficult to remove

from the field, so they tend to accumulate in the literature. Theories, and

explanations based on theories, can be falsified and forgotten. In ecology,

non-scientific explanations provide students with poor examples, and hide

the fact that we can predict relatively little and then only imperfectly. This is

most regrettable because, if we recognized the extent of our scientific igno-

rance, we would also see the many opportunities for improvement that ecol-

ogy offers.

We likely find non-scientific understanding seductive, because we are

unwilling to admit how little we control our environment. If we accepted pre-

dictability as the criterion for scientific knowledge, we would realize that

most of the decisions that govern our lives are not scientifically justified.

Economics is a predictive swamp, politics a scientific quagmire, social inter-

action a bog of intuition, and so forth. If we recognized the limits of our pre-

dictive and manipulative power, our already deep sense of helplessness might

become unbearable.

The explanatory role of understanding may reflect a deeply seated human

need, but that feeling must not hide the importance of predictive power. An

obsession with understanding draws potential researchers away from science,

and the desire to explain makes scientists reluctant to accept Popper’s pre-

dictability criterion as the demarcation between science and non-science.

Instead of confronting scientific short-comings, educators frequently disguise

them with words of explanation and a sense of understanding. This preserves

154 AN EDUCATION IN SCIENCE: EVALUATION

the status quo and social serenity, but confounds the advance of science

because it obscures the problems that scientists should address.

Paradigmatic indoctrination. A common strategy in teaching is to

indoctrinate the students to think and act like their teachers. This is the point

where we teach as to “intending professionals” (Barzun 1964) and where stu-

dents are introduced to the over-arching paradigms of normal science (Kuhn

1962). Teachers know that future researchers will not live or work in a vac-

uum. Would-be scientists must be recognized by the leaders in the field and

by peers, or they will never have a chance to practice science. As in art or in

any creative field, a would-be innovator must play by the rules that govern the

community. Scientific innovators must address questions that are of interest

to their community, they must design their experiments in the appropriate

manner, and they must analyze the data by accepted methods, even if this

means going to extremes, like applying advanced statistical tests where none

is necessary. Fledgling scientists must publish in accepted journals, even

though these are read by only a handful of professionals, and they must write

in the accepted style, even though that style is pompous, dull and nearly

incomprehensible. New scientists must be indoctrinated to do all these things

or their work will not receive a fair hearing.

If we want our students to succeed in science, part of our effort must be to

teach them to conform. However, conformity holds the danger of stagnation.

When a discipline can no longer meet new demands placed on it by society

and by its members, the field is in crisis. New solutions and approaches out-

side the normal paradigms are sought, and eventually a new paradigm may be

found to treat contemporary concerns. Progressive science therefore needs

the occasional revolution (Kuhn 1962).

I believe that environmental degradation has revealed the inadequacy of

traditional ecological theory. Ecology needs a revolution, but the processes of

critical assessment and radicalization that precede revolution are frustrated by

indoctrination into contemporary ecological paradigms. At the end of their

education, too many students simply accept the foundations of their science,

and the only problems they can find to study are minor elaborations of current

paradigms. We teach people to be normal scientists, but we may need a revo-

lution to meet the challenges of contemporary ecology.

Disciplinary description. A description of findings in the discipline is a

part of all strategies: teaching theory, developing understanding, inculcating

paradigms, or promoting revolution. However, theory is only part of descrip-

tion, and in ecology usually a minor part. Even upper level courses may

describe contemporary science as a body of incontrovertible concepts, logical

truths, and law-like facts. Students are encouraged to believe, rather than to

question the corpus of science. As a result, even senior undergraduates and

155STRATEGIES FOR TEACHING

graduate students see science as virtually complete and consequently rather

uninteresting. To the converted, contemporary science seems unlikely to

change.

An Evaluation of Teaching in Biology and Ecology

To summarize the chapter to this point, I have suggested that teachers

should strive to prepare students for careers, to prepare technicians for the

state, and to infect some young minds with the passion for science. If we are

doing our jobs well, students graduating with a B.Sc. should be fluent in the

use of a body of scientific theory and method, and they should be confident in

their ability to learn more skills and theories. Those who go on to research

need these same attributes, but they also need an appetite for scientific

thought and investigation.

A simple example will show how well I think we are achieving the practi-

cal goals of higher education in science. I recently had to hire a technician

and my advertisement attracted five graduates from the undergraduate pro-

gram in biology at my university. To select among them, I thought to use a test

to determine if the applicant could follow routine analytical procedures. I

asked each applicant how he or she would prepare a one molar solution of

sodium chloride and how they would dilute that stock to 0.1 M. I thought this

task would present no difficulty because our undergraduates are required to

complete several courses in chemistry, and the applicants were allowed to use

any books they wished. What astounded me was not just that none could

answer the questions directly, but that none could describe how they might go

about finding out how to answer them. Apparently, they could not apply what

they had learned and were so unconfident in their abilities that they could not

teach themselves either old or new material. How will they meet the chal-

lenges of the current marketplace, much less of the next millennium where

they would spend most of their lives?

Nurture or nature. If our students are not as capable as we would like, we

can blame their genetics (them) or their environment (us). The only fruitful

approach is to blame ourselves.

The material society sends to be educated must be basically sound. During

rare historical periods of exceptional intellectual achievement, small popula-

tions have produced many more masters and geniuses than numbers alone

would suggest possible. One need only compare the architecture and sculp-

ture of Periclean Athens, the painting of renaissance Italy, the literature of

Elizabethan England, or the music of 19th century Germany with the prod-

ucts of our age. These societies contained only a few tens of thousands of

156 AN EDUCATION IN SCIENCE: EVALUATION

potential contributors, many of whom lived in poverty, ignorance and squalor

compared to us. Yet they achieved much more than the well-fed, leisured

millions who make up contemporary mass society. If we cannot succeed in

educating scientists, it is more likely because we, as a society, spoil the mate-

rial we have, than because we receive spoiled material.

Even a few hours with a pre-school or kindergarten class is enough to

show that most young children have ample wit and intelligence. Even later,

after the schools have done their worst, they still deliver superior students to

the universities. For example, Harmon (1961) analyzed the secondary school

IQ’s of eventual winners of doctoral degrees in different fields (Table 13), as

revealed by U.S. Army General Classification Test (AGCT) scores. These

results show that we can be elitist in thinking about education.

Both lines of evidence, the usually untapped potential of humanity and the

demonstrated intelligence of our students, imply that the failure of a science

education is more likely to be institutional. High IQ’s and native ability are

not enough. Indeed, most of our doctorates in science do not succeed in their

discipline. De Solla Price (1986) has shown that of all the contributors to a

field in a given year, a fifth never publish again in the same area and a further

third never publish again in any field. More than half the contributors to a sci-

ence do so only once and then drop out. Only a fifth of the initial contributors

become the core of researchers who are major contributors to the science over

the longer term. We are not using our material well.

The problem with textbooks. If biologists are uncertain about the nature

of science, they cannot be expected to direct students effectively. This uncer-

tainty is echoed in the cursory descriptions of the nature of science offered in

introductory textbooks (Chapter I), but is also apparent in the body of the

textbooks, in courses and in more advanced monographs. When teachers are

157AN EVALUATION OF TEACHING IN BIOLOGY AND ECOLOGY

Discipline IQ

Physics 140

Mathematics 138

Engineering 135

Geology 133

Arts & Humanities 132

Chemistry 132

Biology 126

Education 123

Table 13. IQ scores as recorded in AGCT tests of high-school students who eventually

earned doctoral degrees in different fields. (From Harmon 1961)

uncertain about the field, they are unlikely to deliver clear messages about

what is important to their students.

Evidence of the teachers’ uncertainty about what is important can be seen

in the vast welter of information that typifies contemporary texts. Most intro-

ductory textbooks in biology or ecology are huge undertakings stretching

over hundreds of oversized pages. Even these vast texts soon prove insuffi-

cient to contain all our important findings so new, even larger editions appear

at regular intervals (Table 14).

No instructor can seriously suppose that students will absorb more than a

tiny fraction of this material. The texts therefore cannot teach, and they are

scarcely authoritative enough to be reference works. They serve mainly as

samplers of biological thought, providing a place for most major currents in

the discipline. Publishers approve of this format because such a text will

likely touch on the special interests of the professors who select the texts. The

158 AN EDUCATION IN SCIENCE: EVALUATION

Biology texts

H. Curtis y 1968 1979 1983 1989

n 854 1043 1159 1192

W. T. Keeton y 1967 1972 1980 1986

n 955 888 1080 1175

C. A. Villee y 1960 1962 1972 1977 1985 1989

n 615 625 915 980 1206 1412

P. B. Weisz y 1959 1963 1967 1971 1982

n 796 786 886 656 1009

Ecology texts

C. E. Krebs y 1972 1978 1985

n 694 678 800

E. P. Odum y 1953 1959 1971

n 384 546 574

E. R. Pianka y 1973 1978 1983 1988

n 356 397 416 468

R. Ricklefs y 1973 1979 1990

n 861 966 896

Table 14. The growth of textbooks in ecology and biology (as measured by number of

pages, n) with successive editions (as indicated by the year of copyright, y). Page sizes

also tend to increase in subsequent editions, so this table under-represents growth in the

contents of these texts. Names are those of the authors. Editions were selected accord-

ing to availability in the McGill University library system

teacher, recognizing the impossibility of teaching all of contemporary biol-

ogy (or ecology or limnology), can assuage the inevitable sense of inade-

quacy with the thought that the subject is dealt with somewhere in the text.

Interested students could always pursue the topic there, but the indigestibility

of the material must discourage all but the most dedicated (or insensitive).

Texts do not have to be so comprehensive. The best overview I have ever

read of then contemporary biology was The Ideas of Biology, a pocket-sized

paperback less than 200 pages long (Bonner 1962). T. H. Huxley (1880)

developed a text for biology that dealt only with a single model animal, The

Crayfish. Both authors succeeded because they ignored the imperative to pre-

sent everything, and chose to display their ideas clearly and effectively with

highly selected examples. The student could then use these ideas to organize

other facts and other theories. Contemporary textbooks may begin with simi-

lar aims, but they become cluttered by a seemingly inevitable accretion of

biological detail. Each new edition becomes more bloated as the authors add

information to bolster and illustrate their original conception of the science

(Table 14). Unfortunately the result obscures that conception. The secret of

great teaching lies as much in what is left out, as what is left in.

The problem with courses. The swelling texts are only indicators of

teachers’ confusion about biology. The same process occurs in the design of

university courses, as I can illustrate with another personal example.

Some years ago, the government of Ontario decided that the present biol-

ogy course for senior secondary school students was old-fashioned and that it

had to be jazzed up to appeal to modern students. A committee was formed

and a number of zoologists were invited to provide ideas. We talked and

argued all evening. Finally, a good friend of mine announced that he had the

solution and began to outline a new course. Other committee members added

material that was dear to their hearts, and eventually a new biology course

was developed. This is a quite typical ontogeny for an introductory course,

and I suspect that it has been repeated many times in both secondary schools

and universities. Nevertheless, the final product was a recipe for disaster.

The “new course” my friend helped design for high school students was

actually the course he was then giving to first-year university students. In

proposing that a university course be offered to high school students, he over-

looked the fact that university students had only 18 classroom hours a week,

so they had much more time to think about the subject than students spending

almost 30 hours a week in secondary school. Moreover, he ignored the reality

that a university professor might have only 5 contact hours a week, whereas

colleagues in secondary school had 25. In addition, my friend was a highly

trained and brilliant biologist who later became president of a major univer-

sity. This combination of native ability, professional training, and reduced

159AN EVALUATION OF TEACHING IN BIOLOGY AND ECOLOGY

teaching load should have afforded him greater success in his course than

might reasonably be expected of the average high-school teacher.

The real situation was even worse. Because the two of us were working

very closely, I attended many of his lectures, and I repeatedly found he had

serious difficulty understanding some of the concepts he was trying to teach.

Therefore the new course began with subject matter that a good professor

found difficult, yet the course would almost certainly be taught by less com-

petent teachers to more harried students. I think it extremely unlikely that

most students would find that such a course would pique their interest in

science.

My moral is that we cannot teach everything. There is too much for one

course or one career. Instead, we must use a limited set of materials and

examples to show our students how to learn and how to teach themselves.

Repercussions for graduate training. Not surprisingly, the lack of focus

that characterizes undergraduate texts and courses reappears in the research

proposals that students make soon after entering graduate school, and in the

theses they write at the end of their formal education. Students who are not

trained to cherish scientific theory are less capable of formulating testable

hypotheses for their own research. Too often, students set off “to assess the

impact” of some perturbation, “to determine the importance” of some pro-

cess, “to understand the role” of some organism or “to shed light” on a

phenomenon. These woolly generalities provide little direction and convey

little meaning. They hide an unwillingness to specify what variables will be

measured and what responses are expected. They show that one has not

thought about what one can and should do as a scientist.

The challenge for graduate students is therefore to rise above the general-

ities of undergraduate education by identifying a much more specific, imme-

diate goal for graduate research inside a larger context, as an early step to a

long-term goal. This process requires that the generalities be replaced with

highly simplified hypotheses about the relations between operationally

defined variables. It is however not enough that a prediction be made about

some phenomenon; the relations and predictions should also be scientifically

or societally relevant.

So little is known about so much that there should never be a dearth of

good scientific projects. If there seems to be, it is because students are poorly

prepared for the process of hypothesis formulation and testing. The store of

proper paradigmatic examples is low, the testable implications of the science

they know are few, and their graduate instruction, the antidote to an unsatis-

factory undergraduate experience, is weak.

Graduate students in ecology too rarely recognize the futility of a science

that cannot predict. Their long experience with non-scientific “explanation”

160 AN EDUCATION IN SCIENCE: EVALUATION

has crushed the curiosity, doubt and frustration with ignorance that should

give impetus to science. They see their task as the development of discursive

explanations for an accepted set of observations. Instead they should identify

an hypothesis that could have predicted those observations and set out to test

its predictions. Others assume causal relations in nature and set out to prove

the validity of their assumptions, rather than testing what the relation pre-

dicts. Still others study things simply because they were previously unde-

scribed. Small wonder if after five years of studying inward-looking, often

dead-end projects, the graduated Ph.D. leaves the field.

A lesson from the literature. The problem of trying to do too much is not

limited to formal education. Some years ago, I had occasion to read Alfred

North Whitehead. I found it a humbling experience. Like many great

thinkers, Whitehead had recorded a very large number of interesting ideas.

There was no need for the ideas to be correct, and because correct ideas are

very rare, most of them were not. However, great intellectuals, like White-

head, are arrogant people (otherwise they would not have the confidence to

spend so much time writing), so they produce a vast volume of writings. To

do justice to this material would take years of study, and so almost all readers

are inadequate to the task put to them by the world’s leading intellectuals.

The fault does not lie with the busy reader alone. Great writers have writ-

ten far too much. The same idea may be flogged in different guises in dozens

of books. Padding appears everywhere. The great thinker may develop a liter-

ary style that is at times outstandingly good, but at other times obscure. And

the reader, overawed by the writer and by the obscurity, style and quantity of

the material, is simply incapable of sorting out the useful bits. Consequently,

reading becomes superficial, works are labelled thought-provoking (although

there is rarely time to pursue the provoked thoughts), the writer’s fame

spreads, and more, ordinary mortals feel compelled to read the great man’s

works. Even the writer may be fooled and feel encouraged to broaden his

field. For example, although I was struck by Whitehead’s earlier work, I find

his later, more popular, philosophical writings to be so nearly meaningless as

to be incomprehensible. Eventually, even Whitehead exceeded his ability.

This raises a problem. How much time should the would-be reader devote

to the work of a man like Whitehead? A year would surely be far too little, yet

there are many others who merit study. What is the busy scientist or student

to do? The only answer must be to use teachers who can interpret the work for

other professionals, as Magee (1973) and Pera (1980) interpreted Popper.

Science requires incisive teachers at all levels.

161AN EVALUATION OF TEACHING IN BIOLOGY AND ECOLOGY

XI An Education in Science: Prescriptions

“It is this union of passionate interest in the detailed

facts, with equal devotion to abstract generalization

which forms the novelty in our present society....

This balance of mind has now become part of the

tradition which infects cultivated thought. It is the

salt which keeps life sweet. The main business of the

universities is to transmit this tradition.”

A. N. Whitehead

[Science and the Modern

World (1925)]

In the previous chapter, I described the roles we expect our education system

to play, I gave a simple observation suggesting that there is scope for im-

provement, I identified shortcomings at every level, and I suggested that, in

teaching science, the critical issue is our failure to appreciate the nature of

theory.

The interesting question is “How can we do better?” I am going to

approach this question in a way that is somewhat foreign to professional edu-

cators, but more appropriate to a working scientist and teacher. I will ask

“What makes a good scientist?” and “Can we modify our approach to educa-

tion in any way so as to produce more or better science?” This has the distinct

advantage of bringing the discussion closer to my own experience as an under-

graduate instructor, a graduate supervisor, and a university administrator.

The Undergraduate Program

Let me premise this discussion with the observation that the public’s love

affair with universities has grown cold. University professors will have to

grow accustomed to more meagre moral support, less lavish budgets, and

poorer facilities. Our traditional teaching methods will have to change.

We should not expect that any substantial fraction of the teaching staff at

a university would agree on a particular solution or collective action to these

challenges. Professors are free-thinking, angular individuals who are too con-

vinced of their own righteousness to be much influenced by someone else’s

prescriptions for better teaching. This is how it should be. It would be equally

vain to hope for an institutional response to our difficulties. The unhappy

mass of university educators are pulling the administration in a hundred dif-

ferent directions. Experience at two universities has taught me the virtual

impossibility of an imposed, general solution to the problems of university

education.

The only easy modifications that university teachers can impose on educa-

tion involve their own courses. Chapter X indicated where some changes are

needed, and this chapter indicates some that I try to apply in my own teach-

ing. There is no point in advocating the general introduction of these sugges-

tions, so I offer them for other teachers to use or ignore as they see fit.

The problem of confidence. Over a century ago, Francis Galton (1875)

showed that almost half the members of a group of eminent scientists were

either the eldest or only child in their family (Table 15). This remarkable

observation has since been confirmed and extended. A very high percentage

of our best scientists were the eldest or only child (Table 16), they lost one

parent by death (Table 17) or divorce, and they were lonely, rather asocial

children (Roe 1953). These observations should not suggest that, to produce

researchers, we should identify bright children before they reach 10 years of

age and isolate them from their parents. No one advocates such extreme mea-

sures because they would be both morally wrong and ineffective. Roe (1953)

makes the point that about 25% of homeless men also lost a parent before the

age of 10. Most bright orphans do not achieve scientific fame.

The critical characteristic of the bright orphans who do develop into

researchers is that they are very self-confident and self-reliant with respect to

their interactions with the material world. (Their social interactions are much

less successful, but perhaps that is more incidental to their scientific achieve-

164 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

Birth order Number of scientists

Only child 22

First born 26

Middle children 36

Last born 15

Total 99

Table 15. The birth order of eminent English scientists in the 19th century. The families

of these 99 individuals were large, averaging 6.3 children per family, so the chance of

the eminent scientist being the first or only child was much less than the observed

frequency of almost 50%. (From Galton 1875)

ment.) Family circumstances develop in them the belief that they can do and

understand things. This belief is critical to success as a scientist.

For those bright children who are not fortunate enough to be orphaned

before the age of 10, we teachers should help develop this same confidence.

Present science curricula may be intended to achieve that goal, but unfortu-

nately, they are rarely designed in a way that will achieve their intentions. The

main problem is that our science curricula expect far too much of the stu-

dents. They try to be too good. Unrealistically high goals teach students that

they cannot do science, and massive texts show that there is too much mate-

rial to master. Students are therefore trained to pass exams by learning lec-

tures, so they learn to rely on authority rather than reflection, reading and

experience. As a result, university courses rarely teach students to use or to

improve what they have memorized, and certainly do not encourage students

to be confident in their ability to criticize, to use or to do science. The great-

165THE UNDERGRADUATE PROGRAM

Birth order Number of scientists

139

213

Total 64

Table 16. Birth order of 64 eminent American scientists of the 20th century. Fifteen

only children are included among the first born. (From Roe 1953)

Future field Age at parent’s loss: Total

< 10 yr > 10 yr

Biologist 25 0 25

Physicist 13 9 22

Social scientist 9 18 27

Total 15 9 25

Table 17. Percentage of future eminent scientists who lost a parent in childhood through

death. The expected values for college students would be 6.3% before 10 years of age

and about 10% in total. (From Roe 1953)

est weakness of our present system is that it does not give students confidence

in their abilities.

De-enrichment and dis-integration. Universities and departments like to

present comprehensive programs and integrated courses, perhaps because

such organization implies a mastery of the material. Unfortunately such an

approach misrepresents biology and ecology. Neither discipline consists of

monolithic sets of theories. There is no over-arching theory of great general-

ity that ties together all of modern biology or ecology in the sense that every

theory is a refinement or specification of the general theory. If we insist on

teaching as if there were a single science of biology or ecology, or a central

core of crucial facts, we misinform the students about biology and insure our

own failure as teachers of science. There is instead a heterogeneous collection

of hypotheses with different scopes, variables, formats, domains, and suc-

cesses. Indeed, there are so many of these theories of low generality that they

could never fit into a single degree.

If we wish to give students a realistic view of our science we must teach its

theoretical structure. This requires that we give them a dis-integrated view,

one without a unifying central theory. They must learn that theories in plant

ecology can be falsified or confirmed without impinging on theories of hor-

monal balance, that one can be a good physiologist without mastering popu-

lation genetics, and that success in eutrophication control does not insure

equal success in controlling macrophytes or predicting the yields of terrestrial

herbivores to hunters.

Since we cannot expect students to see the generalities of science if they

are constantly harried and bewildered with the particularities of its sub-

disciplines, students with intelligence and an interest in science require a

factually impoverished or de-enriched program. Teachers might try to cover

one-fifth of the subject matter in most contemporary courses, but ensure that

everything taught in one course reinforces and uses everything taught in other

courses. This would allow students time to contemplate the nature of science

in general and their material in particular. Not all students would do so, but at

least those who wanted to could. The others would be no worse off than they

are already. A de-enriched biology course would cover very little factual

material, but it would show students how to apply knowledge from other

courses and it could build their confidence, graduating students who think “I

can do biology”.

I would teach a few aspects of some homely subject, like limnology or

physiological ecology. These are beautiful subjects with which to introduce

biology because so many aspects can be quantified, and because they depend

on the mathematics, physics and chemistry the students have already learned.

In the laboratories, I would concentrate on a few basic skills in mensuration,

166 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

analysis and handling of biological material using phenomena that are sus-

ceptible to study. Students can easily design and build a water bottle to sam-

ple at depth or a Secchi disc to test general theories. They can build and use

respirometers to measure oxygen consumption by poikilotherms at different

temperatures and levels of activity. They can design and build the equipment

necessary to investigate factors limiting the growth of algae. They can learn

to do biology, and thereby learn to do science. If they do not do so, they will

be lost regardless of the number of facts, concepts and observations they

accumulate. Having done so, they can learn most details about the biology

they need for their careers on their own.

I would also include a hefty dose of the history and philosophy of science

in university training. That material is essential to give students the breadth

and vision to appreciate their science. Philosophy can be a tool to help stu-

dents find optimal strategies in learning and research. It is also a handy

weapon for students to defend themselves against the inevitable attacks from

traditionalists.

There are topics which I would no longer teach. For example, the theory of

evolution by natural selection is a subject that still confuses professionals,

and one that cannot be related to most of the physics, chemistry or mathe-

matics that the students are learning or have learned. It is unlikely that uni-

versity courses will save many fundamentalist students from their ignorance,

and open-minded students can learn most of what they need from a host of

splendid books on evolution, or even from the public press and electronic

media. Above all, neither scientist nor student can do much with the theory

of evolution by natural selection because it makes so few predictions. This

“theory” may satisfy the students’ urge to understand their world in some

emotional, visceral way, but such a sensation is not science. Teaching stu-

dents to seek that form of explanatory gratification is a disservice to their

training as scientists.

I would also avoid some of the exciting new fields, like biochemistry and

biophysics. If they are to be mastered, these fields require a background in

mathematics, physics and chemistry that few biology students have as under-

graduates. In any case, evolution, biochemistry and biophysics will still be

taught by the many professors who will remain with the old curriculum, so

there is no need for me to repeat that material.

A de-enriched and dis-integrated program will impose difficult decisions

on the teacher. The material chosen for the course must be carefully selected,

but no general theory exists to identify relevant material within the sea of bio-

logical detail. The criteria could not be those used by the writers of text-

books, trying to touch all the bases of a huge and complicated field. Nor could

the criteria be those used in so much of contemporary ecology, tying concep-

167THE UNDERGRADUATE PROGRAM

tual argument and extreme detail together with a sense of understanding.

Training different ecologists will require different criteria of biological rele-

vance.

Hierarchical themes for undergraduate education. In the absence of

central theory, relevance in biology or ecology depends on the scientific

demands of society and pedagogy. Material for a course can be selected

because society is interested; for example, we might teach about diseases,

conservation, pollution control, plant production or human population

growth. Material may also be selected because it teaches an effective way to

do science. If we were less concerned to detail all the fruits of scientific inves-

tigation, we might introduce students to particularly creative modes of

thought, to recurrent patterns in the development of theory, to effective criti-

cism of scientific ideas, to effective tests of theories, and to appropriate

responses to both the confirmation and falsification of theory in such tests.

Students would therefore face a series of different examples of scientific and

societal problems that have been addressed, more or less successfully, at dif-

ferent scales and levels of biology.

Such an approach necessitates “hierarchical thinking” (Allen and Starr

1982, O’Neil et al. 1986). The students should learn that similar problems

expressed at different scales may yield to different, even contradictory, solu-

tions. For example, annual mean concentrations of zooplankton and algae are

positively related across communities (McCauley and Kalff 1981, McCauley

et al. 1988), but inversely related in microcosms (Novales et al. 1993) and

over a single season in a single lake (Lampert et al. 1986, Sommer et al.

1986). Phosphorus may be important in lakes (Peters 1986), but marine sys-

tems may depend on nitrogen or iron (Price et al. 1991). An effective course

should therefore draw examples from a range of phenomena and biological

levels to illustrate differences and inconsistencies in our knowledge (Fig. 33).

Within one hierarchy, the student should be introduced to theories of high

generality, which allow predictions of a crude sort but at a very general level,

and theories of low generality that allow more precise predictions about ques-

tions of specific interest. For example, one can make crude estimates of pro-

duction per unit biomass from body size alone for all animals and protozoans,

but if the question is restricted to a single species or population, more precise

and often more complicated relations may be necessary.

The theories of production in Fig. 33 predict similar variables, but at dif-

ferent levels of generality. They coexist because they have different domains

of application. They can be independently falsified or confirmed because they

fall at different points in a hierarchically differentiated science. Similarly,

theories about respiration or ingestion can be resolved at different levels,

again more or less independently of parallel hierarchies. For example,

168 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

169THE UNDERGRADUATE PROGRAM

Fig. 33. One system of theoretical hierarchy that may be used to structure biological

education. The figure shows the relations among theories dealing with productivity, at

various levels of generality, predictive power, and specificity, the relationship of these

theories to other hierarchies dealing with other phenomena, and the relation of all these

hierarchies to still more general theories, like the laws of thermodynamics. I, R, D E,

and P (ingestion, respiration, defecation, excretion and production) are the components

of the balanced growth equation. In the theories of lower generality, B is biomass in g

–2

, W is individual body mass in g, T is mean temperature, P is production and C is

fish catch, both in g yr

–1

. Subscripts indicate if the units of mass are wet (w) or dry (d)

production may be predictable from size, but theories of respiration could be

based on temperature and those for ingestion on food concentration, all oper-

ating under the general restrictions set by the laws of thermodynamics, but

otherwise quite free to use different variables, analytical techniques, and

theoretical structures.

If this material is to be taught, the links among the examples must derive

from an explicit consideration of the qualities of good scientific practice. Stu-

dents should learn about the nature of science, the place of creativity and crit-

icism, the role of theory, and the purposes of observations and tests. Particu-

lar examples of success and failure should be discussed and a framework

of interpretation provided.

A theoretical typology. One format with which to organize such a dispar-

ate set of ecological or biological theories invokes a typology of theories. For

illustration, I have identified four basic types of successful theory, although

there may be others and alternate typologies exist (e.g. Orians et al. 1986).

(1) Simple interpolative theories simply assume that a phenomenon mea-

sured at two or more points persists at intervening points. A common type of

interpolative theory in ecology is the species distribution map. If a species is

recorded at two sites we posit that it will be found at intermediate positions,

provided physical-chemical conditions are similar. In fact, we often use the

absence of a species as the first indication of subtle physical or chemical

change.

(2) Limiting factor, mass balance and inter-conversion theories form a

complex group of interrelated, but simple theories based largely on consis-

tencies in the stoichiometry of living systems and the empirical observation

that matter and energy are neither created nor destroyed in biological reac-

tions. These theories are the basis for all the most important predictions that

ecologists have made. For example, such theories allowed Vollenweider,

Dillon, and Cornett to make some very quantitative predictions about the

future of lakes (Chapter IX).

(3) Empirical holistic theories form the biggest and most diverse class of

all. It is less a distinct set than it is one end of a spectrum of all theories. Such

theories include predictions about the performance of an organism based

on its size (Peters 1983), predictions about species number based on evapo-

transpiration (Currie and Paquin 1987, Currie 1991), predictions of litterfall

based on latitude (Bray and Gorham 1964, Lonsdale 1988), and predictions of

bioconcentration factor and effective lethal concentrations based on the rela-

tive solubilities of organic contaminants in water and an organic solvent

(Verschueren 1983, Hermens 1986, McCarty 1987).

Ecologists frequently underestimate the value of empirical theories. Often

we denigrate them as “black box theories” or “engineering”. At worst, we

170 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

ignore them or believe they are not theories at all. This behaviour is self-

defeating because if we were to look over the history of successful branches

of science, we would discover that the most elegant analytical theories began

their lives as humble empiricisms.

(4) Analytical theories lie at the other extreme of this spectrum. The differ-

ence between empirical, holistic theories and analytical theories is that the for-

mer merely predict, whereas the latter also give us the impression we know

why the theories work. An analytical theory predicts and makes us feel at home

by convincing us that we understand the system (Lehman 1986b). Analytical

theories are usually, but not necessarily always, expressed in terms of the sub-

systems of the system. Sometimes it merely invokes fictitious state variables,

such as gravity, magnetism or even animal magnetism. Most scientists aspire

to produce such theories, but there is a time and place for analytical theories.

The history of science shows that they follow empirical, holistic theories.

I see no gain in imposing my views on others, but I can urge that all of us

who teach an approach to science do so explicitly. If our differences are

exposed fairly and conscientiously, students would have a better grasp of both

the strengths and weaknesses of science. Freed of popular misconceptions,

they would be more confident in their ability to perform as well as their teach-

ers, more willing to cast aside theories and constructs that have outlived their

usefulness, and more prepared to accept the responsibility of creating new

knowledge. They might even discover the real joy and freedom of research.

Graduate Education

One should not do science because it offers a socially acceptable career

with adequate pay and interesting fringe benefits, but because something in

one’s nature compels one to do so. Such a student will find graduate school a

reward in itself and the supervisor should ensure that this is possible.

Many scientists remember graduate school as a golden time when they had

more intellectual freedom, more time to reflect, and fewer extraneous cares

than at any other point in their lives. To preserve as much of this experience

as possible, one must settle on a strategy for graduate study that allows stu-

dents the freedom to do science, and is likely to offer them the chance to con-

tinue to do so after graduation.

The importance of role models. One way to develop theories about effec-

tive education is to look for pattern in the training of highly successful scien-

tists. Galton (1875) provided one such pattern in discovering that future sci-

entists often lost a parent. Another of Galton’s discoveries is that leading

scientists were usually trained by other leading scientists and that they regard

171GRADUATE EDUCATION

that experience as critical to their own scientific development. This pattern

has been repeatedly confirmed (Roe 1953, Merton 1968, Zuckerman 1977).

Ann Roe (1953) examined the experience of eminent American scientists

from physics, biology, and the social sciences. There are many interesting

aspects to that study, but I mention only the brief autobiographical sketches of

family life and education given by each scientist. When reading these

sketches, one recognizes a most interesting omission. Not one scientist com-

mented on the type or quality of education they received, except for those

who dismissed their undergraduate days as boring. However, all vividly

remembered one scientist or teacher who had a strong impact on them and

essentially revealed the meaning of science for them. Often, contact with this

mentor was what started the eminent scientists on their successful careers.

Graduate education works because it is one of the last bastions of the

apprentice system. The student learns by working with a master, and great

masters tend to produce great students. If this hypothesis about eminent sci-

entists is valid, the availability of at least one great teacher is critical to an

effective education in science. We need teachers who inspire students so they

will achieve this potential.

Many great scientists fit this model. Claude Bernard was diverted to a

career in experimental medicine when François Magendie recognized his tal-

ent and chose Bernard to be his assistant. Antoine Lavoisier studied geology

under Étienne Cruetard, a founder of the science, and chemistry with Guil-

laume Rouelle, famous throughout Europe for his classification of salts based

on crystal structure. Johannes Kepler was started on his career by Michael

Mastlin, a famous mathematician and astronomer. Darwin walked with

Henslow. I have yet to find a great scientist who did not trace his beginning to

another great scientist. The closest I have come to an exception was Carl Lin-

naeus whose inspiration came from Aristotle through a set of Aristotle’s col-

lected works given to him by his father on his sixth birthday. In ecology, we

need only look at the success of Hutchinson’s school at Yale (Edmondson

1971): their experience with that great master gave almost all of his students

such ability and confidence that they were to define the science of ecology for

a generation or more.

The phenomenon is well described by Helmholtz whose mentor, the great

Johannes Müller, had influenced and inspired him to study physiology:

When one comes in contact with a man of first rank, the entire scale of

one’s intellectual conception is modified for life; contact with such a man

is perhaps the most interesting thing which life may have to offer.

Wise choices in graduate education. Graduate school provides both the

credentials necessary for a life in science and the training needed to use those

172 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

credentials. Once touched by the peculiar passion that drives scientists, one

must go to graduate school. Selecting a school is an important step.

Since I am convinced that the most important element in the university is

the great scientist who is an inspiring teacher, this must be a major determi-

nant in choosing a graduate school. A single such teacher can make up for

years of mediocre undergraduate instruction. And in the apprenticeship of

graduate education, the presence of a great teacher becomes critical. Some

fortunate students may have found this great teacher during their undergrad-

uate years, so their choice should be clear. The others should strive to enter

the graduate environment which is most likely to provide contacts with great

scientists. One must try to work with the very best.

Although the very best masters are more likely to be found at the greatest

institutions, the right one may be found at any university regardless of size.

Institutional fame alone is a poor guide to graduate studies, because every

university has its strengths and weaknesses, and because past glories may not

signal present competence. One would do better to seek active laboratories,

because there is ample evidence that the best labs train disproportionately

more of the future leaders of the science (Zuckerman 1977).

One may also select among institutions and laboratories to find the intel-

lectual leaders within one’s chosen field, but the choice of teacher is more

crucial than the choice of material. Thus if one must chose between a jour-

neyman within one’s precise field of interest and a master in some ancillary

field, the latter is the wiser choice. Great scientists can train people to answer

more than one question, but weak teachers may not even do that.

The scientist who influences the novitiate need not be the head of the lab-

oratory. Indeed, the recognition that great scientists receive often proves to be

a heavy burden, leaving them little time to interact with their associates.

Much of the training in such laboratories may be done by younger researchers

who are themselves destined for future greatness (Zuckerman 1977). Never-

theless, because great scientists often attract, train and work with other

powerful scientists, larger laboratories and working groups are likely better

choices than smaller isolated ones.

Finding the right laboratory is not easy. Since several applicants may com-

pete for the best positions, the student should prepare for that competition

throughout the undergraduate years: by learning about the field, by earning

marks, and by winning fellowships. When the time comes to select a venue

for graduate study, one might begin with a preliminary list of potential

mentors, compiled from suggestions by instructors and fellow students, from

readings and from lectures. Such a list should emphasize the approach of the

prospective supervisor, not the material, because the approach captures the

essence of the laboratory’s science and usually endures longer. Since past sci-

173GRADUATE EDUCATION

entific fame may not ensure adequate future mentorship, the student should

research potential choices on the list thoroughly: read more of the labora-

tory’s published work, correspond with possible supervisors, and discuss the

possibilities with appropriate teachers in the undergraduate program. If pos-

sible, the prospective student should visit the lab, talk both with the potential

supervisors and with their associates, tell the supervisor what is attractive in

the laboratory’s programme, try to determine if the potential supervisor pro-

vides a positive experience for his or her present associates, and find out if

past associates have built on their experience in the lab to develop successful

independent careers.

Researching potential supervisors takes more forethought, time and effort

than most students are willing to commit. Indeed most are caught flat-footed

by any number of deadlines. As a result, prepared students often stand out

from the crowd, but it is a crowd that only the potential supervisor can see.

Since the student cannot gauge the quality of competition, the worst thing the

student can do is to decide against applying to the best laboratories because

he or she feels unworthy. Science requires confidence.

There is now a tendency to hurry the student through graduate school, sup-

posedly to increase the efficiency of education. I have little enthusiasm for

that approach, because it cheats the student of the leisure needed to develop

into an independent scientist. For similar reasons, prospective graduate stu-

dents should not settle too quickly on a topic because the first topic may not

allow exciting discoveries. Worse, it may immerse the student in stultifying

drudgery. However, the student should not take this freedom as licence for

sloth. Science is a demanding discipline and most scientists should expect to

work 60 to 100 hours a week as they develop their scientific capacities, and

for the rest of their lives. In compensation, the work is fun.

The student should try several avenues to isolate a research topic: thought-

fully considering one’s own interests, perusing current “hot topics”, searching

for an original and valid approach, and using the expertise of the supervisor

to vet and sort alternatives. In most cases, the supervisor will play a major

role in selecting an appropriate topic, because such a selection normally

requires more information and expertise than a beginner is likely to have.

Eventually, a good student will surpass the mentor in that area of specializa-

tion, thereby wresting the problem away from the master and making it that

of the student. This is an essential step because it shows that the student has

the confidence required for scientific independence.

Finally, the student will leave the privileged atmosphere of graduate

school and, usually after the respite of a post-doctoral fellowship, look for a

job. A good job in science is the best guarantee available that one will pre-

serve the freedom to express one’s scientific ideas and skills. Such jobs have

174 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

always been scarce. To get one, the student must, of course, be well-trained

and do a piece of good research. The work must also be eye-catching, in the

sense that other scientists perceive the work as contributing to an important

problem. It is for this reason that I suggested the student look to hot topics.

Ideally, the work should also use a novel methodology or approach because

scientists appreciate such originality, but it must not be too new because

some members of selection committees are likely too dull to appreciate real

novelty.

Administrative Advice

To excel, a university must attract and keep people who can inspire a thirst

for science among the students. In Canada, our record for attracting and keep-

ing scientists of calibre is not good. Thomas Henry Huxley applied to the

University of Toronto for a position in zoology, but despite letters of refer-

ence from Charles Darwin and other international scientists, Huxley was

rejected in favour of a local boy. The successful candidate, who happened to

be related to the provincial prime minister, was and remains totally unknown.

Leopold Infeld, a collaborator of Albert Einstein, came to the University of

Toronto for a while, but the university chose neither to build an institute for

theoretical physics around him, nor to defend him when the local press

attacked him as too leftist; he returned to his native Poland (Infeld 1978). Sir

William Osler, who is still famous as an inspiring teacher, left McGill for

Johns Hopkins and ultimately for Britain. McGill has graduated four Nobel

laureates in science since World War II, but all achieved their eminence in the

United States. Our one laureate, Sir Ernest Rutherford, was attracted to Mon-

treal from New Zealand, and eventually left for greener pastures in England.

The brain-drain is not a particularly Canadian problem. Many smaller

countries and institutions are similarly ineffective at retaining intellectual

leaders. Why do we not attract great educators? And why can we not keep

them when we have them? Perhaps we small players neither recognize nor

want greatness. Many of our most promising individuals emigrate to places

where their ambitions can find more scope. And if they had decided to stay

home, we would interpret this as an indication of lesser stature. Since we do

not recognize greatness, we strive for an egalitarian treatment of scientists

and institutions which further insures that no individual or institution will rise

above the others. We live in a self-imposed mediocrity.

The inability of smaller institutions to hold leaders is worsened by the

advantage of great institutions in attracting such people. Merton (1968) has

discussed this phenomenon as a part of what he called “the Matthew effect in

175ADMINISTRATIVE ADVICE

Science”. In the new testament, Saint Matthew wrote, “To him who hath it

shall be given in abundance: from him who hath not it shall be taken

away.” Great institutions attract great scholars, and so grow at the expense of

smaller, less prestigious ones. Moreover, because these great scientists may

inspire one another, the advantage of the great institution continues to grow,

maintaining its preeminence and increasing its dominance.

If this is true, what can we do? I see only one answer. We must become

more elitist. We can never hope to have great scientists in all departments at

all universities. Let us therefore designate one or a few universities to become

the Harvards or Oxfords of Canada, Sweden, Italy and Australia, or of Ohio,

Ontario and Sicily. If we cannot designate whole universities as centres of

excellence, then within universities, we might specify faculties or groups of

departments for special treatment. If this is not possible, then let departments

favour particular research and teaching groups, like limnologists, behav-

iourists, forest ecologists, and neuro-biologists. If even this is not possible, let

us at least select the very best individuals among our scientific applicants.

Too often, we select against the best scientist on the grounds that the teaching

program or sub-disciplinary balance demands a different specialist, or that the

best scientist may not be the most collegial colleague. This choice ensures

mediocrity by sacrificing individual brilliance for the sake of academic

bureaucrats who treasure the equanimity of undergraduate programs and

departmental mix. Equanimity is almost always the antithesis of excellence.

An elitist choice would signal that we have accepted that we cannot teach

all things to all students, and that the value of a university education does not

depend on the number of facts or the breadth of coverage, but on the appreci-

ation of ideas. In science, ideas are theories. Great theories, like other great

ideas, are produced by inspired and dedicated individuals of great creative

vision. If we wish to promote scientific education, we must encourage those

few who can create powerful theories and, by example, train others to do so

in the master-apprentice relationship. Our first priority must be to attract

great individual scientists.

Once we have identified our favourites among universities, faculties,

departments, research groups, and individuals, our next priority is to pour

enough resources into them that we can keep the very best scientists in some

small number of disciplines. We would then have somewhere to send the very

best students — a place where they would have a good chance of encounter-

ing the odd brilliant scientist who might send them on that magical leap from

the world of pedestrian research to great science.

176 AN EDUCATION IN SCIENCE: PRESCRIPTIONS

XII The Questions of Relevance

“The English ... surpass all other nations in snobbish-

ness; our fastidious distaste for the applied sciences

... has played a large part in bringing England to the

position she occupies in the world today.”

Sir Peter Medawar

[The Limits of Science (1984)]

Previous chapters argue that contemplation of science should lead ecological

researchers, and others, to profound changes in the way we do science. If that

happened, we would be obliged to make consistent changes in other areas as

well. For example the previous chapter discussed the possibility of changing

the ways professors teach and students learn. This chapter instead focuses on

the face which science turns to the public. That too must change, if we are to

be honest with our public patrons and so keep their goodwill and support.

What Use is Science to Society?

Society has elected to support science. Politicians and bureaucrats think

research is important. Every year, each industrialized country spends millions

of dollars to pamper its scientists and researchers and to allow them to per-

form as well as they are able. There are several good reasons that this is so.

First, I can agree with Jacques Barzun (1964) that science is indeed a glo-

rious entertainment. It is a tremendous substitute for material consumption to

get us as happily as possible over that uncomfortable period between the cra-

dle and the grave. Moreover, because science is such good entertainment, it

completely occupies a whole class of technically competent, informed, think-

ing people who might otherwise make trouble because they tend to be

socially difficult. In return, society gets some good from the expense in the

vicarious pride that the country produces and supports good scientists, as well

as good writers, singers and athletes.

The entertainment value of science cannot fully explain the generosity of

society. After all, the arts, humanities, and religion offer many of the same

advantages and somewhat more entertainment, yet they enjoy far less sup-

port. Society expects more from its scientists. It expects us to be useful, and

we scientists encourage society to think so. To show that science merits sup-

port, we must show how useful it has proven to be.

There is really only one way that science is of special benefit to society. It

generates theories that let us make predictions and so look into the unknown.

These predictions help us choose courses of action that will lead to the results

society desires. Science thus helps to achieve societal objectives, but it does

not identify or judge these objectives. Many scientists believe they have the

additional duty to direct society, but that duty should be shared among all cit-

izens. Societal directions are set by policy makers who should represent the

whole of society. The only distinguishing characteristic of scientists is their

ability to produce theory.

Much of society is ignorant about the appropriate uses of science, and sci-

entists too rarely recognise any limitations to those uses. Together, scientists

and society have confounded one another with unrealistic claims and expec-

tations. Their mutual uncertainty would be reduced if both sides were more

aware of what science is, of how it differs from applied research and technol-

ogy, and of what it can hope to achieve. This chapter shows that our jobs as

biologists and ecologists would be much easier if we made explicit use of

theory to define our tasks and capacities as scientists. It also suggests that the

utility of ecology is harder to defend because we have not consistently made

use of theory in the past.

Does science differ from applied research and technology? Science has

the job of building and testing theories. For example, Einstein was definitely

acting as a scientist when he developed the relation that

Energy = Mass × Velocity

(25)

A person engaged in science, a scientist, need not contribute directly to the

solution of practical problems. The best the scientist can do in this respect is

to become interested in a body of data about which society is concerned. For

example, an ecologist concerned with the cycling of materials in ecosystems

might elect to study the cycling of PCB, rather than that of sodium or carbon,

because society is concerned about toxic materials in the environment. This

selection of subject matter is not applied research, but merely a diversion of

theoretical interests towards phenomena about which the society is con-

cerned.

Applied research differs from science in that its purpose is not to build or

to test theories, but to exploit potentially useful predictions from existing

theories. The person who deduces from Eq. (25) that any transformation of

matter resulting in a loss of mass would release an enormous amount of

energy, and then searches for such a transformation in the hope of exploiting

178 THE QUESTIONS OF RELEVANCE

the energy released, is an applied researcher. It is this hope, the motivation of

the research, which distinguishes applied from fundamental research.

Technology is the process of putting the results of applied research into

practice as efficiently as possible. To follow my example, once applied

researchers had identified uranium as having the best potential for the trans-

formation of mass into energy and had investigated the general conditions

under which energy release occurs, the technologists took over. They worked

out effective methods of controlling the rate of transformation and of packag-

ing the whole so it could be delivered to an appropriate site. Technology built

the atomic bomb, and got a man on the moon.

The same person can do applied research, pure science and technology,

but at different times. For example, an applied researcher who fails to achieve

the desired ends may suspect that the fault lies with theory, and begin to test

the theory whose predictions were to be exploited. To maintain my distinction

between applied research and science, I claim that this applied researcher has

become a pure scientist. The distinction is necessary to avoid working at

cross-purposes.

A facile objection to this separation is that because one worker can do all

three jobs, there is no reason to distinguish them. I disagree. To hold that no

distinction exists between these activities is like saying that because one can

eat at one time and talk at another, there is no reason to distinguish the pro-

cess of eating from the process of talking. Although eating and talking are

manifestations of a more general process called life, we still find it useful to

distinguish between them. Similarly we can categorize the activities that con-

stitute research, although we may not be able to categorize the individuals

who do them.

A more difficult objection is the problem of what to call an activity that

could be science, or applied research, or technology. For example, an individ-

ual might experiment with the fission of plutonium, not because he or she

cared about bombs or domestic energy supply, but to test the theory repre-

sented in Eq. (25). In that case, the activities that were applied research or

technology in my previous examples would be science. This might seem a

reason to reject the categorization. I choose not to do so because the distinc-

tion helps focus attention on a most important aspect of research that is often

ignored: the motivation for doing it.

Too much research is done for the same reason that a mountain is climbed

(“because it is there”), and too little time is spent questioning the motives for

doing so. We can ask why rational people have chosen to do something, and

we should expect a cogent, meaningful answer. We need to know what goals

are proposed for any particular piece of research so that we can try to deter-

mine the significance of the project and its likelihood of success. This knowl-

179WHAT USE IS SCIENCE TO SOCIETY?

edge would both help direct our research and protect us from the unrealistic

demands of society, the overweening claims by scientists, and the ineffec-

tiveness of undirected research.

Does Science Merit Support?

Up to this point, I have introduced three simple topics that receive too lit-

tle attention from university scientists: the uses of science, the predictive

aspect of theory and the differences among science, applied research and

technology. I have done so because I feel we could be more effective as teach-

ers and scientists. We can improve, but I also believe that we are unlikely to

do so unless we give serious thought to the questions that serve as headings in

this chapter.

My desire to improve is only partly altruistic. Society’s attitude to the uni-

versity scientist is changing. Our image has become tarnished and as a result,

it is likely that our working conditions will become more austere. We could

react to this by screaming at our tormenters, or we could become more useful

and effective, thus earning a better image. I prefer the latter course.

How can we evaluate our science? Obviously any group of professionals

likes to believe that its members are highly competent and without fault. Con-

sequently, I must present evidence for my unflattering opinion of university

science. I will not address the whole field but only a small part, biological

limnology and, by extension, ecology. I will look at our strengths and weak-

nesses, and speculate on procedures we might adopt to make ourselves more

effective.

Many of my views reflect personal experience with limnology in Canada,

and could be dismissed as the major failings of a minor science in a minor

country. To escape that fate, I must establish the relevance of the sample.

When we consider the size of the Canadian population and the relative new-

ness of science in Canada, the contribution of Canadian aquatic ecologists

has been remarkable. For example, data for 1982 to 1992 compiled by the

Institute for Scientific Information of Philadelphia ranks Canada second in

number of citable publications and in number of citations in both aquatic

sciences and ecology/environment. At the individual level, it is very reassur-

ing and comforting to be a Canadian limnologist abroad. Almost everyone

you meet expresses an interest in visiting Canadian limnological laboratories,

and asks about the recent work of several colleagues. Canadian limnology is

widely recognized and respected.

This reputation is well deserved. We owe it, in part, to the classic, great

limnologists of the past such as A. Huntsman, J. R. Dymond, Ronald Hayes,

180 THE QUESTIONS OF RELEVANCE

Donald Rawson, Bill Ricker, Fred Fry and so on, as well as to imports, like

Noel Hynes, Richard Vollenweider, and Dave Schindler. We can also be

proud of the great federal laboratories, The Freshwater Institute and The

Canada Centre for Inland Waters, that are in large part responsible for

keeping our reputation alive. All in all, I am very proud to be a Canadian

limnologist.

Although Canadians have reason to be pleased with our national accom-

plishments in limnology, we have no cause for smugness. Neither Canadian

limnologists nor those of other nations nor ecologists in general have reason

to be pleased when we evaluate our disciplines in relation to others.

Scientists are normally very careful not to evaluate their science relative to

other sciences. Such evaluations are difficult to do, and potentially embar-

rassing. One tool in such comparisons is the analysis of patterns of citation

because citation is one of the few quantitative measures of the impact of a

given field, an individual or a publication. Although interpretations of these

measures are disputed (Garfield 1985, Taubes 1993), I will begin with them,

because I am a quantitative scientist and because alternative indices are even

worse.

An assessment of the scientists. I began to evaluate limnology quite by

chance while leafing through Current Contents, in which Eugene Garfield

(1977a, b, c) had published a series of articles on the 250 most cited scien-

tists. To hit the top of the pops, a scientist then had to receive at least 266 cita-

tions per year (this threshold would now be considerably higher). I was curi-

ous about where Evelyn Hutchinson would appear in this list so I looked him

up. To my horror, I discovered he did not rate! Thinking that I might have

chosen my top limnologist badly, I began to look for others — Thienemann,

Naumann, Birge, Welch and so on. When I again failed, I went through the

entire list looking for an ecologist. Not one had made it. A subsequent rank-

ing for 1984 (Garfield 1986) does include a few ecologists, like MacArthur,

May, and Schoener (McIntosh 1989), but no limnologists. What does this

mean? What does it tell us about ecology in general and limnology in

particular?

First I want to rule out the comforting interpretation that our peer

group is too small to produce enough citations. The International Society

of Limnology now has about 3000 members; at the time of Garfield’s

1977 analysis, the figure was about 2500. If we consider terrestrial and

marine ecologists, we will find at least as many more. Therefore, the

minimum size of our group is 5000 scientists. If each member publishes

only one paper every second year and if each paper has (on average) 20

citations, ecologists would have collectively generated 50 000 citations per

year. In fact, there are more members, the members are more productive,

181DOES SCIENCE MERIT SUPPORT?

and reference lists are larger (Peters 1989). We therefore generate quite

enough citations to put a few ecologists on the first listing of most-cited

scientists. We can rule out the hypothesis that our group is too small to

produce superstars.

This argument does not falsify the hypotheses that large societies generate

more citations or that their leaders are likely to score higher in such compar-

isons. In other words, the presence of one or more leading practitioners

among Garfield’s immortals is no proof that other sciences are strong. They

undoubtedly share shortcomings with ecology, but that does not excuse our

showing.

At the other extreme, I reject the hypothesis that ecology attracts less

capable scientists and consequently that no ecologist is smart enough to

become a superstar (I know some colleagues in cell and molecular biology

who subscribe to this view). Many limnologists chose their field because they

were interested in and good at physics, chemistry and biology, not because

they were too stupid to become physicists or chemists. They found, in lim-

nology, a discipline that would allow them to pursue their trans-disciplinary

interests.

I have a third hypothesis. My hypothesis is that the state of our discipline

makes it impossible for limnology or ecology in general to have superstars.

The problem with ecology is that it is diffuse. It lacks focus. It isn’t going

anywhere. Ecology lacks the paradigmatic theories that identify exceptional

scientists and their exceptional work.

An assessment of the science. Perhaps some readers are still in doubt about

my meaning. If so, I will try to explain myself further by examining the char-

acteristics of a superstar scientific paper. This information is available to us

because Garfield (1977c) also listed the most highly cited papers written by

each of his superstar scientists. When I looked over this list of 250 papers, I

saw that they could be categorized into three main types: papers that describe

new theories of moderate generality, papers that describe unexpected phe-

nomena, and “methods” papers.

A new theory of moderate generality is a theory that makes very clear

predictions about a moderately large body of phenomena. Darwin’s theory

would not do. It is too general, but a less general theory, like the theory of

particulate inheritance, might count. These theories of intermediate gener-

ality help to link more general theories and concepts to theories of lower

generality and to facts. Such theories suggest many new experimental tests

or possible applications. All papers arising from these studies refer to the

paper that described the new theory of moderate generality. One reason

ecology lacks highly cited papers is that large numbers of ecologists do not

agree about what construct of great generality needs to be linked to obser-

182 THE QUESTIONS OF RELEVANCE

vation. Thus there is no place for exciting theories of moderate generality

in ecology.

New unexpected phenomena excite great interest for one of two reasons.

The first is that these observations are inconsistent with a widely accepted

theory. If this is the case, many scientists immediately attempt to falsify the

observations. If this fails, they will attempt to repeat the anomalous observa-

tions and to reconcile facts with theory. All of this work can generate many

papers that refer back to the first discovery of the anomaly.

A second situation in which new unexpected phenomena are important is

the situation that Thomas Kuhn (1962, 1970) described as a crisis. In science,

a crisis exists when a paradigm has ceased to generate soluble problems.

When this happens, leaders in the field converge on certain categories of

anomalous observations. The paper that first directed them to these observa-

tions would be highly cited. The important common feature of both situations

in which new phenomena are interesting is the existence of a generally

accepted theory to identify the norm. The lack of such norms makes it hard to

identify surprising observations in ecology.

The “methods” paper needs no definition. Everyone knows that the most

highly cited papers are methods papers. One of the best known is the 1951

paper by Lowry and co-workers on protein measurement with the folin

phenol reagent. This paper has been cited over 100000 times (to put this in

perspective, the average paper is cited about 6 times). Fewer scientists

recognize that such success is rare, that most methods papers are rejected

or uncited, and that this is especially so in ecology (Jumars 1987). Good

methods papers are hard to do.

The fact that ecologists do not produce famous methods papers is indica-

tive. God knows we have as many methodological problems as any other

group of scientists. For example, environmental toxicology has been held up

for years by our inability to analyze toxicants accurately. In fact, we still lack

acceptable methods for some commonly measured substances, like chloro-

phyll a or nitrogen. Turning the picture around, we discover that many of the

methods we use have been developed by biochemists or chemists. For exam-

ple, all of our popular methods for phosphorus analyses were developed by

others and adopted by us. Why have no ecologists developed famous

methods?

I think the answer is simple. It is very difficult to persist until a new

method is perfected. Because thorough testing takes a great deal of time and

effort, a good methods paper needs strong motivation. A large part of this

motivation is provided by the recognition that the method is absolutely essen-

tial for scientific progress and the knowledge that one’s peers need and will

use the method. In short, when the whole community of scientists recognizes

183DOES SCIENCE MERIT SUPPORT?

that certain measurements must be made, we know the methods are impor-

tant, and we are willing to make the commitment needed to produce a strong

paper about them. This recognition of important methods presupposes the

direction provided by an overriding theory.

Thus in all three classes that I could identify in Garfield’s list of famous

works, writers and users were directed by a theory that identified what is

important. I hypothesize that ecologists and limnologists do not agree about

their paradigmatic theories and therefore have failed to produce famous

papers and highly cited scientists.

Age of citation. We can test this hypothesis further by analyzing the age of

material cited in different disciplines. If a field is flagging, old papers can be

as valuable as new, so their appearance in the literature may be unheralded but

their lifespan should be long. These comparisons should make some

allowance for that spurious modernity which makes us cite the latest redis-

covery of the wheel rather than the scientist who first did the work.

Where progress in science is rapid, worthwhile papers are discovered

and used shortly after they are published. In such a discipline, papers also

go out of date very rapidly. As an example, Fig. 34 compares citation pat-

terns in ecology and biochemistry. It shows that biochemists cite propor-

184 THE QUESTIONS OF RELEVANCE

Fig. 34. The effects of age of papers, in all journals and in just ecological or biochemi-

cal journals, on the rates of citation to those papers

tionately more new papers, so the number of citations per year rises rapidly

to peak at about 3 years, and then falls off. In ecology, the initial response

is slower and less dramatic; citations rise to a low peak at about 5 years, and

then relatively slowly decline. Comparisons among other journals yield sim-

ilar data (Peters 1989, 1991a). This pattern suggests that ecologists do not

immediately recognize exciting papers as important, or are not writing such

papers.

Extent of application. In the past, some colleagues have thought this com-

parison of ecology and biochemistry unfair. They say that biochemistry dif-

fers from ecology because it has a dependent applied science, medicine. This

additional audience for biochemistry leads to more rapid application and high

citation rates. This objection actually gives additional support to my argu-

ment. Society needs an applied science of environmental management. The

reason it does not have one is that we have failed to build the foundation of

predictive theory that applied research and technology require. Therefore, I

repeat that ecology moves slowly because it lacks paradigmatic theories

which would attract citation, direct research and sustain applied research and

technology.

How can ecology merit support? I have sought to describe a situation in

science and tried to minimize the value judgements that arise from evaluation.

To the extent that I succeeded in avoiding these judgements, I have acted like

most other ecologists. We appear unconcerned with our failure to provide

theory.

I find it sad that we do not care. Society is better disposed towards ecolo-

gists than to other academic scientists. The public accepts that we need

powerful ecological science, applied ecological research and ecological

technology. Society is prepared to pay dearly for such research. Regrettably,

ecologists seem to have turned their backs on this opportunity to merit

support. At least one learned ecological society, the American Society of

Limnology and Oceanography, actually voted not to allow applied research

papers space in their journal, Limnology and Oceanography. The Ecological

Society of America has established an applied journal, Ecological Applica-

tions, but at this early stage much of the material appearing there seems as

academic as that in their established journals, Ecology and Ecological

Monographs. This has also been the fate of the British Ecological Society’s

Journal of Applied Ecology.

It seems I cannot help myself. Even when I try to change the topic, I still

end up diagnosing the ecological disease. Ecological science lacks general

theories; worse, ecologists do not recognize that deficiency or the theories of

low generality that they do have. I must complete the metaphor by suggesting

treatment, and that is how I will finish. The cure is simply to begin making

185DOES SCIENCE MERIT SUPPORT?

theories and testing predictions. The first step in this cure is to ask ourselves

questions about how successful we are as scientists:

(1) What do we want to know?

(2) What predictions do current theories make?

(3) How can we improve old theories?

(4) What research is likely to provide new theories?

I do not know how we will answer these questions. I suspect that the last

two are unanswerable because theory improvement requires creative insight.

However, I believe that the exercise of groping for answers will help give

ecologists the directions we presently lack. We will then be in a position to

earn the support of society, to return our patrons’ investment many times

over, and to fulfil our moral obligations to humanity and to nature.

186 THE QUESTIONS OF RELEVANCE

XIII Funding Decisions

“The course I propose for the discovery of sci-

ences is such as leaves but little to the acute-

ness and strengths of wits, but places all wits

and understandings nearly on a level.”

Francis Bacon

[Novum Organum (1621)]

“Quite ordinary people can be good at science.”

Sir Peter Medawar

[The Limits of Science (1984)]

The search for funds, the writing of proposals and the evaluation of grant

requests by our peers are major elements in the lives of most contemporary

scientists. A clear grasp of what science is and what scientists can do is an

indispensable aid in all those processes. This chapter therefore applies

lessons from my contemplation of science to the various facets of grantsman-

ship. It identifies the legitimate expectations one can have of research pro-

posals, discusses the gamble involved in trying to fund scientific creativity,

and warns against some current practices in science. The chapter ends with an

extended analysis of multi-disciplinary team research as an example of how

the granting agencies’ misconceptions about science can make science more

difficult.

The Central Problem for Research Funding

Basically, a grant proposal promises to do a certain set of tasks in return

for a specified sum of money. The problem for the proponent is to describe

future research so that its promise is great. For the panel, the problem is to

determine which of all the promises it reads are most likely to succeed.

One of the first discoveries one makes as a part of peer review is that ecol-

ogists have been largely untouched by the last three hundred years of philos-

ophy: philosophers showed long ago that the applicants cannot possibly keep

many of the promises their applications make. We all need a better grasp of

what research can and cannot do.

Some applicants imply that theories can be produced when required, like

rabbits from a magician’s hat. They promise that if given enough funds, they

will make predictions about phenomena of immediate interest to society and

resolve long-standing questions in science. The continual barrage of promises

raises unjustifiable expectations in the public, administrators and legislators

who need useful answers from scientists.

Other applicants seem to subscribe to the old belief that theories are pro-

duced by a logical process based on data collection, that theories can be ver-

ified by further observations, and that after sufficient verification, they will be

accepted as true natural laws. This set of beliefs assumes that if we make the

correct observations carefully and thoroughly, the facts will logically and

inevitably lead us to discover true theory. Consequently, applicants believe

that if they can promise to make new observations correctly, then they will

also be able to derive, from these observations, a new theory that would gen-

erate predictions needed by society. David Hume, building on the earlier

work of Locke, Berkeley and others, showed in the middle of the 18th century

that this ancient belief is false.

We now know (to the extent that we can know anything) that a body of

specific facts can never lead logically to more general statements, that logic

cannot lead us to discover a new theory. Medawar (1984) called this idea the

law of conservation of information: “No process of logical reasoning — no

mere act of mind or computer-programmable operation can enlarge the infor-

mation content of the axioms and premises or observations from which it

proceeds.” Instead, any body of facts can give rise to an infinite series of dif-

ferent theories (Chapter I). The competing theories must subsequently be

winnowed and selected by scientific tests.

Scientific theories are a product of an inspired human mind via a process

we neither understand nor control. We cannot promise to be inspired, and for

that reason, scientists cannot design a project that is sure to produce a theory.

Since no one can promise to be inspired, grant reviewers must be suspicious

of any proposal built around an attempt to create a theory. Yet any granting

panel finds application after application that proposes to do just this. Some-

times these proposals even merit funding.

Reasonable expectations from research. Scientists cannot promise to

create a theory, but they can undertake other aspects of research where the

product is fairly certain. Most of these are premised on the prior existence of

some theory, because scientists use accepted theories as paradigms to direct

their research effort. In the absence of theory, ecologists lack direction to do

anything, and research flounders. For example, I believe that the current

188 FUNDING DECISIONS

drifting of ecology reflects the non-existence of the theories ecologists want

and their unwillingness to recognize the theories they have. The goal of this

section is to show how theory structures research and research proposals,

and its motive is to further stress the need for theory in everything scientists

do.

Theory testing. If a theory is any good, it specifies certain observations as

more likely to be observed under given conditions, and others as improbable.

Our grant proposals can promise to test these predictions. A scientist can

make this promise because the test merely involves gathering data specified

in the theory. In this case, the reviewer can expect a clear exposition of the

theory, the logical derivation of deductions from that theory, a statement of

the observations that will be made, specification of what observations would

be inconsistent with the theory, a description of the methods that will be used

to make them, and a statement of the accuracy with which they will be made.

If one or more of the specified, improbable events occurs in a series of tests,

we are likely to reject the theory. If a predicted event occurs, our faith in that

theory becomes stronger than our faith in competing theories. Theory testing

is one scientific activity from which we can expect results.

Since I have repeatedly charged that ecological theories are flawed, unpre-

dictive, unrecognized or non-existent, theory testing may seem irrelevant to

ecology. This need not be so. All that is required is that the proponents elab-

orate the theory themselves before approaching the granting agency. In other

words, we must think about what we are going to do before we do it. This is

not a new paradigm for ecological research, because theory creation has

always been an individual effort, but it does require that the proponent

describe the theoretical prototype and render it interesting to the granting

panel. It also requires that the panel and agency recognize the importance of

funding research that is based on theory, even when the community cannot

agree which theories constitute its paradigms.

Applied research. The preceding chapter defined applied research as a

search for the potentially useful predictions of existing scientific theories.

Scientists can justifiably propose to do an applied research project because, as

I have defined it, applied research does not commit us to the production of

new theory. Instead applied research tests existing theory within the limited

framework of application to socially interesting problems. Neither are we

committed to succeed if the existing theory is wrong.

Technology. Chapter XII also defined technology as the process of extract-

ing maximal benefits from the successes of applied research. This definition

does not preclude the possibility of technological advance on its own nor does

it deny that at times science has developed in the wake of technological

advance. However, I am concerned with designing projects in ecology and in

189THE CENTRAL PROBLEM FOR RESEARCH FUNDING

that field, I believe technological projects will largely exploit the results of

applied research. This again is suitable material for a project, because we do

not have to invent new theories to succeed in technology. We merely have to

find the best ways of applying those that already exist.

Surveillance monitoring. Monitoring involves the routine measurement

of a set of predetermined variables. In surveillance monitoring, the variables

to be measured are selected because they give a sensitive measure of the

state of the system at minimum cost. This process of assessment should not

be confused with research monitoring whose purpose is to discover relation-

ships among the monitored variables, and so to develop new patterns and

generalities.

Programs of surveillance monitoring require theory, but are not intended

to test those theories. They involve simple fact-gathering and can therefore

promise to deliver specified results (tables of measured values) within a spec-

ified time. These facts are empty by themselves, but the collection may be

useful, because these facts may be used as “predictors” or “independent vari-

ables” in existing theories.

For example, mussel-watch programmes to detect phytotoxins in commer-

cial mussels (Mytilus edulis) are a form of surveillance monitoring. In

Canada, when ambient levels of toxin in commercial mussels reach the criti-

cal value of 20 µg l

–1

, potentially contaminated shellfish are kept from market

(Novaczek et al. 1992). Surveillance monitoring is needed because no

accepted theory predicts phytotoxin concentration. The programme is still

derived from theory, because only a theory can associate a given toxin level in

shellfish with the poisoning of human consumers. Nevertheless, the monitor-

ing programme is a form of technology not a test of theory, because we do not

wait to see if the poisoning would actually occur. In other words, the theory is

not tested, it simply directs sampling.

Surveillance monitoring is normally undertaken by consulting firms or

government agencies, not by scientists. If possible, a programme monitors

“primary variables”, those that are of greatest interest to the society. For

example, in eutrophication monitoring, primary variables may be greenness

of the water, fish yield, water taste and odour. Since the primary variables are

not always easy to measure — greenness varies in space and time, fish catch

is influenced by human whims and accidents, taste and odour are hard to

quantify — many monitoring programmes focus on “secondary variables”.

Secondary variables are related to the primary variables by theory, but are

more easily measured (“simplifying secondary variables”: e.g. Secchi disc

depth), vary less (“integrating secondary variables”: e.g. total phosphorus

concentration, hypolimnetic oxygen content) or warn us that the primary

variables that characterize the system are likely to change (“causal secondary

190 FUNDING DECISIONS

variables”: e.g. the number of permits issued for logging or building in the

catchment). There is also place for “confounding variables”, like temperature

or solar radiation, that might obscure trends in the primary and secondary

variables.

Monitoring programmes begin with a crucial decision about what should

be measured, and any proposal for surveillance monitoring must include a

reasoned defense of the variables selected. Since the only acceptable defense

for surveillance is that the variables function in a theory to tell us something

about the primary variables of interest, proposals for surveillance monitoring

must specify the relevant theories.

Since ecology recognizes few relevant theories, many programmes of

surveillance monitoring have not been well defined. As a result, they end in

indefensibly large collections of almost whimsically selected variables. For

example, I was once involved in developing a strategy to monitor eutrophica-

tion in the Great Lakes. As part of this process, three authoritative lists of

potential variables were developed: one from the OECD eutrophication mon-

itoring programme, one from G. Fred Lee, and one from Jack Vallentyne.

These lists (Table 18, overleaf) each identify between 9 and 27 essential vari-

ables, and together include a total of 38 characteristics. The types of variables

considered essential also differed. OECD listed a series of anions and cations,

whereas Lee and Vallentyne ignored them all. Only Lee considered the vari-

ous forms of phosphorus and nitrogen to be essential, and only Vallentyne

recommended any measurements involving benthos or sediments. One may

conclude that different authorities used different criteria to compile their lists,

but these criteria were not made explicit.

The clearest implication of the discordance among the lists in Table 18 is

that the more opinions sought, the more variables will be considered essen-

tial. Surveillance monitoring risks a thoughtless accretion of variables, and

this is especially likely if the programme is developed by a committee. The

only protection for the proponent and for the reviewer is to insist that all mon-

itored variables be tied explicitly and tightly to theory.

How to gamble with research funds. Avenues of research that confi-

dently promise scientific advance are premised on the existence of theory. For

me, such ecological research is exciting because such a programme must con-

tain a rare treasure, testable ecological theory. In contrast, research that is not

premised on theory is almost indefensible.

Because ecology seems to lack theory, but obviously abounds with impor-

tant fundamental and applied problems, scientists often propose to create new

theory to address those problems. Any such proposal is a gamble, and if the

reviewers and the agency administrators decide to fund such a proposal, they

are gambling with research funds. The question I address in this section con-

191THE CENTRAL PROBLEM FOR RESEARCH FUNDING

192 FUNDING DECISIONS

OECD Lee Vallentyne

Physical variables

Temperature

*** ***

Conductivity

*** ***

Water colour

***

Turbidity

Secchi disc

*** ***

Solar radiation

***

Chemical variables

*** ***

Dissolved O

*** *** *

Total P

*** ***

Soluble P

***

Soluble reactive P

***

Total N

***

Nitrate

***

Ammonia

***

Organic N

***

SiO

*** ***

Alkalinity

*** ***

Acidity

***

Total Fe

***

Trace elements

Nutrient load

***

Biological variables

Chlorophyll a

*** *** ***

Particulate organic C

***

Primary production

***

Algal dominants

*** ***

Algal genera

* ***

Zooplankton counts

* ***

Benthic invertebrates

***

Sediment cores for:

Pollen

***

Diatoms

***

Invertebrates

***

Table 18. Variables thought to be essential (

***

) or desirable (

) measurements in a pro-

gramme to monitor eutrophication of lakes, according to three authorities in the early to

mid-1970’s

cerns the odds of the gamble. We know that a new theory cannot be guaran-

teed, but we can shorten the odds in its favour.

Empirical theory. When no brilliant insights are available, one way to

shorten the odds against theoretical success is to develop the simplest kind of

theory. These are empirical, interpolative or correlative theories, and are

based on the identification, analysis and description of naturally occurring

patterns in phenomena of interest: identify the variable of interest, describe

the distribution of its values, and perhaps, explain some of this variation sta-

tistically by reference to other variables. This has been the universal path to

theory in other sciences and is the one which granting agencies should pref-

erentially support.

If the identification of appropriate dependent or independent variables

seems a challenge, there are ways to identify likely possibilities. For example,

one can test the applicability of an existing theory beyond established

limits. We might extrapolate a regression beyond the data base on which it

was built, as Dillon and Rigler (1974a) developed a general phosphorus-

chlorophyll regression by applying Sakamoto’s (1966) relation to non-

Japanese lakes. Or we might attempt to adapt a theory built for one type of

system to another type, as Smith et al. (1984) showed that phosphorus-

chlorophyll response models developed for temperate lakes also apply in the

sub-Arctic.

Another way to increase the likelihood of success in theory-building is to

exploit possible homologies to existing theories. For example, one can be rea-

sonably confident that most physiological rates will be affected by body size

(Peters 1983, Calder 1984), so as yet uncorrelated autecological processes,

like the rate of uptake of organic contaminants or the time to die from expo-

sure to heavy metals, are likely to be predictable from body size. Because the

effects of size are so conservative (Peters 1983, Calder 1984) we can even

hypothesize that the exponents will be 0.75 for individual rates of uptake and

0.25 for physiological times. The homology can be less close: the widespread

occurrence of resource limitation suggests that successful theories to predict

biomass might well use resource level as a predictor (Peters 1991a); similarly,

Keddy (1989) posits, on the basis of a small series of comparisons, that com-

petitive relations will be most easily predicted by differences in competitor

size.

The characteristic of all these relations and patterns is that they can be

elaborated as concrete, testable theories with only a small amount of thought.

Pattern identification is sufficiently easy that a rudimentary theory can be

expected as part of the grant proposal, perhaps based on preliminary results or

literature survey. If ecologists were satisfied with simple patterns as theories,

we would recognize that our science already includes a vast corpus of theory

193THE CENTRAL PROBLEM FOR RESEARCH FUNDING

and potential theory. If we recognized these relations for what they are, we

would soon be led to theory-testing, the soundest basis for research proposals.

Research monitoring. At times, scientists may propose surveillance moni-

toring, but they are usually interested in more than simply gathering facts.

They may believe that the facts will provide inspiration for a new theory; or

they may want to make other measurements that involve little expense over

and above the cost of surveillance. Scientists often wish to collect facts that

were not previously known because they have a gut feeling those facts will be

important, yet the only way they can afford to play their hunch is under the

guise of surveillance monitoring. Such a proposal should be seriously consid-

ered, because the end result can be a more efficient use of research funds, but

the lure of economy should not obscure the fact that this type of work

promises to create theory. Research monitoring must be treated with the scep-

ticism that risky research deserves.

Explanatory theory. There are also ways to increase the odds against

creating theory. The most difficult thing a scientist can do is to develop a new

explanatory theory, and the more general the theory the harder the task.

Regrettably, the majority of ecologists would not be satisfied by seeking pat-

terns in nature. They yearn to develop general, explanatory theories, and by

trying to do so, they make their tasks vastly more difficult.

Because the demands of creating general explanatory theory are great,

such theories are exceptionally rare. The few people who succeeded are

revered as geniuses, like Newton, Einstein, Mendel and Darwin. Perhaps it is

significant that in these particular cases, no proposal was written and the

work was not publicly funded. Indeed, proposals to develop theories of high

generality rarely come to granting agencies, and when they do, they are usu-

ally not funded. The gamble is too large and the pay-off too uncertain.

Science benefits immensely from genius, but researchers of such quality

are too rare to be the basis of science policy. Heroes are not models for

the common-or-garden variety of research proposal. Administrators since

Francis Bacon (Eiseley 1973) have recognized that science policy must be

designed for the best of the common scientists. The agencies hope to recog-

nize and pamper genius if it appears, but they cannot found a policy premised

on the existence of genius. Perhaps the best we can expect is enough funding

for our leading scientists that the select few will find both the freedom and

ability to create in this heroic sense.

Some realities of ecological research. Effective research can be designed

to test an existing theory, to collect data so a theory may be applied, or to use

existing theory in applied research and technology. All of these projects are

premised on the existence of theory. We must also accept that, although no

project can be designed to produce a new theory, we must find ways to fund

194 FUNDING DECISIONS

scientists in the hope that some will succeed in creating a theory anyway.

However, much of what grant applicants propose does not fit any of these

research strategies.

Many scientists try to show how good existing theories are, and their pro-

posals are therefore designed to corroborate, not test. These researchers are

doing normal science (Kuhn 1962, 1970). Some ecological proposals adopt a

similar strategy, even in the absence of theories. They focus on a topic that

interests some sub-component of ecology (the 1991 index issue of The Amer-

ican Naturalist suggests these topics might include, among others, altruism,

sex ratios, density dependence, food web connectivity, patch selection, poly-

gyny, and philopatry) and strive to interpret associated phenomena in terms of

the concepts and theories of their sub-subdiscipline. This methodology

recalls Aristotle’s search for circles in nature. Most such work is usually con-

firmatory and therefore serves to entrench ideas in the sub-subdiscipline.

Such studies are among the least worthy of support. They strive to defend the

status quo, rather than to improve the science.

The Dream of Multi-Disciplinary Environmental Science

Granting agencies have a necessarily close relation to the scientists they

support. As a result, the proponents’ misconceptions about the nature of ecol-

ogy reappear among reviewers and agency representatives. However, because

the agencies are so powerful in shaping science, the misconceptions of their

agents can be particularly dangerous. Given that science continues to flour-

ish, such agencies more or less succeed in their mandate, but whether this

success is because of their interference or in spite of it is usually hard to

judge.

Sometimes, agency initiatives are misplaced. One example of the latter

is the decision to encourage multi-disciplinary research in environmental

science. This initiative reveals a profound failure to appreciate the nature of

science. Yet similar initiatives have been made by most agencies around the

world.

The advantages of team research. I intend to criticize the emphasis on

scientific research by multi-disciplinary teams as counter-productive in ecol-

ogy, so let me begin by stressing that I am not criticizing team research in

general, teams of researchers, or multi-disciplinary approaches to applied

research and technology.

There are many projects for which teams are essential, and even more for

which teams have proven useful and effective. Teams of researchers provide

an economy of scale; two researchers may need no more spectrophotometers,

195THE DREAM OF MULTI-DISCIPLINARY ENVIRONMENTAL SCIENCE

scintillation counters, or chromatographs than one. Sympathetic colleagues

provide support in ways ranging from helping to move the furniture to tem-

pering a personal crisis in one member of the group. Such colleagues, work-

ing on more-or-less related fields, represent informal teams and are invalu-

able as sources of ideas, criticism, and information. I believe too that we

should promote collegial teams so they become centres of excellence, not

because team research is better than individual research or because teams are

more productive than individuals (they are not; Cohen 1991), but because

teams provide a context within which individual scientists are more likely to

flourish (Chapter XI). It is appropriate to encourage research teams, provided

this encouragement does not discourage the single researchers who have

always been the source of most of the new ideas in science.

More coordinated teams are necessary when a single scientist is unable to

test the predictions of existing theories, perhaps because the tests require too

many data collected over too short an interval or too vast a scale. Such prob-

lems must be addressed by team research, but the teams need not be multi-

disciplinary. Indeed, the need for teams of workers who are interested in

addressing the same problem would seem more likely to arise in single disci-

plines with strong central theories. Such theories will attract people to test the

theory the group holds in common. Under this scenario, the requirement for

team research is generated by the science. A funding agency should have

policies in place to accommodate team research proposals as they arise, but

this is very different from the current inclination to impose team research on

sciences which are not ready for them.

Multi-disciplinary teams have repeatedly demonstrated their utility in

applied research and technology. The Manhattan project and NASA are

among the best examples. In those cases, the scientific problems were largely

solved when the team was formed, but immense challenges remained in

application and technology. The basic problem was to construct a mechanism

along established principles that could perform a single well-specified job.

Multi-disciplinary teams function well in attacking such questions. The

mechanism can be reduced to its parts, farmed out among different experts for

solution, and the many parts eventually assembled as the whole machine. The

machine is then tested to see if the assemblage works. If some parts fail, they

can be redeveloped by the appropriate teams. In summary, the success of

multi-disciplinary projects demonstrates the advantages of the guiding theo-

retical structure in mature sciences, of the greater financial efficiency and

camaraderie in teams of researchers, and of a specified goal in applied

research.

The problems of multi-disciplinary research in ecology. I think it is fair

to say that, although scientists need to be continually reminded of their short-

196 FUNDING DECISIONS

comings, some of us ecologists have been bitterly aware of ours for decades.

We have tried to remedy the problem. Our most common response was prob-

ably to ask for more money, but another common response was to form multi-

disciplinary teams to attack the problem.

Before I begin to tell my tale I must carefully define the type of ecologi-

cal question that I am addressing. There are many types of ecological re-

search, and I am discussing only one, the hardest and the most important.

When we really run into trouble and where we have had the poorest record

of success is in trying to forecast the effects of human disturbance on any

ecosystem. The question we almost always fail to answer is “What will

happen if...?” A good example of this type of question is the request for an

impact statement: What will happen to the organisms in a given stream if a

dam is built across it? or What will happen if a factory discharges its wastes

into the stream?

Ecologists hailed the multi-disciplinary approach as a panacea for such

questions. Now we have had enough experience to ask if it has lived up to

expectation. I suggest that the multi-disciplinary approach has not been as

successful as we hoped and that there are two reasons for its failure. First,

these questions ask us to predict in areas where we lack explicit theory, and

second they require that we use theories from many different scientific disci-

plines. Neither difficulty is addressed well by research teams.

Our failure to foresee environmental problems. I have said that we have

proven unsuccessful at ecological forecasting, but I should explain myself.

What I mean is that none of our major environmental problems was pre-

dicted. Instead of warning society that a problem would develop, ecologists

have always had to tell society that a problem has developed. Here are a few

examples.

(1) The eutrophication of our inland waters was documented, not pre-

dicted. Many of our lakes had already turned green at the surface and anaero-

bic at the bottom long before we decided whether phosphorus, nitrogen or

carbon was the element limiting production in lakes.

(2) We condoned the use of DDT to control insect pests without predicting

its bio-accumulation and bio-concentration, or its harmful effects on non-

target species. We discovered the danger of DDT only when it had already

driven several species towards extinction.

(3) We did not predict the accumulation of contaminants, like mercury or

PCB’s, in freshwater fishes. We discovered it only after contaminants had

concentrated to dangerous levels.

(4) While ecologists in Canada were studying the problem of acidification

near the nickel smelters at Sudbury, Ontario, just as they had a generation

before at the Trail smelter in British Columbia, acid precipitation from coal-

197THE DREAM OF MULTI-DISCIPLINARY ENVIRONMENTAL SCIENCE

fuelled generating plants all over eastern North America was quietly acidify-

ing thousands of lakes from New York and Ontario through Québec to New

Brunswick.

In each of these examples, ecologists performed a useful service to soci-

ety, because we discovered the problem. However, in every case we failed to

predict the problem before it arose. Since predictions arise from theories, we

could only forecast such problems if we had a theory of ecosystem response.

If no such theories exist, the most important task for concerned ecologists

must be the creation of pertinent theories.

The scientific activity for which team research is least appropriate is the

creation of new theory. This step depends on inspiration, and inspiration

occurs inside a single human mind. A team cannot undertake to create a new

theory. Indeed, since teams often act like committees, they may discourage

creativity and new directions in research, by striving for consensus. Until

ecology has theories that are general enough to interest many researchers,

team research in ecology will largely be premature.

A false solution. The second reason that environmental forecasts are diffi-

cult is that the required general theory will almost always derive from exist-

ing theories of lesser generality from several scientific disciplines. The gen-

eral theory can then be called multi-disciplinary. The flaw in our approach to

such problems is that we assumed that the development of such theories

required multi-disciplinary teams of uni-disciplinary individuals. The multi-

disciplinary approach to ecology failed, as I think it had to fail, because that

central assumption was erroneous.

We have very good reasons for thinking that progress in environmental

science will be slow if we work within the boundaries of the traditional disci-

plines. Environmental problems never attended university, and therefore do

not respect the conventional compartmentalization of scientific knowledge.

For example, to predict the distribution and effects of air-borne contaminants,

we probably need knowledge from chemical engineering, meteorology, atmo-

spheric physics, phase, surface and inorganic chemistry, botany, soil science,

hydrology, limnology, biochemistry, ecology and so on. Our mistake arises

when we extend this argument to scientists and argue that to solve multi-

disciplinary problems, we must assemble multi-disciplinary teams. That

response was and is counter-productive.

Since we need new theories, we must depend on the individual scientist,

and since the problems transcend conventional disciplines, we need individ-

ual scientists whose training and interests are similarly unconstrained. What

we really need to solve such problems is a new breed of scientists, single

“trans-disciplinary” creators whose breadth is such that they can cross tradi-

tional disciplinary boundaries.

198 FUNDING DECISIONS

The time-honoured solution. We have failed to produce predictive theo-

ries, and the institution of multi-disciplinary research teams has contributed

to this failure. What is the alternative? To find this alternative, and to discover

the flaw in the multi-disciplinary approach, I suggest you examine very care-

fully the history of the branch of science that you know best. When you do

this, you will discover that major scientific progress has always taken place

along a very well-defined pathway:

(1) Identify the class of systems under study.

(2) Observe the behaviour of these systems intact.

(3) Discover pattern and quantify it as empirical theory.

(4) Study the system components, probably by mechanistic dissection.

(5) Replace empirical theory with explanatory theory.

The important point for this discussion is that if successful sciences stud-

ied isolated components of their system at all, they did so only after they had

achieved a theory. Successful scientists discover the regularities of their sys-

tem before they try to explain them. Reductionist methods are used only in

step 4 where they provide inspiration for step 5.

I should digress momentarily to say that although I may appear to be

taking a hard line, I am actually middle-of-the-road. There are very strong

arguments leading to the conclusion that it is never appropriate to study iso-

lated subsystems (Peters 1991a), unless it is the behaviour of isolated sub-

systems that we want to predict. I went into these arguments in Chapter VII,

but here I have taken a weaker position that is justified on historical grounds

only.

What strategy is appropriate to ecology? Earlier I gave examples of our

inability to predict environmental problems. We discovered them after the

fact. This suggests to me that environmental science is at a very early stage. It

has not yet produced an adequate set of empirical theories. If my conclusion

is correct, we should concentrate our efforts at steps 1 and 2 in the sequence.

We should attempt to define and classify the systems about which we need

predictions. When this is done, we should study the behaviour of these sys-

tems. Perhaps then, we will produce the empirical patterns and theories

required for further scientific advance.

Where does the multi-disciplinary approach lead? With these guidelines

in mind let us now think about the multi-disciplinary team, and ask ourselves

how it will approach multi-disciplinary problems. Experience shows that the

multi-disciplinary group quickly decides to dissect the system and to study its

fragments by the techniques appropriate to each discipline. For the physicist

or chemist, this is the approach to which they have been conditioned. They

come from advanced disciplines that are replete with highly explanatory

199THE DREAM OF MULTI-DISCIPLINARY ENVIRONMENTAL SCIENCE

theories. In these disciplines, the tradition of dissecting the system into

smaller and smaller fragments is well established. They succeed to the extent

that commonly held, general theories keep the whole enterprise together.

The ecologist in the team could be expected to act differently because gen-

eral theories in ecology are almost non-existent. However, as I have argued

previously, most ecologists reject the lessons of history. They have decided

that because their systems are more complex than those studied by other sci-

ences, ecologists must reverse the normal process of science. They begin at

step 4. They are methodological reductionists, looking for an explanatory

theory before they have discovered the regularities that need to be explained.

Because the members of the multi-disciplinary team tend to reductionism

so does the team. In the extreme case, each member engages in reductionist

studies aimed at furthering development of his or her discipline rather than in

developing new theories for ecology.

This is the flaw in the multi-disciplinary approach.

Where do we go from here? Since I cannot end on this depressing note,

I will suggest very briefly that there is a viable alternative to the multi-

disciplinary approach. To develop an alternative, I think we must first accept

that ecology and limnology are disciplines in their own right. They depend on

theories of chemistry, physics and biology, but they are not merely an aggre-

gation of these. Because the ecological sciences must predict about a differ-

ent class of systems, their problems are different from the problems of the

chemist, physicist and biologist.

Ecological solutions require a trans-disciplinary generation of scientists.

We must learn to use the theories of the traditional academic disciplines as

tools and to stop making their theories the object of our research. In addition,

we must learn how to train new scientists as ecologists or environmentalists.

They must realize that they are not physicists or biologists who were not for-

tunate enough to get a job in real science. They are scientists with primary

allegiance to a different natural system. In other words, they must be trained

to see their speciality as a science in its own right, not just as an applied

appendage of some “real” science.

200 FUNDING DECISIONS

XIV Darwin and Evolutionary Science

“The amount of assumption and reasoning in a

vicious circle involved in these [current evolu-

tionary theories] renders it certain that none of

them can long survive.”

Sir William Dawson

[Modern Ideas of Evolution (1890)]

In this chapter, I want to show how an appreciation of science can help to

interpret the history of our discipline, and conversely, how a knowledge of

our history can help us to understand our science. I will begin by describing

how Darwin’s observations on the Galapagos may have allowed him to fal-

sify competing theories of the origin of the species and so to develop his own

theory based on that experience. My idea may be wrong, but I find that it

makes Darwin and the Galapagos more interesting and vital than no idea at

all. Having given Darwin some of his due as a scientist, I will then examine

some critics of Darwin’s theory to see if they are equally robust. The purpose

of the exercise is to show that a grasp of the nature of science can clarify the

context of our work.

Like other biologists, I have always admired Charles Darwin. I admire

him because he dedicated decades of his life to an articulated series of stud-

ies involving different methods and organisms, all directed to the develop-

ment of a coherent vision of the living world, because his experimental work

was carefully considered and carefully done, because he saw further than the

rest of us (Ghiselin 1969) and because he succeeded in science without aban-

doning either his family or his community. Nevertheless, I am dismayed

because he is rarely treated with the respect and dignity that a scientist of his

stature has earned.

Darwin is either deified by his followers or vilified by his foes. Both

extremes are inappropriate. Darwin was one of the greatest scientists of all

time, and his ideas should be treated accordingly. We do him greatest honour

when we treat his ideas as instances of contemporary science, open to test,

rejection and revision. If we elevate his writings to the level of sacred texts,

we do him and his science as much insult as those who reject his views as

inconsistent with a literal reading of the Bible. Science needs no dogma.

Darwin on the Galapagos

Biologists all know that while visiting this tiny archipelago over 150 years

ago, Darwin made the observations that sent him reluctantly and inevitably

along a path he had known about but previously avoided. The result of his

subsequent labours was one of the few theoretical revolutions that biology

has ever experienced. It was a revolution that changed our world view dra-

matically and irreversibly. The effects spread like a chain reaction, first

through biology by precipitating new lines of research in comparative

anatomy, comparative embryology, population genetics, etc. Subsequently,

history, economics, ethics, metaphysics, sociology and even art and poetry

were changed beyond recognition by new attitudes engendered by the theory

of evolution by natural selection. All this started on Darwin’s trip to the Gala-

pagos!

The observations Darwin made must have been remarkable. But what

were they? After asking yourself, ask some colleagues to see if they know

what observations he made. If you and your colleagues are as well informed

as I was when I first asked this question, the answers will be disappointing:

“Didn’t he observe finches with different beaks adapted to different foods?”,

or, “He saw the results of finches and turtles evolving to adapt themselves to

new environments.” Although such answers seem satisfactory on first inspec-

tion, a little thought shows us that they are not. If Darwin merely saw that the

body parts of different animals were well suited to a function and to the habits

of those animals he saw nothing new. No one in his time, or before, expected

a lion to live on grass or a cow to be a carnivore. To tell us that Darwin saw

the results of evolution through natural selection on the Galapagos is to

phrase the answer in terms that were meaningless before his theory existed

and to imply that the results of natural selection were not to be seen elsewhere

in the world.

If our standard answers are unsatisfactory, where can we go to find better

ones? Years of conditioning as students and teachers will probably send us to

introductory biology texts. Here we will find more disappointment. By and

large the texts give answers just like ours, although more detailed and accom-

panied by attractive illustrations. At least our own ignorance has been

explained. The answer to my question was unknown when the text-books

from which we learned our biology were written.

Why, then, were these answers either forgotten or undiscovered? The first

reason I suggest is that we mostly subscribe to the old-fashioned “truth theory

of science”: all current theories are true, all discarded theories are false. And

because of this we shy away from serious discussion of rejected theories.

Consequently we were not taught, are not really interested in, and do not

202 DARWIN AND EVOLUTIONARY SCIENCE

teach rejected theories or the reasons theories were rejected. Therefore the

observations that led to the rejection of a theory are not significant to us. In

this particular case however, there is another source of our difficulty and that

is that Darwin never said what observations influenced him while on the

Galapagos. All he gave were some pretty broad hints in his diary from the

voyage of the ‘Beagle’.

Because I believe the events leading up to the rejection of a theory are

important in helping us to understand our science I will try to interpret

Darwin’s hints. To begin, we must know what theory or theories existed in

Darwin’s time. The old biblical theory of creation at a single time and place

had been long abandoned, and two alternatives were competing for domi-

nance. One, proposed by Lamarck, said that God created life with a built-in

drive towards perfection. This force alone caused slow evolution, but the pro-

cess was accelerated and often diverted by the environment. Thus, similar

environments would produce similar species. The competing theory was

proposed by Georges Cuvier, and Charles Darwin encountered a modified

version of this theory in Lyell’s geology text which he read during the

voyage. This theory explained the known facts about fossils and animal dis-

tribution by postulating different centres and times of creation. It did not

allow for production of new species by slow evolutionary change.

Now let us consider the Galapagos in the light of these two conflicting

theories that formed Darwin’s world view. He saw a group of islands that

were obviously of volcanic origin and, unlike South America, obviously very

recent because the lava streams showed no signs of erosion. He saw birds and

plants that were peculiar to the islands, but similar to species he had seen in

South America. Even more surprisingly, the species were unlike anything he

had seen on the Cape Verde islands near Africa, despite the similar climates

and geologies of the two archipelagoes.

Can we explain these facts in the light of Lyell’s or Lamarck’s theo-

ries? According to Lyell, the organisms of the Galapagos, being endemic,

must have been created there. Since South America is ancient and the

Galapagos were recent, they must have been populated by two separate

acts of creation widely separated in time. If so, why would the Author of

Nature, who creates species to suit the conditions they will encounter,

create species for the Galapagos on the South American rather than the

Cape Verde plan? The facts just do not make sense in relation to the the-

ory and to our image of the Creator. Then let us follow Lamarck and see

what he would predict if the Galapagos had been populated by migrants

from South America that subsequently evolved to suit the conditions they

found on the Galapagos. This is where the finches become relevant, be-

cause Darwin had seen one, and only one, species of finch living under

203DARWIN ON THE GALAPAGOS

incredibly diverse conditions all along the west coast of South America.

Clearly this must have been the species that first colonized the Galapagos

where it gave rise to eleven different species. But if species evolved to

adapt to the conditions they encounter, why was there one species in

South America and eleven in the climatically and geologically uniform

Galapagos? Surely Lamarck’s theory would have predicted just the oppo-

site!

Now that we know the theories, we can see that the facts of the Galapagos

seemed to contradict them. Of course, the facts did not force Darwin to pos-

tulate his theory, but they did send him on a quest that led eventually to his

theory. How his thinking was led to ideas about natural selection is quite a

different story that has nothing to do with the Galapagos. In fact, because that

involved a creative step it may have no rational explanation at all, whereas the

rejection of existing theories on the evidence is simply good science by a

great scientist.

Critics of Darwin

McGill University, where I am writing these notes, is well known in evo-

lutionary circles as one of the last outposts of anti-evolutionary thinking. The

famous anti-Darwinist that gave us this reputation was William Dawson, prin-

cipal of McGill from 1855 to 1897.

Dawson was a Nova Scotian who studied geology at the University of

Edinburgh where he put up with the dull lectures much more willingly

than Darwin. On return to Canada he began to publish geological articles

and in 1855, his first book, Acadian Geology, was published. The McGill

University Dawson took over that year was very different from the one

where I work. It had 16 professors, but 15 of them were only on staff part-

time. Dawson played a large part in making the university financially

secure and building its early reputation. Sir William Dawson obviously did

not find the job of establishing McGill very challenging because while

doing this, he also delivered approximately 20 lectures a week on a variety

of subjects, published a series of geological papers and books, and as a

sideline, presumably to fill in his spare time, he tried to demolish Darwin’s

theory of evolution. And that explains how William Dawson wormed

his way into this section of my book, which is not about Darwin, but

about a cacophony of critics. I intend to examine the evolution of anti-

evolutionists.

The first school: early emotionals. As I see it, there are four schools of

anti-Darwinists. Dawson was a holotype of the first of these: the early emo-

204 DARWIN AND EVOLUTIONARY SCIENCE

tionals. This group of Darwin’s critics are easily recognized by their similar-

ity to those Anglo-Saxon tourists who believe that everyone in the world can

understand English provided it is spoken in a sufficiently loud voice. The

early emotionals shouted their opposition rather than learning the language of

their opponents.

The early emotionals were characterized by a clear idea of the way in

which human beings should behave. They saw in Darwinism a dreadful new

religion that would make us deviate even farther from the ideal behaviour.

What Dawson opposed was the idea of a process that was not entirely and

continually guided by a divine intelligence.

If the universe is causeless and a product of fortuitous variation and selec-

tion, and if there is no design or final cause apparent in it, it becomes liter-

ally the enthronement of unreason, and can have no claims to the venera-

tion or regard of an intelligent being. If man is merely an accidentally

improved descendant of apes, his intuitions and decisions as to things

unseen must be valueless and unfounded. Hence it is a lamentable fact that

the greater part of evolutionist men of science openly discard all religious

belief, and teach this unbelief to the multitude who cannot understand the

process by which it is arrived at, but who readily appreciate the immoral

results to which it leads in the struggle for existence or the stretching after

material advantages. It is true that there may be a theistic form of evolu-

tion, but let it be observed that this is essentially distinct from Darwinism

or Neo-Lamarckianism. It postulates a Creator, and regards the develop-

ment of the universe as the development of His plans by secondary causes

of His own institution. It necessarily admits design and final cause.

(Dawson 1890)

Dawson tries to convert us, largely by emotional attacks like this, to show

that the theory of evolution will have a short life and is already dying. Lest I

be unfair to Dawson, let me acknowledge that he also had some scientific

objections. He recognized, for example, that no case of transformation of

species had been observed, that the theory did not account for the origin of

sex, and that a mechanism was required to produce variance, but the only

one postulated, inheritance of acquired characteristics, had been falsified by

August Weisman. However the stronger element in Dawson’s anti-Darwinism

is the appeal to emotion.

Dawson was not a solitary representative of this school. He had some

unusual allies, one of the most surprising being the dogmatic atheist George

Bernard Shaw. Shaw hated evolution. He, like Dawson, had a vision of what

the human race should be, and he saw evolutionary theory as something that

opposed his lifelong battle to cure all of the social and intellectual sickness of

mankind.

205CRITICS OF DARWIN

Shaw attacked Darwin on a number of occasions, the most vicious being

in the preface to Man and Superman (1931).

I really do not wish to be abusive; but when I think of these poor dullards,

with their precarious hold of just that corner of evolution that a black-

beetle can understand — with their retinue of twopenny-halfpenny

Torquemadas wallowing in the infamies of the vivisector’s laboratory, and

solemnly offering us as epoch-making discoveries their demonstrations

that dogs get weaker and die if you give them no food; that intense pain

makes mice sweat; and that if you cut off a dog’s leg the three-legged dog

will have a four-legged puppy, I ask myself what spell has fallen on intel-

ligent and humane men that they allow themselves to be imposed on by

this rabble of dolts, blackguards, imposters, quacks, liars, and, worst of all,

credulous conscientious fools. Better a thousand times Moses and Spur-

geon [a then famous preacher] back again. After all, you cannot under-

stand Moses without imagination nor Spurgeon without metaphysics; but

you can be a thorough-going Neo-Darwinian without imagination, meta-

physics, poetry, conscience, or decency. For “Natural Selection” has no

moral significance: it deals with that part of evolution which has no pur-

pose, no intelligence, and might more appropriately be called accidental

selection, or better still, Unnatural Selection, since nothing is more unnat-

ural than an accident. If it could be proved that the whole universe had

been produced by such Selection, only fools and rascals could bear to live.

In the preface to Back to Methuselah, Shaw (1921) provided his longest

attempt to discredit evolutionary theory. Here we see why Shaw hated it so

much.

There is a hideous fatalism about it, a ghastly and damnable reduction of

beauty and intelligence, of strength and purpose, of honour and aspiration.

Shaw believed that the theory of evolution reduced human virtues to chance

events. And what is wrong with chance events? Shaw says that if they rule us:

What hope is there then of human improvement? According to the Neo-

Darwinists [and] to the mechanists no hope whatever, because improve-

ment can come only through some senseless accident, which must ... be

presently wiped out by some other equally senseless accident.

Shaw also rustled up the odd scientific argument, but his main thrust was

emotional. He ridiculed evolutionists and tried to defeat them by demonstrat-

ing his intellectual superiority.

Biologists withstood the attack. The early emotional school is now virtu-

ally dead. As expounded by fundamentalist Christians, it still serves a role in

206 DARWIN AND EVOLUTIONARY SCIENCE

allowing novices in evolutionary theory a chance to fight against a weak foe,

and so sharpen their intellectual teeth. If this opposition is often a match for

us, it is a measure of the over-confidence scientists put in their positions and

a warning about the need for thought and preparation of even a clear-cut

case.

The second school: directional deists. The directional deists constitute a

more formidable and organized opposition to Darwin than the early emotion-

als. This is because they not only bring a wider range of scientific objections

to bear on Darwinian theory, but also because they are more constructive.

They do not just destroy Darwinian theory. They provide an alternative.

This is essentially a French school of thought, derived from Lamarck’s

early theory. Lamarck postulated that when God created the earliest single-

celled creatures, He built into them a directive force that influenced the direc-

tion of evolution. Thus evolution according to Lamarck is not a random,

directionless process. There may be random elements in it caused by unusual

interactions of a species with its environment, but the mainstream of evolu-

tion inexorably flowed towards a god-like creature: Homo sapiens. The three

best-known directional deists are, in order of appearance, Henri Bergson,

Pierre Lecomte de Noüy and Pierre Teilhard de Chardin.

The first of the three is particularly interesting. Bergson (1911) disliked

evolution, not for its own sake, but because he thought it supported determin-

ism. He wanted to believe that human beings have free choice. He disliked

Darwinian evolution because he disliked deterministic philosophy and deter-

ministic science. Bergson developed a whole battery of probabilistic argu-

ments to show that the selection of random mutations was simply not power-

ful enough to cause the evolution of highly complex structures. He postulated

the existence of an élan vitale that would drive evolution towards improve-

ment.

The eye particularly fascinated Bergson. He argued that so complex and

perfect a structure as the eye could not evolve by accumulation of chance

mutations, because any mutation would make it less effective. Take this in

conjunction with the fact that the eye and brain must evolve simultaneously

and we are straining credulity. Finally, when we consider that similar eyes of

great perfection evolved independently in vertebrates and in the scallop

(Pecten), we realize the eye could not possibly have arisen by Neo-Darwinian

evolution.

Bergson’s criticism implies that the eye must be perfectly and fully formed

if it is to function. But this is contrary to observation. Comparative anatomy

provides us with a series of photo-receptors ranging from simple light sensi-

tive cells to the complexities of a falcon’s eye, all of which are functional and

useful to their possessors. Similarly, we ought not be surprised that evolution

207CRITICS OF DARWIN

in different lines should converge to one of a few solutions to the same phys-

ical problems: light sensitivity.

Bergson produced a series of impressive arguments of this type but they all

had the same weakness. They were founded on totally non-quantitative statis-

tics. Bergson was a master of the “logically-black-is-white-slide’ (Flew

1975, Peters 1991a) whereby improbable becomes highly improbable and

ultimately impossible.

Lecomte du Noüy (1947), a biochemist, made his contribution by over-

coming this weakness of qualitative argument. He worked on the origin of life

and demonstrated — to his own satisfaction — that for a single protein

molecule to have originated by chance, within the lifespan of our universe,

we would have needed a universe entirely made of amino acids, 10

light

years in diameter. He also developed an argument from the second law of

thermodynamics to the effect that because the universe tends to disorder, evo-

lution to greater order is impossible.

Both of du Noüy’s objections now seem easy to dismiss. Arguments about

the probability of an observed event depend on the null model one has in

mind; whether an event seems probable or not depends on the selected model.

We need only posit rules for the assembly and duration of amino acids to

make the events that are improbable to du Noüy probable to an evolutionist,

and there is now experimental evidence that the latter position is more cor-

rect. Similarly, no one is any longer puzzled by local increases in complexity

in parts of an open system like the biosphere: the solar system is tending to

greater entropy and the biosphere simply slows this flux temporarily. Biolog-

ical complexity is an eddy in the heat death of the universe.

Finally, Teilhard de Chardin (1955, 1959) does not attack the old, but

creates anew. For Bergson’s élan vitale, he substitutes a universal mind-

substance that has God-given tendency to coalesce. Evolution is proceeding

to “point Omega” when all the mind in the universe will coalesce in perfect

unity with the mind of God. Needless to say, we have not reached point

Omega yet, but it does provide a goal for the universe, and that is apparently

a bodily need for this school of critics. They are vitalists who introduce an

unobservable into science and thereby make the universe more understand-

able, but no more predictable.

The third school: cataclysmic creationists. The catastrophists have a

long honourable lineage that can be traced back to Buffon and Cuvier. Their

argument is that there has not been enough time for Darwinian evolution to

produce the vast array of highly perfected species we see on earth. To speed

up the process, they postulate a series of cataclysmic events that eliminated

most existing species, followed by either a new supernatural act of creation or

a sudden evolutionary spurt.

208 DARWIN AND EVOLUTIONARY SCIENCE

The most esteemed of the cataclysmic creationists was Louis Agassiz.

Agassiz, like Dawson, was a geologist and a powerful academic. He is best

known as an advocate of the theory of the ice age and as a teacher at Harvard

University.

Agassiz argued until he died that the facts falsified evolutionary theory

and fitted special creation. He believed that God had created four distinct

groups of animals at the beginning: chordates, molluscs, articulates and ver-

tebrates. Agassiz (1859) held that these four groups have no anatomical sim-

ilarities and thus offer no evidence of evolutionary connections. And as God

creates new species, he always follows one of these four basic plans. Since

the four coexist everywhere, the effect of environment on animals must be

negligible.

A more recent cataclysmic creationist is Immanuel Velikovsky. He is dis-

tinct from all other cataclysmic creationists in that God is missing from his

scheme. Velikovsky’s cataclysms were produced by natural events. Briefly,

he believed that planetary near-collisions so dislocated the earth that the con-

ditions of life on earth changed dramatically and instantaneously (Chap-

ter III). These changes caused mass extinctions, but instead of postulating

supernatural acts of creation, Velikovsky postulated that the great heat and

intense radiation associated with his cataclysms would cause multiple muta-

tions and instantaneous formation of new species. Unfortunately, Velikov-

sky’s genetic ideas are presented so summarily that it is not clear how these

new species arise.

Although they differ greatly in matters of detail, the catastrophists agree

on one point: they reject uniformitarianism, and hold that we cannot explain

the facts of life unless we postulate the existence of unobserved phenomena

such as world-wide cataclysmic events. This school has perhaps gained new

respectability in the last decade or so, because paleontologists are increas-

ingly willing to entertain the idea of catastrophes and variable evolutionary

rates. However, contemporary ideas about catastrophes require no fundamen-

tal change on the part of the scientific community and have been incorporated

into evolutionary thought relatively easily. They differ from their predeces-

sors in using the full scope of geological time and so need no recourse to spe-

cial creation or novel causes of evolutionary change.

The fourth school: Popperian purists. The last group of critics of evolu-

tionary theory are a strangely schizophrenic lot because they do not reject

evolutionary theory. Neither do they try to replace it with another

theory. Deep in their hearts they believe in evolutionary theory as if it were a

truth.

Let me describe these Popperian purists to you. Their name comes from

their prophet: Sir Karl Popper, a philosopher of science. He is largely respon-

209CRITICS OF DARWIN

sible for convincing us that we cannot verify a theory; we can only falsify it.

Thus Popper holds that science progresses by discovering mistakes and cor-

recting them, not by establishing truths. Scientists do this by testing the pre-

dictions of their theories. It is a corollary of this view that theories are rated

not by their truth value, but by the richness of their predictions. A good theory

makes many predictions about different categories of facts and consequently

offers us many opportunities to falsify it. A poor theory makes predictions

about a small body of facts. If a statement makes no predictions, it is not a

theory at all.

To look at Popper’s arguments another way, what a scientific theory really

tells us is that, given present circumstances and knowledge, one or more

specifiable states will not be observed. The best theory rules out all but one

future observation. It is easily falsified. The worst theory rules out no future

state; so whatever happens is consistent with the theory. Nothing can falsify

such a bad theory.

I can illustrate these differences with a simple example. The theory that

“on April 1, the sun rose at 7:06 AM south-east of Montreal” is a good

theory. The theory that “the sun rose on April 1” is less good. And the

theory that “either the sun rose sometime in an unspecified direction from

somewhere, or it did not” is such a bad theory that it is no theory at all. The

Popperian purist judges a theory only by its value as a predictive tool. I have

purposely set this example in the past to stress that the theory predicts an

unknown state, not simply a future state. And I have chosen this familiar

example to stress that the knowledge we gain is personal knowledge, not

just the realization that someone else knows the answer. Alternatively one

may say that the future which a theory predicts is the future state of our

knowledge.

Not all Popperian purists are anti-evolutionists. Those who are believe

that the theory of natural selection is no theory at all because it makes no

predictions that we can falsify. Most are not so extreme. They are like the

agnostic who is desperate to believe, but argues against the existence of God

in the hope that someone will provide the conclusive evidence that She

exists. They argue against the theory of evolution by natural selection, but

hope that their argument will one day attract an evolutionist who can con-

clusively demonstrate that the theory makes falsifiable predictions. This is

my position.

I claim to be a Popperian purist, but I am very close to agnosticism. My

childhood conditioning and undergraduate training were so effective that in

the innermost, animal reaches of my brain, where there is no science, there is

the knowledge that the theory of evolution by natural selection is true. Unfor-

tunately, I cannot show this to be so.

210 DARWIN AND EVOLUTIONARY SCIENCE

Two other biological schools. There are other kinds of biologists. Bio-

logical historicists see science as a narrative describing the sequence of

causal events that preceded any observation, and the true chronicle of events

that preceded the present on earth. They are fascinated by evolution, but are

more interested in explaining past observations than predicting new ones. If

they acknowledge the importance of prediction at all, it is to justify the expla-

nation they have already developed.

A sixth group of biologists I will call the heurists. They see science as a

way to inspire themselves to create more theories or to realize a unity with

nature that they call understanding. For example, many Darwinians and Neo-

Darwinians try to re-trace the thoughts of their name-sake. They hope that

this vicarious recreation of Darwin’s mind will inspire them to similar under-

standing and creativity. If heurists accept that prediction is important, it is

because they see prediction as a useful way of warranting their understand-

ing. If their understanding is sound, it should lead to predictive success, but

whether that prediction helps us gain control over our lives is incidental.

Conclusions

What is the message of this re-examination of old arguments and observa-

tions? In part, it serves to remind the reader of a tradition of anti-Darwinism

that dates back to the last century, and to suggest that not all of this resistance

is rooted in fundamentalist dogma. There are alternative ways of viewing

science. A university program in biology should offer a wide assortment of

historicists, heurists, and Popperian Purists. The student would then have the

opportunity to sample all points of view, and come out of the system behav-

ing more like a scientist than like a Pavlovian dog. I hope these students,

better trained and more aware than I was, will think more about the nature of

science than I did, and so avoid the slavish conditioning that still restricts my

thought.

211CONCLUSIONS

XV Is The Future Grim?

“A man’s reach should exceed his grasp, else

what’s a heaven for?”

Robert Browning

[Andrea del Sarto (1855)]

For most university biologists, science remains a glorious entertainment. For

them, calls to change or to rethink the foundations of research seem unneces-

sary. After all, they can pursue their profession in the same way as their pre-

decessors, earn a decent wage, enjoy the respect of their peers, and sometimes

make a contribution towards the sum of human happiness. Most of us want

little more.

This chapter suggests that, pleasant as a life in science may have been,

those who imagine it will not change are living in a fool’s paradise. I believe

that society feels the time has come to change the university. If university

scientists were to think about science, we too would see that a change is in

store. If professors do not lead the way in this process, society may force us

to accept changes that are both more onerous and less productive.

Any imposed change threatens our ideals as professors. These are to mas-

ter the current ideas of humanity, to contribute our own ideas to this precious

store, and to disseminate both. There is little else that justifies our place in

society. Indeed, because ideas are the most lasting of human accomplish-

ments, there may be nothing else that matters in life, but ideas. University

staff are therefore in a rarely privileged position. We are the pampered

guardians of the intellectual traditions of humanity.

The best ideas in science are theories. Thus our efforts as university scien-

tists are directed to the assessment of existing theories and the production of

new ones. As idealists, we should encourage changes that favour theory, but

inflexibly oppose any change that makes theorizing more difficult. Any

changes to the university should be intended to produce, in our lives and in

the lives of our graduate students, the conditions that are most conducive to

theory-making and theory-testing.

The Gilt Age of University Research

After World War II, an awe-struck society held an unrealistically exagger-

ated view of the collective prowess of its scientists. Science, particularly the

pure science of the universities, was touted as a panacea. University scientists

were consulted on all important matters, quoted in the press, invited to advise

governments, and raised up in the social hierarchy. During this period, we dis-

covered a social conscience. Staff lectured to schools, associations and politi-

cians. We joined extra-mural committees and spent time consulting with

industry or working on government commissions.

The postwar enthusiasm for universities convinced us of our greatness. It

convinced us that we could be all things to all people and that in us alone lay

the power and knowledge to save the world. We would solve practical prob-

lems, teach everything to the new generations and preach to the community at

large. We would discover truth, and our success would demonstrate the supe-

riority of intellect over materialism. These beliefs made every two-bit depart-

ment aspire to greatness.

Not only were we wooed rapidly into accepting society’s inflated opinion

of universities, but we also convinced ourselves that these remarkable powers

would, if provided with the proper nourishment and exercise, continue to

grow. Young turks dismissed the aging scholars in cluttered labs as irrelevant.

They talked not of a science they loved, but of developing excellence, import-

ing eminence, capturing the very best of the young Ph.D.’s, and building

inter-disciplinary teams. We ridiculed the short-sighted granting agencies that

did no more than keep us salivating with slow infusions of thin gruel, and

were encouraged to seek new, more generous sources. We pressured the

library for our share of new journals and symposia volumes, and the univer-

sity for new buildings and research facilities. At one time, we even put six

graduate students in the space designed for three.

Meanwhile, growth of the university and the egocentricity of its staff

caused committees to proliferate and administrative duties to become more

onerous. Within my department alone over twenty committees flourished. I

could go on to recount our forays into big science and our discovery of multi-

disciplinary institutes, but these stories are familiar. We had the money and

time to do more and more, and we did. All these extra duties left little time for

reading. To keep up with science we became world travellers, attending sci-

entific gatherings at up to three exotic places a year.

The Gathering Challenge to University Science

Adulation, like power, corrupts. Our particular form of corruption was

that we came to believe what the newspapers said about us. We could do

anything provided we had enough money. The money came (we could and

did say even that was not enough), the years passed, but we did not pro-

214 IS THE FUTURE GRIM?

duce the promised successes. Our disillusioned bride realized our failure

first and now we too suspect the truth. We had not fully recognized our

limitations.

The postwar honeymoon of the university and the public was primarily

due to the widespread belief that a university degree was the surest key to

the good life for society and personal success for the individual. Student ac-

tivism, devaluation of the degree designation by mass education, and then

economic realities destroyed that faith; and a more realistic evaluation of the

material value of university degrees has decreased teaching allocations. A

second problem for university science is a growing suspicion that much of

the work scientists define as important is actually irrelevant and that useful

scientific output per dollar may be unrelated to the dollars per scientist.

Governments have already reacted to these changes by reducing support for

universities.

I doubt that our modern troubles arose simply because society sometimes

wavers in its support for science. Sometimes, society adopts new patterns. I

think the latter is happening now. Society has permanently changed its atti-

tude to universities, and that changing temper of society will inevitably

change the conditions of university science. The new trend is not a local

Canadian problem. It permeates the United States, Britain, Germany and

other nations because it reflects a fundamental limitation of resources. As

new patterns form in society, some old institutions suffer. I fear the university

is due for a little suffering.

We should expect our budgets to become still less generous. Science has

grown exponentially since the 17th century. Its doubling time is about 10 to

15 years, twice as fast as the economy and three or four times faster than the

population of North America and Europe (Chapter I; Price 1986). This can

only be a temporary situation. Eventually, the growth rate of science must

decrease until it comes into line with the economy and the population.

Although we cannot predict the final share of society’s resources and person-

nel that science can expect, this decrease must make itself felt sometime

within the next 100 years. By then, extrapolation of historical rates of growth

show that science would be as large as the economy and that the population

of scientists would exceed the number of people (Price 1986). This Malthu-

sian argument against the continuing unrestricted growth of science, com-

pounded by the disillusionment of society with university science, leads me

to suppose that the financial pinch in which we now find ourselves is no tem-

porary correction. It is a permanent change.

Since we can expect further belt-tightening, ‘Science Policy’ will continue

to evolve in its present direction. We ought to expect more economic

restraint, not a return to opulence. Tighter control over research monies

215THE GATHERING CHALLENGE TO UNIVERSITY SCIENCE

means these monies will be redirected from universities to government agen-

cies where costs and research can be better controlled. Even more emphasis

will be placed on contract work, industrial and government partnerships, and

on group research into subjects of direct interest to government agencies.

There will be less call for independent theory-making, and pure research by

university staff will be further downgraded. Graduate students, who now per-

form the bulk of university research, will be less in demand and many of

those who do enter graduate school will work on applied research, not

science. If this scenario is even approximately correct, the attitudes we have

fostered over the last 50 years may have to be abolished.

University Responses

We professors must respond to government and societal penny-pinching.

But how? Should we spend more time in public relations, shouting our

praises? Should we lobby for a larger share of the tax revenues? Should we

try to convince the appropriate agencies that because our particular university

is better than others, it needs a bigger share of the budget for post-secondary

education?

Before we spring to the accustomed defensive position of every privileged

minority, we should ask whether or not this reduction in status and financial

support really will decrease our ability to do good science. I think it could, but

only if we respond inappropriately. I also think it has given us the opportunity

to re-evaluate ourselves and to do better science.

I had six years experience with big science while directing the Char

Lake Project which was but a trivial part of the massive International

Biological Program. This experience convinced me that big money makes

administrators of scientists and produces data but not ideas. I believe that

big science restricts, rather than expands, our mental horizons. In our uni-

versity role, we should exercise our talents to produce ideas, not harassed

executives.

An inappropriate response to shrinking budgets will simply dissipate our

energies striving for funds to maintain our research budgets and defending

our own area in frantic turf wars with other researchers. If I thought that spir-

ited defense of our present position would succeed and that success would

help us achieve our ideals, I would counsel battle. But we would not succeed.

Battles must sometimes be fought, but one should always avoid a battle when

the outcome will be disastrous. There is no gain for us in a protracted defense

of the big science we have come to practice.

216 IS THE FUTURE GRIM?

Even if we fought and won a momentary respite, I am uncertain that a

return to fat budgets and more-of-the-same would achieve our ideals. The

universities could perhaps find a new functional role for themselves that

would justify a bigger share of the pie, but our concern is to protect our old

role, the preservation and development of ideas, not to acquire new duties.

And in any case, the Malthusian restriction, that we cannot indefinitely grow

faster than our resources, would make itself felt again in short order.

My colleagues and I already spend our days and nights racing to keep up

to our image of what a scientist should be. We cannot fight harder, indeed

most of us have already compromised ourselves by trying to do too much.

Deep down, we know we are frauds (Medawar 1990). University scientists

are simply normal men and women doing our best to keep our heads above

the flood of duties, demands and interests that only a superman could do well,

but afraid to admit that we can only do them badly. Perhaps we will offer a

secret sigh of relief if society takes away our Captain Marvel cloaks and

forces us to consider where we go from here.

The cure I recommend involves no genius, no technological break-

throughs, nor any other mythical unicorn horn. It is simply the ecological

solution that we must learn to live with less: less waste, less heat, less ineffi-

ciency and less ineffectiveness, but not with fewer ideals or fewer ideas. We

should seek out any change that will lower our aspirations until they come

within shouting range of our abilities. I simply recommend that we return to

our ideals.

A Policy for the Future: Closing the Aspiration Gap

There is now so large a gap between what we can do and what we are

expected to do that a sense of frustration and impotency is inevitable. A gap

may be essential, but a chasm is counter-productive. I suggest that we deter-

mine what it is we must do and try to find the most efficient way to achieve

those ends. To do so, we must sacrifice many of the trappings we have accu-

mulated in the last generation, but we need not compromise our effectiveness

in learning, teaching and developing theory. All of my recommendations are

therefore intended to produce more uninterrupted time for thought and

research without spoiling our teaching efforts.

Undergraduate teaching. The equilibrium between teaching and re-

search is unstable, so there can be no optimum balance between these two

critical activities of a university professor. Nevertheless, we must recognize

that we are paid to teach, and that everything else is largely self-imposed. In

217A POLICY FOR THE FUTURE: CLOSING THE ASPIRATION GAP

keeping with our loss of prestige, we can expect society to stress the impor-

tance of undergraduate teaching. Since there will be no decrease in student

numbers, no increase in staff, and continued demands for good teaching, we

must make our teaching much more efficient and effective.

Equalize teaching loads. Assuming that a happy teacher is a better teacher,

we should equalize teaching loads. This will make teachers happy because

the greatest source of friction in most departments is the perceived inequality

of the commitments of various colleagues to the burden of undergraduate

instruction. The reassignment of teaching loads must be done without refer-

ence to outside duties, to the number of pages of print we produce annually,

or to the number of graduate students we train. The workload should be

evenly distributed. This will protect those who enter the system in the future

from being pushed into too much teaching, but it will also help to close the

aspiration gap by impressing us with the fact that we are here as teachers and

we should not be rewarded for other activities by having our teaching load

reduced.

Abolish tenure. It is a corollary of the central role of teaching in university

life that we should be judged as teachers and that useless teachers should be

dismissed. This freedom can only be achieved if we abolish tenured posi-

tions. I see no virtue in cut-throat competition, so some alternatives to throw-

ing our colleagues into the street must be found. Perhaps those who fail as

teachers too late in life to find another job could be transferred to administra-

tive posts.

Tenure is widely applauded as a bastion protecting those whose views

challenge authority. Thus, the abolition of tenure is abhorred because it would

leave the most precious members of the community open to arbitrary dis-

missal. The protection of deadwood is seen as the cost of academic freedom.

This defense seems disingenuous: professors with unpopular views have

never been well defended by tenure, because university and state administra-

tions have too often buckled to public pressure. Tenure really protects incom-

petence.

The end of tenure will impress on us the fact that we are ordinary mortals,

not above judgement. It will also make it easier for new staff to become good

teachers, because they will justifiably devote more time to preparation for

teaching. Neither will they have to do research in desperate haste to achieve

the number of publications demanded by tenure committees. They can do it

because they enjoy it.

Reduce course offerings. The equalization of teaching loads could stifle

research, unless we are careful to contain the total teaching burden. Therefore

I recommend that we reduce the number of course offerings by pooling

specialized courses and allowing students more freedom of choice among

218 IS THE FUTURE GRIM?

courses and subject matter. This reduction would be facilitated by eliminating

labs from many courses, and limiting the number of lecture hours, thus giving

students more time for independent work.

We should also eliminate all courses with less than 10 to 30 students. The

cut-off is arbitrary but a minimum class-size acknowledges that small courses

waste money and professorial time. If offered at all, they should be offered

only every other or every third year. Small, specialized courses are in demand

by staff who see in them the opportunity to study their own speciality in even

more detail and to teach an easy subject. They are defended as a device to

attract graduate students, but obviously this is not so. If it were, enrolments

would be larger.

Reduce teaching burdens. To make our work as efficient as possible, we

should eliminate or at least limit the mind-numbing chores that seem so much

a part of university teaching. We should exploit the multi-media approach, the

computer and any other approach or device that will eliminate repetition of

lectures and hand-marking of anything over 100 identical examinations in a

week or two by one professor. Our objective should be to make teaching large

classes an enjoyable job.

Graduate training. Graduate education is also one of our primary duties.

I have de-emphasized it in my considerations because graduate education will

be less important in the university science of the future. Decreased budgets,

increased emphasis on undergraduate education and the de-emphasis of inde-

pendent research will relieve us of the obligation we once felt to increase our

graduate training programme. Indeed, a slower rate of growth of science will

mean that our graduate training programmes will have to be curtailed. Pro-

fessors will therefore have more time and will be able to do the work them-

selves.

To encourage this curtailment, we should institute a policy that will pro-

tect us from our own inability to refuse good applicants. Even good graduates

cost money and thus distract professors from research by sending them out

looking for more or bigger research grants. Weak students do this, and also

demand even more professorial time in training.

Scholarship. Scholarship is what we modestly call “our own work”. My

schemes are intended to make it possible for us to do and enjoy our own work

in the coming university environment. We must find ways to avoid the busy

work that cuts us off from research.

For example, the telephone is probably the single greatest obstruction to

scholarship and meaningful intercourse amongst staff. I would remove all

telephones from professors’ offices, although I would not prohibit graduate

students or staff from renting their own. Fax machines and E-mail are simi-

larly invasive.

219A POLICY FOR THE FUTURE: CLOSING THE ASPIRATION GAP

The mobility of big science also robs us of the calm we need to think and

to develop theory by bringing us colleagues and visiting lecturers who them-

selves dedicate days of their time to deliver an hour’s lecture. Too often, that

lecture is appreciated by only a tiny fraction of the audience. The rest are

there only to hold up the side, or as a courtesy to the visitor. This is clearly

inefficient. All visiting lecturers and seminars should be aimed at undergrad-

uates first and graduates second, since students more frequently are the

people with the time to listen to and the minds to learn from visitors.

Inter-disciplinary institutes are also devices to sabotage meaningful

research. They are based on a flawed model of our needs and abilities

(Chapter XIII) and they lock the individual into the narrow confines of his or

her speciality as one element in a systems approach (Chapter VIII). If one

wishes to develop one’s own ideas in science, one must not start such insti-

tutes or participate in their programmes.

Staff members should be actively discouraged from seeking large re-

search grants. They might, for example, be asked to justify their proposals

in terms of their ideals to the department staff. Large research grants in-

crease the output of data, but spending money is such a time-consuming

occupation that it can reduce the quality of research. The danger will in-

crease in the future because the evolving science policy will mean that when

we get large grants, we will be required to conduct research programs de-

signed more by others than by ourselves. All of this is obviously anathema

to our ideals as professors.

Administration. Administration presents a problem for which I have no

solution. At the departmental level, we have some control over the amount of

administrative busy-work we impose on ourselves, but we have none over the

university as a whole. Thus, university committees and commissions will

continue to propagate regardless of our attitude toward them. Furthermore,

we will be expected to serve on them.

My limited experience with these activities is that they waste a great

deal of time. They are unnecessarily protracted by aspiring administrators

who cannot bear the thought of disappearing back into the obscurity of

their own office, whereas any professor worthy of the name should be eager

to return to the lab or office to pursue his or her ideas. Although we cannot

escape the feeling of obligation to contribute our minimal share towards the

running of the university, it would probably function just as well if we were

to opt out.

Perhaps there is nothing we can do about this impediment to teaching and

scholarship, but we should disabuse ourselves of the belief that active partic-

ipation in university affairs is a virtue. Certainly, administrative duties should

be irrelevant to advancement and job security at the university.

220 IS THE FUTURE GRIM?

Two reservations. What I have tried to say is that for almost half a cen-

tury, we have been obsessed with a chimera: we have tried to achieve better

science with grantsmanship instead of scholarship. I have made entirely rea-

sonable suggestions like these in the past and been surprised that they were

not universally accepted. My listeners instead suggested that such changes

could undermine science by setting such low goals that researchers would

cease to strive for new ideas and become apathetic towards science. We

would return to a tweedy and unproductive past. From these objections, I can

only infer that my cloudy literary style can obscure the dazzling brilliance of

my ideas. Therefore, I will end with a brief rebuttal of those suggestions.

A formula for apathy? There is a widespread belief that because we have

an animal need to strive, it would be undesirable for us to reach our ideals.

This fear is now particularly acute, because apathy is the disease of the age. It

is not my position that we should stop striving. That would merely aggravate

the situation and produce more apathy. The modesty of my proposals could

inadvertently discourage some scientists and prevent them from trying to

improve, but that is not my intent.

Unlike Browning’s Andrea del Sarto, I believe it is more frustrating to

attempt the impossible than to set our goals so low that we can actually reach

some of them. If we actually did achieve our modest goals, we would not be

finished as scientists. Success would stimulate, not inhibit us.

The goals of a scientist are like those of the exhausted traveller. It is not

the end of the journey, but the next tree or stone that remains the goal. This is

the view of science propagated by 20th century philosophers like Sir Karl

Popper and historians of science like T. S. Kuhn (Chapter III). We never reach

an ultimate truth. We merely continue to elaborate and change our ideas as we

progress, not to a lasting goal, but farther and farther away from our primi-

tive, fumbling beginnings. Thus I think we can be both realistic and idealis-

tic. By combining the two, we will stimulate not inhibit scientific excitement.

A step back? For some, my suggestions represent a step back to some lower

rung of the evolutionary ladder of science, but that applies only for some

unessential aspects of research. I am looking back or down only if it is retro-

gressive to emphasize doing science rather than chasing research dollars. For

a generation, university scientists aspired to greatness, and almost destroyed

themselves. Individuals competed, unified departments fragmented, and some

of us discovered that university life was no longer pleasant. In this sense, I

hope my solutions are retrogressive.

I want to escape what the modern university has become. However, I am

not prepared to return to mindless, unchallenging research that grubs for new

facts or defends favourite theories from scientific scrutiny. The opportunity

that social change offers us is not a return to the trifling puzzles of the past,

221A POLICY FOR THE FUTURE: CLOSING THE ASPIRATION GAP

but the chance to consider what we have done, what we are doing, and what

we should do. If we can escape from the trap of our own self-image, we can

begin to contemplate science.

Conclusion

Big science and societal power have caused professors to lose track of

their ideals and goals. In doing so, they have almost destroyed the university

as an intellectual retreat. When I begin to hear more staff members whistling

in the corridors or humming in their labs, I will be content that we have come

into a happier equilibrium with reality. Under these conditions we will not

only be able to do more effective research, but we will also discharge our duty

to society. We will pass on the tradition that intellectual activity is more excit-

ing than material consumption. We will have learned to contemplate science.

222 IS THE FUTURE GRIM?

Acknowledgements

I thank the many individuals who have helped so much in the production of the book.

The Rigler family helped transcribe and edit the lectures. Andréa Grottoli Everett drew

most of the figures; Greg Scarborough and Gary Bowen have been invaluable in the

final stages. I am deeply indebted to David Currie of the University of Ottawa, John

Downing of the University of Montreal, Don Kramer of McGill and to Yves Prairie and

David Bird, both of the Université de Québec at Montréal, for their comments on ear-

lier drafts of the manuscript.

The passage that serves as a prologue is from Molloy by Samuel Beckett, translated

this translation 1955, 1959, 1966, 1971, and 1976 by Samuel Beckett. Reproduced by

permission of the Beckett Estate and the Calder Educational Trust, London. Rigler

played a reading of this passage by Cyril Cusack at the beginning, and again at the end,

of his courses in history and philosophy of science at both the University of Toronto and

McGill University.

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About the Author and the Book

Professor Robert H. Peters is the winner of the

ECOLOGY INSTITUTE PRIZE 1991 in limnetic

ecology. Born in 1946 in Toronto, Canada, he ob-

tained his Ph.D. in 1972 from the University of

Toronto under the supervision of Frank H. Rigler, a

major figure in limnology, who died much too

early, leaving behind a host of important work and

thought. In his EE book, Peters presents highlights

of Rigler’s unpublished notes and ideas and com-

bines them masterfully with his own accomplish-

ments and expertise.

Chaired by Professor Jürgen Overbeck (Max-

Planck-Institut für Limnologie, Plön, Germany)

the ECI Jury selected Rob Peters for his work on

phosphorus cycling in lakes, which provides exam-

ples of excellent research and illuminates impor-

tant insights into the measurement and availability

of phosphorus in aquatic systems.

This book reaches far into the realms of science history, philosophy and methodology,

the significance of science for society, and the research and teaching in universities. It

documents that ecologists have collected impressive amounts of observations and facts,

but that they have failed to sufficiently identify and formulate theories which go beyond

the facts — theories that can be tested and that can predict.

About the Ecology Institute (ECI)*

The international ECI is a not-for-profit organization of research ecologists. Director and

scientific staff — 52 marine, terrestrial and limnetic ecologists of outstanding profes-

sional reputation — strive to honor excellence in ecological research; to further the

exchange among marine, terrestrial and limnetic ecologists; to promote advancement in

environmental sciences; and to bridge the gap between ecological science and its appli-

cation for the benefit of nature and society.

In order to approach these goals the ECI annually sets out two international prizes, the

ECI and IRPE (International Recognition of Professional Excellence) Prize, and it sup-

ports — via the Otto Kinne Foundation (OKF) — promising young environmental scien-

tists in Eastern European countries by providing financial assistance for professional

travel, scientific equipment or published information. Each ECI Prize Laureate is re-

quested to author a book taking into account ECI’s aims. The book is published in the

series “Excellence in Ecology” and made available worldwide at cost price; a consider-

able number of books are donated to libraries in Third-World countries. In this way

leading ecologists are offered the possibility of disseminating their personal views on

current ecological issues and of serving the general public who depend acutely on defini-

tive ecological knowledge for planning our present and future.

* Nordbünte 23, D-21385 Oldendorf/Luhe, Germany

Tel. (+49) (0) 4132 7127; Fax (+49) (0) 4132 8883; E-mail 100327[email protected]

Robert H. Peters