The art of scientific investigation

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THE ART OF
SCIENTIFIC INVESTIGATION

MICHAEL FARADAY 179I-1867

EDWARJ) jENNER 1749-182^^

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THOMAS HUXLEY 1 823- 1 895

GREGOR MENDEL 1 822-1 884

THE ART OF

SCIENTIFIC

INVESTIGATION

ooy.

By
W. I. B. BEVERIDGE

Professor of Animal Pathology, University of Cambridge

" Scientific research is not itself a science;
it is still an art or craft." — VV. H. George

WW- NORTON & COMPANY • INC • New York

ALL RIGHTS RESERVED
FIRST PUBLISHED IN THE UNITED STATES OF AMERICA, I95O

REVISED EDITION, igS7

Library of Congress Catalog Card No. 57-14582

PRINTED IN THE UNITED STATES OF AMERICA

CONTENTS

CHAPTER Pog^

Preface viii

I. Preparation

Study I

Setting about the Problem 8

II. Experimentation

Biological experiments 13

Planning and assessing experiments 19

Misleading experiments 23

III. Change

Illustrations 27

Role of chance in discoveries 31

Recognising chance opportunities 34

Exploiting opportunities 37

IV. Hypothesis

Illustrations 41

Use of hypothesis in research 46

Precautions in the use of hypothesis 48

V. Imagination

Productive thinking 53

False trails 58

Curiosity as an incentive to thinking 61

Discussion as a stimulus to the mind 63

Conditioned thinking 64

VI. Intuition

Definitions and illustrations 68

Psychology of intuition 73

Technique of seeking and capturing intuitions 76

Scientific taste 78

P/ yC'6

CHAPTER Page

VII. Reason

Limitations and hazards 82

Some safeguards in use of reason in research 86

The role of reason in research 92

VIII. Observation

Illustrations 96

Some general principles in observation 98

Scientific observation 102

IX. Difficulties

Mental resistance to new ideas 106

Opposition to discoveries 1 1 1

Errors of interpretation 1 1 5

X. Strategy

Planning and organising research 121

Different types of research 126

The transfer method in research 129

Tactics 131

XI. Scientists

Attributes required for research 1 39

Incentives and rewards 142

The ethics of research 1 45

Different types of scientific minds 148

The scientific fife 151

Appendix i 60

Bibliography 169

Index 175

(The reference numbers throughout the book refer to
the numbers in the bibliography)

VI

LIST OF PLATES

PLATE

I. Michael Faraday Frontispiece

Edward Jenner
Thomas Huxley
Gregor Mendel

Facing Page

IL Claude Bernard 68

Louis Pasteur
Charles Darwin
Paul Ehrligh

in. Theobald Smith 69

Walter B. Cannon
Sir Frederick Gowland Hopkins
Sir Henry Dale

IV. Sir Alexander Fleming 100

Sir Howard Florey
G. S. Wilson
Sir MagFarlane Burnet

V. Max Plangk ioi

Sir Ronald Fisher
C. H. Andre WES

J. B. CONANT

vu

PREFACE

ELABORATE apparatus plays an important part in the science
of to-day, but I sometimes wonder if we are not inclined to
forget that the most important instrument in research must always
be the mind of man. It is true that much time and effort is devoted
to training and equipping the scientist's mind, but little attention
is paid to the technicalities of making the best use of it. There
is no satisfactory book which systematises the knowledge available
on the practice and mental skills — the art — of scientific investiga-
tion. This lack has prompted me to write a book to serve as an
introduction to research. My small contribution to the literature
of a complex and difficult topic is meant in the first place for the
student about to engage in research, but I hope that it may also
interest a wider audience. Since my own experience of research
has been acquired in the study of infectious diseases, I have
written primarily for the student of that field. But nearly all the
book is equally applicable to any other branch of experimental
biology and much of it to any branch of science.

I have endeavoured to analyse the methods by which dis-
coveries have been made and to synthesise some generalisations
from the views of successful scientists, and also to include certain
other information that may be of use and interest to the young
scientist. In order to work this material into a concise, easily
understandable treatise, I have adopted in some places a frankly
didaciic attitude and I may have over-simplified some of the
issues. Nothing, however, could be further from my intentions
than to be dogmatic. I have tried to deduce and state simply as
many guiding principles of research as possible, so that the student
may have some specific opinions laid before him. The reader is
not urged to accept my views, but rather to look upon them as
suggestions for his consideration.

Research is one of those highly complex and subtle activities
that usually remain quite unformulated in the minds of those who
practise them. This is probably why most scientists think that it is

viii

PREFACE

not possible to give any formal instruction in how to do research.
Admittedly, training in research must be largely self-training,
preferably with the guidance of an experienced scientist in the
handling of the actual investigation. Nevertheless, I believe that
some lessons and general principles can be learnt from the experi-
ence of others. As the old adage goes, " the wise man learns from
the experience of others, the fool only from his own." Any train-
ing, of course, involves much more than merely being "told how".
Practice is required for one to learn to put the precepts into effect
and to develop a habit of using them, but it is some help to be told
what are the skills one should acquire. Too often I have been able
to do Httle more than indicate the difficulties likely to be met —
difficulties which we all have to face and overcome as best we can
when the occasion arises. Yet merely to be forewarned is often a
help.

Scientific research, which is simply the search for new know-
ledge, appeals especially to people who are individualists and their
methods vary from one person to another. A policy followed by
one scientist may not be suitable for another, and different
methods are required in different branches of science. However,
there are some basic principles and mental techniques that are
commonly used in most types of investigation, at least in the
biological sphere. Claude Bernard, the great French physiologist,
said :

" Good methods can teach us to develop and use to better
purpose the faculties with which nature has endowed us, while
poor methods may prevent us from turning them to good account.
Thus the genius of inventiveness, so precious in the sciences,
may be diminished or even smothered by a poor method, while
a good method may increase and develop it. . . . In biological
sciences, the role of method is even more important than in the
other sciences because of the complexity of the phenomena and
countless sources of error." ^^

The rare genius with a flair for research will not benefit from
instruction in the methods of research, but most would-be research
workers are not geniuses, and some guidance as to how to go about
research should help them to become productive earher than they
would if left to find these things out for themselves by the wasteful
method of personal experience. A well-known scientist told me

ix

PREFACE

once that he purposely leaves his research students alone for some
time to give them an opportunity to find their own feet. Such a
policy may have its advantages in selecting those that are worth-
while, on a sink or swim principle, but to-day there are better
methods of teaching swimming than the primitive one of throw-
ing the child into water.

There is a widely held opinion that most people's powers of
originahty begin to decline at an early age. The most creative
years may have already passed by the time the scientist, if he
is left to find out for himself, understands how best to conduct
research, assuming that he will do so eventually. Therefore, if in
fact it is possible by instruction in research methods to reduce his
non-productive probationary period, not only will that amount
of time in training be saved, but he may become a more pro-
ductive worker than he would ever have become by the slower
method. This is only a conjecture but its potential importance
makes it worth considering. Another consideration is the risk that
the increasing amount of formal education regarded as necessary
for the intending research worker may curtail his most creative
years. Possibly any such adverse effect could be offset by instruc-
tion along the lines proposed.

It is probably inevitable that any book which attempts to deal
with such a wide and complex subject will have many defects.
I hope the shortcomings of this book may provoke others whose
achievements and experience are greater than mine to write about
this subject and so build up a greater body of organised know-
ledge than is available in the literature at present. Perhaps I have
been rash in trying to deal with psychological aspects of research
without having had any formal training in psychology; but I
have been emboldened by the thought that a biologist venturing
into psychology may be in no more danger of going seriously
astray than would a psychologist or logician writing about bio-
logical research. Most books on the scientific method treat it from
the logical or philosophical aspect. This one is more concerned
with the psychology and practice of research.

I have had difficulty in arranging in a logical sequence the
many diverse topics which are discussed. The order of the chapters
on chance, hypothesis, imagination, intuition, reason and observa-
tion is quite arbitrary. The procedure of an investigation is

PREFACE

epitomised in the second section of Chapter One. Trouble has
been taken to collect anecdotes showing how discoveries have
been made, because they may prove useful to those studying the
ways in which knowledge has been advanced. Each anecdote is
cited in that part of the book where it is most apt in illustrating
a particular aspect of research, but often its interest is not limited
to the exemplification of any single point. Other anecdotes are
given in the Appendix. I apologise in advance for referring in
several places to my own experience as a source of intimate
information.

I sincerely thank many friends and colleagues to whom I am
greatly indebted for helpful suggestions, criticism and references.
The following kindly read through an early draft of the book and
gave me the benefit of their impressions : Dr. M. Abercrombie,
Dr. C. H. Andrewes, Sir Frederic Bartlett, Dr. G. K. Batchelor,
Dr. A. C. Crombie, Dr. T. K. Ewer, Dr. G. S. Graham-Smith,
Mr. G. C. Grindley, Mr. H. Lloyd Jones, Dr. G. Lapage, Sir
Charles Martin, Dr. I. Macdonald, Dr. G. L. McClymont, Dr.
Marjory Stephenson and Dr. D. H. Wilkinson. It must not be
inferred, however, that these scientists endorse all the views
expressed in the book.

PREFACE TO SECOND EDITION

It is most gratifying to be able to add now that the methods of
research outlined in this book have received endorsement by a
considerable number of scientists, both in reviews and in private
communications. I have not yet met any serious disagreement
with the main principles. Therefore it is now possible to oflfer the
book with greater confidence.

I am deeply grateful to the many well-wishers who have written
to me, some with interesting confirmation of views expressed in
the book, and some drawing attention to minor errors. The
alterations introduced in this second edition are for the most part
minor revisions but the chapter on Reason has been partly
rewritten.

Cambridge, July 1953. W.I.B.B.

XI

PREFACE

PREFACE TO THIRD EDITION

This edition differe only sUghdy from the previous one. The
opportunity has been taken to make a few alterations, mostly of
a minor nature, and add to the Appendix two good stories iUus-
trating the role of chance.

Cambridge, September 1957. W.I.B.B.

xu

CHAPTER ONE

PREPARATION

" The lame in the path outstrip the swift
who wander from it." — Francis Bacon

Study

THE research worker remains a student all his Ufe. Preparation
for his work is never finished for he has to keep abreast with
the growth of knowledge. This he does mainly by reading current
scientific periodicals. Like reading the newspapers, this study
becomes a habit and forms a regular part of the scientist's life.

The 1952 edition of the World List of Scientific Periodicals
indexes more than 50,000 periodicals. A simple calculation shows
this is equivalent to probably two million articles a year, or 40,000
a week, which reveals the utter impossibility of keeping abreast
of more than the small fraction of the Uterature which is most
pertinent to one's interest. Most research workers try to see
regularly and at least glance through the titles of the articles in
twenty to forty periodicals. As with the newspaper, they just skim
through most of the material and read fully only those articles
which may be of interest.

The beginner would be well advised to ask an experienced
research worker in his field which journals are the most important
for him to read. Abstracting journals are of limited value, if only
because they necessarily lag some considerable time behind the
original journals. They do, however, enable the scientist to cover
a wide range of Uterature and are most valuable to those who
have not access to a large number of journals. Students need
some guidance in ways of tracing references through indexing
journals and catalogues and in using libraries.

It is usual to study closely the Uterature deahng with the
particular problem on which one is going to work. However,
surprising as it may seem at first, some scientists consider that
this is unwise. They contend that reading what others have

I

THE ART OF SCIENTIFIC INVESTIGATION

written on the subject conditions the mind to see the problem in
the same way and makes it more difficuh to find a new and fruit-
ful approach. There are even some grounds for discouraging an
excessive amount of reading in the general field of science in
which one is going to work. Charles Kettering, who was associated
with the discovery of tetraethyl lead as an anti-knock agent in
motor fuels and the development of diesel engines usable in trucks
and buses, said that from studying conventional text-books we
fall into a rut and to escape from this takes as much effort as to
solve the problem. Many successful investigators were not trained
in the branch of science in which they made their most brilliant
discoveries : Pasteur, Metchnikoff and Galvani are well-known
examples. A sheepman named J. H. W. Mules, who had no
scientific training, discovered a means of preventing blowfly
attack in sheep in Australia when many scientists had failed.
Bessemer, the discoverer of the method of producing cheap steel,
said :

" I had an immense advantage over many others dealing with
the problem inasmuch as I had no fixed ideas derived from long
established practice to control and bias my mind, and did not
suffer from the general belief that whatever is, is right."

But in his case, as with many such "outsiders", ignorance and
freedom from established patterns of thought in one field were
joined with knowledge and training in other fields. In the same
vein is the remark by Bernard that " it is that which we do know
which is the great hindrance to our learning not that which we do
not know." The same dilemma faces all creative workers. Byron
wrote :

" To be perfectly original one should think much and read
little, and this is impossible, for one must have read before one
has learnt to think."

Shaw's quip " reading rots the mind " is, characteristically, not
quite so ridiculous as it appears at first.

The explanation of this phenomenon seems to be as follows.
When a mind loaded with a wealth of information contemplates
a problem, the relevant information comes to the focal point of

2

PREPARATION

thinking, and if that information is sufficient for the particular
problem, a solution may be obtained. But if that information is
not sufficient — and this is usually so in research — then that mass
of information makes it more difficult for the mind to conjure
up original ideas, for reasons which will be discussed later.
Further, some of that information may be actually false, in which
case it presents an even more serious barrier to new and pro-
ductive ideas.

Thus in subjects in which knowledge is still growing, or where
the particular problem is a new one, or a new version of one
already solved, all the advantage is with the expert, but where
knowledge is no longer growing and the field has been worked
out, a revolutionary new approach is required and this is more
Hkely to come from the outsider. The scepticism with which the
experts nearly always greet these revolutionary ideas confirms
that the available knowledge has been a handicap.

The best way of meeting this dilemma is to read critically,
striving to maintain independence of mind and avoid becoming
conventionalised. Too much reading is a handicap mainly to
people who have the wrong attitude of mind. Freshness of outlook
and originality need not suffer greatly if reading is used as a
stimulus to thinking and if the scientist is at the same time engaged
in active research. In any case, most scientists consider that it is
a more serious handicap to investigate a problem in ignorance
of what is already known about it.

One of the most common mistakes of the young scientist start-
ing research is that he believes all he reads and does not distinguish
between the results of the experiments reported and the author's
interpretation of them. Francis Bacon said :

" Read not to contradict and confute, nor to believe and take
for granted . . . but to weigh and consider." ^

The man with the right outlook for research develops a habit
of correlating what is read with his knowledge and experience,
looking for significant analogies and generalisations. This method
of study is one way in which hypotheses are developed, for
instance it is how the idea of survival of the fittest in evolution
came to Darwin and to Wallace.

Successful scientists have often been people with wide interests.

9

THE ART OF SCIENTIFIC INVESTIGATION

Their originality may have derived from their diverse knowledge.
As we shall see in a later chapter on Imagination, originality
often consists in linking up ideas whose connection was not pre-
viously suspected. Furthermore, variety stimulates freshness of
outlook whereas too constant study of a narrow field predisposes
to dullness. Therefore reading ought not to be confined to the
problem under investigation nor even to one's own field of science,
nor, indeed, to science alone. However, outside one's immediate
interests, in order to minimise time spent in reading, one can read
for the most part superficially, relying on summaries and reviews
to keep abreast of major developments. Unless the research
worker cultivates wide interests his knowledge may get narrower
and narrower and restricted to his own speciality. One of the
advantages of teaching is that it obliges the scientist to keep
abreast of developments in a wider field than he otherwise would.

It is more important to have a clear understanding of general
principles, without, however, thinking of them as fixed laws, than
to load the mind with a mass of detailed technical infonnation
which can readily be found in reference books or card indexes.
For creative thinking it is more important to see the wood than
the trees ; the student is in danger of being able to see only the
trees. The scientist with a mature mind, who has reflected a good
deal on scientific matters, has not only had time to accumulate
technical details but has acquired enough perspective to see the
wood.

Nothing that has been said above ought to be interpreted as
depreciating the importance of acquiring a thorough grounding
in the fundamental sciences. The value to be derived from super-
ficial and "skim" reading over a wide field depends to a large
extent on the reader having a background of knowledge which
enables him quickly to assess the new work reported and grasp
any significant findings. There is much truth in the saying that
in science the mind of the adult can build only as high as the
foundations constructed in youth will support.

In reading that does not require close study it is a great help
to develop the art of skim-reading. Skimming properly done
enables one to cover a large amount of literature with economy
of time, and to select those parts which are of special interest.
Some styles of writing, of course, lend themselves more to skim-

4

PREPARATION

ming than others, and one should not try to skim closely reasoned
or condensed writing or any work which one intends to make
the object of a careful study.

Most scientists find it useful to keep a card index with brief
abstracts of articles of special interest for their work. Also the
preparation of these abstracts helps to impress the salient features
of an article in the memory. After reading quickly through the
article to get a picture of the whole, one can go back to certain
parts, whose full significance is then apparent, re-read these and
make notes.

The recent graduate during his first year often studies some
further subject in order better to fit himself for research. In the
past it has been common for English-speaking research students
to study German if they had no knowledge of that language and
had already learnt French at school. In the biological sciences I
think students would now benefit more from taking a course in
biometrics, the importance of which is discussed in the next
chapter. In the past it was important to be able to read German,
but the output of Germany in the biological and medical sciences
has been very small during the last ten years, and it does not
seem likely to be considerable for some years to come. Scientists
in certain other countries, such as Scandinavia and Japan, who
previously often published in the German language, are now
publishing almost entirely in English, which, with the vast expan-
sion of science in America as well as throughout the British
Commonwealth is becoming the international scientific language.
Unless the student of biology has a special reason for wanting to
learn German, I think he could employ his time more usefully
on other matters until German science is properly revived. In this
connection it may be worth noting the somewhat unusual view
expressed by the great German chemist, Wilhelm Ostwald, who
held that the research student should refrain from learning
languages. He considered that the conventional teaching of Latin,
in particular, destroys the scientific outlook. ^'^ Herbert Spencer
has also pointed out that the learning of languages tends to
increase respect for authority and so discourage development of
the faculty of independent judgment, which is so important,
especially for scientists. Several famous scientists — including
Darwin and Einstein — had a strong distaste for Latin, probably

5

THE ART OF SCIENTIFIC INVESTIGATION

because their independent minds rebelled against developing the
habit of accepting authority instead of seeking evidence.

The views expressed in the preceding paragraph on the possible
harmful effect of learning languages are by no means widely
accepted. However, there is another consideration to be taken
into account when deciding whether or not to study a language,
or for that matter any other subject. It is that time and effort
spent in studying subjects not of great value are lost from the
study of some other subject, for the active-minded scientist is
constantly faced with what might be called the problem of com-
peting interests : he rarely has enough time to do all that he
would like to and should do, and so he has to decide what he
can afford to neglect. Bacon aptly said that we must determine
the relative value of knowledges. Cajal decries the popular idea
that all knowledge is useful; on the contrary, he says, learning
unrewarding subjects occupies valuable time if not actual space
in the mind.^^° However, I do not wish to imply that subjects
should be judged on a purely utilitarian basis. It is regrettable
that we scientists can find so little time for general Hterature.

If the student cannot attend a course in biometrics, he can
study one of the more easily understood books or articles on
the subject. The most suitable that have come to my notice
are those of G. W. Snedecor,*'^ which deals with the applica-
tion of statistics to animal and plant experimentation, and
A. Bradford HilV^ which deals mainly with statistics in human
medicine. Topley and Wilson's text-book of bacteriology con-
tains a good chapter on the application of biometrics to bacteri-
ology.^^ Professor R. A. Fisher's two books are classical works,
but some people find them too difficult for a beginning.^ ^' ^°
It is not necessary for the biologist to become an expert at
biometrics if he has no liking for the subject, but he ought
to know enough about it to avoid either undue neglect or
undue respect for it and to know when he should consult a
biometrician.

Another matter to which the young scientist might well give
attention is the technique and art of writing scientific papers.
The general standard of English in scientific papers is not high
and few of us are above criticism in this matter. The criticism
is not so much against the inelegance of the English as lack of

6

PREPARATION

clarity and accuracy. The importance of correct use of language
lies not only in being able to report research well; it is with
language that we do most of our thinking. There are several
good short books and articles on the writing of scientific papers.
Trelease'^ deals particularly with the technicalities of writing
and editing and Kapp" and Allbutt^ are mainly concerned with
the writing of suitable English. Anderson' has written a useful
paper on the preparation of illustrations and tables for scientific
papers. I have found that useful experience can be gained by
writing abstracts for publication. Thereby one becomes familiar
with the worst faults that arise in reporting scientific work and at
the same time one is subjected to a salutary discipline in writing
concisely.

The scientist will find his life enriched and his understanding
of science deepened by reading the lives and works of some of
the great men of science. Inspiration derived from this source
has given many young scientists a vision that they have carried
throughout their lives. Two excellent recent biographies I can
recommend are Ehibos' Louis Pasteur: Freelance of Science^^^
and Marquardt's Paul Ehrlich.^^^ In recent years more and more
attention is being given to the study of the history of science
and every scientist ought to have at least some knowledge of this
subject. It provides an excellent corrective to ever-increasing
specialisation and broadens one's outlook and understanding of
science. There are books which treat the subject not as a mere
chronicle of events but with an insight which gives an apprecia-
tion of the growth of knowledge as an evolutionary process
(e.g. ^°" ^^). There is a vast literature dealing with the philosophy
of science and the logic of scientific method. Whether one takes
up this study depends upon one's personal inclinations, but,
generally speaking, it will be of little help in doing research.

It is valuable experience for the young scientist to attend
scientific conferences. He can there see how contributions to
knowledge are made by building on the work of others, how
papers are criticised and on what basis, and learn something of
the personalities of scientists working in the same field as him-
self It adds considerablv to the interest of research to be
personally acquainted with the authors of the papers one reads,
or even merely to know what they look like. Conferences also

7

THE ART OF SCIENTIFIC INVESTIGATION

provide a good demonstration of the healthy democracy of
science and the absence of any authoritarianism, for the most
senior members are as Uable to be criticised as is anyone else.
Every opportunity should be taken to attend occasional special
lectures given by eminent scientists as these can often be a rich
source of inspiration. For instance, F. M. Burnet^^ said in 1944
that he had attended a lecture in 1920 by Professor Orme
Masson, a man with a real feeUng for science, who showed with
superb clarity both the coming progress in atomic physics and
the intrinsic deUght to be found in a new understanding of
things. Burnet said that although he had forgotten most of the
substance of that lecture, he would never forget the stimulus it
conveyed.

Setting about the Problem

In starting research obviously one has first to decide what prob-
lem to investigate. While this is a matter on which consultation
with an experienced research worker is necessary, if the research
student is mainly responsible for choosing his own problem
he is more likely to make a success of it. It will be something
in which he is interested, he will feel that it is all his own and
he will give more thought to it because the responsibility of
making a success of it rests on himself It is wise for him to
choose a subject within the field which is being cultivated by
the senior scientists in his laboratory. He will then be able to
benefit from their guidance and interest and his work will increase
his understanding of what they are doing. Nevertheless, if a
scientist is obliged to work on a given problem, as may be the
case in applied research, very often an aspect of real interest
can be found if he gives enough thought to it. It might even
be said that most problems are what the worker makes them.
The great American bacteriologist Theobald Smith said that
he always took up the problem that lay before him, chiefly
because of the easy access of material, without which research
is crippled. ^^ The student with any real talent for research
usually has no difficulty in finding a suitable problem. If he
has not in the course of his studies noticed gaps in knowledge,
or inconsistencies, or has not developed some ideas of his own,

8

PREPARATION

it does not augur well for his future as a research worker. It is
best for the research student to start with a problem in which
there is a good chance of his accomplishing something, and,
of course, which is not beyond his technical capabilities. Success
is a tremendous stimulus and aid to further progress whereas
continued frustration may have the opposite effect.

After a problem has been selected the next procedure is to
ascertain what investigations have already been done on it.
Text-books, or better, a recent review article, are often useful
as starting points, since they give a balanced summary of
present knowledge, and also provide the main references. A text-
book, however, is only a compilation of certain facts and hypo-
theses selected by the author as the most significant at the time of
writing, and gaps and discrepancies may have been smoothed
out in order to present a coherent picture. One must, there-
fore, always consult original articles. In each article there are
references to other appropriate articles, and trails followed up in
this way lay open the whole literature on the subject. Indexing
journals are useful in providing a comprehensive coverage of
references on any subject to within a year or so of the present,
and where they cease a search is necessary in appropriate
individual journals. The Quarterly Cumulative Index Medicus,
Zoological Record^ Index Veterinarius and the Bibliography of
Agriculture are the standard indexing journals in their respec-
tive spheres. Trained librarians know how to survey literature
systematically and scientists fortunate enough to be able to call
on their services can obtain a complete list of references on any
particular subject. It is advisable to make a thorough study of
all the relevant literature early in the investigation, for much
effort may be wasted if even only one significant article is missed.
Also during the course of the investigation, as well as watching
for new articles on the problem, it is very useful to read super-
ficially over a wide field keeping constant watch for some new
principle or technique that may be made use of

In research on infectious diseases usually the next step is to
collect as much firsthand information as possible about the
actual problem as it occurs locally. For instance, if an animal
disease is being investigated, a common procedure is to carry
out field observations and make personal enquiries from farmers.

9

THE ART OF SCIENTIFIC INVESTIGATION

This is an important prerequisite to any experimental work,
and occasionally investigators who have neglected it undertake
laboratory work which has little relation to the real problem.
Appropriate laboratory examination of specimens is usually
carried out as an adjunct to this field work.

Farmers, and probably lay people generally, not infrequently
colour their evidence to fit their notions. People whose minds are
not disciplined by training often tend to notice and remember
events that support their views and forget others. Tactful and
searching enquiry is necessary to ascertain exactly what they have
observed — to separate their observations from their interpreta-
tions. Such patient enquiry is often well repaid, for farmers have
great opportunities of gathering information. The important
discovery that ferrets are susceptible to canine distemper acose
from an assertion of a gamekeeper. His statement was at first
not taken seriously by the scientists, but fortunately they later
decided to see if there was anything in it. It is said that for
two thousand years the peasants of Italy have believed that
mosquitoes were concerned with the spread of malaria although
it was only about fifty years ago that this fact was established by
scientific investigation.

It is helpful at this stage to marshal and correlate all the data,
and to try to define the problem. For example, in investigating
a disease one should try to define it by deciding what are its
manifestations and so distinguish it from other conditions with
which it may be confused. Hughlings Jackson is reported to
have said : " The study of the causes of things must be preceded
by the study of things caused." To show how necessary this is,
there is the classical example of Noguchi isolating a spirochaete
from cases of leptospiral jaundice and reporting it as the cause of
yellow fever. This understandable mistake delayed yellow fever
investigations (but the rumour that it led to Noguchi's suicide
has no basis in fact). Less serious instances are not infrequently
seen closer at hand.

The investigator is now in a position to break the problem
down into several formulated questions and to start on the
experimental attack. EKiring the preparatory stage his mind will
not have been passively taking in data but looking for gaps
in the present knowledge, differences between the reports of

10

PREPARATION

different writers, inconsistencies between some observed aspect
of the local problem and previous reports, analogies with related
problems, and for clues during his field observations. The active-
minded investigator usually finds plenty of scope for the formula-
tion of hypotheses to explain some of the information obtained.
From the hypotheses, certain consequences can usually be proved
or disproved by experiment, or by the collection of further
observational data. After thoroughly digesting the problem in
his mind, the investigator decides on an experiment which is
likely to give the most useful information and which is within
the limitations of his own technical capacity and the resources
at his disposal. Often it is advisable to start on several aspects
of the problem at the same time. However, efforts should not
be dispersed on too wide a front and as soon as one finds some-
thing significant it is best to concentrate on that aspect of the
work.

As with most undertakings, the success of an experiment
depends largely on the care taken with preliminary preparations.
The most effective experimenters are usually those who give
much thought to the problem beforehand and resolve it into
crucial questions and then give much thought to designing experi-
ments to answer the questions. A crucial experiment is one which
gives a result consistent with one hypothesis and inconsistent with
another. Hans Zinsser writing of the great French bacteriologist,
Charles Nicolle, said :

" Nicolle was one of those men who achieve their successes by
long preliminary thought before an experiment is formulated,
rather than by the frantic and often ill-conceived experimental
activities that keep lesser men in ant-like agitation. Indeed, I have
often thought of ants in observing the quantity output of ' what-
of-it ' literature from many laboratories. . . . Nicolle did relatively
few and simple experiments. But every time he did one, it was
the result of long hours of intellectual incubation during which
all possible variants had been considered and were allowed for
in the final tests. Then he went straight to the point, without
wasted motion. That was the method of Pasteur, as it has been
of all the really great men of our calling, whose simple, conclu-
sive experiments are a joy to those able to appreciate them."^°®

Sir Joseph Barcroft, the great Cambridge physiologist, is said to
have had the knack of reducing a problem to its simplest elements

II

THE ART OF SCIENTIFIC INVESTIGATION

and then finding an answer by the most direct means. The general
subject of planning research is discussed later under the tide
" Tactics ".

SUMMARY

One of the research worker's duties is to follow the scientific
literature, but reading needs to be done with a critical, reflective
attitude of mind if originaUty and freshness of outlook are not
to be lost. Merely to accumulate information as a sort of capital
investment is not sufficient.

Scientists tend to work best on problems of their own choice
but it is advisable for the beginner to start on a problem which
is not too difficult and on which he can get expert guidance.

The following is a common sequence in an investigation on
a medical or biological problem, (a) The relevant literature is
critically reviewed. (6) A thorough collection of field data or
equivalent observational enquiry is conducted, and is supple-
mented if necessary by laboratory examination of specimens.

(c) The information obtained is marshalled and correlated and
the problem is defined and broken down into specific questions.

(d) Intelligent guesses are made to answer the questions, as many
hypotheses as possible being considered, (e) Experiments are
devised to test first the likeliest hypotheses bearing on the most
crucial questions.

12

CHAPTER TWO

EXPERIMENTATION

" The experiment serves two purposes, often independent
one from the other: it allows the observation of new facts,
hitherto either unsuspected, or not yet well defined; and it
determines whether a working hypothesis fits the world of
observable facts." — Rene J. Dubos.

Biological experiments

SCIENCE as we know it to-day may be said to date from the
introduction of the experimental method during the
Renaissance. Nevertheless, important as experimentation is in
most branches of science, it is not appropriate to all types of
research. It is not used, for instance, in descriptive biology,
observational ecology or in most forms of clinical research in
medicine. However, investigations of this latter type make use
of many of the same principles. The main difference is that
hypotheses are tested by the collection of information from
phenomena which occur naturally instead of those that are
made to take place under experimental conditions. In writing
the last part of the previous chapter and the first part of this
one I have had in mind the experimentalist, but there may be
some points of interest in these also for the purely observational
investigator.

An experiment usually consists in making an event occur under
known conditions where as many extraneous influences as possible
are eliminated and close observation is possible so that relation-
ships between phenomena can be revealed.

The " controlled experiment " is one of the most important
concepts in biological experimentation. In this there are two
or more similar groups (identical except for the inherent vari-
ability of all biological material); one, the "control" group, is
held as a standard for comparison, while the other, the " test "
group, is subjected to some procedure whose effect one wishes to

13

THE ART OF SCIENTIFIC INVESTIGATION

determine. The groups are usually formed by ' randomisation ',
that is to say, by assigning individuals to one group or the other
by drawing lots or by some other means that does not involve
human discrimination. The traditional method of experimenta-
tion is to have the groups as similar as possible in all respects
except in the one variable factor under investigation, and to
keep the experiment simple. " Vary one thing at a time and make
a note of all you do." This principle is still widely followed,
especially in animal experiments, but with the aid of modem
statistical techniques it is now possible to plan experiments to test
a number of variables at the same time.

As early as possible in an investigation, a simple crucial experi-
ment should be carried out in order to determine whether or not
the main hypothesis under consideration is true. The details
can be worked out later. Thus it is usually advisable to test the
whole before the parts. For example, before you try to reproduce
a disease with a pure culture of bacteria it is usually wise to
attempt transmission with diseased tissue. Before testing chemical
fractions for toxicity, antigenicity or some other effect, first test
a crude extract. Simple and obvious as this principle appears,
it is not infrequently overlooked and consequently time is wasted.
Another application of the same principle is that in making
a first test of the effect of some quantitative factor it is usually
advisable to determine at the outset whether any effect is pro-
duced under extreme conditions, for example, with a massive dose.

Another general principle of a rather similar kind is the process
of systematic elimination. This method is well exemplified in the
guessing game where a series of questions such as " animal,
vegetable or mineral " is asked. One can often find the unknown
more quickly by systematically narrowing down the possibiUties
than by making direct but blind guesses. This principle is used
in weighing, when weights that are too heavy and too light
are tried, and then the two extremes are gradually brought
together. The method is especially useful in seeking an unknown
substance by chemical means, but it also has many applications
in various branches of biology. In investigating the cause of a
disease, for instance, sometimes one eliminates the various
alternatives until at last a narrow field is left for one to
concentrate on.

EXPERIMENTATION

In biology it is often good policy to start with a modest
preliminary experiment. Apart from considerations of economy,
it is seldom desirable to undertake at the outset an elaborate
experiment designed to give a complete answer on all points. It
is often better for the investigation to progress from one point
to the next in stages, as the later experiments may require
modification according to the results of the earher ones. One
type of preliminary experiment is the " pilot " experiment,
which is often used when human beings or farm animals are the
subjects. This is a small-scale experiment often carried out at
the laboratory to get an indication as to whether a full-scale
field experiment is warranted. Another type of preliminary
experiment is the "sighting" experiment done to guide the
planning of the main experiment. Take, for example, the case
of an in vivo titration of an infective or toxic agent. In the
sighting experiment dilutions are widely spaced (e.g. hundred-
fold) and few animals (e.g. two) are used for each dilution.
When the results of this are available, dilutions less widely
spaced (e.g. fivefold) are chosen just staggering the probable
end-point, and larger groups of animals (e.g. five) are used. In
this way one can attain an accurate result with the minimum
number of animals.

The so-called " screening " test is also a type of preliminary
experiment. This is a simple test carried out on a large number
of substances with the idea of finding out which of them warrant
further trial, for example, as therapeutic agents.

Occasionally quite a small experiment, or test, can be arranged
so as to get a provisional indication as to whether there is any-
thing in an idea which alone is based on evidence too slender
to justify a large experiment. A sketchy experiment of this nature
sometimes can be so planned that the results will be of some
significance if they turn out one way though of no significance
if the other way. However, there is a minimum below which
it is useless to reduce the " set up " of even a preliminary
experiment. If the experiment is worth doing at all it must be
planned in such a way that it has at least a good chance of
giving a useful result. The young scientist is often tempted
through impatience, and perhaps lack of resources, to rush in
and perform ill-planned experiments that have httle chance of

15

THE ART OF SCIENTIFIC INVESTIGATION

giving significant results. Sketchy experiments are only justifiable
when preliminary to more elaborate experiments planned to
give a reUable result. Each stage of the investigation must be
established beyond reasonable doubt before passing on to the
next, or else the work may be condemned, quite properly, as
being "sloppy".

The essence of any satisfactory experiment is that it should
be reproducible. In biological experiments it not infrequently
happens that this criterion is difficult to satisfy. If the results of
the experiment vary even though the known factors have not
been altered, it often means that some unrecognised factor or
factors is affecting the results. Such occurrences should be
welcomed, because a search for the unknown factor may lead
to an interesting discovery. As a colleague remarked to me
recently : " It is when experiments go wrong that we find things
out." However, first one should see if a mistake has been made,
as a technical error is the most common explanation.

In the execution of the experiment it is well worth while
taking the greatest care with the essential points of technique.
By taking great pains and paying careful attention to the im-
portant details the originator of a new technical method some-
times is able to obtain results which other workers, who are less
familiar with the subject or less painstaking, have difficulty in
repeating. It is in this connection that Carlyle's remark that
genius is an infinite capacity for taking pains is true. A good
example is provided by Sir Almroth Wright's selection of the
Rawlings strain of typhoid bacillus when he introduced vaccina-
tion against that disease. Only quite recently, since certain
techniques have become available, has it been found that the
Rawlings strain was an exceptionally good strain for use in making
vaccine. Wright had carefully chosen the strain for reasons which
most people would have considered of no consequence. Theobald
Smith, one of the few really great bacteriologists, said of
research :

" It is the care we bestow on apparently trifling, unattractive

and very troublesome minutiae which determines the result." ^^

Some discrimination, however, should be used, for it is possible
to waste time in elaborating unnecessary detail on unimportant
aspects of the work.

i6

EXPERIMENTATION

The careful recording of all details in experimental work is
an elementary but important rule. It happens surprisingly often
that one needs to refer back to some detail whose significance
one did not realise when the experiment was carried out. The
notes kept by Louis Pasteur afford a beautiful example of the
careful recording of every detail. Apart from providing an
invaluable record of what is done and what observed, note-
taking is a useful technique for prompting careful observation.

The experimenter needs to have a proper understanding of
the technical methods he uses and to realise their limitations and
the degree of accuracy attainable by each. It is essential to be
thoroughly famihar with laboratory methods before using them
in research and to be able to obtain consistent and reUable results.
There are few methods that cannot at times go wrong and
give misleading results and the experimenter should be able
to detect trouble of this nature quickly. Where practicable,
estimations and titrations of crucial importance should be checked
by a second method. The scientist must also understand his
apparatus. Modem complicated apparatus is often convenient
but it is not always foolproof, and experienced scientists often
tend to avoid it because they fear it may give misleading results.

Difficulties often arise in organising experiments with subjects
over which there is only limited control — human beings or
valuable farm animals. Unless the basic needs of the controlled
experiment can be satisfied it is better to abandon the attempt.
Such a statement may appear self-evident, but not infrequently
investigators find the difficulties too great and compromise on
some arrangement that is useless. Large numbers in no way offset
the necessity of a satisfactory control group. The outstanding
illustration is supplied by the story of B.C.G. vaccination in
children. This procedure was introduced twenty-five years ago
and was then claimed to protect people against tuberculosis; but
although a large number of experiments have since been carried
out, there is still to-day controversy as to its value in preventing
the disease in people of European stock. Most of the experiments
have proved nothing because the controls were not strictly
comparable. The review on B.C.G. vaccination by Professor
G. S. Wilson provides a good lesson in the difficulties and pitfalls
of experimentation. He concludes :

17

THE ART OF SCIENTIFIC INVESTIGATION

" These results show how important it is when carrying out a
controlled investigation on human subjects to do everything
possible to ensure that the vaccinated and control children are
similar in every respect, including such factors as age, race, sex,
social, economic and housing conditions, intellectual level and
co-operativeness of the parents, risk of exposure to infection,
attendance at infant welfare or other clinics and treatment when

in." 106

Professor Wilson has pointed out to me in conversation that
unless decisive experiments are done before an alleged remedy
is released for use in human medicine, it is almost impossible
subsequently to organise an experiment with untreated controls,
and so the alleged remedy becomes adopted as a general practice
without anyone knowing if it is really of any use at all. For
example, Pasteur's rabies treatment has never been proved by
proper experiment to prevent rabies when given to persons after
they are bitten and some authorities doubt if it is of any value,
but it is impossible now to conduct a trial in which this treatment
is withheld from a control group of bitten persons.

Sometimes it is a necessary part of a field experiment to keep
the groups in different surroundings. In such experiments one
cannot be sure that any differences observed are due to the
particular factor under scrutiny and not to other variables
associated with the different environments. This difficulty can
sometimes be met by replicating both test and control groups
so that any effects due to environment will be exposed and
perhaps cancel out. If variables which are recognised but thought
to be extraneous cannot be eliminated, it may be necessary to
employ a series of control groups, or carry out a series of experi-
ments, in order to isolate experimentally each known difference
between the two populations being compared.

Whenever possible the results of experiments should be assessed
by some objective measurement. However, occasionally this
cannot be done, as for instance where the results concern the
severity of clinical symptoms or the comparison of histological
changes. When there is a possibility of subjective influences
affecting the assessment of results, it is important to attain
objectivity by making sure that the person judging the results
does not know to which group each individual belongs. No

i8

EXPERIMENTATION

matter how objectively minded the scientist may believe him-
self to be, it is very difficult to be sure that his judgment
may not be subconsciously biased if he knows to which group
the cases belong when he is judging them. The conscientious
experimenter, being aware of the danger, may even err by
biasing his judgment in the direction contrary to the expected
result. Complete intellectual honesty is, of course, a first essential
in experimental work.

When the experiment is complete and the results have been
assessed, if necessary with the aid of biometrics, they are
interpreted by relating them to all that is already known about
the subject.

Planning and assessing experiments

Biometrics, or biostatistics, the application of the methods of
mathematical statistics to biology, is a comparatively new branch
of science and its importance in research has only lately won
general recognition. Books dealing with this subject have been
mentioned in Chapter One and I do not intend to do more here
than call attention to a few generalities and stress the need for
the research worker to be acquainted at least with the general
principles. Some knowledge of statistical methods is necessary
for any form of experimental or observational research where
numbers are involved, but especially for the more complex
experiments where there is more than one variable.

One of the first things which the beginner must grasp is that
statistics need to be taken into account when the experiment is
being planned, or else the results may not be worth treating
statistically. Therefore biometrics is concerned not only with the
interpretations of results but also with the planning of experi-
ments. It is now usually taken as including, besides the purely
statistical techniques, also the wider issues involved in their appli-
cation to experimentation such as the general principles of the
design of experiments and the logical issues concerned. Sir
Ronald Fisher, who has done so much to develop biometrical
methods, discusses these topics in his book, The Design of
Experiments.^^

In selecting control and test groups, logic and common sense
have first to be satisfied. A common fallacy, for instance, is to
compare groups separated by time — the data of one year being

19

THE ART OF SCIENTIFIC INVESTIGATION

compared to data obtained in previous years. Evidence obtained
in this way is never conclusive, though it may be usefully sugges-
tive. "If when the tide is falling you take out water with a
twopenny pail, you and the moon can do a great deal." In
biological investigations there may be many unsuspected factors
that influence populations separated by time or geographically.
When general considerations have been satisfied, statistical
methods are used to decide on the necessary size of the groups,
to select animals according to weight, age, etc. and, while taking
these particulars into account, to distribute the animals into groups
without sacrificing the principle of random selection.

No two groups of animals or plants are ever exactly similar,
owing to the inherent variabihty of biological material. Even
though great pains are taken to ensure that all individuals in
both groups are nearly the same in regard to sex, age, weight,
breed, etc., there will always be variation that depends on factors
not yet understood. It is essential to realise the impossibility of
obtaining exactly similar groups. The difficulty must be met by
estimating the variability and taking it into account when assess-
ing the results. Within reasonable limits it is desirable to choose
the animals for an experiment showing little variability one with
another, but it is not essential to go to great lengths to achieve
this. Its purpose is to increase the sensitivity of the experiment,
but this can be done in other ways, such as by increasing the
numbers in the groups. There are mathematical techniques for
making corrections in certain cases for diflferences between
individuals or groups.

Another method of meeting the difficulty of variability in
experimental animals is by " pairing " : the animals are arrayed
in pairs closely resembling each other ( perhaps pairs of twins or
litter mates). Each animal is compared only with its fellow and
thus a series of experimental results is obtained. By using identical
twins one can often effect great economy in numbers, which is
important in investigations on animals that are expensive to buy
and keep. Experiments carried out in New Zealand on butterfat
yield showed that as much information was obtained per pair
of identical twin cows as from two groups each of 55 cows. In
experiments with growth rates, identical twins were about 25
times more useful than ordinary calves.*

20

EXPERIMENTATION

When testing out a procedure for the first time it is often
impossible to estimate in advance how many animals are required
to ensure a decisive result. If expensive animals are involved
economy may be effected by doing a test first with a few animals
and repeating the test until the accumulated results are sufficient
to satisfy statistical requirements.

One of the basic conceptions in statistics is that the individuals
in the group under scrutiny are a sample of an infinitely large,
hypothetical population. Special techniques are available for
random samphng and for estimating the necessary size of the
sample for it to be representative of the whole. The number
required in the sample depends on the variability of the material
and on the degree of error that will be tolerated in the results,
that is to say, on the order of accuracy required.

Fisher considers that in the past there has been too much
emphasis placed on the importance of varying only one factor
at a time in experimentation and shows that there are distinct
advantages in planning experiments to test a number of variables
at the same time. Appropriate mathematical techniques enable
several variables to be included in the one experiment, and this
not only saves time and effort, but also gives more information
than if each variable were treated separately. More information
is obtained because each factor is examined in the light of a
variety of circumstances, and any interaction between the factors
may be detected. The traditional method of experimental isola-
tion of a single factor often involves a somewhat arbitrary
definition of that factor and the testing of it under restricted,
unduly simphfied circumstances. Complex, multiple factor experi-
ments, however, are not so often applicable to work with animals
as to work with plants, although they can be used with advantage
in feeding trials where various combinations of several com-
ponents in the ration are to be tested.

Statistics, of course, like any other research technique, has
its uses and its limitations and it is necessary to understand its
proper place and function in research. It is mainly valuable in
testing an hypothesis, not in initiating a discovery. Discoveries
may originate from taking into consideration the merest hints,
the slightest diflferences in the figures between different groups,
suggesting something to be followed up; whereas statistics are

21

THE ART OF SCIENTIFIC INVESTIGATION

usually concerned with carefully pre-arranged experiments set up
to test an idea already bom. Also, in trying to provide sufficient
data for statistical analysis, the experimenter must not be tempted
to do so at the expense of accurate observation and of care w^ith
the details of the experiment.

The use of statistics does not lessen the necessity for using
common sense in interpreting results, a point which is sometimes
forgotten. Fallacy is especially likely to arise in dealing with field
data in which there may be a significant difference between two
groups. This does not necessarily mean that the difference is
caused by the factor which is under consideration because
possibly there is some other variable whose influence or import-
ance has not been recognised. This is no mere academic possi-
bility, as is shown for example by the confusion that has arisen
in many experiments with vaccination against tuberculosis, the
common cold and bovine mastitis. Better hygienic measures
and other circumstances which may influence the results are
often coupled with vaccination. Statistics may show that people
who smoke do not on the average five as long as people who do
not smoke but that does not necessarily mean that smoking
shortens life. It may be that people who do not smoke take more
care of their health in other and more important ways. Such
fallacies do not arise in well designed experiments where the
initial process of randomisation ensures a valid comparison of
the groups.

The statistician, especially if he is not also a biologist, may be
inclined to accept data given him for analysis as more reliable
than they really are, or as being estimated to a higher degree of
accuracy than was attempted. The experimenter should state
that measurements have been made only to the nearest centi-
metre, gram or whatever was the unit. It is helpful for the
statistician to have had some personal experience of biological
experimentation and he ought to be thoroughly familiar with all
aspects of experiments on which he is advising. Close co-opera-
tion between the statistician and the biologist can often enable
enlightened common sense to by-pass a lot of abstruse mathe-
matics.

Occasionally scientific reports are marred by the authors
giving their results only as averages. Averages often convey

22

EXPERIMENTATION

little information and may even be misleading. The frequency
distribution should be given and some figures relating to indiv-
iduals are often helpful in giving a complete picture. Graphs also
can be misleading and the data on which they are based needs
to be examined critically. If the plotted points on a graph are
not close together — that is, if the observations have not been
made at frequent intervak — it is not always justifiable to connect
them with straight or curved lines. Such lines may not represent
the true position, for one does not know what actually occurred
in the interval. There may, for instance, have been an unsuspected
rise and fall.

Misleading experiments

Some of the hazards associated with the use of reason, hypo-
thesis and observation in research are discussed in the appropriate
chapters of this book. As a corrective to any tendency to put
excessive faith in experimentation, it is as well here to remind
the reader that experiments also can at times be quite misleading.
The most common cause of error is a mistake in technique.
Reliance cannot be placed on results unless the experimenter is
thoroughly competent and familiar with the technical procedures
he uses. Even in the expert's hands technical methods have to be
constantly checked against known " positive " and " negative "
specimens. Apart from technical slips, there are more subtle
reasons why experiments sometimes " go wrong ".

John Hunter deliberately infected himself with gonorrhoea to
find out if it was a distinct disease from syphilis. Unfortunately
the material he used to inoculate himself contained also the
syphilis organism, with the result that he contracted both diseases
and so established for a long time the false behef that both were
manifestations of the same disease. Needham's experiments with
flasks of broth led himself and others to believe that spontaneous
generation was possible. Knowledge at the time was insufficient
to show that the fallacy arose either from accidental contamina-
tion or insufficient heating for complete sterilisation. In recent
years we have seen an apparently weU-conducted experiment
prove that patulin has therapeutic value against the common cold.
Statistical requirements were well satisfied. But no one since has

23

THE ART OF SCIENTIFIC INVESTIGATION

been able to show any benefit from patulin and why it seemed
to be efficacious in the first experiment remains a mystery.^*

When I saw a demonstration of what is known as the Mules
operation for the prevention of blowfly attack in sheep, I realised
its significance and my imagination was fired by the great
potentialities of Mules' discovery. I put up an experiment involv-
ing thousands of sheep and, without waiting for the results,
persuaded colleagues working on the blowfly problem to carry
out experiments elsewhere. When about a year later, the results
became available, the sheep in my trial showed no benefit from
the operation. The other trials, and all subsequent ones, showed
that the operation conferred a very valuable degree of protec-
tion and no satisfactory explanation could be found for the
failure of my experiment. It was fortunate that I had enough
confidence in my judgment to prevail upon my colleagues to put
up trials in other parts of the country, for if I had been more
cautious and awaited my results they would probably have
retarded, the adoption of the operation for many years.

Several large-scale experiments in the U.S.A. proved that
immunisation greatly reduced the incidence of influenza in 1 943
and again in 1945, yet in 1947 the same type of vaccine failed.
Subsequently it was found that this failure was due to the 1947
strain of virus being different from those current in earher years
and used in making the vaccine.

It is not at all rare for scientists in different parts of the world
to obtain contradictory results with similar biological material.
Sometimes these can be traced to unsuspected factors, for
instance, a great difference in the reactions of guinea-pigs to diph-
theria toxin was traced to a difference in the diets of the animals.
In other instances it has not been possible to discover the
cause of the disagreement despite a thorough investigation. In
Dr. Monroe Eaton's laboratory in the United States influenza
virus can be made to spread from one mouse to another, but in
Dr. C. H. Andrewes' laboratory in England this cannot be
brought about, even though the same strains of mice and virus,
the same cages and an exactly similar technique are used.

We must remember that, especially in biology, experimental
results are, strictly speaking, only valid for the precise conditions
under which the experiments were conducted. Some caution is

24

EXPERIMENTATION

necessary in drawing conclusions as to how widely applicable
are results obtained under necessarily limited sets of circum-
stances.

Darwin once said half seriously, " Nature will tell you a direct
lie if she can." Bancroft points out that all scientists know from
experience how difficult it often is to make an experiment come
out correctly even when it is known how it ought to go. There-
fore, he says, too much trust should not be put in an experiment
done with the object of getting information.^"

The examples quoted are experiments which gave results that
were actually " wrong " or misleading. Fortunately they are
exceptional. Commoner, however, is the failure of an experiment
to demonstrate something because the exact conditions necessary
are not known, such as Faraday's early repeated failures to obtain
an electric current by means of a magnet. Such experiments
demonstrate the well-known difficulty of proving a negative
proposition, and the folly of drawing definite conclusions from
them is usually appreciated by scientists. It is said that some
research institutes deliberately destroy records of " negative
experiments ", and it is a commendable custom usually not to
publish investigations which merely fail to substantiate the hypo-
thesis they were designed to test.

SUMMARY

The basis of most biological experimentation is the controlled
experiment, in which groups, to which individuals are assigned at
random, are comparable in all respects except the treatment under
investigation, allowance being made for the inherent variability
of biological material. Two useful principles are to test the whole
before the part, and to ehminate various possibilities systemati-
cally. In the execution of an experiment close attention to detail,
careful note-taking and objectivity in the reading of results are
important.

Biometrics is concerned with the planning of experiments
as well as the interpretation of results. A basic concept in
biometrics is that there is an infinitely large, hypothetical popula-
tion of which the experimental group or data are a random
sample. The difficulty presented by the inherent variability of

25

THE ART OF SCIENTIFIC INVESTIGATION

biological material is circumvented by estimating the variability
and taking it into account when assessing the results.

Experimentation, like other measures employed in research, is
not infallible. Inability to demonstrate a supposition experi-
mentally does not prove that it is incorrect.

26

CHAPTER THREE

CHANCE

" Chance favours only those who know
how to court her." — Charles Nicolle

Illustrations

IT WILL be simpler to discuss the role of chance in research if
we first consider some illustrative examples of discoveries in
which it played a part. These anecdotes have been taken from
sources believed to be authentic, and one reference is quoted
for each although in many instances several sources have been
consulted. Only ten are included in this section but seventeen
others illustrating the role of chance are to be found in the
Appendix.

Pasteur's researches on fowl cholera were interrupted by the
vacation, and when he resumed he encountered an unexpected
obstacle. Nearly all the cultures had become sterile. He attempted
to revive them by sub-inoculation into broth and injection into
fowls. Most of the sub-cultures failed to grow and the birds
were not affected, so he was about to discard everything and
start afresh when he had the inspiration of re-inoculating the
same fowls with a fresh culture. His colleague Duclaux relates :

" To the surprise of all, and perhaps even of Pasteur, who was
not expecting such success, nearly all these fowls withstood the
inoculadon, although fresh fowls succumbed after the usual
incubation period."

This resulted in the recognition of the principle of immunisation
with attenuated pathogens.^ ^

The most important method used in staining bacteria is that
discovered by the Danish physician G. Gram. He described how
he discovered the method fortuitously when trying to develop a
double stain for kidney sections. Hoping to stain the nuclei violet
and the tubules brown, he used gentian violet followed by iodine

27

THE ART OF SCIENTIFIC INVESTIGATION

solution. Gram found that after this treatment the tissue was
rapidly decolourised by alcohol but that certain bacteria remained
blue-black. The gentian violet and iodine had unexpectedly
reacted with each other and with a substance present in some
bacteria and not others, thus providing not only a good stain but
also a simple test which has proved of the greatest value in
distinguishing different bacteria. ^°^

While engaged in studying the function of the pancreas in
digestion in 1889 at Strasbourg, Professors von Mering and
Minkowski removed that organ from a dog by operation. Later
a laboratory assistant noticed that swarms of flies were attracted
by the urine of the operated dog. He brought this to the attention
of Minkowski, who analysed the urine and found sugar in it.
It was this finding that led to our understanding of diabetes and
its subsequent control by insulin. ^^ More recently the Scotsman,
Shaw Dunn, was investigating the cause of the kidney damage
which follows a severe crush injury to a limb. Among other
things he injected alloxan and he found that it caused necrosis
of the islet tissue of the pancreas. This unexpected finding has
provided a most useful tool in the study of diabetes.^^

The French physiologist, Charles Richet, was testing an extract
of the tentacles of a sea anemone on laboratory animals to
determine the toxic dose when he found that a small second dose
given some time after the first was often promptly fatal. He
was at first so astounded at this result that he could hardly believe
that it was due to anything he had done. Indeed he said it was
in spite of himself that he discovered induced sensitisation or
anaphylaxis and that he would never have believed that it was
possible." Another manifestation of the same phenomenon was
discovered independently by Sir Henry Dale. He was applying
serum to strips of involuntary muscle taken from guinea-pigs
when he encountered one that reacted violently to the application
of horse serum. Seeking an explanation of this extraordinary
observation he found that that guinea-pig had some time
previously been injected with horse serum. ^^

It was the usual practice among physiologists to use physio-
logical saline as a perfusion fluid during experiments on isolated
frogs' hearts. By this means they could be kept beating for
perhaps half an hour. Once at the London University College

28

CHANCE

Hospital a physiologist was surprised and puzzled to find his
frogs' hearts continued to beat for many hours. The only possible
explanation he could think of was that it was a seasonal effect
and this he actually suggested in a report. Then it was found
that the explanation was that his laboratory assistant had used
tap water instead of distilled water to make up the saline solution.
With this clue it was easy to determine what salts in the tap
water were responsible for the increased physiological activity.
This was what led Sidney Ringer to develop the solution which
bears his name and which has contributed so much to experi-
mental physiology. ^^

Dr. H. E. Durham has left the following written account of
the discovery of agglutination of bacteria by antiserum.

"It was a memorable morning in November 1894, when we
had all made ready with culture and serum provided by Pfeiffer
to test his diagnostic reaction in vivo. Professor Gruber called out
to me ' Durham ! Kommen Sie her, schauen Sie an ! ' Before
making our first injection with the mixtures of serum and vibrios,
he had put a specimen under the microscope and there agglutina-
tion was displayed. A few days later, we had been making our
mixtures in small sterilised glass pots, it happened that none
were ready sterilised, so I had to make use of sterile test-tubes;
those containing the mixture of culture and serum were left
standing for a short time and then I called, ' Herr Professor !
Kommen Sie her, schauen Sie an! ' the phenomenon of sedi-
mentation was before his eyes! Thus there were two techniques
available, the microscopic and the macroscopic."

The discovery was quite unexpected and not anticipated by any
hypothesis. It occurred incidentally in the course of another
investigation, and macroscopic agglutination was found owing
to the fortuitous lack of sterilised glass pots. [I am indebted to
Professor H. R. Dean for showing me Durham's manuscript.]
Gowland Hopkins, whom many consider the father of bio-
chemistry, gave his practical class a certain well-known test for
proteins to carry out as an exercise, but all the students failed to
elicit the reaction. Investigation revealed that the reaction was
only obtained when the acetic acid employed contained an
impurity, glyoxylic acid, which thereafter became the standard
test reagent. Hopkins followed up this clue further and sought

29

THE ART OF SCIENTIFIC INVESTIGATION

the group in the protein with which the glyoxylic acid reacted,
and this led him to his famous isolation of tryptophane.^*

When Weil and Felix were investigating cases of louse-borne
typhus in Poland in 19 15 they isolated the bacterium known as
" Proteus X " from some patients. Thinking it might be the
cause of the disease they tried agglutination of the organism
with the patients' sera and obtained positive results. It was then
found that Proteus X was not the causal organism of the disease ;
nevertheless agglutination of this organism proved to be a reliable
and most valuable means of diagnosing typhus. In the course
of their experimental study of this serological reaction Weil and
Felix identified the O and H antigens and antibodies, and this
discovery in turn opened up a completely new chapter in serology.
Later it was found that in Malaya those cases of typhus con-
tracted in the scrub failed to show agglutination to Proteus X19.
Strangely enough a new strain of Proteus, obtained from England
and beUeved to be a typical strain of Proteus X19, agglutinated
with sera from cases of scrub typhus but not with sera from the
cases contracted in the town (shop typhus), which were reacting
satisfactorily with the Proteus X19 strain that had been used in
many parts of the world. Later it transpired that scrub typhus
and shop typhus were two different rickettsial diseases. How it
came about that the strain of Proteus sent out from England
was not only not typical Proteus X19, but had changed to just
what was wanted to diagnose the other disease, remains a
profound mystery. ^^

Agglutination of red blood cells of the chick by influenza virus
was first observed quite unexpectedly by Hirst and independently
by McClelland and Hare when they were examining chick
embryos infected with the virus. Fluid containing virus got mixed
with blood cells which became agglutinated and the alert and
observant scientists quickly followed up this clue. The discovery
of this phenomenon has not only revolutionised much of our
technique concerned with several viruses, but has opened up a
method of approach to fundamental problems of virus-cell
relationships.^^' ^" Following this discovery, other workers tried
haemagglutination with other viruses and Newcastle disease, fowl
plague and vaccinia were found to produce the phenomenon.
However it was again by chance observation that haemagglutina-

30

CHANCE

tion with the virus of mumps and later of mouse pneumonia
was discovered.

Rickettsiae (microbes closely related to viruses) cause typhus
and several other important diseases and are difficult to cultivate.
Dr. Herald Cox spent much time and effort trying to improve on
methods of growing them in tissue culture and had tried adding
all sorts of extracts, vitamins and hormones without achieving
anything. One day while setting up his tests he ran short of chick
embryo tissue for tissue culture, so to make up the balance he
used yolk sac which previously he, like everyone else, had
discarded. When he later examined these cultures, to his "amaze-
ment and surprise", he found terrific numbers of the organisms
in those tubes where he had happened to put yolk sac. A few
nights later while in bed the idea occurred to him of inoculating
the rickettsiae directly into the yolk sac of embryonated eggs.
Getting out of bed at 4 a.m. he went to the laboratory and made
the first inoculation of rickettsiae into the yolk sac. Thus was
discovered an easy way of growing masses of rickettsiae, which
has revolutionised the study of the many diseases they cause and
made possible the production of effective vaccines against them.
[Personal communication.]

Role of chance in discovery

These ten examples, together with nineteen others given in the
Appendix and some of those in Chapters Four and Eight provide
striking illustration of the important part that chance plays in
discovery. They are the more remarkable when one thinks of the
failures and frustrations usually met in research. Probably the
majority of discoveries in biology and medicine have been come
upon unexpectedly, or at least had an element of chance in them,
especially the most important and revolutionary ones. It is scarcely
possible to foresee a discovery that breaks really new ground,
because it is often not in accord with current beliefs. Frequently
I have heard a colleague, relating some new finding, say almost
apologetically, " I came across it by accident." Although it is
common knowledge that sometimes chance is a factor in the
making of a discovery, the magnitude of its importance is seldom
realised and the significance of its role does not seem to have
been fully appreciated or understood. Books have been written on

31

THE ART OF SCIENTIFIC INVESTIGATION

scientific method omitting any reference to chance or empiricism
in discovery.

Perhaps the most striking examples of empirical discoveries are
to be found in chemotherapy where nearly all the great discoveries
have been made by following a false hypothesis or a so-called
chance observation. Elsewhere in this book are described the
circumstances in which were discovered the therapeutic effects of
quinine, salvarsan, sulphanilamide, diamidine, paraminobenzoic
acid and penicillin. Subsequent rational research in each case
provided only relatively small improvements. These facts are the
more amazing when one thinks of the colossal amount of rational
research that has been carried out in chemotherapy.

The research worker should take advantage of this knowledge
of the importance of chance in discovery and not pass over it
as an oddity or, worse, as something detracting from the credit
due to the discoverer and therefore not to be dwelt upon.
Although we cannot deliberately evoke that will-o'-the-wisp,
chance, we can be on the alert for it, prepare ourselves to
recognise it and profit by it when it comes. Merely realising the
importance of chance may be of some help to the beginner. We
need to train our powers of observation, to cultivate that attitude
of mind of being constantly on the look-out for the unexpected
and make a habit of examining every clue that chance presents.
Discoveries are made by giving attention to the slightest clue.
That aspect of the scientist's mind which demands convincing
evidence should be reserved for the proof stage of the investiga-
tion. In research, an attitude of mind is required for discovery
which is different from that required for proof, for discovery and
proof are distinct processes. We should not be so obsessed with
our hypothesis that we miss or neglect anything not directly
bearing on it. With this in mind, Bernard insisted that, although
hypotheses are essential in the planning of an experiment, once
the experiment is commenced the observer should forget his
hypothesis. People who are too fond of their hypotheses, he said,
are not well fitted for making discoveries. The anecdote (related
in Chapter Eight) about Bernard's work starting from the
observation that the rabbits passed clear urine, provides a beauti-
ful example of discovery involving chance, observation and a
prepared mind.

32

CHANCE

A good maxim for the research man is " look out for the
unexpected."

It is unwise to speak of luck in research as it may confuse our
thinking. There can be no objection to the word when it is used
to mean merely chance, but for many people luck is a meta-
physical notion which in some mystical way influences events, and
no such concept should be allowed to enter into scientific thinking.
Nor is chance the only factor involved in these unexpected
discoveries, as we shall discuss more fully in the next section.
In the anecdotes cited, many of the opportunities might well
have been passed over had not the workers been on the look-out
for anything that might arise. The successful scientist gives
attention to every unexpected happening or observation that
chance offers and investigates those that seem to him promising.
Sir Henry Dale has aptly spoken of opportunism in this con-
nection. Scientists without the flair for discovery seldom notice or
bother with the unexpected and so the occasional opportunity
passes without them ever being aware of it. Alan Gregg
wrote :

" One wonders whether the rare ability to be completely atten-
tive to, and to profit by, Nature's slightest deviation from the
conduct expected of her is not the secret of the best research
minds and one that explains why some men turn to most remark-
ably good advantage seemingly trivial accidents. Behind such
attention lies an unremitting sensitivity."'*^

Writing of Charles Darwin, his son said :

" Everybody notices as a fact an exception when it is striking
and frequent, but he had a special instinct for arresting an
exception. A point apparently slight and unconnected with his
present work is passed over by many a man almost unconsciously
with some half considered explanation, which is in fact no explan-
ation. It was just these things that he seized on to make a start
from." 28

It is of the utmost importance that the role of chance be
clearly understood. The history of discovery shows that chance
plays an important part, but on the other hand it plays only
one part even in those discoveries attributed to it. For this
reason it is a misleading half-truth to refer to unexpected dis-
coveries as " chance discoveries " or " accidental discoveries ".

33

THE ART OF SCIENTIFIC INVESTIGATION

If these discoveries were made by chance or accident alone,
as many discoveries of this type would be made by any
inexperienced scientist starting to dabble in research as by
Bernard or Pasteur. The truth of the matter lies in Pasteur's
famous saying : "In the field of observation, chance favours
only the prepared mind." It is the interpretation of the chance
observation which counts. The role of chance is merely to
provide the opportunity and the scientist has to recognise it and
grasp it.

Recognising chance opportunities

In reading of scientific discoveries one is sometimes struck
by the simple and apparently easy observations which have given
rise to great and far-reaching discoveries making scientists
famous. But in retrospect we see the discovery with its significance
established. Originally the discovery usually has no intrinsic
significance; the discoverer gives it significance by relating it
to other knowledge, and perhaps by using it to derive further
knowledge. The difficulties in the way of making discoveries
in which chance is involved may be discussed under the following
headings.

(a) Infrequency of opportunities. Opportunities, in the form
of significant clues, do not come very often. This is the only
aspect aflfected by sheer chance, and even here the scientist does
not play a purely passive role. The successful researchers are
scientists who spend long hours working at the bench, and who
do not confine their activities to the conventional but try out
novel procedures, therefore they are exposed to the maximum
extent to the risk of encountering a fortunate " accident ".

(b) Noticing the clue. Acute powers of observation are often
required to notice the clue, and especially the ability to remain
alert and sensitive for the unexpected while watching for the
expected. Noticing is discussed at length in the chapter on
observation, and it need only be said here that it is mainly a
mental process.

(c) Interpreting the clue. To interpret the clue and grasp its
possible significance is the most difficult phase of all and requires
the " prepared mind ". Let us consider some instances of
failure to grasp opportunities. The history of discovery teems

34

CHANCE

with instances of lost opportunities — clues noticed but their
significance not appreciated. Before Rontgen discovered X-rays,
at least one other physicist had noticed evidence of the rays
but was merely annoyed. Several people now recall having
noticed the inhibition of staphylococcal colonies by moulds
before Fleming followed it up to discover penicillin. Scott, for
instance, reports that he saw it and considered it only a nuisance
and he protests against the view that Fleming's discovery was
due to chance, for, he says, it was due mainly to his perspicacity
in seizing on the opportunity others had let pass.*^ Another
interesting case is related by J. T. Edwards. ^^ In 19 19 he noticed
that one of a group of cultures of Brucella abortus grew much
more luxuriantly than the others and that it was contaminated
with a mould. He called the attention of Sir John M'Fadyean
to this, suggesting it might be of significance, but was greeted
with scorn. It was not till later that it was discovered that
Br. abortus grew much better in the presence of CO2, which
explains why Edwards' culture had grown much better in the
presence of the mould. Bordet and others had casually noticed
agglutination of bacteria by antisera, but none had seen the
possibilities in it until Gruber and Durham did. Similarly,
others had seen the phenomenon of bacteriophage lysis before
Twort and D'Herelle. F. M. Burnet for one now admits having
seen agglutination of chick embryos' red blood cells in the
presence of influenza virus and probably others had too but
none followed it up till G. K. Hirst, and McClelland and Hare.
Many bacteriologists had seen rough to smooth colony variation
in bacteria before Arkwright investigated it and found it to be
associated with change in virulence and antigenicity. It is now,
of course, one of the fundamental facts in immunology and
serology.

Sometimes the significance of the clue which chance brings
our way is quite obvious, but at others it is just a trivial incident
of significance only for the well prepared mind, the mind loaded
with relevant data and ripe for discovery. When the mind has
a lot of relevant but loosely connected data and vague ideas, a
clarifying idea connecting them up may be helped to crystallise
by some small incident. Just as a substance may crystallise out
of solution in the presence of a nucleus consisting of a minute

35

THE ART OF SCIENTIFIC INVESTIGATION

crystal with the correct configuration, so did the falling apple
provide a model for Newton's mind. Sir Henry Souttar has
pointed out that it is the content of the observer's brain,
accumulated by years of work, that makes possible the moment
of triumph. This aspect of chance observation will be discussed
further in the chapters on observation and on intuition.

Anyone with an alertness of mind will encounter during the
course of an investigation numerous interesting side issues that
might be pursued. It is a physical impossibility to follow up all
of these. The majority are not worth following, a few will reward
investigation and the occasional one provides the opportunity of
a lifetime. How to distinguish the promising clues is the very
essence of the art of research. The scientist who has an indepen-
dent mind and is able to judge the evidence on its merits rather
than in light of prevailing conceptions is the one most likely to
be able to realise the potentialities in something really new. He
also needs imagination and a good fund of knowledge, to know
whether or not his observation is new and to enable him to see
the possible implications. In deciding whether a Hne of work
should be followed, one should not be put off it merely because
the idea has already been thought of by others or even been tried
without it leading anywhere. This does not necessarily indicate
that it is not good; many of the classic discoveries were
anticipated in this way but were not properly developed until
the right man came along. Edward Jenner was not the first to
inoculate people with cowpox to protect them against smallpox,
William Harvey was not the first to postulate circulation of the
blood, Darwin was by no means the first to suggest evolution,
Columbus was not the first European to go to America, Pasteur
was not the first to propound the germ theory of disease,
Lister was not the first to use carbolic acid as a wound antiseptic.
But these men were the ones who fully developed these ideas
and forced them on a reluctant world, and most credit rightly
goes to them for bringing the discoveries to fruition. It is not
only new ideas that lead to discoveries. Indeed few ideas are
entirely original. Usually on close study of the origin of an
idea, one finds that others had suggested it or something very
like it previously. Charles NicoUe calls these early ideas that are
not at first followed up, " precursor ideas ".

36

CHANCE

Exploiting opportunities
When a discovery has passed these hurdles and reached a
stage where it is recognised and appreciated by its originator,
there are still at least three more ways in which its general
acceptance may be delayed.

(d) Failure to follow up the initial finding. The initial disclosure
may not be made the most of because it may not be followed up
and exploited. The most productive scientists have not been
satisfied with clearing up the immediate question but having
obtained some new knowledge, they made use of it to uncover
something further and often of even greater importance.
Steinhaeuser discovered in 1840 that cod-liver oil cured rickets
but this enormously important fact remained unproved and no
more than an opinion for the next eighty years.^* In 1903
Theobald Smith discovered that some motile baciUi may exist
in culture as the normal motile form or as a non-motile variant,
and he demonstrated the significance of these two forms in
immunological reactions. This work passed almost unnoticed
and was forgotten until the phenomenon was rediscovered in
1 91 7 by Weil and FeUx. It is now regarded as one of the
fundamental facts in immunological reactions.'^ Fleming
described crude preparations of penicillin in 1929, but after a
few years he dropped work on it without developing a therapeutic
agent. He got no encouragement or assistance from others
because they knew of many similar stories that had come to
nothing. It was some years later that Florey took the work up
from where Fleming left off and developed penicillin as a
therapeutic agent.

(e) Lack of an application. There may be no possible applica-
tions of the discovery until years later. Neufeld discovered
a rapid method of typing pneumococci in 1902, but it was not
till 1 93 1 that it became of any importance when type-specific
serum therapy was introduced. Landsteiner discovered the human
blood groups in 1901, but it was not till anticoagulants were
found and blood transfusion was developed in the 1 914—18 war
that Landsteiner's discovery assumed importance and attracted
attention.

(f ) Indifference and opposition. Finally the discovery has to
run the gauntlet of scepticism and often resistance on the part

37

THE ART OF SCIENTIFIC INVESTIGATION

of Others. This can be one of the most difficult hurdles of all
and it is here that the scientist occasionally has to fight and in the
past has sometimes even lost his life. The psychology of mental
resistance to new ideas, and actual opposition to discoveries are
discussed in a later chapter.

Several of the points discussed in this and the preceding
section may be illustrated by narrowing the story of Jenner's
recognition of the potentialities of vaccination and his exploita-
tion of it. Artificial immunisation against smallpox by means
of inoculation with virulent smallpox material (variolation) had
long been practised in the Orient. Some say that looo years B.C.
it was the custom of China to insert material from smallpox
lesions into the noses of children, others that variolation was
introduced into China from India about a.d. iooo.^^' ^^' ^°*
Variolation was introduced from Constantinople into England
about the middle of the eighteenth century and became an
accepted though not very popular practice about the time that
Edward Jenner was bom. When Jenner was serving his appren-
ticeship between thirteen and eighteen years of age, his attention
was called to the local behef in Gloucestershire that people
who contracted cow-pox from cattle were subsequently immune
to smallpox. Jenner found that the local physicians were mostly
familiar with the traditional belief but did not take it seriously,
although they also were encountering instances of failure of
people to develop infection when given variolation after they
had had cow-pox. Jenner evidently kept the matter in mind
for years without doing anything about it. After returning to
country practice he confided in a friend that he intended trying
vaccination. He divulged his intentions under a bond of secrecy
because he feared ridicule if they should fail. Meanwhile he
was exercising his genius for taking pains and making accurate
observation by carrying out experiments in other directions. He
was making observations on the temperature and digestion of
hibernating animals for John Hunter, experimenting with agri-
cultural fertilisers for Joseph Banks and on his own behalf
carrying out studies on how the young cuckoo gets rid of its
fellow nestlings. He married at thirty-eight and when his wife
had a child he inoculated him with swine-pox and showed he
was subsequently immune to smallpox. Still none of his colleagues

38

CHANCE

— John Hunter among them — took much interest in Jenner's
ideas about using cow-pox to vaccinate against smallpox and
his first tentative paper on the subject was returned to him
and apparently rejected. It was not till he was forty-seven years
old (in the memorable year 1796) that he made his first
successful vaccination from one human being to another. He
transferred material from a pustule on the hand of a milkmaid,
Sarah Nelmes, to an eight-year-old boy named James Phipps
who thereby gained fame in the same odd way as did Joseph
Meister for being the first person to receive Pasteur's treatment
for rabies nearly a century later.* This is taken as the classical
origin of vaccination but, as is often the case in the history of
scientific discovery, the issue is not clear-cut. At least two others
had actually performed it earUer but failed to follow it up.
Jenner continued his experiments, and in 1798 published his
famous Inquiry, reporting some twenty- three cases who were
either vaccinated or had contracted cow-pox naturally and were
subsequently shown to be immune to smallpox. Soon afterwards
vaccination was taken up widely and spread throughout the
world, despite severe opposition from certain quarters which
curiously and interestingly enough persists even to-day in a fairly
harmless form. Jenner suffered abuse but honours were soon
showered on him from all quarters of the globe. ^^' ^^

This history provides an admirable demonstration of how
difficult it usually is to recognise the true significance of a new
fact. Without knowing the full history one might well suppose
Jenner's contribution to medical science a very simple one not
meriting the fame subsequently bestowed on it. But neither John
Hunter nor any of Jenner's colleagues and contemporaries were
able to grasp the potentialities in advance, and similar oppor-
tunities had occurred and been let pass in other countries. There
was an interval of thirty years after the experimentally minded
Jenner himself became interested in the popular belief, before
he performed the classical, crucial experiments. With our present
conceptions of immunisation and of experimentation this may
appear surprising but we must remember how revolutionary the
idea was, even given the fact that variolation was an accepted

* Meister remained at the Pasteur Institute as concierge until the occupa-
tion of Paris by the Germans in 1940, when he committed suicide.

39

THE ART OF SCIENTIFIC INVESTIGATION

practice. The fact that others who had the same opportunity
failed to discover vaccination and that it took Jenner thirty
years shows what a difficult discovery it was to make. Animals
were at that time regarded with repugnance by most people
so the idea of infecting a human being with a disease of animals
created utmost disgust. All sorts of dire results were prophesied,
including " cow-mania " and " ox-faced children " (one was
actually exhibited ! ) . Like many great discoveries it did not
require great erudition- and it mainly devolved on having bold-
ness and independence of mind to accept a revolutionary idea
and imagination to realise its potentialities. But Jenner also
had practical difficulties to overcome. He found that cows
were subject to various sores on the teats, some of which
also affected the milkers but did not give immunity to small-
pox. Even present day virus specialists have great difficulty
in distinguishing between the different types of sores that
occur on cows' teats; and the position is comphcated by
observations suggesting that an attack of cow-pox does not confer
immunity against a second attack of the same disease in the cow,
a point Jenner himself noted.

Jenner's discovery has its element of irony which so often lends
additional interest to scientific anecdotes. Modem investigators
believe that the strains of vaccinia now used throughout
the world for many years are not cow-pox but have derived
from smallpox. Their origin is obscure but it seems that in the
early days cow-pox and smallpox got mixed up and an attenuated
strain of smallpox developed and was mistakenly used for
cow-pox.

SUMMARY

New knowledge very often has its origin in some quite un-
expected observation or chance occurrence arising during an
investigation. The importance of this factor in discovery should
be fully appreciated and research workers ought deliberately to
exploit it. Opportunities come more frequently to active bench
workers and people who dabble in novel procedures. Interpreting
the clue and realising its possible significance requires knowledge
without fixed ideas, imagination, scientific taste, and a habit of
contemplating all unexplained observations.

40

CHAPTER FOUR

HYPOTHESIS

" In science the primary duty of ideas is to be useful and
interesting even more than to be ' true '." — Wilfred Trotter

Illustrations

THE role of hypothesis in research can be discussed more
effectively if we consider first some examples of discoveries
which originated from hypotheses. One of the best illustrations
of such a discovery is provided by the story of Christopher
Columbus' voyage ; it has many of the features of a classic dis-
covery in science, {a) He was obsessed with an idea — that since
the world is round he could reach the Orient by sailing west,
(b) the idea was by no means original, but evidently he had
obtained some additional evidence from a sailor blown off his
course who claimed to have reached land in the west and
returned, (c) he met great difficulties in getting someone to
provide the money to enable him to test his idea as well as in the
actual carrying out of the experimental voyage, (d) when finally
he succeeded he did not find the expected new route, but instead
found a whole new world, ( e ) despite all evidence to the contrary
he clung to the bitter end to his hypothesis and beheved that he
had found the route to the Orient, (/) he got little credit or
reward during his lifetime and neither he nor others realised the
full implications of his discovery, (g) since his time evidence
has been brought forward showing that he was by no means the
first European to reach America.

In his early investigations on diphtheria, Loffler showed that
in experimental animals dying after inoculation with the diph-
theria bacillus, the bacteria remained localised at the site of
injection. He suggested that death was caused by toxin produced
by the bacteria. Following this hypothesis, Emile Roux made
numerous experiments attempting to demonstrate such a toxin
in cultures of bacteria, but, try as he might, he could not

41

THE ART OF SCIENTIFIC INVESTIGATION

demonstrate it. However, he persisted in his conviction and
finally in desperation he injected the heroic dose of 35 ml. of
culture filtrate into a guinea-pig. Rather surprisingly the guinea-
pig survived the injection of this volume of fluid and in due
course Roux had the satisfaction of seeing the animal die with
lesions of diphtheria intoxication. Having established this point
Roux was soon able to find out that his difficulties were due
to the cultures not having been incubated long enough to
produce much toxin, and by prolonged incubation he was able
to produce powerfully toxic filtrates. This discovery led to
immunisation against diphtheria and the therapeutic use of
antiserum.^"

Following the hypothesis that impulses pass along sympathetic
nerves and set up chemical changes producing heat in the skin,
Claude Bernard severed the cervical sympathetic nerve in the
expectation of it leading to cooling of the rabbit's ear. To his
surprise the ear on that side became warmer. He had disconnected
the blood vessels of the ear from the nervous influence which
normally holds them moderately contracted, resulting in a
greater flow of blood and hence warming of the ear. Without
at first realising what he had done, he had stumbled on to the
fact that the flow of blood through the arteries is controlled by
nerves, one of the most important advances in knowledge of
circulation since Harvey's classical discovery. An interesting and
important illustration of what often happens in the field of
observation is provided by Bernard's statement that from 1841
onwards he had repeatedly divided the cervical sympathetic
without observing these phenomena which he saw for the first
time in 1851. In the previous experiments his attention was
directed to the pupil; it was not till he looked for changes in the
face and ear that he saw them.^*

Claude Bernard reasoned that the secretion of sugar by the
liver would be controlled by the appropriate nerve, which he
supposed was the vagus. Therefore he tried puncturing the origin
of the nerve in the floor of the fourth ventricle, and found
that the glycogenic function of the liver was greatly increased
and the blood sugar rose to such an extent that sugar appeared
in the urine. However, Bernard soon realised that, interesting
and important as were the results obtained, the hypothesis on

42

HYPOTHESIS

which the experiment was founded was quite false because
this effect was still obtained even after the vagus had been
severed. He again showed his capacity to abandon the original
reasoning and followed the new clue. In telling this story he
said :

"We must never be too absorbed by the thought we are
pursuing,"

This investigation has also interest from another point of view.
After his first success in producing diabetes by puncturing the
fourth ventricle he had great trouble in repeating it and only
succeeded after he had ascertained the exact technique necessary.
He was indeed fortunate in succeeding in the first attempt, for
otherwise after faiUng two or three times he would have aban-
doned the idea.

** We wish to draw from this experiment another general
conclusion . . . negative facts when considered alone never teach
us anything. How often must man have been and still must be
wrong in this way? It even seems impossible absolutely to avoid
this kind of mistake." ^^

Towards the end of the last century nothing was known about
the nature and cause of the condition in cows known as milk
fever. There was no treatment of any value, and many valuable
animals died of it. A veterinarian named Schmidt in Kolding,
Denmark, formed an hypothesis that it was an auto-intoxication
due to absorption of "colostrum corpuscles and degenerated
old epithelial cells" from the udder. So, with the object of
"checking the formation of colostral milk and paralysing any
existing poison" he treated cases by injecting a solution of
potassium iodide into the udder. At first he said that a small
amount of air entering the udder during the operation was
beneficial because it helped the Hberation of free iodine. The
treatment was strikingly successful. Later he regarded the
injection of copious amounts of air along with the solution as an
important part of the treatment, on the ground that the air
made it possible to massage the solution into all parts of the
udder. The treatment was adopted widely and modified in
various ways and soon it was found that the injection of air
alone was quite as effective. This treatment based on a false idea

43

THE ART OF SCIENTIFIC INVESTIGATION

became standard practice twenty-five years before the bio-
chemical processes involved in milk fever were elucidated;
indeed the basic cause of the disease is still not understood,
nor do we know why the injection of air usually cures the
disease/'* *^

An hypothesis may be fruitful, not only for its propounder,
but may lead to developments by others. Wassermann himself
testified that his discovery of the complement fixation test for
syphilis was only made possible by EhrUch's side-chain theory.
Also the development of the Wassermann test has another
interesting aspect. Since it was not possible to obtain a culture
of the spirochaete which causes syphilis, he used as antigen
an extract of liver of syphiHtic stillborn children, which he
knew contained large numbers of spirochaetes. This worked very
well and it was not until some time later that it was found that
not only was it unnecessary to use syphilitic hver but equally
good antigens could be prepared from normal organs of other
animals. To this day it is a mystery why these antigens give a
complement fixation reaction which can be used to diagnose
syphilis, and only one thing is certain : that the idea that
prompted Wassermann to use an extract of liver was entirely
fortuitous. But since we still see no reasoned explanation, we
would probably still have no serological test for syphilis but for
Wasserman's false but fruitful idea.

The foundation of chemotherapy was due to Paul Ehrlich's
idea that, since some dyes selectively stained bacteria and
protozoa, substances might be found which could be selectively
absorbed by the parasites and kill them without damaging the
host. His faith in this idea enabled him to persist in the face
of long continued frustration, repeated failure and attempts by
his friends to dissuade him from the apparently hopeless task.
He met with no success until he found that trypan red had some
activity against protozoa and, developing further along lines
suggested by this, he later developed salvarsan, an arsenical
compound effective therapeutically against syphiHs, the six hun-
dred and sixth compound of the series. This is perhaps the
best example in the history of the study of disease of faith
in a hypothesis triumphing over seemingly insuperable difficulties.
It would be satisfying to end the story there but, as so often

44

HYPOTHESIS

happens, in science, the final note must be one of irony. Ehrhch's
search for substances which are selectively absorbed by patho-
genic organisms was inspired by his firm belief that drugs cannot
act unless fixed to the organisms; but to-day many effective
chemotherapeutic drugs are known not to be selectively fixed to
the infective agents.

However the story is not yet finished. Gerhard Domagk,
impressed by Ehrlich's early work, tried the effects of a great
number of dyes belonging to the group called " azo-dyes " to
which Ehrlich's trypan red belonged. Then in 1932 he found a
dye of this series, prontosil, which was effective therapeutically
against streptococci without damaging the infected animal. This
discovery marked the beginning of a new era in medicine. But
when the French chemist, Trefouel, set to work on the composi-
tion of the drug he was amazed to find its action was in no
way due to the fact that it was a dye, but was due to it con-
taining sulphanilamide, which is not a dye. Again Ehrlich's
false idea had led to a discovery that can justly be described as
miraculous. Sulphanilamide had been known to chemists since
1 9 08 but no one had any reason to suspect it had therapeutic
properties. It has been said that, had its properties been known,
sulphanilamide could have saved 750,000 lives in the 191 4-18
war alone.* Ehrlich's early work with dyes is said also to be the
starting point of the work which led to the discovery of the
modern anti-malarial drug atebrin without which the Allies might
not have won the war in the Pacific.

Another group of chemotherapeutic substances which were
evolved by following an hypothesis is the diamidine group used
against the leishmania v.'hich causes kala-azar. The idea with
which the investigation was started off was to interfere with the
natural metabolic processes of the parasite, especially with its
glucose metabolism, by using certain derivatives of insulin. One
of these, synthalin, was found to have a remarkable leish-
manicidal action, but in a dilution far higher than could possibly
affect glucose metabolism. Thus, although the hypothesis was
wrong, it led to the discovery of a new group of useful
drugs.

In certain parts of Great Britain and Western Australia there
occurs a nervous disease of sheep known as swayback, the cause

45

THE ART OF SCIENTIFIC INVESTIGATION

of which baffled investigators for years. In Western Australia,
H. W. Bennetts for certain reasons suspected that the disease
might be due to lead intoxication. To test this hypothesis he
treated some sheep with ammonium chloride which is the
antidote to lead. The first trial with this gave promising results,
which, however, were not borne out by subsequent trials. This
suggested that the disease might be due to the deficiency of some
mineral which was present in small amounts in the first batch
of ammonium chloride. Following up this clue, Bennetts was
soon able to show that the disease was due to deficiency of copper,
a deficiency never previously known to produce disease in any
animal. In Bennetts' own words :

" The solution of the etiology came in Western Australia from
an accidental ' lead ' [clue] resulting from the testing of a false
hypothesis."^^

Use of hypothesis in research

Hypothesis is the most important mental technique of the
investigator, and its main function is to suggest new experiments
or new observations. Indeed, most experiments and many
observations are carried out with the deliberate object of
testing an hypothesis. Another function is to help one see the
significance of an object or event that otherwise would mean
nothing. For instance, a mind prepared by the hypothesis of
evolution would make many more significant observations on a
field excursion than one not so prepared. Hypotheses should be
used as tools to uncover new facts rather than as ends in
themselves.

The illustrations given above show some of the ways in which
hypotheses lead to discoveries. The first thing that arrests
attention is the curious and interesting fact that an hypothesis
is sometimes very fruitful without being correct — a point that
did not escape the attention of Francis Bacon. Several of the
illustrations have been selected as striking demonstrations of
this point, and it should not be thought that they are a truly
representative sample, for correct guesses are more hkely to be
productive than ones that are wrong, and the fact that the
latter are sometimes useful does not detract from the importance
of striving for correct explanations. The examples are, however,

46

HYPOTHESIS

realistic in that the vast majority of hypotheses prove to be
wrong.

When the results of the first experiment or set of observations
are in accord with expectations, the experimenter usually still
needs to seek further experimental evidence before he can place
much confidence in his idea. Even when confirmed by a number
of experiments, the hypothesis has been established as true only
for the particular circumstances prevailing in the experiments.
Sometimes this is all the experimenter claims or requires for he
now has a solution of the immediate problem or a working
hypothesis on which to plan further investigation of that
problem. At other times the value of the hypothesis is as a
base from which new lines of investigation branch out in various
directions, and it is appHed to as many particular cases as
possible. If the hypothesis holds good under all circumstances,
it may be elevated to the category of a theory or even, if
sufficiently profound, a "law". An hypothesis which is a
generalisation cannot, however, be absolutely proved, as is
explained in the chapter on Reason ; but in practice it is accepted
if it has withstood a critical testing, especially if it is in accord
with general scientific theory.

When the results of the first experiment or observation fail
to support the hypothesis, instead of abandoning it altogether,
sometimes the contrary facts are fitted in by a subsidiary clarify-
ing hypothesis. This process of modification may go on till
the main hypothesis becomes ridiculously overburdened with
ad hoc additions. The point at which this stage is reached is
largely a matter of personal judgment or taste. The whole
edifice is then broken down and supplanted by another that
makes a more acceptable synthesis of all the facts now available.

There is an interesting saying that no one believes an hypo-
thesis except its originator but everyone believes an experiment
except the experimenter. Most people are ready to believe
something based on experiment but the experimenter knows
the many little things that could have gone wrong in the
experiment. For this reason the discoverer of a new fact seldom
feels quite so confident of it as do others. On the other hand
other people are usually critical of an hypothesis, whereas the
originator identifies himself with it and is liable to become

47

THE ART OF SCIENTIFIC INVESTIGATION

devoted to it. It is as well to remember this when criticising
someone's suggestion, because you may offend and discourage
him if you scorn the idea. A corollary to this observation that
an hypothesis is a very personal matter, is that a scientist usually
works much better when pursuing his own than that of someone
else. It is the originator who gets both the personal satisfaction
and most of the credit if his idea is proved correct, even if he
does not do the work himself A man working on an hypothesis
which is not his own often abandons it after one or two
unsuccessful attempts because he lacks the strong desire to con-
firm it which is necessary to drive him to give it a thorough trial
and think out all possible ways of varying the conditions of
the experiment. Knowing this, the tactful director of research
tries to lead the worker himself to suggest the line of work
and then lets him feel the idea was his.

Precautions in the use of hypothesis

(a) Not to cling to ideas proved useless. Hypothesis is a tool
which can cause trouble if not used properly. We must be
ready to abandon or modify our hypothesis as soon as it is shown
to be inconsistent with the facts. This is not as easy as it sounds.
When delighted by the way one's beautiful brain-child seems to
explain several otherwise incongruous facts and offers promise
of further advances, it is tempting to overlook an observation
that does not fit into the pattern woven, or to try to explain
it away. It is not at all rare for investigators to adhere to their
broken hypotheses, turning a blind eye to contrary evidence,
and not altogether unknown for them deliberately to suppress
contrary results. If the experimental results or observations are
definitely opposed to the hypothesis or if they necessitate unduly
complicated or improbable subsidiary hypotheses to accom-
modate them, one has to discard the idea with as few regrets
as possible. It is easier to drop the old hypothesis if one can
find a new one to replace it. The feeling of disappointment too
will then vanish.

It was characteristic of both Darwin and Bernard that they
were ready to drop or modify their hypotheses as soon as they
ceased to be supported by the facts observed. The scientist who
has a fertile mind and is rich in ideas does not find it so difficult

48

HYPOTHESIS

to abandon one found to be unsatisfactory as does the man
who has few. It is the latter who is most in danger of wasting
time in hanging on to a notion after the facts warrant its
discard. Zinsser picturesquely refers to people clinging to sterile
ideas as resembling hens sitting on boiled eggs.

On the other hand, faith in the hypothesis and perseverance
is sometimes very desirable, as shown by the examples quoted
concerning Roux and Ehrlich. Similarly Faraday persisted with
his idea in the face of repeated failures before he finally succeeded
in producing electric current by means of a magnet. As Bernard
observed, negative results mean very little. There is a great
difference between (a) stubborn adherence to an idea which is
not tenable in face of contrary evidence, and (b) persevering
with an hypothesis which is very difficult to demonstrate but
against which there is no direct evidence. The investigator must
judge the case with ruthless impartiality. However, even when
the facts fit into the second category^ there may come a time
when if no progress is being made it is wisest to abandon the
attempt, at least temporarily. The hypothesis may be perfectly
good but the techniques or knowledge in related fields required
for its verification may not yet be available. Sometimes a project
is put on one side for years and taken up again when fresh
knowledge is available or the scientist has thought of a new
approach.

(b) Intellectual discipline of subordinating ideas to facts. A
danger constantly to be guarded against is that as soon as one
formulates an hypothesis, parental aflfection tends to influence
observations, interpretation and judgment; "wishful thinking"
is likely to start unconsciously. Claude Bernard said :

" Men who have excessive faith in their theories or ideas are
not only ill-prepared for making discoveries; they also make poor
observations."

Unless observations and experiments are carried out with
safeguards ensuring objectivity, the results may unconsciously
be biased. No less an investigator than Gregor Mendel seems
to have fallen into this trap, for Fisher^* has shown that his
results were biased in favour of his expectations. The German
zoologist, Gatke, was so convinced of the truth of his views on
the high speed that birds are capable of that he reported actual

49

THE ART OF SCIENTIFIC INVESTIGATION

observations of birds covering four miles in a minute. He is
believed to have been quite sincere but allowed his beliefs to
delude him into making false observations/^

The best protection against these tendencies is to cultivate an
intellectual habit of subordinating one's opinions and wishes to
objective evidence and a reverence for things as they really are,
and to keep constantly in mind that the hypothesis is only a
supposition. As Thomas Huxley so eloquently said :

" My business is to teach my aspirations to conform themselves
to fact, not to try to make facts harmonise with my aspirations.
Sit down before fact as a little child, be prepared to give up
every preconceived notion, follow humbly wherever nature leads,
or you will learn nothing."

An interesting safeguard has been suggested by Chamberlain,^*
namely, the principle of multiple hypotheses in research. His
idea was that as many hypotheses as possible should be invented
and all kept in mind during the investigation. This state of
mind should prompt the observer to look for facts relative to
each and may endow otherwise trivial facts with significance.
However, I doubt if this method is often practicable. The
more usual practice is a succession of hypotheses, selecting the
most likely one for trial, and, if it is found wanting, passing on
to another.

When Darwin came across data unfavourable to his hypothesis,
he made a special note of them because he knew they had a way
of slipping out of the memory more readily than the welcome
facts.

(c) Examining ideas critically. One should not be too ready
to embrace a conjecture that comes into the mind; it must be
submitted to most careful scrutiny before being accepted even
as a tentative hypothesis, for once an opinion has been formed
it is more difficult to think of alternatives. The main danger
lies in the idea that seems so " obvious " that it is accepted
almost without question. It seemed quite reasonable, in cases of
cirrhosis of the liver, to rest that organ as much as possible by
giving a low protein diet, but recent investigations have shown
that this is just what should not be done, for low protein diet
can itself cause liver damage. The practice of resting sprained

50

HYPOTHESIS

joints was questioned by no one until a few years ago when a
bold spirit found they got better much quicker under a regimen
of exercise. For many years farmers practised keeping the surface
of the soil loose as a mulch, believing this to decrease the loss of
water by evaporation. B. A. Keen showed that this beHef was
based on inadequate experiments and that under most circum-
stances the practice was useless. He thus saved the community
from a great deal of useless expenditure.

(d) Shunning misconceptions. Examples have been quoted
showing how hypotheses may be fruitful even when wrong, but
nevertheless the great majority have to be abandoned as useless.
More serious is the fact that false hypotheses or concepts some-
times survive which, far from being productive, are actually
responsible for holding up the advance of science. Two
examples are the old notion that every metal contains mercury,
and the phlogiston doctrine. According to the latter, every
combustible substance contains a constituent which is given up
on burning, called phlogiston. This notion for long held up the
advance of chemistry, and stood in the way of an understanding
of combustion, oxidation, reduction, and other processes. It
was finally exposed as a fallacy by Lavoisier in 1778, but the
great English scientists, Priestley, Watt and Cavendish, clung to
the belief for some time afterwards and Priestley had not been
converted to the new outlook when he died in 1804.

The exposure of serious fallacies can be as valuable in the
advance of science as creative discoveries, Pasteur fought and
conquered the notion of spontaneous generation and Hopkins
the semi-mystical concept of protoplasm as a giant molecule.
Misconceptions in medicine, apart from holding up advances,
have been the cause of much harm and unnecessary suffering.
For example, the famous Philadelphian physician, Benjamin
Rush (i 745-181 3), gave as an instance of the sort of treatment
he meted out :

"From a newly arrived Englishman I took 144 ounces at 12
bleedings in 6 days; four were in 24 hours; I gave within the
course of the same 6 days nearly 150 grains of calomel with the
usual proportions of jalop and gamboge."

' 66

Once ideas have gained credence, they are rarely abandoned

51

THE ART OF SCIENTIFIC INVESTIGATION

merely because some contrary facts are found. False ideas are
only dropped when hypotheses more in accord with the new
facts are put forward.

SUMMARY

The hypothesis is the principal intellectual instrument in
research. Its function is to indicate new experiments and
observations and it therefore sometimes leads to discoveries even
when not correct itself

We must resist the temptation to become too attached to
our hypothesis, and strive to judge it objectively and modify
or discard it as soon as contrary evidence is brought to light.
Vigilance is needed to prevent our observations and interpreta-
tions being biased in favour of the hypothesis. Suppositions can
be used without being believed.

52

CHAPTER FIVE

IMAGINATION

" With accurate experiment and observation to work upon,
imagination becomes the architect of physical theory."

— Tyndall

Productive thinking

THIS chapter and the next contain a brief discussion on
how ideas originate in the mind and what conditions are
favourable for creative mental eflfort. The critical examination
of the processes involved will be rendered easier if I do as I
have done in other parts of this book, and make an arbitrary
division of what is really a single subject. Consequently much
of the material in this chapter should be considered in connection
with Intuition and much of the next chapter appUes equally to
Imagination.

Dewey analyses conscious thinking into the following phases.
First comes awareness of some difficulty or problem which
provides the stimulus. This is followed by a suggested solution
springing into the conscious mind. Only then does reason come
into play to examine and reject or accept the idea. If the idea
is rejected, our mind reverts to the previous stage and the
process is repeated. The important thing to realise is that the
conjuring up of the idea is not a dehberate, voluntary act. It
is something that happens to us rather than something we do.^'

In ordinary thinking ideas continually " occur " to us in this
fashion to bridge over the steps in reasoning and we are so
accustomed to the process that we are hardly aware of it. Usually
the new ideas and combinations result from the immediately pre-
ceding thought calling up associations that have been developed
in the mind by past experience and education. Occasionally, how-
ever, there flashes into the mind some strikingly original idea, not
based on past associations or at any rate not on associations that
are at first apparent. We may suddenly perceive for the first time

53

THE ART OF SCIENTIFIC INVESTIGATION

the connection between several things or ideas, or may take a
great leap forward instead of the usual short step where the
connections between each pair or set of ideas are well established
and " obvious ". These sudden, large progressions occur not
only when one is consciously puzzling the problem but also not
uncommonly when one is not thinking of anything in particular,
or even when one is mildly occupied with something different,
and in these circumstances they are often startling. Although
there is probably no fundamental difference between these ideas
and the less exciting ones that come to us almost continually,
and it is not possible to draw any sharp distinction, it will be
convenient to consider them separately in the next chapter under
the title " intuitions ".In this section we will draw attention to
some general features of productive or creative thinking.

Dewey advocates what he calls " reflective thinking ", that is,
turning a subject over in the mind and giving it ordered and
consecutive consideration, as distinct from the free coursing of
ideas through the head. Perhaps the best term for the latter
is day-dreaming; it also has its uses, as we shall see presently.
But thinking may be reflective and yet be inefficient. The thinker
may not be sufficiently critical of ideas as they arise and may
be too ready to jump to a conclusion, either through impatience
or laziness. Dewey says many people will not tolerate a state of
doubt, either because they will not endure the mental discomfort
of it or because they regard it as evidence of inferiority.

" To be genuinely thoughtful, we must be willing to sustain
and protract that state of doubt which is the stimulus to thorough
enquiry, so as not to accept an idea or make a positive assertion
of a belief, until justifying reasons have been found."^^

Probably the main characteristic of the trained thinker is that
he does not jump to conclusions on insufficient evidence as the
untrained man is inclined to do.

It is not possible deliberately to create ideas or to control their
creation. When a difficulty stimulates the mind, suggested
solutions just automatically spring into the consciousness. The
variety and quaUty of the suggestions are functions of how well
prepared our mind is by past experience and education pertinent
to the particular problem. What we can do deliberately is to
prepare our minds in this way, voluntarily direct our thoughts

54

IMAGINATION

to a certain problem, hold attention on that problem and appraise
the various suggestions thrown up by the subconscious mind.
The intellectual element in thinking is, Dewey says, what we do
with the suggestions after they arise.

Other things being equal, the greater our store of knowledge,
the more likely it is that significant combinations will be thrown
up. Furthermore, original combinations are more likely to come
into being if there is available a breadth of knowledge extend-
ing into related or even distant branches of knowledge. As
Dr. E. L. Taylor says :

" New associations and fresh ideas are more likely to come
out of a varied store of memories and experience than out of
a collection that is all of one kind." ^"^

Scientists who have made important original contributions
have often had wide interests or have taken up the study of a
subject different from the one in which they were originally
trained. Originahty often consists in finding connections or
analogies between two or more objects or ideas not previously
shown to have any bearing on each other.

In seeking original ideas, it is sometimes useful to abandon
the directed, controlled thinking advocated by Dewey and allow
one's imagination to wander freely — to day-dream. Harding
says all creative thinkers are dreamers. She defines dreaming in
these words :

" Dreaming over a subject is simply . . . allowing the will to
focus the mind passively on the subject so that it follows the
trains of thought as they arise, stopping them only when unprofit-
able but in general allowing them to form and branch naturally
until some useful and interesting results occur." ^^

Max Planck said :

" Again and again the imaginary plan on which one attempts
to build up order breaks down and then we must try another.
This imaginative vision and faith in the ultimate success are
indispensable. The pure rationalist has no place here."^°

In meditating thus, many people find that visualising the
thoughts, forming mental images, stimulates the imagination. It
is said that Clerk Maxwell developed the habit of making a
mental picture of every problem. Paul Ehrlich was another
great advocate of making pictorial representations of ideas, as

55

THE ART OF SCIENTIFIC INVESTIGATION

\''<:^^'j '-~''

EHRLICH S DRAWINGS OF HIS SIDE-CHAIN THEORY

one can see from his illustrations of his side-chain theory.
Pictorial analogy can play an important part in scientific think-
ing. This is how the German chemist Kekule hit on the concep-
tion of the benzene ring, an idea that revolutionised organic
chemistry. He related how he was sitting writing his chemical
text-book :

" But it did not go well; my spirit was with other things. I
turned the chair to the fireplace and sank into a half sleep. The
atoms flitted before my eyes. Long rows, variously, more closely,
united; all in movement wriggling and turning like snakes. And
see, what was that? One of the snakes seized its own tail and
the image whirled scornfully before my eyes. As though from a
flash of lightning I awoke; I occupied the rest of the night in
working out the consequences of the hypothesis. . . . Let us
learn to dream, gentlemen."^*

However, physics has reached a stage where it is no longer
possible to visualise mechanical analogies representing certain

56

IMAGINATION

phenomena which can only be expressed in mathematical terms.

In the study of infectious diseases, it is sometimes helpful
to take the biological view, as Burnet has done, and look upon
the causal organism as a species struggling for continued survival,
or even, as Zinsser has felt inclined to do with typhus, which he
spent a lifetime studying, personifying the disease in the
imagination.

An important inducement to seeking generalisations, especially
in physics and mathematics, is the love of order and logical
connection between facts. Einstein said : i

" There is no logical way to the discovery of these elemental
laws. There is only die way of intuition, which is helped by a
feeling for the order lying behind the appearance." ^^

W. H. George remarks that a feeling of tension is produced
when an observer sees the objects lying in his field of vision as
forming a pattern with a gap in it, and a feeling of relaxation
or satisfaction is experienced when the gap is closed, and all
parts of the pattern fit into their expected places. Generalisa-
tions may be regarded as patterns in ideas.^^ Another
phenomenon which may be explained by this concept is the
satisfaction experienced on the completion of any task. This
may be quite rnassociated with any consideration of reward
for it applies equally to unimportant, self-appointed tasks such
as doing a crossword puzzle, climbing a hill or reading a book.
The instinctive sense of irritation we feel when someone disagrees
with us or when some fact arises which is contrary to our
beliefs may be due to the break in the pattern we have formed.

The tendency of the human mind to seek order in things did
not escape the penetrating intelligence of Francis Bacon. He
warned against the danger that this trait may mislead us into
believing we see a greater degree of order and equality than there
really is.

When one has succeeded in hitting upon a new idea, it has
to be judged. Reason based on knowledge is usually sufficient
in everyday affairs and in straightforward matters in science,
but in research there is often insufficient information available
for effective reasoning. Here one has to fall back on " feelings "
or " taste ". Harding says :

57

THE ART OF SCIENTIFIC INVESTIGATION

*' If the scientist has during the whole of his Hfe observed
carefully, trained himself to be on the look out for analogy, and
possessed himself of relevant knowledge, then the ' instrument of
feeling ' . . . will become a powerful divining rod ... in creative
science feeling plays a leading part."^^

Writing of the importance of imagination in science Tyndall
said :

" Newton's passage from a falling apple to a falling moon was
an act of the prepared imagination. Out of the facts of chemistry
the constructive imagination of Dalton formed the atomic theory.
Davy was richly endowed with the imaginative faculty, while
with Faraday its exercise was incessant, preceding, accompanying
and guiding all his experiments. His strength and fertility as a
discoverer are to be referred in great part to the stimulus of
the imagination."^^

Imagination is of great importance not only in leading us
to new^ facts, but also in stimulating us to new efforts, for it
enable us to see visions of their possible consequences. Facts
and ideas are dead in themselves and it is the imagination that
gives hfe to them. But dreams and speculations are idle fantasies
unless reason turns them to useful purpose. Vague ideas captured
on flights of fancy have to be reduced to specific propositions
and hypotheses.

False trails

While imagination is the source of inspiration in seeking new
knowledge, it can also be dangerous if not subjected to discipline;
a fertile imagination needs to be balanced by criticism and judg-
ment. This is, of course, quite different from saying it should be
repressed or crushed. The imagination merely enables us to
wander into the darkness of the unknown where, by the dim
light of the knowledge that we carry, we may glimpse something
that seems of interest. But when we bring it out and examine
it more closely it usually proves to be only trash whose glitter
had caught our attention. Things not clearly seen often take on
grotesque forms. Imagination is at once the source of all hope
and inspiration but also of frustration. To forget this is to court
despair.

Most hypotheses prove to be wrong whatever their origin may
be. Faraday wrote :

58

IMAGINATION

" The world little knows how many of the thoughts and
theories which have' passed through the mind of a scientific
investigator have been crushed in silence and secrecy by his own
severe criticism and adverse examinations; that in the most
successful instances not a tenth of the suggestions, the hopes,
the wishes, the preliminary conclusions have been realised."

Every experienced research worker will confirm this statement.
Darwin went even further :

" I have steadily endeavoured to keep my mind free so as to
give up any hypothesis, however much beloved (and I cannot
resist forming one on every subject) as soon as facts are shown
to be opposed to it. ... / cannot remember a single first formed
hypothesis which had not after a time to he given up or be
greatly modified." -^ (Italics mine.)

T. H. Huxley said that the great tragedies of science are the
slaying of beautiful hypotheses by ugly facts. F. M. Burnet has
told me that most of the "bright ideas" that he gets prove
to be wrong.

There is nothing reprehensible about making a mistake,
provided it is detected in time and corrected. The scientist who
is excessively cautious is not likely to make either errors or
discoveries. Whitehead has expressed this aptly : " panic of
error is the death of progress." Humphrey Davy said : " The
most important of my discoveries have been suggested to me
by my failures." The trained thinker shows to great advantage
over the untrained person in his reaction to finding his idea to
be wrong. The former profits from his mistakes as much as
from his successes. Dewey says :

" What merely annoys and discourages a person not accus-
tomed to thinking ... is a stimulus and guide to the trained
enquirer. ... It either brings to light a new problem or helps to
define and clarify the problem." ^^

The productive research worker is usually one who is not
afraid to venture and risk going astray, but who makes a rigorous
test for error before reporting his findings. This is so not only
in the biological sciences but also in mathematics. Hadamard
states that good mathematicians often make errors but soon
perceive and correct them, and that he himself makes more
errors than his students. Commenting on this statement, Sir

59

THE ART OF SCIENTIFIC INVESTIGATION

Frederic Bartlett, Professor of Psychology at Cambridge, suggests
that the best single measure of mental skill may lie in the speed
with which errors are detected and thrown out/^ Lister once
remarked :

" Next to the promulgation of the truth, the best thing I can
conceive that a man can do is the public recantation of an error."

W. H. George points out that even with men of genius, with
whom the birth rate of hypotheses is very high, it only just
manages to exceed the death rate.

Max Planck, whose quantum theory is considered by many
to be an even more important contribution to science than
Einstein's theory of relativity, said when he was awarded the
Nobel Prize :

" Looking back . . . over the long and labyrinthine path
which finally led to the discovery [of the quantum theory], I
am vividly reminded of Goethe's saying that men will always be
making mistakes as long as they are striving after something."^"

Einstein in speaking of the origin of his general theory of
relativity said :

" These were errors in thinking which caused me two years
of hard work before at last, in 1915, I recognised them as such.
. . . The final results appear almost simple; any intelligent under-
graduate can understand them without much trouble. But the
years of searching in the dark for a truth that one feels, but
cannot express; the intense desire and the alternations of confi-
dence and misgiving, until one breaks through to clarity and
understanding, are only known to him who has himself experi-
enced them."^^

Perhaps the most interesting and revealing anecdote on these
matters was written by Hermann von Helmholtz^^ :

"In 1 89 1 I have been able to solve a few problems in mathe-
matics and physics including some that the great mathematicians
had puzzled over in vain from Euler onwards. . . . But any pride
I might have felt in my conclusions was perceptibly lessened by
the fact that I knew that the solution of these problems had
almost always come to me as the gradual generalisation of favour-
able examples, by a series of fortunate conjectures, after many
errors. I am fain to compare myself with a wanderer on the
mountains who, not knowing the path, climbs slowly and pain-
fully upwards and often has to retrace his steps because he can

60

IMAGINATION

go no further — then, whether by taking thought or from luck,
discovers a new track that leads him on a little till at length
when he reaches the summit he finds to his shame that there is
a royal road, by which he might have ascended, had he only had
the wits to find the right approach to it. In my works, I naturally
said nothing about my mistake to the reader, but only described
the made track by which he may now reach the same heights
without difiiculty."

Curiosity as an incentive to thinking

In common with other animals we are bom with an instinct
of curiosity. It provides the incentive for the young to discover
the world in which they live — what is hard or soft, movable or
fixed, that things fall downwards, that water has the property we
call wetness, and all other knowledge required to enable us to
accommodate ourselves to our environment. Infants whose
mental reflexes have not yet been conditioned are said not to
exhibit the " attack-escape " reaction as do adults, but to show
rather the opposite type of behaviour. By school age we have
usually passed this stage of development, and most of our
acquisition of new knowledge is then made by learning from
others, either by observing them or being told or reading. We
have gained a working knowledge of our environment and our
curiosity tends to become blunted unless it is successfully trans-
ferred to intellectual interests.

The curiosity of the scientist is usually directed toward seeking
an understanding of things or relationships which he notices
have no satisfactory explanation. Explanations usually consist
in connecting new observations or ideas to accepted facts or
ideas. An explanation may be a generalisation which ties together
a bundle of data into an orderly whole that can be connected
up with current knowledge and beliefs. That strong desire
scientists usually have to seek underlying principles in masses of
data not obviously related may be regarded as an adult form or
sublimation of curiosity. The student attracted to research is
usually one who retains more curiosity than usual.

We have seen that the stimulus to the production of ideas is
the awareness of a difificulty or problem, which may be the
realisation of the present unsatisfactory state of knowledge.
People with no curiosity seldom get this stimulus, for one usually

6i

THE ART OF SCIENTIFIC INVESTIGATION

becomes aware of the problem by asking why or how some
process works, or something takes the form that it does. That
a question is a stimulus is demonstrated by the fact that when
someone asks a question it requires an effort to restrain oneself
from responding.

Some purists contend that scientists should wonder " how "
and not " why ". They consider that to ask " why " implies that
there is an intelligent purpose behind the design of things and
that activities are directed by a supernatural agency toward
certain aims. This is the teleological view and is rejected by
present-day science, which strives to understand the mechanism
of all natural phenomena. Von Bruecke once remarked :

" Teleology is a lady without whom no biologist can live; yet
he is ashamed to show himself in public with her."

In biology, asking " why " is justified because all events have
causes; and because structures and reactions usually fulfil some
function which has survival value for the organism, and in that
sense they have a purpose. Asking " why " is a useful stimulus
towards imagining what the cause or purpose may be. " How "
is also a useful question in provoking thought about the
mechanism of a process.

There is no satisfying the scientists' curiosity, for with each
advance, as Pavlov said, " we reach a higher level from which
a wider field of vision is open to us, and from which we see
events previously out of range." It may be appropriate to give
here an illustration of how curiosity led John Hunter to carry
out an experiment which led to an important finding.

While in Richmond Park one day Hunter saw a deer with
growing antlers. He wondered what would happen if the blood
supply were shut off on one side of the head. He carried out
the experiment of tying the external carotid artery on one side,
whereupon the corresponding antler lost its warmth and ceased
to grow. But after a while the horn became warm again and
grew. Hunter ascertained that his ligature still held, but neigh-
bouring arteries had increased in size till they carried an adequate
supply of blood. The existence of collateral circulation and the
possibility of its increasing were thus discovered. Hitherto no
one had dared to treat aneurism by ligation for fear of gangrene,
but now Hunter saw the possibilities and tried ligation in the

62

IMAGINATION

case of popliteal aneurism. So the Hunterian operation, as it is
known in surgery to-day, came into an assured existence.^^ An
insatiable curiosity seems to have been the driving force behind
Hunter's prolific mind which laid the foundation of modem
surgery. He even paid the expenses of a surgeon to go and
observe whales for him in the Greenland fisheries.

Discussion as a stimulus to the mind

Productive mental effort is often helped by intellectual inter-
course. Discussing a problem with colleagues or with lay
persons may be helpful in one of several ways.

(a) The other person may be able to contribute a useful
suggestion. It is not often that he can help by directly indicating
a solution of the impasse, because he is unlikely to have as
much pertinent knowledge as has the scientist working on the
problem, but with a different background of knowledge he may
see the problem from a different aspect and suggest a new
approach. Even a layman is sometimes able to make useful
suggestions. For example, the introduction of agar for making
solid media for bacteriology was due to a suggestion of the
wife of Koch's colleague Hesse. ^*

{h) A new idea may arise from the pooling of information
or ideas of two or more persons. Neither of the scientists alone
may have the information necessary to draw the inference which
can be obtained by a combination of their knowledge.

{c) Discussion provides a valuable means of uncovering errors.
Ideas based on false information or questionable reasoning may
be corrected by discussion and likewise unjustified enthusiasms
may be checked and brought to a timely end. The isolated
worker who is unable to talk over his work with colleagues will
more often waste his time in following a false trail.

[d) Discussion and exchange of views is usually refreshing,
stimulating and encouraging, especially when one is in difficulties
and worried.

{e) The most valuable function of discussion is, I believe, to
help one to escape from an established habit of thought which
has proved fruitless, that is to say, from conditioned thinking.
The phenomenon of conditioned thinking is discussed in the
next section.

63

THE ART OF SCIENTIFIC INVESTIGATION

Discussions need to be conducted in a spirit of helpfulness
and mutual confidence and one should make a deliberate effort
to keep an open receptive mind. Discussions are usually best
when not more than about six are present. In such a group no
one should be afraid of admitting his ignorance on certain
matters and so having it corrected, for in these days of extreme
specialisation everyone's knowledge is restricted. Conscious
ignorance and intellectual honesty are important attributes for
the research man. Free discussion requires an atmosphere
unembarrassed by any suggestion of authority or even respect.
Brailsford Robertson tells the story of the great biochemist,
Jacques Loeb, who, when asked a question by a student after
a lecture, replied characteristically :

" I cannot answer your question, because I have not yet read
that chapter in the text-book myself, but if you will come to me
to-morrow I shall then have read it, and may be able to answer
you."^*

Students sometimes quite wrongly think that their teachers
are almost omniscient, not knowing that the lecturers usually
spend a considerable amount of time preparing their lectures,
and that outside the topic of the lecture their knowledge is often
much less impressive. Not only does the author of a text-book
not carry in his head all the information in the book, but the
author of a research paper not infrequently has to refer to the
paper to recall the details of the work which he himself did.

The custom of having lunch and afternoon tea in groups at
the laboratory is a valuable one as it provides ample opportunities
for these informal discussions. In addition, slightly more formal
seminars or afternoon tea meetings at which workers present
their problems before and during, as well as after, the investiga-
tion are useful. Sharing of interests and problems among workers
in a department or institute is also valuable in promoting a
stimulating atmosphere in which to work. Enthusiasm is infectious
and is the best safeguard against the doldrums.

Conditioned thinking

Psychologists have observed that once we have made an error,
as for example in adding up a column of figures, we have a

64

IMAGINATION

tendency to repeat it again and again. This phenomenon is known
as the persistent error. The same thing happens when we ponder
over a problem; each time our thoughts take a certain course,
the more hkely is that course to be followed the next time. Asso-
ciations form between the ideas in the chain of thoughts and
become firmer each time they are used, until finally the connec-
tions are so well established that the chain is very difficult to
break. Thinking becomes conditioned just as conditioned reflexes
are formed. We may have enough data to arrive at a solution to
the problem, but, once we have adopted an unprofitable line of
thought, the oftener we pursue it, the harder it is for us to
adopt the profitable line. As Nicolle says, " The longer you are in
the presence of a difficulty, the less likely you are to solve it."

Thinking also becomes conditioned by learning from others
by word of mouth or by reading. In the first chapter we discussed
the adverse eflfect on originality of uncritical reading. Indeed,
all learning is conditioning of the mind. Here, however, we are
concerned with the eflfects of conditioning which are unprofitable
for our immediate purpose, that of promoting original thought.
This does not only concern learning or being conditioned to
incorrect opinions for, as we have seen in the first chapter, read-
ing, even the reading of what is true so far as it goes, may
have an adverse effect on originality.

The two main ways of freeing our thinking from conditioning
are temporary abandonment and discussion. If we abandon a
problem for a few days or weeks and then return to it the old
thought associations are partly forgotten or less strong and often
we can then see it in a fresh light, and new ideas arise. The
beneficial eflfect of temporary abandonment is well shown by
laying aside for a few weeks a paper one has written. On coming
back to it, flaws are apparent that escaped attention before,
and fresh pertinent remarks may spring into the mind.

Discussion is a valuable aid in breaking away from sterile
lines of thought that have become fixed. In explaining a prob-
lem to another person, and especially to someone not familiar
with that field of science, it is necessary to clarify and amplify
aspects of it that have been taken for granted and the familiar
chain of thought cannot be followed. Not infrequently it happens
that while one is making the explanation, a new thought occurs

65

THE ART OF SCIENTIFIC INVESTIGATION

to one without the other person having said a word. The same
may happen during the delivery of a lecture, for when the
teacher explains something he "sees" it more clearly himself
than he had before. The other person, by asking questions, even
ill-informed ones, may make the narrator break the established
chain, even if only to explain the futiUty of the suggestion, and
this may result in him seeing a new approach to the problem or
the connection between two or more observations or ideas that
he had not noticed before. The effect that questioning has on
the mind might be Ukened to the stimulus given to a fire by
poking ; it disturbs the settled arrangement and brings about new
combinations. In disturbing fixed Hnes of thought, discussion is
perhaps more likely to be helpful when carried on with someone
not familiar with your field of work, for near colleagues have
many of the same thought habits as yourself The writing of a
review of the problem may prove helpful in the same way as
the giving of a lecture.

A further useful application of the conception of conditioned
thinking is that when a problem has defied solution it is best
to start again right from the beginning, and if possible with a
new approach. For example, I worked unsuccessfully for several
years trying to discover the micro-organism which causes foot-rot
in sheep. I met with repeated frustrations but each time I started
again along the same lines, namely, trying to select the causal
organism by microscopy and then isolating it in culture. This
method seemed the sensible one to follow and only when I had
exhausted all possibilities and was forced to abandon it, did I
think of a fundamentally different approach to the problem,
namely, to try mixed cultures on various media until one was
found which was capable of setting up the disease. Work along
these lines soon led to the solution of the problem.

SUMMARY

Productive thinking is started off by awareness of a difficulty.
A suggested solution springs into the mind and is accepted or
rejected. New combinations in our thoughts arise from rational
associations, or from fancy or perhaps chance circumstances. The
fertile mind tries a large number and variety of combinations.

66

IMAGINATION

The scientific thinker becomes accustomed to withholding judg-
ment and remaining in doubt when the evidence is insufficient.
Imagination only rarely leads one to a correct answer, and most
of our ideas have to be discarded. Research workers ought not
to be afraid of making mistakes provided they correct them in
good time.

Curiosity atrophies after childhood unless it is transferred to
an intellectual plane. The research worker is usually a person
whose curiosity is turned toward seeking explanations for pheno-
mena that are not understood.

Discussion is often helpful to productive thinking and informal
daily discussion groups in research institutes are valuable.

Once we have contemplated a set of data, the mind tends to
follow the same line of thought each time and therefore unprofit-
able lines of thought tend to be repeated. There are two aids to
freeing our thought from this conditioning; to abandon the
problem temporarily and to discuss it with another person, prefer-
ably someone not familiar with our work.

67

CHAPTER SIX

INTUITION

" The really valuable factor is intuition." — Albert Einstein

Definition and illustration

THE word intuition has several slightly different usages, so
it is necessary to indicate at the outset that it is employed
here as meaning a sudden enlightenment or comprehension of a
situation, a clarifying idea which springs into the consciousness,
often, though not necessarily, when one is not consciously think-
ing of that subject. The terms inspiration, illumination and
" hunch " are also used to describe this phenomenon but these
words are very often given other meanings. Ideas coming drama-
tically when one is not consciously thinking of the subject are
the most striking examples of intuition, but those arriving
suddenly when the problem is being consciously pondered are
also intuitions. Usually these were not self-evident when the data
were first obtained. All ideas, including the simple ones that
form the gradual steps in ordinary reasoning, probably arise by
the process of intuition and it is only for convenience that we
consider separately in this chapter the more dramatic and import-
ant progressions of thought.

Valuable contributions on the subject of intuition in scientific
thought have been made by the American chemists Piatt and
Baker, ^^ by the French mathematicians Henri Poincare^^ and
Jacques Hadamard,^" by W. B. Cannon,^^ the American physio-
logist, and by Graham Wallas,^^ the psychologist. In writing this
chapter I have drawn freely from the excellent article by Piatt
and Baker who conducted an enquiry on the subject among
chemists by questionnaire. The following illustrations are quoted
from material collected by them.

" Freeing my mind of all thoughts of the problem I walked
briskly down the street, when suddenly at a definite spot which

68

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LOUIS PASTEUR 1822-1895

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SIR HENRY DALE 1875-

INTUITION

I could locate to-day — as if from the clear sky above me — an idea
popped into my head as emphatically as if a voice had shouted it."

" I decided to abandon the work and all thoughts "relative to it,
and then, on the following day, when occupied in work of an
entirely different type, an idea came to my mind as suddenly as a
flash of lightning and it was the solution . . . the utter simplicity
made me wonder why I hadn't thought of it before."

" The idea came with such a shock that I remember the exact
position quite clearly.""^

Prince Kropotkin wrote :

" Then followed months of intense thought in order to find
out what the bewildering chaos of scattered observations meant
until one dav all of a sudden the whole became as clear and
comprehensible as if it were illuminated with a flash of light . . .
There are not many joys in human life equal to the joy of the
sudden birth of a generalisation illuminating the mind after a
long period of patient research."

Von Helmholtz, the great German physicist said that after
previous investigation of a problem " in all directions . . . happy
ideas came unexpectedly without effort like an inspiration." He
found that ideas did not come to him when his mind was fatigued
or when at the working table, but often in the morning after a
night's rest or during the slow ascent of wooded hills on a
sunny day.

After Darwin had conceived the basic idea of evolution, he
was reading Malthus on population for relaxation one day when
it struck him that under the struggle for existence favourable
variations would tend to be preserved and unfavourable ones
destroyed. He wrote a memorandum around this idea, but there
was still one important point not accounted for, namely, the
tendency in organic beings descended from the same stock to
diverge as they become modified. The clarification of this last
point came to him under the following circumstances :

" I can remember the very spot in the road, whilst in my
carriage, when to my joy the solution occurred to me."

The idea of survival of the fittest as a part of the explanation
of evolution also came independently to A. R. Wallace when he
was reading Malthus' Principles of Population during an illness.

69

THE ART OF SCIENTIFIC INVESTIGATION

Malthus gave a clear exposition of the checks to increase in the
human population and mentioned that these eliminated the least
fit. Then it occurred to Wallace that the position was much the
same in the animal world.

" Vaguely thinking over the enormous and constant destruc-
tion this implied, it occurred to me to ask the question, * Why
do some die and some live? ' and the answer was clearly that on
the whole the best fitted live. . . . Then it suddenly flashed upon
me that this self-acting process would improve the race . . .
the fittest would survive. Then at once I seemed to see the whole
effect of this." ^^

Here is Metchnikoff's own account of the origin of the idea of
phagocytosis :

" One day when the whole family had gone to the circus to
see some extraordinary performing apes, I remained alone with
my microscope, observing the life in the mobile cells of a trans-
parent starfish larva, when a new thought suddenly flashed across
my brain. It struck me that similar cells might serve in the
defence of the organism against intruders. Feeling that there was
in this something of surpassing interest, I felt so excited that I
began striding up and down the room and even went to the
seashore to collect my thoughts." ^^

Poincare relates how after a period of intense mathematical
work he went for a journey into the country and dismissed his
work from mind.

" Just as I put my foot on the step of the brake, the idea
came to me . . . that the transformations I had used to define
Fuchsian functions were identical with those of non-Euclidian
geometry." ^^

On another occasion when baflfled by a problem he went to the
seaside and

" thought of entirely different things. One day, as I was walking
on the cliff the idea came to me, again with the same character-
istics of conciseness, suddenness and immediate certainty, that
arithmetical transformations of indefinite ternary quadratic forms
are identical with those of non-Euclidian geometry."

Hadamard cites an experience of the mathematician Gauss,
who wrote concerning a problem he had tried unsuccessfully to
prove for years,

70

INTUITION

" finally two days ago I succeeded . . . like a sudden flash of
lightning the riddle happened to be solved. I cannot myself say
what was the conducting thread which connected what I pre-
viously knew with what made my success possible."

Intuitions sometimes occur during sleep and a remarkable
example is quoted by Cannon. Otto Loewi, professor of pharma-
cology at the University of Graz, awoke one night with a brilliant
idea. He reached for a pencil and paper and jotted down a few
notes. On waking next morning he was aware of having had an
inspiration during the night, but to his consternation could not
decipher his notes. All day at the laboratory in the presence of
familiar apparatus he tried to remember the idea and to decipher
the note, but in vain. By bedtime he had been unable to recall
anything, but during the night to his great joy he again awoke
with the same flash of insight. This time he carefully recorded it
before going to sleep again.

" The next day he went to his laboratory and in one of the
neatest, simplest and most definite experiments in the history of
biology brought proof of the chemical mediation of nerve
impulses. He prepared two frogs' hearts which were kept beating
by means of salt solution. He stimulated the vagus nerve on
one of the hearts, thus causing it to stop beating. He then
removed the salt solution from this heart and applied it to the
other one. To his great satisfaction the solution had the same
effect on the second heart as the vagus stimulating had had on
the first one: the pulsating muscle was brought to a standstill.
This was the beginning of a host of investigations in many
countries throughout the world on chemical intermediation, not
only between nerves and the muscles and the glands they affect
but also between nervous elements themselves." ^^

Cannon states that from his youth he was accustomed to get
assistance from sudden and unpredicted insight and that not
infrequently he would go to sleep with a problem on his mind
and on waking in the morning the solution was at hand. The
following passage shows a slightly different use of intuition.

" As a matter of routine I have long trusted unconscious pro-
cesses to serve me — for example, when I have had to prepare a
public address. I would gather points for the address and write

71

THE ART OF SCIENTIFIC INVESTIGATION

them down in rough outUne. Within the next few nights I would
have sudden spells of awakening, with an onrush of illustrative
instances, pertinent phrases, and fresh ideas related to those
already listed. Paper and pencil at hand permitted the capture
of these fleeting thoughts before they faded into oblivion. The
process has been so common and so reliable for me that I have
supposed that it was at the service of everyone. But evidence indi-
cates that it is not." -^

Similarly, in preparing this book ideas have frequently come to
me at odd times of the day, sometimes when I was thinking of
it, sometimes when I was not. These were all jotted down and
later sorted out.

These examples should be ample to enable the reader to under-
stand the particular sense in which I am using the word intuition
and to realise its importance in creative thinking.

Most but not all scientists are familiar with the phenomenon of
intuition. Among those answering the questionnaire of Piatt and
Baker 33 per cent reported frequent, 50 per cent occasional, and
17 per cent no assistance from intuition. From other enquiries
also it is known that some people, so far as they are aware, never
get intuitions, or at any rate not striking ones. They have no com-
prehension of what an intuition is, and believe that they derive
their ideas only from conscious thinking. Some of these opinions
may be based on insufhcient examination of the working of one's
own mind.

The examples cited may leave the reader with the impression
that all intuitions are correct or at least fruitful, which, if so,
would be inconsistent with what has been said about hypotheses
and ideas in general. Unfortunately intuitions, being but the
products of falUble human minds, are by no means always
correct. In Piatt and Baker's enquiry, 7 per cent of scientists
replying said their intuitions were always correct, and the
remainder gave estimates varying from 10 per cent to 90 per
cent of the intuitions as subsequently proving to be correct.
Even this is probably an unduly favourable picture, because
successful instances would tend to be remembered rather than
the unsuccessful. Several eminent scientists have stated that most
of their intuitions subsequently prove to be wrong and are
forgotten.

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INTUITION

Psychology of intuition

The most characteristic circumstances of an intuition are a
period of intense work on the problem accompanied by a desire
for its solution, abandonment of the work perhaps with attention
to something else, then the appearance of the idea with dramatic
suddenness and often a sense of certainty. Often there is a feeUng
of exhilaration and perhaps surprise that the idea had not been
thought of previously.

The psychology of the phenomenon is not thoroughly under-
stood. There is a fairly general, though not universal, agreement
that intuitions arise from the subconscious activities of the mind
which has continued to turn over the problem even though
perhaps consciously the mind is no longer giving it attention.

In the previous chapter it was pointed out that ideas spring
straight into the conscious mind without our having deliberately
formed them. Evidently they originate from the subconscious
activities of the mind which, when directed at a problem,
immediately brings together various ideas which have been
associated with that particular subject before. When a possibly
significant combination is found it is presented to the cons<cious
mind for appraisal. Intuitions coming w^hen we are consciously
thinking about a problem are merely ideas that are more startling
than usual. But some further explanation is needed to account for
intuitions coming when our conscious mind is no longer dwelhng
on that subject. The subconscious mind has probably continued
to be occupied with the problem and has suddenly found a
significant combination. Now, a new idea arriving during con-
scious thinking often produces a certain emotional reaction — we
feel pleased about it and perhaps somewhat excited. Perhaps the
subconscious mind is also capable of reacting in this way and
this has the eflfect of bringing the idea into the conscious mind.
This is only a conjecture, but there can be Httle doubt that a
problem may continue to occupy the subconscious mind, for
common experience shows that sometimes you " can't get a
problem off your mind " because it keeps cropping up involun-
tarily in your thoughts. Secondly, there is no doubt about the
emotion often associated with an intuition.

Some ideas come into consciousness and are grasped, but might
not some fail to appear in the conscious mind or only appear

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THE ART OF SCIENTIFIC INVESTIGATION

fleetingly and disappear again like the things we were about to
say but slipped away irretrievably before there was a break in
the conversation? According to the hypothesis just outlined the
more emotion associated with the idea the more likely it would
be to get through to the consciousness. On this reasoning one
would expect it to be helpful to have a strong desire for a solution
to the problem and also to cultivate a "taste" in scientific matters.
It would be interesting to know whether scientists who say they
never get intuitions are those who find no joy in new ideas or are
deficient in emotional sensitivity.

The conception of the psychology of intuition outlined is in
accord with what is known about the conditions that are con-
ducive to their occurrence. It provides an explanation for the
importance of (a) freedom from other competing problems and
worries, and {b) the helpfulness of periods of relaxation in
allowing for the appearance of the intuition, for messages from
the subconscious may not be received if the conscious mind is
constantly occupied or too fatigued. There have been several
instances of famous generalisations coming to people when they
were ill in bed. The idea of natural selection in evolution came
to Wallace during a bout of malaria, and Einstein has reported
that his profound generalisation connecting space and time
occurred to him while he was sick in bed. Both Cannon and
Poincare report having got bright ideas when lying in bed unable
to sleep — the only good thing to be said for insomnia ! It is said
that James Brindley, the great engineer, when up against a
difficult problem, would go to bed for several days till it was
solved. Descartes is said to have made his discoveries while lying
in bed in the morning and Cajal refers to those placid hours after
awakening which Goethe and so many others considered pro-
pitious to discovery. Walter Scott wrote to a friend :

" The half hour between waking and rising has all my life
proved propitious to any task which was exercising my invention.
... It was always when I first opened my eyes that the desired
ideas thronged upon me."

Baker finds lying in the bath the ideal time and suggests that
Archimedes hit upon his famous principle in the bath because of
the favourable conditions and not because he noticed the
buoyancy of his body in water. The favourable effects of the bed

74

INTUITION

and the bath are probably due to complete freedom from dis-
traction and to the fact that all the circumstances are conducive
to reverie. Others attest to the value of leisure or of relaxing
light occupations such as walking in the country or pottering in
the garden. Hughlings Jackson used to advise his students to sit
in a comfortable chair after the day's work was over and allow
their thoughts to wander around things which had interested
them during the day and write down the ideas that came.

It is evident that to get bright ideas the scientist needs time
for meditation. The favourable effect of temporary abandonment
may be to escape from unprofitable conditioned thinking. Intense
concentration on a problem too long continued may produce a
state of mental blockade such as may occur when you try too
hard to recall something that has slipped from your mind.

According to Wallas^ ^ intuitions always appear at the fringe of
consciousness, not at the focus. He considers that an effort should
be made to grasp them and that a watch should be kept for
valuable ideas in the eddies and backwashes rather than in the
main current of thought.

It is said that certain people get some kind of warning preced-
ing an intuition. They become aware that something of that
nature is imminent without knowing exactly what it will be.
Wallas calls this " intimation ". This curious phenomenon does
not seem to be at all general.

My colleague, F. M. Burnet, finds that intuitions come to him
mainly when he is writing and, unlike most people, rarely when
he is relaxing. My own experience is that when I have been con-
centrating on a subject for several days, it keeps coming back
into my mind after I have stopped deliberately working on it.
During a lecture, social evening, concert or cinema my thoughts
will frequently revert to it and then sometimes after a few
moments of conscious thought a new idea will occur. Occasionally
the idea springs into the consciousness with Uttle or perhaps no
preliminary conscious thinking. The brief preliminary conscious
thinking may be similar to Wallas' "intimation", and can easily
be missed or forgotten. A number of people have commented
on the favourable influence of music but there is by no means
universal agreement on this point. I find some, but not all,
forms of music conducive to intuitions, both when I am attending

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THE ART OF SCIENTIFIC INVESTIGATION

an entertainment and when I am writing. The enjoyment of
music is rather similar, emotionally, to the enjoyment derived
from creative mental activity, and suitable music induces the right
mood for productive thought.

Elsewhere mention has been made of the tremendous emotional
stimulus many people get when they either make a new discovery
or get a brilliant intuition. Possibly this emotional reaction is
related to the amount of emotional and mental effort that has
been invested, as it were, in the problem. Also there is the sudden
release from all the frustrations that have been associated with
work on the problem. In this connection it is interesting to note
the revealing statement of Claude Bernard :

" Those who do not know the torment of the unknown cannot
have the joy of discovery."

Emotional sensitivity is perhaps a valuable attribute for a scien-
tist to possess. In any event the great scientist must be regarded
as a creative artist and it is quite false to think of the scientist
as a man who merely follows rules of logic and experiment.
Some of the masters of the art of research have displayed
artistic talents in other directions. Einstein was a keen musician
and so was Planck. Pasteur and Bernard early showed consfder-
able promise in painting and play-writing, respectively. Nicolle
comments on the interesting and curious fact that the ancient
Peruvian language had a single word (hamavec) for both poet
and inventor. ^^

Technique of seeking and capturing intuitions

It may be useful to recapitulate and set out systematically the
conditions which most people find conducive to intuition.

(a) The most important prerequisite is prolonged contemplation
of the problem and the data until the mind is saturated with it.
There must be a great interest in it and desire for its solution. The
mind must work consciously on the problem for days in order
to get the subconscious mind working on it. Naturally the more
relevant data the mind has to work on, the better are the chances
of reaching a conclusion.

(b) An important condition is freedom from other problems
or interests competing for attention, especially worry over private
affairs.

76

INTUITION

Referring to these two prerequisites Piatt and Baker say :

" No matter how diligently you apply your conscious thought
to your work during office hours, if you are not really wrapped
up in your work sufficiently to have your mind unconsciously
revert to it at every opportunity, or if you have problems of so
much more urgency that they crowd out the scientific problems,
then you can expect little in the way of an intuition."

(c) Another favourable condition is freedom from interruption
or even fear of interruption or any diverting influence such as
interesting conversation within earshot or sudden and excessively
loud noises.

(d) Most people find intuitions are more likely to come during
a period of apparent idleness and temporary abandonment of the
problem following periods of intensive work. Light occupations
requiring no mental effort, such as walking in the country,
bathing, shaving, travelhng to and from work, are said by some
to be when intuitions most often appear, probably because under
these circumstances there is freedom from distraction or interrup-
tion and the conscious mind is not so occupied as to suppress
anything interesting arising in the subconscious. Others find lying
in bed most favourable and some people deliberately go over the
problem before going to sleep and others before rising in the
morning. Some find that music has a helpful influence but it is
notable that only very few consider that they get any assistance
from tobacco, coffee or alcohol. A hopeful attitude of mind
may help.

{e) Positive stimulus to mental activity is provided by some form
of contact with other minds : (i) discussion with either a colleague
or a lay person; (ii) writing a report on the investigation, or giving
a talk on it ; (iii) reading scientific articles, including those giving
views with which one disagrees. When reading articles on topics
quite unrelated to the problem, the concept underlying a
technique or principle may be absorbed and thrown out again as
an intuition relating to one's own work.

(/) Having considered the mental technicalities of deliberately
seeking intuitions, there remains one further important practical
point. It is a common experience that new ideas often vanish
within a minute or so of their appearance if an effort is not made
to capture them by focusing attention on them long enough to

77

THE ART OF SCIENTIFIC INVESTIGATION

fix them in the memory. A valuable device which is widely used
is to make a habit of carrying pencil and paper and noting down
original ideas as they flash into the mind. It is said that Thomas
Edison had a habit of jotting down almost every thought that
occurred to him, however insignificant it may have appeared at
the moment. This technique has also been much used by poets
and musicians, and Leonardo da Vinci's notes provide a classical
example of its use in the arts. Ideas coming during sleep are
likely to be particularly elusive, and some psychologists and
scientists always leave a pencil and paper nearby; this is also
useful for capturing ideas which occur before one goes to sleep
or while lying in bed in the morning. Ideas often make their
appearance in the fringe of consciousness when one is reading,
writing or otherwise engaged mentally on a theme which it is
not desirable to interrupt. These ideas should be roughly jotted
down as quickly as possible ; this not only preserves them but also
serves the useful purpose of getting them "off your mind" with
the minimum interruption to the main interest. Concentration
requires that the mind should not be distracted by retaining ideas
on the fringe of consciousness.

(g) Three very important adverse influences have already been
mentioned ; interruption, worry and competing interests. It takes
time to get your mind "warmed up" and working efficiently on
a subject, holding a mass of relevant data on the fringe of
consciousness. Interruptions disturb this delicate complex and
break the mood. Also mental and physical fatigue, too constant
working on the problem (especially under pressure), petty irrita-
tions and really distracting types of noise can miUtate against
creative thinking. These remarks do not conflict with what is said
in Chapter Eleven about the best work sometimes being done
under adversity and mental stress. There I am referring rather
to the deep-seated problems of life which sometimes may drive
one to work in an attempt to escape them. In this chapter I am
speaking of the immediate problems of everyday life.

Scientific taste

This seems the most appropriate place to discuss the concept
"scientific taste". Hadamard and others have made the interesting
observation that there is such a thing as scientific taste, just as

78

INTUITION

there is a literary and an artistic taste/" Dale speaks of "the
subconscious reasoning which we call instinctive judgment 'V'^
W. Ostwald*^ refers to "scientific instinct", and some people use
the words "intuition" and "feeling" in this connection, by which
they mean the same thing, but it seems to me more correct to
call this faculty taste. It is probably synonymous with "personal
judgment", which some scientists would probably prefer, but
I think that expression is even less illuminating than is "taste".
It is perhaps more exact to say that taste is that on which we
base our personal judgment.

Taste can perhaps best be described as a sense of beauty or
aesthetic sensibility, and it may be reUable or not, depending on
the individual. Anyone who has it simply feels in his mind that
a particular line of work is of interest for its own sake and worth
following, perhaps without knowing why. How reUable one's
feelings are can be determined only by the results. The concept
of scientific taste may be explained in another way by saying
that the person who possesses the flair for choosing profitable lines
of investigation is able to see further whither the work is leading
than are other people, because he has the habit of using his
imagination to look far ahead instead of restricting his thinking
to established knowledge and the immediate problem. He may
not be able to state explicitly his reasons or envisage any particular
hypothesis, for he may see only vague hints that it leads towards
one or another of several crucial questions.

An illustration of taste in non-scientific matters is the choice
of words and composition of sentences when writing. Only
occasionally is it necessary to check the correctness of the language
used by submitting it to grammatical analysis; usually we just
"feel" that the sentence is correct or not. The elegance and
aptness of the English which is produced largely automatically
is a function of the taste we have acquired by training in
choice and arrangement of words. In research, taste plays an
important part in choosing profitable subjects for investigation,
in recognising promising clues, in intuition, in deciding on a
course of action where there are few facts with which to reason,
in discarding hypotheses that require too many modifications and
in forming an opinion on new discoveries before the evidence is
decisive.

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THE ART OF SCIENTIFIC INVESTIGATION

Although, as with other tastes, people may be endowed with
the capacity for scientific taste to varying degrees, it may also be
cultivated by training oneself in the appreciation of science, as,
for example, in reading about how discoveries have been made.
As with other tastes, taste in science will only be found in people
with a genuine love of science. Our taste derives from the
summation of all that we have learnt from others, experienced
and thought.

Some scientists may have difficulty in comprehending such an
abstract concept as taste, and some may find it unacceptable,
because all the scientist's training is toward making him eliminate
subjective influences from his work. No one would dispute the
policy of keeping the subjective element out of experimentation,
observation and technical procedures to the greatest possible
extent. How far such a pohcy can effectively be carried out in a
scientist's thinking is more open to question. Most people do not
realise how often opinions that are supposed to be based on reason
are in fact but rationalisations of prejudice or subjective motives.
There is a very considerable part of scientific thinking where
there is not enough sound knowledge to allow of effective
reasoning and here the judgment will inevitably be largely
influenced by taste. In research we continually have to take action
on issues about which there is very little direct evidence. There-
fore, rather than delude ourselves, I think it is wise to face the
fact of subjective judgment and accept the concept of scientific
taste, which seems a useful one. But by accepting the idea, I do
not mean to suggest that we should adopt taste as a guide in
cases where there is enough evidence on which to base an
objectively reasoned judgment. The phrase, "scientific taste",
must not be allowed to blind us to the risks which are associated
with all subjective thinking.

SUMMARY

Intuition is used here to mean a clarifying idea that springs
suddenly into the mind. It by no means always proves to be
correct.

The conditions most conducive to intuitions are as follows :
(a) The mind must first be prepared by prolonged conscious
puzzling over the problem, (b) Competing interests or worries are

80

INTUITION

inimical to intuitions, {c) Most people require freedom from
interruptions and distractions, (d) Intuitions often make their
appearance when the problem is not being worked on. (e) Positive
stimuli are provided by intellectual contacts with other minds
such as in discussion, critical reading or writing. (/) Intuitions
often disappear from the mind irretrievably as quickly as they
come, so should be written down, {g) Unfavourable influences
include, in addition to interruptions, worry and competing
interests, also mental or physical fatigue, too constant working
on a problem, petty irritations and distracting types of noises.
Often in research our thoughts and actions have to be guided
by personal judgment based on scientific taste.

8i

CHAPTER SEVEN

REASON

" Discovery should come as an adventure rather than as
the result of a logical process of thought. Sharp, prolonged
thinking is necessary that we may keep on the chosen road,
but it does not necessarily lead to discovery."

— Theobald Smpth

Limitations and hazards

BEFORE considering the role of reason in research it may be
useful to discuss the limitations of reason. These are more
serious than most people realise, because our conception of science
has been given us by teachers and authors who have presented
science in logical arrangement and that is seldom the way in which
knowledge is actually acquired.

Everyday experience and history teach us that in the biological
and medical sciences reason seldom can progress far from the
facts without going astray. The scholasticism and authoritarianism
prevailing during the Middle Ages was incompatible with science.
With the Renaissance came a change in outlook : the beUef that
things ought and must behave according to accepted views
(mostly taken from the classics) was supplanted by a desire to
observe things as they really are, and human knowledge began
to grow again. Francis Bacon had a great influence on the
development of science mainly, I think, because he showed that
most discoveries had been made empirically rather than by use
of deductive logic. In 1 605 he said :

" Men are rather beholden . . . generally to chance, or anything

else, than to logic, for the invention of arts and sciences ",*

and in 1620,

" the present system of logic rather assists in confirming and
rendering inveterate the errors founded on vulgar notions, than
in searching after truth, and is therefore more hurtful than
useful." 7

82

REASON

Later the French philosopher Rene Descartes made people realise
that reason can land us in endless fallacies. His golden rule was :

" Give unqualified assent to no propositions but those the
truth of which is so clear and distinct that they cannot be
doubted."

Every child, indeed one might even say, every young verte-
brate, discovers gravity; and yet modern science with all its
knowledge cannot yet satisfactorily " explain " it. Not only are
reason and logic therefore insufficient to provide a means of
discovering gravity without empirical knowledge of it, but all
the reason and logic apphed in classical times did not even
enable inteUigent men to deduce correctly the elementary facts
concerning it.

F. C. S. Schiller, a modem philosopher, has made some illum-
inating comments on the use of logic in science and I shall quote
from him at length :

" Among the obstacles to scientific progress a high place must
certainly be assigned to the analysis of scientific procedure which
logic has provided. ... It has not tried to describe the methods
by which the sciences have actually advanced, and to extract . . .
rules which might be used to regulate scientific progress, but has
freely re-arranged the actual procedure in accordance with its
prejudices, for the order of discovery there has been substituted
an order of proof."®"

Credence of the logician's view has been encouraged by the
method generally adopted in the writing of scientific papers.
The logical presentation of results which is usually followed is
hardly ever a chronological or full account of how the investi-
gation was actually carried out, for such would often be dull and
difficult to follow and, for ordinary purposes, wasteful of space.
In his book on the writing of scientific papers, Allbutt specifically
advocates that the course of the research should not be followed
but that a deductive presentation should be adopted.

To quote again from Schiller, who takes an extreme view :

" It is not too much to say that the more deference men of
science have paid to logic, the worse it has been for the scientific
value of their reasoning. . . . Fortunately for the world, however,
the great men of science have usually been kept in salutary
ignorance of the logical tradition." ®°

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THE ART OF SCIENTIFIC INVESTIGATION

He goes on to say that logic was developed to regulate debates in
the Greek schools, assemblies and law-courts. It was necessary to
determine which side won, and logic served this purpose, but it
should not occasion surprise that it is quite unsuitable in science,
for which it was never intended. Many logicians emphatically
declare that logic, interested in correctness and validity, has
nothing at all to do with productive thinking.

Schiller goes even further in his criticism of traditional logic
and says that not only is it of little value in making new dis-
coveries, but that history has shown it to be of little value in
recognising their validity or ensuring their acceptance when they
have been proclaimed. Indeed, logical reasoning has often
prevented the acceptance of new truths, as is illustrated by the
persecution to which the great discoverers have so often been
subjected.

" The slowness and difficulty with which the human race makes
discoveries and its blindness to the most obvious facts, if it
happens to be unprepared or unwilling to see them, should suffice
to show that there is something gravely wrong about the logician's
account of discovery."

Schiller was protesting mainly against the view of the scientific
method expounded by certain logicians in the latter half of the
nineteenth century. Most modem philosophers concerning them-
selves with the scientific method do not interpret this phrase as
including the art of discovery, which they consider to be outside
their province. They are interested in the philosophical implica-
tions of science.

Wilfred Trotter^* also had some provocative things to say
about the poor record which reason has in the advancement of
scientific knowledge. Not only has it few discoveries to its credit
compared to empiricism, he says, but often reason has obstructed
the advance of science owing to false doctrines based on it. In
medicine particularly, practices founded on reason alone have
often prevailed for years or centuries before someone with an
independent mind questioned them and in many cases showed
they were more harmful than beneficial.

Logicians distinguish between inductive reasoning (from par-
ticular instances to general principles, from facts to theories) and
deductive reasoning (from the general to the particular, applying

84

REASON

a theory to a particular case). In induction one starts from
observed data and develops a generalisation which explains the
relationships between the objects observed. On the other hand, in
deductive reasoning one starts from some general law and applies
it to a particular instance. Thus in deductive reasoning the derived
conclusion is contained within the original premiss, and should
be true if the premiss is true.

Since deduction consists of applying general principles to further
instances, it cannot lead us to new generalisations and so cannot
give rise to major advances in science. On the other hand the
inductive process is at the same time less trustworthy but more
productive. It is more productive because it is a means of arriving
at new theories, but is less trustworthy because starting from a
collection of facts we can often infer several possible theories, all
of which cannot be true as some may be mutually incompatible ;
indeed none of them may be true.

In biology every phenomenon and circumstance is so complex
and so poorly understood that premisses are not clear-cut and
hence reasoning is unreliable. Nature is often too subtle for our
reasoning. In mathematics, physics and chemistry the basic
premisses are more firmly established and the attendant circum-
stances can be more rigidly defined and controlled. Therefore
reason plays a rather more dominant part in extending knowledge
in these sciences. Nevertheless the mathematician Poincare said :
" Logic has very Httle to do with discovery or invention." Similar
views were expressed by Planck and Einstein (pp. 55, 57). The
point here is that inductions are usually arrived at not by the
mechanical application of logic but by intuition, and the course
of our thoughts is constantly guided by our personal judgment.
On the other hand the logician is not concerned with the way
the mind functions but with logical formulation.

From his experience in finding that his hypotheses always had
to be abandoned or at least greatly modified Darwin learnt to
distrust deductive reasoning in the biological sciences. He said :

" I must begin with a good body of facts, and not from
principle, in which I always suspect some fallacy."^*

A basic difficulty in applying reason in research derives from
the fact that terms often cannot be defined accurately and

85

THE ART OF SCIENTIFIC INVESTIGATION

premisses are seldom precise or unconditionally true. Especially
in biology premisses are only true under certain circumstances.
For careful reasoning and clarity of thought one should first
define the terms one uses but in biology exact definitions are often
difficult or impossible to arrive at. Take, for example, the
statement " influenza is caused by a virus." Influenza w^as
originally a clinical concept, that is to say, a disease defined on
clinical characters. We now know that diseases caused by several
different microbes have been embraced by what the clinician
regards as influenza. The virus worker would now prefer to
define influenza as a disease caused by a virus with certain
characters. But this only passes on the difficulty to the defining
of an influenza virus which in turn escapes precise definition.

These difficulties are to some extent resolved if we accept the
principle that in all our reasoning we can deal only in probabili-
ties. Indeed much of our reasoning in biology is more aptly
termed speculation.

I have mentioned some limitations inherent in the application
of logical processes in science; another common source of error
is incorrect reasoning, such as committing some logical fallacy.
It is a delusion that the use of reason is easy and needs no training
or special caution. In the following section I have tried to outline
some general precautions which it may be helpful to keep in mind
in using reason in research.

Some safeguards in use of reason in research

The first consideration is to examine the basis from which we
start reasoning. This involves arriving at as clear an understanding
as possible of what we mean by the terms we employ, and examin-
ing our premisses. Some of the premisses may be well-established
facts or laws, while others may be purely suppositions. It is often
necessary to admit provisionally some assumptions that are not
well established, in which case one needs to be careful not to
forget that they are only suppositions. Michael Faraday warned
against the tendency of the mind " to rest on an assumption " and
when it appears to fit in with other knowledge to forget that it
has not been proved. It is generally agreed that unverified
assumptions should be kept down to the bare minimum and the

86

REASON

hypothesis with the fewest assumptions is to be preferred. (This
is known as the maxim of parsimony, or " Occam's Razor ". It
was propounded by William of Occam in the fourteenth century.)

How easy it is for unverified assumptions to creep into our
reasoning unnoticed ! They are often introduced by expressions
such as "obviously", "of course", "surely". I would have
thought that it was a fairly safe assumption that well-fed animals
live longer on the average that underfed ones, but in recent
experiments mice whose diet was restricted to a point where their
growth rate was below normal Uved much longer than mice
allowed to eat as much as they wished.

Having arrived at a clear understanding of the basis from
which we start, at every step in our reasoning it is essential to
pause and consider whether all conceivable alternatives have been
taken into account. The degree of uncertainty or supposition is
usually greatly magnified at each step.

It is important not to confuse facts with their interpretations,
-tbatJs to say, to distinguish between data and generalisations.
Facts are particular observational data relating to the past or
present. To take an obvious illustration : it may be a fact that
when a certain drug was administered to rabbits it killed them,
but to say that the drug is poisonous for rabbits is not a statement
of a fact but a generalisation or law arrived at by induction. The
change from the past tense to the present usually involves stepping
from the facts to the induction. It is a step which must often be
taken but only with an understanding of what one is doing.
Confusion may also arise from the way in which the results are
interpreted : strictly the facts arising from experiments can only
be described by a precise statement of what occurred. Often in
describing an experiment we interpret the results into other terms,
perhaps without realising we are departing from a statement of
the facts.

A difficulty we are always up against is that we have to argue
from past and present to the future. Science, to be of value, must
predict. We have to reason from data obtained in the past by
experiment and observation, and plan accordingly for the future.
This presents special difficulties in biology because, owing to the
incompleteness of our knowledge, we can seldom be sure that
changed circumstances in the future may not influence the results.

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THE ART OF SCIENTIFIC INVESTIGATION

Take, for example, the testing of a new vaccine against a disease.
The vaccine may prove effective in several experiments but we
must still be cautious in saying it will be effective in future.
Influenza vaccine gave a considerable degree of protection in large
scale trials in U.S.A. in 1943 and 1945, but against the next
epidemic in 1947 it was of no value. Regarded as a problem in
logic the position is that by inductive inference from our data we
arrive at a generalisation (for instance, that the vaccine is effec-
tive). Then in future when we wish to guard against the disease we
use this generalisation deductively and apply it to the particular
practical problem of protecting certain people. The difficult
point in the reasoning is, of course, making the induction. Logic
has little to say here that is of help to us. All we can do is to
refrain from generalising until we have collected fairly extensive
data to provide a wide basis for the induction and regard as
tentative any conclusion based on induction or, as we more often
hear in everyday language, be cautious with generalisations.
Statistics help us in drawing conclusions from our data by ensur-
ing that our conclusions have a certain reliability, but even
statistical conclusions are strictly valid only for events which have
already occurred.

Generalisations can never be proved. They can be tested by
seeing whether deductions made from them are in accord with
experimental and observational facts, and if the results are not
as predicted, the hypothesis or generalisation may be disproved.
But a favourable result does not prove the generalisation, because
the deduction made from it may be true without its being true.
Deductions, themselves correct, may be made from palpably
absurd generalisations. For instance, the truth of the hypothesis
that plague is due to evil spirits is not established by the correct-
ness of the deduction that you can avoid the disease by keeping
out of the reach of the evil spirits. In strict logic a generalisation
is never proved and remains on probation indefinitely, but if it
survives all attempts at disproof it is accepted in practice,
especially if it fits well into a wider theoretical scheme.

If scientific logic shows we must be cautious in arriving at
generalisations ourselves, it shows for the same reasons that we
should not place excessive trust in any generalisation, even widely
accepted theories or laws. Newton did not regard the laws he

88

REASON

formulated as the ultimate truth, but probably most following
him did until Einstein showed how well-founded Newton's
caution had been. In less fundamental matters how often do we
see widely accepted notions superseded !

Therefore the scientist cannot afford to allow his mind to
become fixed, with reference not only to his own opinions but
also to prevailing ideas. Theobald Smith said :

" Research is fundamentally a state of mind involving con-
tinual re-examination of doctrines and axioms upon which
current thought and action are based. It is, therefore, critical of
existing practices."*^

No accepted idea or " established principle " should be regarded
as beyond being questioned if there is an observation challenging
it. Bernard wrote :

" If an idea presents itself to us, we must not reject it simply
because it does not agree with the logical deductions of a reign-
ing theory."

Great discoveries have been made by means of experiments
devised with complete disregard for well accepted beliefs.
Evidently it was Darwin who introduced the expression " fool's
experiment " to refer to such experiments, which he often under-
took to test what most people would consider not worth testing.

People in most other walks of Ufe can allow themselves the
indulgence of fixed ideas and prejudices which make thinking
so much easier, and for all of us it is a practical necessity to hold
definite opinions on many issues in everyday life, but the research
worker must try to keep his mind malleable and avoid holding
set ideas in science. We have to strive to keep our mind receptive
and to examine suggestions made by others fairly and on their
own merits, seeking arguments for as well as against them. We
must be critical, certainly, but beware lest ideas be rejected
because an automatic reaction causes us to see only the arguments
against them. We tend especially to resist ideas competing with
our ov^m.

A useful habit for scientists to develop is that of not trusting
ideas based on reason only. As Trotter says, they come into the
mind often with a disarming air of obviousness and certainty.
Some consider that there is no such thing as pure reasoning, that
is to say, except where mathematical symbols are involved.

89

THE ART OF SCIENTIFIC INVESTIGATION

Practically all reasoning is influenced by feelings, prejudice and
past experience, albeit often subconsciously. Trotter wrote :

" The dispassionate intellect, the open mind, the unprejudiced
observer, exist in an exact sense only in a sort of intellectualist
folk-lore; states even approaching them cannot be reached with-
out a moral and emotional effort most of us cannot or will not
make."

A trick of the mind well known to psychologists is to " rational-
ise ", that is, to justify by reasoned ai^ument a view which in
reality is determined by preconceived judgment in the sub-
conscious mind, the latter being governed by self-interest,
emotional considerations, instinct, prejudice and similar factors
which the person usually does not realise or admit even to him-
self In somewhat similar vein is W. H. George's warning against
believing that things in nature ought to conform to certain
patterns or standards and regarding all exceptions as abnormal.
He says that the " should-ought mechanism " has no place what-
ever in research, and its complete abandonment is one of the
foundation stones of science. It is premature, he considers, to
worry about the technique of experimentation until a man has
become dissatisfied with the " should-ought " way of thinking.

It has been said by some that scientists should train them-
selves to adopt a disinterested attitude to their work. I cannot
agree with this view and think the investigator should try to
exercise sufficient self-control to consider fairly the evidence
against a certain outcome for which he fervently hopes, rather
than to try to be disinterested. It is better to recognise and face
the danger that our reasoning may be influenced by our wishes.
Also it is unwise to deny ourselves the pleasure of associating
ourselves whole-heartedly with our ideas, for to do so would be
to undermine one of the chief incentives in science.

It is important to distinguish between interpolation and extra-
polation. Interpolating means filling in a gap between estabUshed
facts which form a series. When one draws a curve on a graph by
connecting the points one interpolates. Extrapolating is going
beyond a series of observations on the assumption that the same
trend continues. Interpolation is considered permissible for most
purposes provided one has a good series of data to work from,
but extrapolation is much more hazardous. Apparently obvious

90

REASON

extensions of our theories beyond the field in which they have
been tested often lead us astray. The process of extrapolation is
rather similar to implication and is useful in providing suggestions.

A useful aid in getting a clear understanding of a problem is
to write a report on all the information available. This is helpful
when one is starting on an investigation, when up against a
difficulty, or when the investigation is nearing completion. Also
at the beginning of an investigation it is useful to set out clearly
the questions for which an answer is being sought. Stating the
problem precisely sometimes takes one a long way toward the
solution. The systematic arrangement of the data often discloses
flaws in the reasoning, or alternative lines of thought which had
been missed. Assumptions and conclusions at first accepted as
" obvious " may even prove indefensible when set down clearly
and examined critically. Some institutions make it a rule for all
research workers to furnish a report quarterly on the work done,
and work planned. This is useful not only for the director to keep
in touch with developments but also to the workers themselves.
Certain directors prefer verbal reports which they consider more
useful in helping the research worker " get his ideas straight ".

Careful and correct use of language is a powerful aid to
straight thinking, for putting into words precisely what we
mean necessitates getting our own minds quite clear on what
we mean. It is with words that we do our reasoning, and
writing is the expression of our thinking. Discipline and training
in writing is probably the best training there is in reasoning.
Allbutt has said that slovenly writing reflects slovenly thinking,
and obscure writing usually confused thinking. The main aim in
scientific reports is to be as clear and precise as possible and make
each sentence mean exactly what it is intended to and be incap-
able of other interpretation. Words or phrases that do not have
an exact meaning are to be avoided because once one has given
a name to something, one immediately has a feeling that the
position has been clarified, whereas often the contrary is true.
"A verbal cloak of ignorance is a garment that often hinders
progress." ^^

The role of reason in research

Although discoveries originate more often from unexpected
experimental results or observations, or from intuitions, than

91

THE ART OF SCIENTIFIC INVESTIGATION

directly from logical thought, reason is the principle agent in most
other aspects of research and the guide to most of our actions.
It is the main tool in formulating hypotheses, in judging the
correctness of ideas conjured up by imagination and intuition,
in planning experiments and deciding what observations to
make, in assessing the evidence and interpreting new facts, in
making generalisations and finally in finding extensions and
applications of a discovery.

The methods and functions of discovery and proof in research
are as different as are those of a detective and of a judge in a
court of law. While playing the part of the detective the investi-
gator follows clues, but having captured his alleged fact, he turns
judge and examines the case by means of logically arranged
evidence. Both functions are equally essential but they are
diflferent.

It is in " factual " discoveries in biology that observation and
chance — empiricism — plays such an important part. But facts
obtained by observation or experiment usually only gain signi-
ficance when we use reason to build them into the general body
of knowledge. Darwin said :

" Science consists in grouping facts so that general laws or
conclusions may be drawn from them."^*

In research it is not sufficient to collect facts; by interpreting
them, by seeing their significance and consequences we can often
go much further. Walshe considers that just as important as
making discoveries is what we make of our discoveries, or for
that matter, of those of other people. ^°° To help retain and use
information our minds require a rationalised, logically consistent
body of knowledge. Hughlings Jackson said that

" We have multitudes of facts, but we require, as they accumu-
late, organisations of them into higher knowledge; we require
generalisations and working hypotheses."

The recognition of a new general principle is the consummation
of scientific study.

Discoveries originating from so-called chance observations,
from unexpected results in experiments or from intuitions are
dramatic and arrest attention more than progress resulting from
purely rational experimentation in which each step follows

92

REASON

logically on the previous one so that the discovery only gradually
unfolds. Therefore the latter, less spectacular process may be
responsible for more advances than has been imphed in the other
chapters of this book. Moreover, as Zinsser said :

" The preparatory accumulation of minor discoveries and of
accurately observed details ... is almost as important for the
mobilisation of great forward drives as the periodic correlation
of these disconnected observations into principles and laws by
the vision of genius."^"*

Often when one looks into the origin of a discovery one finds
that it was a much more gradual process than one had imagined.

In nutritional research, the discovery of the existence of the
various vitamins was in a number of instances empirical, but sub-
sequent development of knowledge of them was rational. Usually
in chemotherapy, after the initial empirical discovery opening up
the field, rational experimentation has led to a series of improve-
ments, as in the development of sulphathiazole, sulphamerazine,
sulphaguanidine, etc., following on the discovery of the thera-
peutic value of sulphanilamide, the first compound of this type
found to have bacteriostatic properties.

As described in the Appendix, Fleming followed up a chance
observation to discover that the mould Penicillium notatum
produced a substance that had bacteriostatic properties and was
non-toxic. However, he did not pursue it sufficiently to develop
a chemotherapeutic agent and the investigation was dropped.
During the latter quarter of the last century and first part of this
there were literally dozens of reports of discoveries of antibacterial
substances produced by bacteria and fungi.^^ Even penicillin
itself was discovered before Fleming or Rorey."^ Quite a number
of writers had not only suggested that these products might be use-
ful therapeutically but had employed them and in some instances
good results seem to have been obtained.^^ But all these empirical
discoveries were of little consequence until Florey, by a deliber-
ately planned, systematic attack on the problem, produced peni-
cillin in a relatively pure and stable form and so was able to
demonstrate its great clinical value. Often the original discovery,
like the crude ore from the mine, is of little value until it has
been refined and fully developed. This latter process, less specta-
cular and largely rational, usually requires a diflferent type of

93

THE ART OF SCIENTIFIC INVESTIGATION

scientist and often a team. The role of reason in research is not
so much in exploring the frontiers of knowledge as in developing
the findings of the explorers.

A type of reasoning not yet mentioned is reasoning by analogy,
which plays an important part in scientific thought. An analogy
is a resemblance between the relationship of things, rather than
between the things themselves. When one perceives that the
relationship between A and B resembles the relationship between
X and T on one point, and one knows that A is related to 5 in
various other ways, this suggests looking for similar relationships
between X and T. Analogy is very valuable in suggesting clues or
hypotheses and in helping us comprehend phenomena and
occurrences we cannot see. It is continually used in scientific
thought and language but it is as well to keep in mind that analogy
can often be quite misleading and of course can never prove any-
thing.

Perhaps it is relevant to mention here that modem scientific
philosophers try to avoid the notion of cause and effect. The
current attitude is that scientific theories aim at describing associa-
tions between events without attempting to explain the relation-
ship as being causal. The idea of cause, as implying an inherent
necessity, raises philosophical difficulties and in theoretical physics
the idea can be abandoned with advantage as there is then no
longer the need to postulate a connection between the cause and
effect. Thus, in this view, science confines itself to description —
"how", not "why".

This outlook has been developed especially in relation to
theoretical physics. In biology the concept of cause and effect is
still used in practice, but when we speak of the cause of an event
we are really over-simplifying a complex situation. Very many
factors are involved in bringing about an event but in practice we
commonly ignore or take for granted those that are always present
or well-known and single out as the cause one factor which is
unusual or which attracts our attention for a special reason. The
cause of an outbreak of plague may be regarded by the bacterio-
logist as the microbe he finds in the blood of the victims, by the
entomologist as the microbe-carrying fleas that spread the disease,
by the epidemiologist as the rats that escaped from the ship and
brought the infection into the port.

94

REASON

SUMMARY

The origin of discoveries is beyond the reach of reason. The
role of reason in research is not hitting on discoveries — either
factual or theoretical — but verifying, interpreting and developing
them and building a general theoretical scheme. Most biological
" facts " and theories are only true under certain conditions and
our knowledge is so incomplete that at best we can only reason on
probabilities and possibiUties.

95

CHAPTER EIGHT

OBSERVATION

" Knowledge comes from noticing resemblances and
recurrences in the events that happen around us."

— Wilfred Trotter

Illustrations

PASTEUR was curious to know how anthrax persists endemi-
cally, recurring in the same fields, sometimes at intervals
of several years. He was able to isolate the organisms from soil
around the graves in which sheep dead of the disease had been
buried as long as 1 2 years before. He was puzzled as to how the
organism could resist sunlight and other adverse influences so
long. One day while walking in the fields he noticed a patch of
soil of different colour from the rest and asked the farmer the
reason. He was told that sheep dead of anthrax had been buried
there the previous year.

" Pasteur, who always examined things closely, noticed on the
surface of the soil a large number of worm castings. The idea
then came to him that in their repeated travelling from the
depth to the surface, the worms carried to the surface the earth
rich in humus around the carcase, and with it the anthrax spores
it contained. Pasteur never stopped at ideas but passed straight
to the experiment. This justified his forecast. Earth contained
in a worm, inoculated into a guinea-pig produced anthrax."^*

This is a fine example of the value of direct personal observation.
Had Pasteur done his thinking in an armchair it is unlikely that
he would have cleared up this interesting bit of epidemiology.

When some rabbits from the market were brought into Claude
Bernard's laboratory one day, he noticed that the urine which
they passed on the table was clear and acid instead of turbid and
alkaline as is usual with herbivorous animals. Bernard reasoned
that perhaps they were in the nutritional condition of carnivora
from having fasted and drawn on their own tissues for susten-

96

OBSERVATION

ance. This he confirmed by ahemately feeding and starving
them, a process which he found altered the reaction of their
urine as he had anticipated. This was a nice observation and
would have satisfied most investigators, but not Bernard. He
required a " counterproof ", and so fed rabbits on meat. This
resulted in an acid urine as expected, and to complete the experi-
ment he carried out an autopsy on the rabbits. To use his words :

" I happened to notice that the white and milky lymphatics
were first visible in the small intestine at the lower part of the
duodenum, about 30 cm. below the pylorus. The fact caught
my attention because in dogs they are first visible much higher
in the duodenum just below the pylorus."

On observing more closely, he saw that the opening of the
pancreatic duct coincided with the position where the lymphatics
began to contain chyle made white by emulsion of the fatty
materials. This led to the discovery of the part played by pan-
creatic juice in the digestion of fats.^^

Darwin relates an incident illustrating how he and a colleague
failed to observe certain unexpected phenomena when they were
exploring a valley :

" Neither of us saw a trace of the wonderful glacial phenomena
all around us; we did not notice plainly scored rocks, the
perched boulders, the lateral and terminal moraines."'

28

These things were not observed because they were not expected
or specifically looked for.

While watching the movements of the bacteria which cause
butyric acid fermentation, Louis Pasteur noticed that when the
organisms came near the edge of the drop they stopped moving.
He guessed this was due to the presence of oxygen in the fluid
near the air. Puzzling over the significance of this observation he
concluded that there was no free oxygen where the bacteria were
actively moving. From this he made the far reaching deduction
that Ufe can exist without oxygen, which at that time was thought
not possible. Further he postulated that fermentation is a meta-
bolic process by which microbes obtain oxygen from organic sub-
stances. These important i^leas which Pasteur later substantiated
had their origin in the observation of a detail that many would
not have noticed.

97

THE ART OF SCIENTIFIC INVESTIGATION

Many of the anecdotes cited in Chapters Three and Four and
in the Appendix also provide illustrations of the role of observa-
tion in research.

Some general principles in observation

In discussing the thoroughly unreliable nature of eye-witness
observation of everyday events, W. H. George says :

" What is observed depends on who is looking. To get some
agreement between observers they must be paying attention,
their lives must not be consciously in danger, their prime neces-
sities of life must preferably be satisfied and they must not be
taken by surprise. If they are observing a transient phenomenon,
it must be repeated many times and preferably they must not
only look at, but must look for, each detail."*^

As an illustration of the difficulty of making careful observa-
tions, he tells the following story.

At a congress on psychology at Gottingen, during one of the
meetings, a man suddenly rushed into the room chased by another
with a revolver. After a scuffle in the middle of the room a shot
was fired and both men rushed out again about twenty seconds
after having entered. Immediately the chairman asked those
present to write down an account of what they had seen.
Although the observers did not know it at the time, the incident
had been previously arranged, rehearsed and photographed. Of
the forty reports presented, only one had less than 20 per cent
mistakes about the principal facts, 14 had from 20 to 40 per cent
mistakes, and 25 had more than 40 per cent mistakes. The most
noteworthy feature was that in over half the accounts, 10 per
cent or more of the details were pure inventions. This poor
record was obtained in spite of favourable circumstances, for
the whole incident was short and sufficiently striking to arrest
attention, the details were immediately written down by people
accustomed to scientific observation and no one was himself
involved. Experiments of this nature are commonly conducted
by psychologists and nearly always produce results of a similar

type.

Perhaps the first thing to realise about observations is that not
only do observers frequently miss seemingly obvious things, but
what is even more important, thev often invent quite false

98

OBSERVATION

observations. False observations may be due to illusions, where
the senses give wrong information to the mind, or the errors may
have their origin in the mind.

Illustrations of optical illusions can be provided from various
geometrical figures (see, for example, George*^) and by distor-
tions caused by the refraction of light when it passes through
water, glass or heated air. Remarkable demonstrations of the
unreliability of visual observations are provided by the tricks
of " magicians " and conjurors. Another illustration of false
information arising from the sense organs is provided by placing
one hand in hot water and one in cold for a few moments and
then plunging them both into tepid water. A curious fallacy of
this nature was recorded by the ancient Greek historian,
Herodotus :

" The water of this stream is lukewarm at early dawn. At the
time when the market fills it is much cooler; by noon it has
grown quite cold; at this time therefore they water their gardens.
As the afternoon advances, the coldness goes off, till, about
sunset the water is once more lukewarm."

In all probability the temperature of the water remained constant
and the change noticed was due to the difference between water
and atmospheric temperatures as the latter changed. Fallacious
observations of a similar type can be shown to arise from illu-
sions associated with sound.

The second class of error in registering and reporting observa-
tion has its origin in the mind itself Many of these errors can
be attributed to the fact that the mind has a trick of unconsciously
filling in gaps according to past experience, knowledge and con-
scious expectations. Goethe has said :

" We see only what we know."

" We are prone to see what lies behind our eyes rather than what
appears before them," an old saying goes. An illustration of this
is seen in the cinema film depicting a lion chasing a negro. The
camera shows now the lion pursuing, now the man fleeing, and
after several repetitions of this we finally see the lion leap on
something in the long grass. Even though the lion and the man
may have at no time appeared on the screen together, most
people in the audience are convinced they actually saw the lion

99

THE ART OF SCIENTIFIC INVESTIGATION

leap on the man, and there have been serious protests that natives
were sacrificed to make such a film. Another illustration of the
subjective error is provided by the following anecdote. A
Manchester physician, while teaching a ward class of students,
took a sample of diabetic urine and dipped a finger in it to taste
it. He then asked all the students to repeat his action. This they
reluctantly did, making grimaces, but agreeing that it tasted
sweet. " I did this," said the physician with a smile, " to teach
you the importance of observing detail. If you had watched me
carefully you would have noticed that I put my first finger in
the urine but licked my second finger !"

It is common knowledge that different people viewing the
same scene will notice different things according to where their
interests lie. In a country scene a botanist will notice the
different species of plants, a zoologist the animals, a geologist
the geological structures, a farmer the crops, farm animals,
etc. A city dweller with none of these interests may see only
a pleasant scene. Most men can pass a day in the company of
a woman and afterwards have only the vaguest ideas about what
clothes she wore, but most women after meeting another woman
for only a few minutes could describe every article the other was
wearing.

It is quite possible to see something repeatedly without register-
ing it mentally. For example, a stranger on arrival in London
commented to a Londoner on the eyes that are painted on the
front of many buses. The Londoner was surprised, as he had
never noticed them. But after his attention had been called to
them, during the next few weeks he was conscious of these eyes
nearly every time he saw a bus.

Changes in a familiar scene are often noticed even though the
observer may not have been consciously aware of the details of
the scene previously. Indeed sometimes an observer may be
aware that something has changed in a familiar scene without
being able to tell what the change is. Discussing this point,
W. H. George says :

" It seems as if the memory preserves something like a photo-
graphic negative of a very familiar scene. At the next examina-
tion this memory image is unconsciously placed over the visual
image present, and, just as with two similar photographic nega-

100

j^^^^^s

SIR ALEXANDER FLEMING

SIR HOWARD FLOREY

G. S. WILSON

F. M. BLRNET

MAX PLANCK

SIR RONALD FISHER

C. H. ANDREWES

J. B. CONANT

OBSERVATION

tives, attention is immediately attracted to the places where the
two do not exactly fit, that is, where there is a change in one
relative to the other. It is noteworthy that this remembered whole
cannot always be recalled to memory so as to enable details to
be described."*^

This analogy should not be taken too literally because the same
phenomenon is seen with memory of other things such as
stories or music. A child who is familiar with a story will often
call attention to slight variations when it is retold even though he
does not know it by heart himself George continues :

" The perception of change seems to be a property of all of
the sense organs, for changes of sound, taste, smell and tempera-
ture are readily noticed. ... It might almost be said that a con-
tinuous sound is only ' heard ' when it stops or the sound
changes." ^^

If we consider that the comparison of the old and new images
takes place in the subconscious, we can draw an analogy with
the hypothesis as to how intuitions gain access to the conscious
mind. One would expect the person to become aware of the
notable facts, that is, the changes, even though he may be unable
to bring all the details into consciousness.

It is important to realise that observation is much more than
merely seeing something; it also involves a mental process. In
all observations there are two elements : {a) the sense-perceptual
element (usually visual) and {b) the mental, which, as we have
seen, may be partly conscious and partly unconscious. Where
the sense-perceptual element is relatively unimportant, it is often
difficult to distinguish between an observation and an ordinary
intuition. For example, this sort of thing is usually referred to as
an observation : "I have noticed that I get hay fever whenever
I go near horses." The hay fever and the horses are perfectly
obvious, it is the connection between the two that may require
astuteness to notice at first, and this is a mental process not dis-
tinguishable from an intuition. Sometimes it is possible to draw
a line between the noticing and the intuition, e.g. Aristotle com-
mented that on observing that the bright side of the moon is al-
ways toward the sun, it may suddenly occur to the observer that
the explanation is that the moon shines by the light of the sun.

lOI

THE ART OF SCIENTIFIC INVESTIGATION

Similarly in three of the anecdotes given at the beginning of
this chapter, the observation was followed by an intuition.

Scientific observation

We have seen how unreliable an observer's report of a complex
situation often is. Indeed, it is very difficult to observe and
describe accurately even simple phenomena. Scientific experi-
ments isolate certain events which are observed by the aid of
appropriate techniques and instruments which have been
developed because they are relatively free from error and have
been found to give reproducible results which are in accord
with the general body of scientific knowledge. Claude Bernard
distinguished two types of observation : (a) spontaneous or
passive observations which are unexpected; and (b) induced or
active observations which are deliberately sought, usually on
account of an hypothesis. It is the former in which we are
chiefly interested here.

Eflfective spontaneous observation involves firstly noticing
some object or event. The thing noticed will only become
significant if the mind of the observer either consciously or
unconsciously relates it to some relevant knowledge or past
experience, or if in pondering on it subsequently he arrives at
some hypothesis. In the last section attention was called to the
fact that the mind is particularly sensitive to changes or differ-
ences. This is of use in scientific observation, but what is more
important and more difficult is to observe (in this instance mainly
a mental process) resemblances or correlations between things
that on the surface appeared quite unrelated. The quotation
from Trotter at the beginning of this chapter refers to this
point. It required the genius of Benjamin Franklin to see the
relationship between frictional electricity and lightning. Recently
veterinarians have recognised a disease of dogs which is manifest
by encephalitis and hardening of the foot pads. Many cases of
the disease have probably been seen in the past without anyone
having noticed the surprising association of the encephalitis with
the hard pads.

One cannot observe everything closely, therefore one must
discriminate and try to select the significant. When practising
a branch of science, the " trained " observer deUberately looks

102

OBSERVATION

for specific things which his training has taught him are
significant, but in research he often has to rely on his own
discrimination, guided only by his general scientific knowledge,
judgment and perhaps an hypothesis which he entertains. As
Alan Gregg, the Director of Medical Sciences for the Rockefeller
Foundation has said :

" Most of the knowledge and much of the genius of the
research worker lie behind his selection of what is worth observ-
ing. It is a crucial choice, often determining the success or failure
of months of work, often differentiating the brilliant discoverer
from the . . . plodder."*^

When Faraday was asked to watch an experiment, it is said
that he would always 2isk what it was he had to look for but
that he was still able to watch for other things. He was following
the principle enunciated in the quotation from George in the
preceding section, that preferably each detail should be looked
for. However, this is of little help in making original observa-
tions. Claude Bernard considered that one should observe an
experiment with an open mind for fear that if we look only
for one feature expected in view of a preconceived idea, we will
miss other things. This, he said, is one of the greatest stumbling
blocks of the experimental method, because, by failing to note
what has not been foreseen, a misleading observation may be
made. " Put off your imagination," he said, " as you take off
your overcoat when you enter the laboratory." Writing of
Charles Darwin, his son tells us that :

" He wished to learn as much as possible from an experiment
so he did not confine himself to observing the single point
to which the experiment was directed, and his power of seeing
a number of things was wonderful. . . . There was one quality of
mind which seemed to be of special and extreme advantage in
leading him to make discoveries. It was the power of never letting
exceptions pass unnoticed."^'

If, when we are experimenting, we confine our attention to
only those things we expect to see, we shall probably miss the
unexpected occurrences and these, even though they may at
first be disturbing and troublesome, are the most likely to point
the way to important unsuspected facts. It has been said that
it is the exceptional phenomenon which is likely to lead to the

103

THE ART OF SCIENTIFIC INVESTIGATION

explanation of the usual. When an irregularity is noticed, look
for something with which it might be associated. In order to
make original observations the best attitude is not to concentrate
exclusively on the main point but to try and keep a look-out
for the unexpected, remembering that observation is not passively
watching but is an active mental process.

Scientific observation of objects calls for the closest possible
scrutiny, if necessary with the aid of a lens. The making of
detailed notes and drawings is a valuable means of prompting
one to observe accurately. This is the main reason for
making students do drawings in practical classes. Sir MacFarlane
Burnet has autopsied tens of thousands of mice in the course
of his researches on influenza, but he examines the lungs of
every mouse with a lens and makes a careful drawing of the
lesions. In recording scientific observations one should always
be as precise as possible.

Powers of observation can be developed by cultivating the
habit of watching things with an active, enquiring mind. It is
no exaggeration to say that well developed habits of observation
are more important in research than large accumulations of
academic learning. The faculty of observation soon atrophies
in modem civilisation, whereas with the savage hunter it may
be strongly developed. The scientist needs consciously to develop
it, and practical work in the laboratory and the clinic should assist
in this direction. For example, when observing an animal, one
should look over it systematically and consciously note, for in-
stance, breed, age, sex, colour markings, points of conformation,
eyes, natural orifices, whether the abdomen is full or empty, the
mammary glands, condition of the coat, its demeanour and
movements, any peculiarities and note its surroundings including
any faeces or traces of food. This is, of course, apart from, or
preliminary to, a clinical examination if the animal is ill.

In carrying out any observation you look deliberately for
each characteristic you know may be there, for any unusual
feature, and especially for any suggestive associations or relation-
ships among the things you see, or between them and what
you know. By this last point I mean such things as noticing
that on a plate culture some bacterial colonies inhibit or favour
others in their vicinity, or in field observations any association

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OBSERVATION

between disease and type of pasture, weather or system of
management. Most of the relationships observed are due to
chance and have no significance, but occasionally one will lead
to a fruitful idea. It is as well to forget statistics when doing
this and consider the possibiUty of some significance behind
slender associations in the observed data, even though they
would be dismissed at a glance if regarded on a mathematical
basis. More discoveries have arisen from intense observation
of very limited material than from statistics appUed to large
groups. The value of the latter Hes mainly in testing hypotheses
arising from the former. While observing one should cultivate
a speculative, contemplative attitude of mind and search for clues
to be followed up.

Training in observation follows the same principles as training
in any activity. At first one must do things consciously and
laboriously, but with practice the activities gradually become
automatic and unconscious and a habit is established. Effective
scientific observation also requires a good background, for only
by being familiar with the usual can we notice something as
being unusual or unexplained.

SUMMARY

Accurate observation of complex situations is extremely
difficult, and observers usually make many errors of which
they are not conscious. Effective observation involves noticing
something and giving it significance by relating it to something
else noticed or already known; thus it contains both an element
of sense-perception and a mental element.

It is impossible to observe everything, and so the observer
has to give most of his attention to a selected field, but he
should at the same time try to watch out for other things,
especially anything odd.

105

CHAPTER NINE

DIFFICULTIES

" Error is all around us and creeps in at the least oppor-
tunity. Every method is imperfect." — Charles Nicolle.

Mental resistance to new ideas

WHEN the great discoveries of science were made they
appeared in a very different light than they do now.
Previous ignorance on the subject was rarely recognised, for
either a blind eye was turned to the problem and people were
scarcely aware of its existence, or there were weU accepted
notions on the subject, and these had to be ousted to make way
for the new conceptions. Professor H. Butterfield points out
that the most difficult mental act of all is to re-arrange a familiar
bundle of data, to look at it differently and escape from the
prevailing doctrine.^" This was the great intellectual hurdle
that confronted such pioneers as Galileo, but in a minor form
it crops up with every important original discovery. Things
that are now quite easy for children to grasp, such as the
elementary facts of the planetary system, required the colossal
intellectual feat of a genius to conceive when his mind was
already conditioned with AristoteHan notions.

WiUiam Harvey's discovery of the circulation of the blood
might have been relatively easy but for the prevailing beliefs
that the blood ebbed and flowed in the vessels, that there were
two sorts of blood and that the blood was able to pass from
one side of the heart to the other. His first cause for dissatisfac-
tion with these doctrines was his finding of the direction in
which the valves faced in the veins of the head and neck — a
small stubborn fact which the current hypothesis did not fit. He
dissected no fewer than eighty species of animals including rep-
tiles, crustaceans and insects, and spent many years on the investi-
gation. The big difficulty in establishing the conception of the
circulation was the absence of any visible connection between

io6

DIFFICULTIES

the terminal arteries and the veins, and he had to postulate
the existence of the capillaries, which were not discovered until
later. Harvey could not demonstrate the circulation, so had to
leave it as an inference. He required courage to announce how
much blood he calculated that the heart pumped out. Harvey
himself wrote :

" But what remains to be said about the quantity and source
of the blood which thus passes, is of so novel and unheard-of
character that I not only fear injury to myself from the envy of
a few, but I tremble lest I have mankind at large for my enemies,
so much doth want and custom, that become as another nature,
and doctrine once sown and that hath struck deep root, and
respect for antiquity, influence all men : still the die is cast, and
my trust is in my love of truth, and the candour that inheres in
cultivated minds." ^"^

His fears were well founded for he was subjected to derision
and abuse and his practice suffered badly. Only after a struggle
of over twenty years did the circulation of the blood become
generally accepted.

Other illustrations of resistance to new ideas are provided by
the stories about Jenner and Mules already recounted and that
about Semmelweis given later in this chapter.

Vesalius in his early anatomical studies related that he could
hardly believe his own eyes when he found structures not in
accord with Galen's descriptions. Lesser men did, in fact,
disbelieve their own eyes, or at least thought that the subject
for dissection or their own handiwork was at fault. It is often
curiously difficult to recognise a new, unexpected fact, even
when obvious. Only people who have never found themselves
face to face with a new fact laugh at the inabihty of medieval
observers to beUeve their own eyes. Teachers well know that
students often ignore the results of their experiments and mistrust
their observations if they do not coincide with their expecta-
tions.

In nearly all matters the human mind has a strong tendency
to judge in the light of its own experience, knowledge and
prejudices rather than on the evidence presented. Thus new
ideas are judged in the light of prevailing beHefs. If the ideas
are too revolutionary, that is to say, if they depart too far from

107

THE ART OF SCIENTIFIC INVESTIGATION

reigning theories and cannot be fitted into the current body of
knowledge, they will not be acceptable. When discoveries are
made before their time they are almost certain to be ignored
or meet with opposition which is too strong to be overcome,
so in most instances they may as well not have been made.
Dr. Marjory Stephenson likens discoveries made in advance of
their time to long salients in warfare by which a position may
be captured. If, however, the main army is too far behind to
give necessary support, the advance post is lost and has to be
re-taken at a later date.*'

McMunn discovered cytochrome in 1886, but it meant little
and was ignored until Keilin rediscovered it thirty-eight years
later and was able to interpret it. Mendel's discovery of the
basic principles of genetics is another good example of inability
of even the scientific world always to recognise the importance
of a discovery. His work established the foundation of a new
science, yet it was ignored for thirty-five years after it had been
read to a scientific .society and published. Fisher has said that each
generation seems to have found in Mendel's paper only what it
expected to find and ignored what did not conform to its own
expectations.^' His contemporaries saw only a repetition of
hybridisation experiments already published, the next generation
appreciated the importance of his views on inheritance but
considered them difficult to reconcile with evolution. And now
Fisher tells us that some of Mendel's results when examined in
the hard cold light of modern statistical methods show unmistak-
able evidence of being not entirely objective — of being biased in
favour of the expected result !

The work of some psychologists on extrasensory perception
and precognition may be a present-day example of a discovery
before its time. Most scientists have difficulty in accepting the
conclusions of these workers despite apparently irrefutable
evidence, because the conclusions cannot be reconciled with
present knowledge of the physical world.

Unless made by someone outside accepted scientific circles,
discoveries made when the time is ripe for them are more
readily accepted because they fit into and find support in
prevailing concepts, or indeed, grow out of the present body
of knowledge. This type of discovery is bound to occur as part

108

DIFFICULTIES

of the main current of the evolution of science and may arise
more or less simultaneously in different parts of the world.
Tyndall said :

" Before any great scientific principle receives distinct enun-
ciation by individuals, it dwells more or less clearly in the
general scientific mind. The intellectual plateau is already high,
and our discoverers are those who, like peaks above the plateau,
rise a little above the general level of thought at the time." *^

Such discoveries, nevertheless, often encounter some resistance

before they are generally accepted.

There is in all of us a psychological tendency to resist new
ideas which come from without just as there is a psychological
resistance to really radical innovations in behaviour or dress. It
perhaps has its origin in that inborn impulse which used to be
spoken of as the herd instinct. This so-called instinct drives
man to conform within certain limits to conventional customs
and to oppose any considerable deviation from prevailing
behaviour or ideas by other members of the herd. Conversely,
it gives widely held beliefs a spurious validity irrespective of
whether or not they are founded on any real evidence. Instinc-
tive behaviour is usually rationalised, but the " reasons " are
only secondary, being formed by the mind to justify its opinions.

Wilfred Trotter said :

" The mind likes a strange idea as little as the body likes a
strange protein and resists it with similar energy. It would not
perhaps be too fanciful to say that a new idea is the most quickly
acting antigen known to science. If we watch ourselves honestly
we shall often find that we have begun to argue against a new
idea even before it has been completely stated."^*

When adults first become conscious of something new they
usually either attack or try to escape from it.'*^ This is called
the " attack-escape " reaction. Attack includes such mild forms
as ridicule, and escape includes merely putting out of mind.
The attack on the first man to carry an umbrella in London
was an exhibition of the same reaction as has so often been
displayed toward startling new discoveries in science. These
attacks are often accompanied by rationalisations — the attacker
giving the " reasons " why he attacks or rejects the idea. Scepti-
cism is often an automatic reaction to protect ourselves against

109

THE ART OF SCIENTIFIC INVESTIGATION

a new idea. How often do we catch ourselves automatically
resisting a new idea someone presents to us. As Walshe says,
the itch to suffocate the infant idea bums in all of us.^°^

Dale describes the ridicule which greeted Rontgen's first
announcement of his discovery of X-rays.^^ An interesting
feature of the story is that the great physicist J. J. Thomson
did not share in the general scepticism, but on the contrary
expressed a conviction that the report would prove to be true.
Similarly, when Becquerel's discovery that uranium salts emitted
radiations was announced, Lord Rayleigh was prepared to
believe it while others were not. Thomson and Rayleigh had
minds that were not enslaved by current orthodox views.

Some discoveries have had to be made several times before
they were accepted. Writing of the resistance to new ideas
Schiller says :

" One curious result of this inertia, which deserves to rank
among the fundamental ' laws ' of nature, is that when a dis-
covery has finally won tardy recognition it is usually found to
have been anticipated, often with cogent reasons and in great
detail. Darwinism, for instance, may be traced back through the
ages to Heraclitus and Anaximander."^"

It is not uncommon for opponents of an innovation to base
their judgment on an " all or nothing " attitude, i.e., since it
does not provide a complete solution to the practical problem,
it is no use. This unreasonable attitude sometimes prevents or
delays the adoption of developments which are very useful in
the absence of anything better. We all know some scientists who
steadfastly refuse to be convinced by the evidence in support
of a discovery which conflicts with their preconceived ideas.
Perhaps the persistent sceptic serves a useful purpose in the
community, but I admit that it is not one which I admire. It is
said that even today there are some people who still insist that
the world is flat !

Nevertheless, exasperating and even harmful as resistance to
discovery often is, it fulfils a function in buffering the community
from the too hasty acceptance of ideas until they have been
well proved and tried. But for this innate conservatism, wild
ideas and charlatanry would be more rife than they are. Nothing
could be more damaging to science than the abandonment of

no

DIFFICULTIES

the critical attitude and its replacement by too ready acceptance
of hypotheses put forward on slender evidence. The
inexperienced scientist often errs in being too willing to believe
plausible ideas. Superficially one's reaction to a new claim
appears to be an example of the general problem of conservatism
versus progressiveness. These attitudes of mind may sub-
consciously influence a person toward taking one side or the
other in a dispute but we should strive against both of them,
what we must aim at is honest, objective judgment of the
evidence, freeing our minds as much as possible from opinion
not based on fact, and suspend judgment where the evidence
is incomplete. There is a very important distinction between
a critical attitude of mind (or critical " faculty ") and a sceptical
attitude.

Opposition to discoveries

Hitherto we have been concerned with psychological resistance
to new ideas. In this section we will discuss some other aspects
of opposition to discoveries.

Innovations are often opposed because they are too disturbing
to entrenched authority and vested interests in the widest sense
of that term. Zinsser quotes Bacon as saying that the dignitaries
who hold high honours for past accomplishments do not usually
like to see the current of progress rush too rapidly out of their
reach. Zinsser comments :

" Our task, as we grow older in a rapidly advancing science, is
to retain the capacity of joy in discoveries which correct older
ideas, and to learn from our pupils as we teach them. That is the
only sound prophylaxis against the dodo-disease of middle
age."i°«

Trouble over innovations is sometimes aggravated by the
personality of the discoverer. Discoverers are often men with
little experience or skill in human relations, and less trouble
would have arisen had they been more diplomatic. The fact
that Harvey succeeded eventually in having his discovery
recognised, and that Semmelweis failed, may be explained on
this basis. Semmelweis showed no tact at all, but Harvey
dedicated his book to King Charles, drawing the parallel between
the King and realm, and the heart and body. His biographer,

1 1 1

THE ART OF SCIENTIFIC INVESTIGATION

Willis, says he possessed in a remarkable degree the power of
persuading and conciliating those with whom he came in contact.
Harvey said :

" Man comes into the world naked and unarmed, as if nature
had destined him for a social creature and ordained that he
should live under equitable laws and in peace; as if she had
desired that he should be guided by reason."

In discussing his critics he remarked :

" To return evil speaking with evil speaking, however, I hold
to be unworthy in a philosopher [i.e. scientist] and searcher
after the truth." *°^

Writing on the same subject Michael Faraday said :

" The real truth never fails ultimately to appear : and opposing
parties, if wrong, are sooner convinced when replied to for-
bearingly than when overwhelmed."^^

The discoverer requires courage, especially if he is young and
inexperienced, to back his opinion about the significance of his
finding against indifferences and scepticism of others and to
pursue his investigations. We take joy in reading of the courage
displayed by men like Harvey, Jenner, Semmelweis and Pasteur
in the face of opposition, but how often have profitable lines
of investigation been dropped and lost in oblivion when the
discoverer lacked the necessary zeal and courage ? Trotter relates
the story of J. J. Waterston who in 1845 wrote a paper on the
molecular theory of gases anticipating much of the work of
Joule, Clausius and Clerk Maxwell. The referee of the Royal
Society to whom the paper was submitted said : " The paper is
nothing but nonsense ", and the work lay in utter obhvion until
exhumed forty-five years later. Waterston lived on disappointed
and obscure for many years and then mysteriously disappeared
leaving no sign. As Trotter remarks, this story must strike a
chill upon anyone impatient for the advancement of knowledge.
Many discoveries must have thus been stillborn or smothered at
birth. We know only those that survived.

Although in most countries to-day there is no risk attached to
pursuing what are now orthodox scientific fields, it would be
wrong to conclude that obscurantism and reaction are things
only of the past. Barely thirty years ago Einstein suffered a
virulent and organised campaign of persecution and ridicule

1 12

DIFFICULTIES

in Germany*^ and in U.S.A. in 1925, at the notorious "Tennes-
see monkey trial ", a science teacher was prosecuted for teaching
evolution. In totalitarian states, the intrusion of poHtics into
scientific matters, as was seen under the Nazi regime and now
in Russia over the genetics controversy, may introduce authori-
tarianism into science with consequent suppression of the work
of those not willing to bow to the party dictum on scientific
theories.^ A mild form of reaction persists in societies devoted
to combating vaccination and vivisection. Nor should we
scientists ourselves be too complacent, for even within scientific
circles to-day a new discovery may be ignored or opposed if it
is revolutionary in principle and made by someone outside
approved circles. The discoverer may still be required to show
the courage of his convictions.

It has been said that the reception of an original contribution
to knowledge may be divided into three phases : during the first
it is ridiculed as not true, impossible or useless; during the
second, people say there may be something in it but it would
never be of any practical use; and in the third and final phase,
when the discovery has received general recognition, there are
usually people who say that it is not original and has been
anticipated by others.* Theobald Smith spoke truly when he
said :

" The joy of research must be found in doing, since every other
harvest is uncertain."®*

It is a commonplace that in the past the great scientists have
often been rewarded for their gifts to mankind by persecution.
A good example of this curious fact is provided by the following
story of what happened to Ignaz Semmelweis, when he showed
how the dreadful suffering and loss of life due to puerperal fever
that was then the rule in the hospitals of Europe could be pre-
vented.

In 1847 Semmelweis got the idea that the disease was carried
to the women on the hands of the medical teachers and students
coming direct from the post-mortem room. To destroy the
*' cadaveric material" on the hands he instituted a strict routine

* This saying seems to have originated from Sir James Mackenzie {The
Beloved Physician, by R. M. Wilson, John Murray, London).

THE ART OF SCIENTIFIC INVESTIGATION

of washing the hands in a solution of chlorinated lime before
the examination of the patients. As a result of this procedure,
the mortality from puerperal fever in the first obstetric clinic of
the General Hospital of Vienna fell immediately from 12 per
cent to 3 per cent, and later almost to i per cent. His doctrine
was well received in some quarters and taken up in some
hospitals, but such revolutionary ideas, incriminating the
obstetricians as the carriers of death, roused opposition from
entrenched authority and the renewal of his position as assistant
was refused. He left Vienna and went to Budapest where he
again introduced his methods with success. But his doctrine
made little headway and was even opposed by so great a man
as Virchow. He wrote a book, the famous Etiology, to-day
recognised as one of the classics of medical literature; but then
he could not sell it. Frustration made him bitter and irascible
and he wrote desperate articles denouncing as murderers those
who refused to adopt his methods. These met only with ridicule
and finally he came to a tragic end in a lunatic asylum in 1865.
Mercifully and ironically a few days after entering the asylum
he died from an infected wound received in the finger during
his last gynaecological operation : a victim of the infection to
the prevention of which his whole life had been devoted. His
faith that the truth of his doctrine would ultimately prevail
was never shaken. In a rather pathetic foreword to his Etiology
he wrote :

" When I look back upon the past, I can only dispel the sad-
ness which falls upon me by gazing into that happy future when
the infection will be banished. But if it is not vouchsafed to me
to look upon that happy time with my own eyes . . . the convic-
tion that such a time must inevitably sooner or later arrive will
cheer my dying hour."

The work of others, especially Tamier and Pasteur in
France and Lister in England, forced the world reluctantly to
recognise, some ten years or more later, that what Semmelweis
had taught was correct.

Semmelweis' failure to convince most people was probably
because there was no satisfactory explanation of the value of
disinfecting hands until bacteria were shown to be the cause of
disease, and probably also because he did not exercise any

1 14

DIFFICULTIES

diplomacy or tact. It is not clear that Semmelweis' efforts had
much, or indeed any, influence on the final acceptance of the
principles he discovered. Others seem to have solved the problem
independently.^*

Errors of interpretation

For want of a more appropriate place, I shall mention here
some of the commoner pitfalls which are encountered in inter-
preting observations or experimental results and which have
not already been discussed.

The most notorious source of fallacy is probably post hoc,
ergo propter hoc, that is, to attribute a causal relationship
between what has been done and what follows, especially to
conclude in the absence of controls that the outcome has been
influenced by some interference. All our actions and reason
are based on the legitimate assumption that all events have their
cause in what has gone before, but error often arises when we
attribute a causal role to a particular preceding event or inter-
ference on our part which in reality had no influence on the
outcome observed. The faith which the lay public has in
medicines is due in a large measure to this fallacy. Until very
recently the majority of medicines were of negligible value and
had little or no influence on the course of the illness for which
they were taken, nevertheless, many people firmly believed when
they recovered that the medicine had cured them. A lot of people
including some doctors, are convinced that certain bacterial
vaccines prevent the common cold, because by a fortunate coinci-
dence some patients had no cold the year following vaccination.
Yet all the many controlled experiments done with similar
vaccines failed to show the least benefit. The controlled experi-
ment is the only way of avoiding this type of fallacy.

Much the same logical fallacy is involved in wrongly assuming
that when an association between two events is demonstrated,
the relationship is necessarily one of cause and effect. Sometimes
data are collected which show that the incidence of a certain
disease in a quarter of a city which is very smoky, or which
is very low-lying, is much higher than in other quarters. The
author may conclude that the smoke or low-lying ground pre-
disposes to the disease. Often such conclusions are quite

115

THE ART OF SCIENTIFIC INVESTIGATION

unjustified, and the cause should probably be sought in the
poverty and overcrowding which is to be found in these
insalubrious areas. Virchow, in refuting Semmelweis' doctrine
about the causation of puerperal fever, asserted that the
weather played an important part, because the highest incidence
occurred in winter. Semmelweis replied that the association
between epidemics and winter was due to the fact that it was in
winter that the midwifery students spent most time on the dis-
section of dead bodies.

False conclusions can be drawn by attributing a causal role
to a newly introduced factor whereas, in fact, the cause lies in
the withdrawal of the factor which was replaced. Tests carried
out among people accustomed to drinking coffee at night could
show that a better night's sleep was obtained when a proprietary
drink was taken instead of coffee. It might be claimed that the
proprietary drink induced sleep whereas the better sleep might
well be entirely due to coffee not having been taken. Similarly,
false conclusions in dietetic experiments have sometimes been
drawn when a new constituent has replaced another. The
supposed effect of the new constituent has later proved to be
due to the absence of the article of diet displaced. It was
found that the blooming of some plants was influenced by
supplementing day light with artificial light. At first this was
thought to be due to the prolonged " day ", but subsequently
it was found to be due to the shortened " night ", for breaking
into the night with a brief period of illumination at midnight,
was even more effective than a longer period of illumination
near the evening or morning.

There is always a risk in applying conclusions reached from
experimentation in one species, to another species. Many
mistakes were made in concluding that man or a domestic
animal required this or that vitamin because rats or other
experimental animals did, but nowadays the error of this is
generally appreciated. More recently the same trouble arose in
chemotherapy. The sulphonamides which gave the best results
in man were not always found to be the best against the same
bacteria in some of the domestic animals.

A rather more insidious source of fallacy is failure to realise
that there may be several alternative causes of one process.

ii6

DIFFICULTIES

W. B. Cannon^^ comments on the false deduction once made
that adrenahne does not play a part in controlUng the sugar
level in the blood by calling forth sugar from the liver, on the
ground that the blood-sugar level is maintained after removal
of the adrenal medulla. The fact is that there are other methods
of mobilising sugar reserves from the liver but none are so
effective as adrenaline. Shivering by itself can prevent body
temperatures from falUng, but that does not prove that other
processes cannot play a part. A variant of this " fallacy of a
single cause " has been described by Winslow.^*"^ When a
combination of two factors causes something, and one is
universally present, it is usually rashly concluded that the other
is the sole causal factor. In the nineteenth century it was
believed that insanitary conditions in themselves caused enteric
fever. The causal microbes were then universally present and
the incidence of the disease was determined by presence or
absence of sanitation. The cause of a disease is complex,
consisting of a combination of causal microbe, the conditions
necessary for its conveyance from one host to the next and
factors affecting the susceptibility of the host. Any happening is
the result of a complex of causal factors, one of which we usually
single out as the cause owing to its not being commonly present
as are the other circumstances.

Wrong conclusions about the incidence of some condition
in a population are sometimes drawn through basing the observa-
tions on a section of the population which is not representative
of the whole. For example, certain figures were generally
accepted and printed in text-books as an index of the proportion
of children at different ages that gave a negative reaction to
the Schick test for immunity to diphtheria. Many years later
these figures were found to be true only for children of the
poorer classes attending public hospitals in the city. The figures
for other sections of the population were very different. When
I went to the U.S.A. in 1938, scarcely anyone I met could say
a good word for President Roosevelt, but Dr. Gallup's method
of sampling public opinion showed that more than fifty per cent
supported him. There is a great temptation to generalise on
one's own observations or experience, although often it is not
based on a sample that is truly random or sufficiently large to

"7

THE ART OF SCIENTIFIC INVESTIGATION

be representative. Bacon warned against being led into error
by relying on impressions.

" The human understanding is most excited by that which
strikes and enters the mind at once and suddenly, and by which
the imagination is immediately filled and inflated. It then begins
almost imperceptibly to conceive and suppose that everything is
similar to the few objects which have taken impression on the
mind."

A very common way in which mistakes arise is by making
unjustified assumptions on incomplete evidence. To cite a
classic example, in the lecture in which he enunciated his famous
postulates, Robert Koch described how he had been led into
error by making what appeared to be a reasonable assumption.
In his pioneer work on the tubercle bacillus he obtained strains
from a large variety of animal species and after having subjected
them to a series of tests he concluded that all tubercle bacilli
are similar. Only in the case of the fowl did he omit to do
pathogenicity and cultural examinations because he could not
at the time obtain fresh material. However, since the morphology
was the same, he assumed that the organism from the fowl was
the same as those from the other animals. Later he was sent
several atypical strains of the tubercle bacillus which, despite
a protracted investigation, remained a complete puzzle. He said :

" When every attempt to discover the explanation of the dis-
crepancy had failed, at length an accident cleared up the
question."

He happened to get some fowls with tuberculosis and when
he cultured the organisms from these :

" I saw to my astonishment that they had the appearance and
all the other characters of the mysterious cultures."

Thus it was he found that avian and mammalian tubercle
bacteria are different. ^^ Incidentally, this reference, which I
found when looking for something else, seems to have been
" lost ", for some current text-books state that there is no evidence
that Koch ever put forward the well-known postulates contained
in this lecture.

One can easily be led astray when attempting to isolate an
infective agent by inoculation and passage in experimental

ii8

DIFFICULTIES

animals. Many mice carry in their nose latent viruses which,
when any material is inoculated into the lungs through the nose,
are carried into the lungs where they multiply. If the lungs
from these mice are used to inoculate other mice in the same
way, pneumonia is sometimes set up and, as a result, it might
be wrongly concluded that a virus had been isolated from the
original material. Also in attempting to isolate a virus by
inoculating material on to the skin of experimental animals, it
is possible to set up a transmissible condition which originated
from the environment and not from the original inoculum.

Early investigations on distemper of dogs incriminated as the
causal agent a certain bacterium isolated from cases of the
disease because on inoculation it set up a disease resembling
distemper. When later a virus was shown to be the true cause
of the distemper, it became apparent that the early investigators
had been misled either because they had isolated a pathogenic
secondary invader or because they had not taken sufficiently rigid
measures to quarantine their experimental dogs.

When the investigator has done his best to detect any errors
in his work, a service that colleagues are usually glad to assist
with is criticism. He is a bold man who submits his paper for
pubUcation without it having first been put under the microscope
of friendly criticism by colleagues.

SUMMARY

The mental resistance to new ideas is partly due to the fact
that they have to displace established ideas. New facts are not
usually accepted unless they can be correlated with the existing
body of knowledge; it is often not sufficient that they can be
demonstrated on independent evidence. Therefore premature
discoveries are usually neglected and lost. An unreasoning,
instinctive mental resistance to novelty is the real basis of excessive
scepticism and conservatism.

Persecution of great discoverers was due partly to mental
resistance to new ideas and partly to the disturbance caused to
entrenched authoritv and vested interests, intellectual and
material. Sometimes lack of diplomacy on the part of the
discoverer has aggravated matters. Opposition must have killed

"9

THE ART OF SCIENTIFIC INVESTIGATION

at birth many discoveries. Obscurantism and authoritarianism
are not yet dead.

Included among the many possible sources of fallacy are
post hoc, ergo propter hoc, comparing groups separated by time,
assuming that when two factors are correlated the relationship
is necessarily one of cause and effect, and generalising from
observations on samples that are not representative.

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CHAPTER TEN

STRATEGY

" Work, Finish, Publish." — Michael Faraday.

Planning and organising research

MUCH controversy has taken place over planning in research.
The main disagreement is on the relative merits of pure
and applied research, on what proportion of the research in a
country should be planned and to what degree it should be
planned. The extreme advocates of planning consider that the
only research worth while is that which is undertaken in a
deliberate attempt to meet some need of society, and that pure
research is seldom more than an elegant and time-wasting
amusement. On the other hand the anti-planners (in England
there is a Society for Freedom in Science) maintain that the
research worker who is organised becomes only a routine
investigator because, with the loss of intellectual freedom,
originality cannot flourish.

Discussions on planning research are often confused by failure
to make clear what is meant by planning. It is useful to dis-
tinguish three different levels of planning. The first is the
actual conduct of an investigation by the worker engaged in
the problem. This corresponds with tactics in warfare. It is
short term and seldom goes far beyond the next experiment.
The second level involves planning further ahead on broad lines
and corresponds with strategy in warfare. Planning at this level
is not confined to the man engaged in the problem but is also
often the concern of the research director and the technical
committee. Finally there is planning of policy. This type of
planning is mostly done by a committee which decides what
problems should be investigated and what projects or workers
should receive support.

It has already been pointed out that many discoveries are

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THE ART OF SCIENTIFIC INVESTIGATION

quite unforeseen, and that the principal elements in biological
research are intensely individual efforts in (a) recognising the
unexpected discovery and following it up, and {b) concentrated
prolonged mental effort resulting in the birth of ideas. Major
discoveries probably result less frequently from the systematic
accumulation of data along planned lines. It is not a fact, as
some suppose, that no solution to a problem is likely to be
found until we have fundamental knowledge on the subject.
Frequently an empirical discovery is made providing a solution
and the rationale is worked out afterwards. One of the
principal morals to be drawn from the discoveries described in
this book is that the research worker ought not, having decided
on a course of action, to put on mental blinkers and, like a cart-
horse, confine his attention to the road ahead and see nothing by
the way.

In view of these lessons which are to be learnt from the
history of scientific discovery, research is less likely to
be fruitful where the investigation is planned at the tactical
level by a committee than when the person actually doing the
research works out his own tactics as the investigation unfolds.
Research is for most workers an individualistic thing and the
responsibility for tactical planning is best left to the individual
workers, who will devote their mental energies to the subject if
they are allowed the incentives and rewards that are essential
for fruitful research. Initiative can be easily discouraged by too
much supervision for a man will seldom put his whole heart
into a problem unless he feels that it is his own. Simon Flexner,
the founder of the Rockefeller Institute of Medical Research,
always believed that men of the right sort could be trusted to
have better ideas than others could think up for them." The
scientist should not even be expected to adhere in detail to a
programme of work which he himself has drawn up, but should
be allowed to vary it as developments require.

The late Professor W. W. C. Topley said :

" Committees are dangerous things that need most careful
watching. I believe that a research committee can do one useful
thing and one only. It can find the workers best fitted to attack
a particular problem, bring them together, give them the facilities
they need, and leave them to get on with the work. It can review

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STRATEGY

progress from time to time, and make adjustments; but if it
tries to do more, it will do harm."^^

Technical committees and research directors can often help
in planning at the strategic level providing they work in consulta-
tion with the man who is going to do the work and do not
attempt to dictate tactics. Committees are of most value in
planning at the poUcy level, in calling attention to problems of
importance to the community and making available the necessary
finances and scientists. Another useful function that a com-
mittee can sometimes perform is to accelerate advances by seeing
that workers in different laboratories are kept informed of each
other's progress without the usual delay entailed in publication.
Some war-time committees did useful service in co-ordinating
scattered work in this way.

It is perhaps so obvious as to be scarcely worth mentioning
that planning at the strategic and poUcy levels places a heavy
responsibiUty on the planners, and is only likely to be successful
when entrusted to people who have a real understanding of
research as well as a good general knowledge in science. It is
generally recognised that a committee which draws up pro-
grammes of research at the strategic level should consist mainly
of men actively engaged in the field of research in which the
problem falls. Unfortunately often committees are too incUned to
play safe and support only projects which are planned in detail
and follow conventional lines of work. Worthwhile advances are
seldom made without taking risks.

Plans and projects are in order for tackling recognised
problems, that is to say, for applied research, but science also
needs the independent worker who pursues pure research without
thought of practical results.

In team work some individual or individuals should usually
take the lead and do the thinking. There are, of course, some
scientists who are not well fitted to do independent research
and yet who may be very useful working under close direction
as members of a team. Other things being equal, the person
with a fertile imagination makes a better leader than someone
with a purely logical mind, for the former is more inspiring as
well as more useful in providing ideas. But the leader of
a team needs to be actively engaged on the problem himself.

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THE ART OF SCIENTIFIC INVESTIGATION

In Other words the tactical planning is best done by the bench
worker, not the office administrator. Where there is not an
acknowledged leader of the team, the problem can often be
divided up so that each person capable of independent work
has his own aspect of the problem for which he is responsible.
The thing to avoid is too detailed and rigid planning by the
assembled team. However, when team work is undertaken, the
work ought to be sufficiently co-ordinated for each to understand
not only his own special aspect but have a good grasp of the
problem as a whole. The principles of team work were well
expressed by Ehrlich : " Centralisation of investigation with
independence of the individual worker." All plans must be
regarded as tentative and subject to revision as the work pro-
gresses. One must not confuse the planning of research with the
planning of individual experiments. No one would dispute the
advisability of devoting great care to the planning of experi-
ments and carrying them through according to plan.

Team work is essential in research in the investigation of
problems which overlap into several branches of science, for
instance, the investigation of a disease by a clinician, bacteriolo-
gist and biochemist. Large teams are most frequently used in
biochemical investigations where there is need for a large amount
of co-ordinated skilled technical work. Also team work is often
required to develop discoveries which have originated from
individual workers.

Another important use of the team is to increase the capacity
of the brilliant man beyond what he could do with only his
hands and technical assistance. The research team, especially
of this type, also is valuable in providing an opportunity for
the beginner to learn to do research. The young scientist benefits
more from working in collaboration with an experienced research
worker than by only having supervision from him. Also in this
way he is more likely to get a taste of success, which is a
tremendous help. Moreover, the association of the freshness
and originality of youth with the accumulated knowledge and
experience of a mature scientist can be a mutually beneficial
arrangement. Where close collaboration is involved, the personali-
ties of the individuals are, of course, an important consideration.
Most brilliant men are stimulating to others, but some are so

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STRATEGY

full of ideas from their own fertile mind and are so keen to
try them out that they have a cramping effect on a junior
colleague who wants to try out his own ideas. Moreover, it is
possible for a man to be a brilliant scientist and yet be quite
undeveloped in the knowledge and practice of human personal
relations.

The objection most often raised against team work is that
those discoveries which arise from unexpected side issues will
be missed if the worker is not free to digress from his investiga-
tion. Reming has pointed out that had he been working in
a team he would not have been able to drop what he was doing
and follow the clue that led to penicillin.*^

For his own guidance the research worker himself needs to

make at least some tentative general plan of an investigation

at the outset and to make very careful detailed plans for actual

experiments. It is here that the experience of the research

director can be most helpful to the young scientist. The latter

presents for discussion a general picture of the information he

has collected, together with his ideas for the proposed work. The

inexperienced scientist usually does not realise the limitations

of what is practicable in research, and often proposes for one

year's work a plan that would occupy him for ten. The

experienced man knows that it is a practical necessity to confine

himself to a fairly simple project because he realises how much

work even that entails. From hearing of only the successful

investigations the uninitiated often gets a false idea of the

easiness of research. Advances are nearly always slow and

laborious and one person can attempt only a limited objective

at a time. It is as well for the beginner to discuss with his

supervisor any important deviations from the plan because

although fruitful clues may arise which should be followed, it

is neither possible nor desirable to pursue every unanswered

question that comes up. To give advice on these issues and to

help when difficulties are met are the main functions of a

director of research, and the successes of those under his direction

are a measure of his understanding of the nature of scientific

investigation. As the young scientist develops he should be

encouraged to become less and less dependent on his seniors.

The rate at which this independence develops will be deter-

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THE ART OF SCIENTIFIC INVESTIGATION

mined by the aptitude that he shows and the success he attains.

Both the team worker and the individual worker usually find
it useful to keep a list of the ideas and experiments he intends
to try — a work programme, which is revised continuously.

Some consider that the best work is done in small research
institutes where the director can keep in intimate touch with
all the work, and that when this size is passed efficiency drops.
It is undoubtedly true that there are examples of small institutes
whose output per man is better than in the average large
institute. In such places one usually finds a director who is not
only a capable scientist but who also stimulates enthusiasm in
his staff High productivity in large institutes perhaps depends
on there being several active foci, each centred on a good leader.

Different types of research

Research is commonly divided into "applied" and "pure".
This classification is arbitrary and loose, but what is usually
meant is that applied research is a deliberate investigation of a
problem of practical importance, in contradistinction to pure
research done to gain knowledge for its own sake. The pure
scientist may be said to accept as an act of faith that any
scientific knowledge is worth pursuing for its own sake, and,
if pressed, he usually claims that in most instances it is eventually
found to be useful. Most of the greatest discoveries, such as
the discovery of electricity, X-rays, radium and atomic energy,
originated from pure research, which allows the worker to follow
unexpected, interesting clues without the intention of achieving
results of practical value. In applied research it is the project
which is given support, whereas in pure research it is the man.
However, often the distinction between pure and applied research
is a superficial one as it may merely depend on whether or not
the subject investigated is one of practical importance. For
example, the investigation of the life cycle of a protozoon in a
pond is pure research, but if the protozoon studied is a parasite
of man or domestic animal the research would be termed applied.
A more fundamental differentiation, which corresponds only very
roughly with the applied and pure classification is {a) that in

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STRATEGY

which the objective is given and the means of obtaining it are
sought, and {b) that in which the discovery is first made and then
a use for it is sought.

There exists in some circles a certain amount of intellectual
snobbery and tendency to look disdainfully on applied investiga-
tion. This attitude is based on the following two false ideas :
that new knowledge is only discovered by pure research while
applied research merely seeks to apply knowledge already avail-
able, and that pure research is a higher intellectual activity
because it requires greater scientific ability and is more difficult.
Both these ideas are quite wrong. Important new knowledge has
frequently arisen from applied investigation; for instance, the
science of bacteriology originated largely from Pasteur's investiga-
tions of practical problems in the beer, wine and silkworm
industries. Usually it is more difficult to get results in applied
research than in pure research, because the worker has to stick
to and solve a given problem instead of following any promising
clue that may turn up. Also in applied research most fields have
already been well worked over and many of the easy and
obvious things have been done. Applied research should not be
confused with the routine practice of some branch of science
where only the application of existing knowledge is attempted.
There is need for both pure and applied research for they tend
to be complementary.

Practical problems very often require for their solution more
than the mere application of existing knowledge. Frequently
gaps in our knowledge are found that have to be filled in.
Furthermore, if applied research is limited to finding a solution
to the immediate problem without attempting to arrive at an
understanding of the underlying principles, the results will
probably be applicable only to the particular local problem and
will not have a wide general application. This may mean that
similar and related problems have to be investigated afresh,
whereas had the original investigation been done properly it
would have provided the solution to the others. Even an
apparently simple matter such as the practical development of
a discovery may present unsuspected difficulties. When the new
insecticide, gammexane, was adopted for use as a sheep dipping
fluid, very careful tests and field trials were conducted to deter-

127

THE ART OF SCIENTIFIC INVESTIGATION

mine that it was non-toxic and in every way harmless. But despite
its having passed an extensive series of tests, when it became
widely used in the field, sheep in a number of flocks developed
severe lameness after dipping. Investigation showed that the
lameness was not due to the gammexane but to infection with
a certain bacterium. The dipping fluid had become fouled with
this bacterium which was carried in by some of the sheep.
Dipping fluids used previously had a germicidal action against
this bacterium, but gammexane had not. Problems of control in
biology are often different in different localities. The malaria
parasite may have as an intermediate host a different species
of mosquito and the liver fluke may utilise a different snail.

Applied research cuts horizontally across several pure sciences
looking for newly found knowledge that can be used in the
practical problem. However, the applied scientist is not content
with waiting for the discoveries of the pure scientist, valuable
as they are. The pure scientist leaves serious gaps in those aspects
of the subject which do not appeal to him, and the applied
scientist may have to initiate fundamental research in order to
fill them.

Scientific research may also be divided into the exploratory
type which opens up new territory, and developmental type
which follows on the former. The exploratory type is free and
adventurous; occasionally it gives us great and perhaps
unexpected discoveries; or it may give us no results at all.
Developmental type of research is more often carried on by the
very methodical type of scientist who is content to consolidate the
advances, to search over the newly won country for more modest
discoveries, and to exploit fully the newly gained territory by
putting it to use. This latter type of research is sometimes spoken
of as "pot-boiling" or "safety first" research.

"Borderline" research is research carried on in a field where
two branches of science meet. This can be very productive in
the hands of a scientist with a sufficiently wide training because
he can both use and connect up knowledge from each branch
of science. A quite ordinary fact, principle or technique from
one branch of science may be novel and fruitful when applied
in the other branch.

Research may be divided into different levels which are reached

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STRATEGY

successively as a branch of science or a subject becomes more
advanced. First comes the observational type of research carried
out by naturalists in the field or by scientists with similar mental
attributes in the laboratory. Gradually the crude phenomena and
materials become refined to more precise but more restricted
laboratory procedures, and these ultimately are reduced to exact
physical and chemical processes. It is almost a practical impossi-
bility for anyone to have a specialist knowledge of more than a
limited field at one level. The natural historian type, who is
no less useful than his colleagues, owes most of his success to
his powers of observation and natural wit and often lacks the
depth of basic scientific knowledge necessary to develop his
findings to the full. On the other hand, the specialist in a basic
science may be too far removed, mentally and physically, from
phenomena occurring in nature to be the equal of the natural
historian type in starting new lines of work.

The transfer method in research

All scientific advances rest on a base of previous knowledge.
The discoverers are the people who supply the keystone to
another arch in the building and reveal to the world the com-
pleted structure built mainly by others. In this section, however,
I am referring not so much to the background of knowledge
on which one tries to build but rather to the adaptation of a
piece of new knowledge to another set of circumstances.

Sometimes the central idea on which an investigation hinges
is provided by the appHcation or transfer of a new principle
or technique which has been discovered in another field. The
method of making advances in this way will be referred to as
the "transfer" method in research. This is probably the most
fruitful and the easiest method in research, and the one most
employed in appHed research. It is, however, not to be in any
way despised. Scientific advances are so difficult to achieve that
every useful stratagem must be used. Some of these contributions
might be more correctly called developments rather than dis-
coveries since no new principles and little new knowledge may be
brought to light. However, usually in attempting to apply the

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THE ART OF SCIENTIFIC INVESTIGATION

newly discovered principle or technique to the different problem,
some new knowledge does arise.

Transfer is one of the principal means by which science evolves.
Most discoveries have applications in fields other than those in
which they are made and when applied to these new fields they
are often instrumental in bringing about further discoveries.
Major scientific achievements have sometimes come from transfer.
Lister's development of antiseptic surgery was largely a transfer
of Pasteur's work showing that decomposition was due to
bacteria.

It might be thought that as soon as a discovery is announced,
all its possible applications in other fields follow almost im-
mediately and automatically, but this is seldom so. Scientists some-
times fail to realise the significance which a new discovery in
another field may have for their own work, or if they do realise it
they may not succeed in discovering the necessary modifications.
Years elapsed between the discovery of most of the principles of
bacteriology and immunology and all their applications to various
diseases. It was some time before the principle of haemagglutina-
tion by viruses, discovered by Hirst with influenza virus, was
found to hold with several other viruses, however with modifica-
tions in some instances, as one might have expected, and still later
it has been extended to certain bacteria.

An important form of the transfer method is the exploitation
of a new technique adopted from another branch of science.
Some workers deliberately take up a new technique and look for
problems in which its special virtues offer new openings. Partition
chromatography and haemagglutination have, for example, been
used in this way in fields far removed from those in which they
were first developed.

The possibility of developments by the transfer method is
perhaps the main reason why the research man needs to keep
himself informed of at least the principal developments taking
place in more than his own narrow field of work.

In this section we might also mention the scientific develop-
ments of customs and practices already in use without any
scientific background. A large number of drugs used in thera-
peutics came into use in this way. Quinine, cocaine, curare and
ephedrine were used long before they were studied scientifically

130

STRATEGY

and their pharmacological action understood. The medicinal pro-
perties of the herb Ma Huang, from which ephedrine is derived
are said to have been discovered in China, 5,000 years ago by the
emperor Shen Nung. The discoveries of quinine, cocaine and
curare by the natives in South America are lost in antiquity but
obviously they must have been purely empirical. Incidentally,
the tree from which quinine is obtained was named after the
Countess of Cinchona who used it to cure malaria in 1638 and
subsequently introduced it into Europe from Peru. Another
example of this type of investigation is research into age-old
processes such as tanning, cheese making and fermentation of
various kinds. Many of these processes have now been developed
into exact scientific procedures and thereby improved, or at least
made more dependable. Vaccination could perhaps also be classi-
fied under this heading.

Tactics

In order to examine and get a better understanding of a
complex process, it is often useful to analyse it into component
phases and consider each separately. This is what has been done
in this treatise on research. I have tried to describe the role of
hypothesis, reason, experimentation, observation, chance and
intuition in research and to indicate the special uses and defects
of each of these factors. However, in practice these factors
of course do not operate separately. Several or all are usually
required in any investigation, although often the actual key to
the solution of the problem is provided by one, as is shown in
many of the anecdotes cited.

A general outline of how a straightforward problem in experi-
mental medicine or biology may be tackled has been given in
Chapters One and Two and the special role of each factor in
research has been discussed in subsequent chapters. The order of
the chapters has no special significance, nor does the space devoted
to each subject bear much relationship to its relative importance.
There remain to be discussed only some general considerations
about tactics. In doing this it may be useful to recapitulate and
bring together some of the points already made elsewhere.

No set rules can be followed in research. The investigator has

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THE ART OF SCIENTIFIC INVESTIGATION

to exercise his ingenuity, originality and judgment and take
advantage of every useful stratagem. F. C. S. Schiller wrote :

" Methods that succeed must have value. . . . The success has
shown that in this case the enquirer was right to select the facts
he fixed upon as significant, and to neglect the rest as irrelevant,
to connect them as he did by the ' laws ' he applied to them, to
theorise about them as he did, to perceive the analogies, to
weigh the chances, as he did, to speculate and to run the risks
he did. But only in this case. In the very next case, which he
takes to be * essentially the same ' as the last, and as nearly
analogous as is humanly possible, he may find that the differences
(which always exist between cases) are relevant, and that his
methods and assumptions have to be modified to cope with it
successfully."®"

Research has been likened to warfare against the unknown.
This suggests some useful analogies as to tactics. The first con-
sideration is proper preparation by marshaUing all available
resources of data and information, as well as the necessary
material and equipment. The attacker will have a great advantage
if he can bring to bear a new technical weapon. The procedure
most likely to lead to an advance is to concentrate one's forces
on a very restricted sector chosen because the enemy is believed
to be weakest there. Weak spots in the defence may be found by
preliminary scouting or by tentative attacks; when a stiff resis-
tance is encountered it is usually better to seek a way around it
by some manoeuvre instead of persisting in a frontal attack.
Very occasionally, when a really important break-through is
effected, it may be expedient, although risky, to overrun quickly
a large territory and leave much of the consolidation to followers,
provided the work is important enough to attract them. However,
generally speaking, advances proceed by stages; when a new
position is taken it should be firmly consoHdated before any
attempt is made to use it as a base for further advance. This
rhythm is the normal form of progression not only in scientific
research but in all forms of scholarship : the gathering of
information leads naturally to a pause for synthesis and interpreta-
tion which in turn is followed by another stage of collection of
crude data selected in light of the new generalisations reached.
Even in applied research, such as the investigation of a disease

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STRATEGY

of man or of domestic animals, the usual procedure is first to
find out as much as possible about any or all of the aspects of
the problem, without deliberately aiming at a particular objective
of practical use. Experience has shown quite definitely that a
fuller understanding of the subject nearly always reveals useful
facts. Sometimes one finds a vulnerable link in the life-cycle of
the parasite causing the disease and this may lead to a simple
means of control. Having such a possibility in view it is helpful
to consider the biology of the infective agent, whether it be virus
or helminth, and to ponder on how it manages to survive,
especially when making its way from one host to the next.

Biological discoveries are often at first recognised in the form
of qualitative phenomena and one of the first aims is usually to
refine them to quantitative, reproducible processes. Eventually
they may be reduced to a chemical or physical basis. It is note-
worthy that the declared aim of a large proportion of investiga-
tions described in the leading scientific journals is to disclose the
mechanism of some biological process. It is a fundamental belief
that all biological functions can eventually be explained in terms
of physics and chemistry. Vitalism, which postulated mysterious
" vital " forces, and teleology, which postulated a supernatural
directing agency, have long ago been abandoned by experi-
mental biologists. However, teleology is admissible in a modified
sense that an organ or function fulfils a purpose toward aiding
the survival of the organism as a whole or survival of the
species.

The most honoured and acclaimed advances in science are the
perception of new laws and principles and factual discoveries
of direct practical use to man. Usually little prominence is given
to the inventions of new laboratory techniques and apparatus
despite the fact that the introduction of an important new tech-
nique is often responsible for a surge of progress just as much
as is the discovery of a new law or fact. Solid media for the
culture of bacteria, bacterial filters, virus haemagglutination and
partition chromatography are outstanding examples. It may be
profitable for research workers and the organisers of research to
pay more attention to the developments of new techniques than
has been the custom.

It was a characteristic of Faraday, Darwin, Bernard and

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THE ART OF SCIENTIFIC INVESTIGATION

probably all great investigators to follow up their discoveries and
not leave the trail till they had exhausted it. The story of
Bernard's experiments with digestion in rabbits recounted earlier
provides a good illustration of this poHcy. When Gowland
Hopkins found that a certain test for proteins was due to the
presence of glyoxylic acid as an impurity in one of the reagents,
he followed this up to find what group in the protein it reacted
with and this led to his famous isolation of tryptophane. Any
new fact is potentially an important new tool to be used for
uncovering further knowledge and a small discovery may lead
to something much greater. As Tyndall said :

" Knowledge once gained casts a faint light beyond its own
immediate boundaries. There is no discovery so limited as not
to illuminate something beyond itself."

95

As soon as anything new is discovered the successful scientist
immediately looks at it from all possible points of view and by
connecting it with other knowledge seeks new avenues for investi-
gation. The real and lasting pleasure in a discovery comes not so
much from the accomplishment itself as from the possibility of
using it as a stepping stone for fresh advances.

Anyone with a spark of the research spirit does not need to be
exhorted to chase for all he is worth a really promising clue when
one is found, dropping for the time being other activities and
interests as far as practicable. But in research most of the time
progress is difficult and often one is up against what appears to
be a " brick wall ". It is here that all resources of ingenuity and
method are required. Perhaps the first thing to try is to abandon
the subject for a few days and then reconsider the whole problem
with a fresh mind. There are three ways in which benefit may
be derived from temporary abandonment of a difficulty. It allows
time for "incubation ", that is for the subconscious to digest the
data, it allows time for the mind to forget conditioned thinking,
and lastly, by not doggedly persisting, one avoids fixing too
strongly the unprofitable lines of thought. The principle of
temporary abandonment is, of course, widely practised in every-
day life, as for example, in postponing the making of a difficult
decision until one has " slept on it ". Elsewhere the usefulness
of discussion has been stressed, not so much for seeking technical

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STRATEGY

advice as for promoting new ideas. Also discussion helps one to
gain that clear understanding of the problem, which is so essen-
tial.

Another thing to try when one is up against an impasse is
to go back to the beginning and try to find a new Hne of
approach by looking at the problem in a different way. It may
be possible to collect more data from the field or clinic. Fresh
field or clinical observations may also be useful in prompting
new ideas. As a result of trying to reduce the problem to an
experimental inquiry, the worker may have selected a sterile and
erroneous refinement of the problem. When the crude problem
is seen again he may select some other aspect for investigation.
Sometimes it is possible to resolve the difficulty into simpler
components which can be tackled separately. If the difficulty
cannot be overcome, perhaps a way around it can be found by
using an alternative technical method. It may be helpful to look
for analogies between the problem presented and others that have
been solved.

If, after persistent attempts to resolve the difficulty, no advance
is being made, it is usually best to drop the problem for a few
weeks or months and take up something else, but to think and
talk about it occasionally. A new idea may arise or a new devel-
opment in other fields may occur which enable the problem to be
taken up again. If nothing fresh turns up, the problem will have
to be abandoned as being insoluble in the present state of know-
ledge in related fields. It is, however, a serious fault in a research
worker to be too ready to drop problems as soon as he encoun-
ters a difficulty or gets seized by enthusiasm for another line of
work. Generally speaking one should make every effort to com-
plete an investigation once it has been started. The worker who
repeatedly changes his problem to chase his newest bright idea
is usually ineffectual.

As soon as a piece of work is nearing completion it should be
written up as for publication. It is important to do this before
the work has been brought to a close because frequently one
finds gaps or weak points which can be remedied while the
materials are still at hand. Even when the work is not nearing
completion, it is as well to write up an investigation at least
once a year, because otherwise when one writes up work from

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old notes, one's memory of the experiments has become dim so
that the task is more difficult and cannot be done so well. Also, for
reasons discussed elsewhere, it is desirable to review the problem
periodically. However, work that has not produced significant
results is better not published. It cluttei^s up the journals and
does more harm than good to the author's reputation in the minds
of the discerning.

When the work has been completed, it is wise to submit the
article to an experienced colleague for criticism — not only because
the colleague may be more experienced than the author, but also
because it is easier to see flaws in another's work or language than
in one's own.

A word of caution might be given against publishing work that
is not conclusive and especially about making interpretations that
are not fully justified by the experimental results or observations.
Whatever is written will remain permanently in the literature and
one's scientific reputation can be damaged by publishing some-
thing that is later proved incorrect. Generally speaking, it is a
safe policy to give a faithful record of the results obtained and
to suggest only cautiously the interpretation, distinguishing
clearly between facts and interpretation. Premature publication
of work that could not be substantiated has at times spoilt the
reputation of promising scientists. Superlatives and exaggeration
are anathema to most scientists, the greatest of whom have
usually been modest and cautious. Faraday wrote to a friend in
1831 :

" I am busy just now again on electro-magnetism, and think I

have got hold of a good thing, but can't say. It may be a weed

instead of a fish that, after all my labour, I may at last pull up."

What he pulled up was the electric dynamo. In 1940 Sir Howard
Florey wrote to the Rockefeller Foundation for financial sup-
port for his work on penicillin, which he then had good reason
for believing could be developed into a therapeutic agent even
more effective than the sulphonamides. In such a letter one might
be expected to present the work in the most favourable light, but
this is all that Florey allowed himself to say :

" I don't think I am too optimistic in thinking that this is a
very promising line."'^

What a classic piece of understatement that has proved to be !

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STRATEGY

I confess that I did not read Bacon until after I had nearly
finished writing this book and only then did I realise how clearly
he had seen that discovery is more often than not empirical — the
same view as I have reached from studying the methods which
have produced results during recent times. He quotes with
approval Celsus as saying :

" That medicines and cures were first found out, and then after
the reasons and causes were discoursed; and not the causes first
found out, and by light from them the medicines and cures
discovered."^

No more apt commentary could be made about the advances in
chemotherapy of this century than this remark of Celsus' about
the medical science of 1800 years ago. When one reflects that
chance and empiricism is the method by which organic evolution
developed, it is perhaps not so surprising that these factors play
such an important part in biological research.

In research we often have to use our techniques at their extreme
limit and even beyond — like Schaudinn discovering the pale
spirochaete of syphilis which others could barely see by the
methods then available. So also with our reasoning; for usually
discovery is beyond the reach of reason.

In physics inductive logic is as inadequate as in biology. Ein-
stein leaves us in no doubt on this point when he says :

" There is no inductive method which could lead to the funda-
mental concepts of physics. Failure to understand this fact
constituted the basic philosophical error of so many investigators
of the nineteenth century. . . . We now realise with special clarity,
how much in error arcy those theorists who believe that theory
comes inductively from experience."

In formal education the student is implicitly, if not explicitly,
led to believe that reason is the main, or even the only, means by
which science advances. This view has been supported by the con-
ception of the so-called " scientific method " outlined mainly by
certain logicians of the last century who had little real under-
standing of research. In this book I have tried to show the error
of this outlook and have emphasised the limitations of reason
as an instrument in making discoveries. I have not questioned the
belief that reason is the best guide in known territory, though

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THE ART OF SCIENTIFIC INVESTIGATION

even here the hazards in its use are probably greater than gener-
ally realised. But in research we are continually groping beyond
known territory and here it is not so much a question of abandon-
ing reason as finding that we are unable to employ it because
there is not sufficient information available on which to use it
properly. Rather than delude ourselves that we are able effec-
tively to use reason in complex natural phenomena when we have
only inadequate information and vague ideas, it seems to me
better openly to recognise that we have often to resort to taste
and to recognise the important roles of chance and intuition in
discovery.

In research, as indeed in everyday life, very often we have of
necessity to decide our course of action on personal judgment
based on taste. Only the technicalities of research are " scientific "
in the sense of being purely objective and rational. Paradoxical
as it may at first appear, the truth is that, as W. H. George has
said, scientific research is an art, not a science."*^

SUMMARY

Tactics are best worked out by the worker engaged on the
problem. He should also have a say in planning strategy, but here
he can often be assisted by a research director or by a technical
committee which includes scientists familiar with the particular
field of work. The main function of committees is planning
matters of poUcy. Research can be planned but discovery
cannot.

When discoveries are transferred to another field of science
they are often instrumental in uncovering still further knowledge.
I have given some hints on how best to go about the various
activities that constitute research, but explicit rules cannot be
laid down because research is an art.

The general strategy of research is to work with some clear
object in view but nevertheless to keep alert for and seize any
unexpected opportunities.

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CHAPTER ELEVEN

SCIENTISTS

" It is not the talents we possess so much as the use we
make of them that counts in the progress of the world."

Brailsford Robertson

Attributes required for research

IN MANY respects the research worker resembles the pioneer.
He explores the frontiers of knowledge and requires many of
the same attributes : enterprise and initiative, readiness to face
difficulties and overcome them with his own resourcefulness and
ingenuity, perseverance, a spirit of adventure, a certain dissatis-
faction with well-known territory and prevailing ideas, and an
eagerness to try his own judgment.

Probably the two most essential attributes for the research
worker are a love of science and an insatiable curiosity. The
person attracted to research usually is one who retains more
than usual of the instinct of curiosity. Anyone whose imagination
cannot be fired by the prospect of finding out something never
before found by man will only waste his and others' time by
taking up research, for only those will succeed who have a genuine
interest and enthusiasm for discovery. The most successful
scientists are capable of the zeal of the fanatic but are discipUned
by objective judgment of their results and by the need to meet
criticism from others. Love of science is hkely to be accompanied
by scientific taste and also is necessary to enable one to persist
in the face of frustration.

A good intelligence, internal drive, wiUingness to work hard
and tenacity of purpose are further prerequisites for success in
research, as in nearly all walks of life. The scientist also needs
imagination so that he can picture in his mind how processes
work, how things take place that cannot be observed and conjure
up hypotheses. The research worker is sometimes a difficult person

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THE ART OF SCIENTIFIC INVESTIGATION

because he has no great confidence in his opinions, yet he also
is sceptical of others' views. This characteristic can be incon-
venient in everyday life. Cajal commenting on the importance
of mental independence in the scientist, remarks that humility
may be fitting for saints but seldom for scientists.^ ^"

A spirit of indomitable perseverance has characterised nearly
all successful scientists, for most worth while achievements re-
quired persistence and courage in face of repeated frustrations.
So strong was this trait in Darwin that his son said it went beyond
ordinary perseverance and could better be described as dogged-
ness. Pasteur said :

" Let me tell you the secret that has led me to my goal. My
only strength lies in my tenacity."^ ^^

People may be divided roughly into those who habitually
react vigorously to external influences — including ideas — and
those who are passive and accept things as they come. The
former question everything they are told even as children and
often rebel against the conventional. They are curious and want
to find out things for themselves. The other type fits into life with
less trouble and, other things being equal, more easily accumu-
lates information given as formal teaching. The mind of this
latter type becomes furnished with generally accepted ideas and
set opinions, whereas the reactive type has fewer fixed opinions
and his mind remains free and flexible. Of course, not everyone
can be classed as belonging to one of these two extremes, but
clearly those approximating to the passive type are not cut out
for research.

Preparing a list of the required attributes is not much help
in the vexing problem of how to select promising people for
research or of deciding yourself if you are suitable, because there
is at present no objective means of measuring the qualities listed.
However, this is a problem which psychologists might be able to
solve in time. For example, it might be possible to devise a test
of a person's knowledge of everyday things that would be a
measure of his curiosity and powers of observation — his success
in " discovering " things in his environment, for life can be a
perpetual process of discovering. Tests might also be devised to
measure ability to generalise, to formulate hypotheses to fit given

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SCIENTISTS

data. Possibly love of science might be tested by determining the
response — being delighted or not — on learning of scientific dis-
coveries.

Ordinary examinations are not a good guide to a student's
ability at research, because they tend to favour the accumulators
of knowledge rather than the thinkers. Brilliant examinees are
sometimes no good at research, while on the other hand some
famous scientists have made a poor showing at examinations.
Paul Ehrlich only got through his final medical examinations by
the grace of the examiners who had the good sense to give recog-
nition to his special talents, and Einstein failed at the entrance
examination to the Polytechnic School. Probably the student
who is reflective and critical is at a disadvantage in accumulating
information as compared with the student who accepts without
question all he is told. Charles Nicolle goes so far as to say that
the inventive genius is not able to store knowledge and that inven-
tiveness may be killed by bad teaching, fixed ideas and erudition. ^^

I have noticed that in England a great many research workers
in both the biological and non-biological sciences are, or have
been in their youth, keen naturalists. The pursuing of some
branch of natural history as a hobby by a young man may be a
valuable indication of an aptitude for research. It shows that he
gets pleasure from studying natural phenomena and is curious
to find out things for himself by observation.

At present the only way of selecting promising research talent
— of " discovering discoverers " as Rous has put it — is by giving
the candidate an opportunity of trying his hand at research for
at least one or two years. Until the young scientist has shown that
he has definite ability in research, it is wiser for him not to be
given a permanent research position. This precaution is as
important for the future welfare and happiness of the scientist
as it is for the good of the research institution. It is helpful for
undergraduates to be given an opportunity during their final
year to dabble in research, as this often gives a preliminary indica-
tion of a person's suitability for research. One favourable indica-
tion is for the young graduate to show real desire to do research
by taking steps to get a research position; in other words, the
best research workers tend to select themselves.

Whatever the exact mental requirements may be, it is a

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THE ART OF SCIENTIFIC INVESTIGATION

widely held opinion that not everyone is able to undertake
research successfully, just as not everyone has talent for com-
posing music, but lack of the particular requirements should not
be regarded as a slur on the person's intelligence or his ability in
other directions.

Incentives and rewards

The chief incentives of research are to satisfy curiosity, to
satisfy the creative instinct, the desire to know whether one's
conjecture has led to the creation of new knowledge and the
desire for the feeling of importance by gaining recognition.
More mundane incentives are the need to gain a livelihood and
the ambition to "get on in the world", "showing" certain
individuals who did not believe in your ability on the one hand,
and on the other hand, trying to justify the confidence that others
may have shown in you. Recognition of work done is an import-
ant incentive as is illustrated by the ill-feeling sometimes dis-
played over contentious points of priority in publication. Even
great scientists are usually jealous of getting all due credit for
their discoveries. The desire to see one's name in print and be
credited throughout the scientific world with one's accomplish-
ments is undoubtedly one of the most important incentives in
research. In addition to these incentives which are common to all
types of research, in applied research there is the desire to
accomplish something for the good of mankind. This is likely to
be more eflfective if it is not merely a vague ideal but if those
to benefit are known to, or in some way associated with, the
research worker.

The man or woman with a research mind is fascinated by the
mental challenge of the unexplained and delights in exercising
the wits in trying to find a solution. This is just a manifestation
of the phenomenon that many people find pleasure in solving
problems, even when there is no reward attached, as is shown by
the popularity of crossword puzzles and detective stories. In-
cidentally Paul Ehrlich loved detective mysteries. Interest in a
particular branch of science sometimes originates from the intrin-
sic beauty of the material or technique employed. Naturalists
and zoologists are often attracted to study a group of animals
because they find their appearance pleasing and a bacteriologist

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SCIENTISTS

may like using a certain technique because it appeals to his
aesthetic sensibility. Very likely it was Ehrlich's extraordinary
love of bright colours (he is said to have derived an ecstatic
pleasure from them) that gave him an interest in dyes and so
determined the direction in which his work developed.

Albert Einstein distinguishes three types of research workers :
those who take up science because it offers them an opportunity
to exercise their particular talents and who exult in it as an
athlete enjoys exercising his prowess; those who regard it as
a means of livelihood and who but for circumstances might
have become successful business men; and lastly the true
devotees, who are rare but make a contribution to knowledge out
of proportion to their numbers. ^^

Some psychologists consider that man's best work is usually
done under adversity and that mental stress and even physical
pain may act as a mental stimulant. Many prominent men have
suffered from psychological troubles and various diflRculties but
for which perhaps they would never have put forward that
effort required to excel.

The scientist seldom gets a large monetary reward for his
labours so he should be freely granted any just fame arising
from his work. But the greatest reward is the thrill of discovery.
As many scientists attest, it is one of the greatest joys that life
has to offer. It gives a tremendous emotional uplift and great
sense of well-being and satisfaction. Not only factual discoveries
but the sudden realisation of a generalisation can give the same
feeling of exhilaration. As Prince Kropotkin wrote :

" He who has once in his life experienced this joy of scientific
creation will never forget it."

Baker quotes the story of the great British biologist Alfred Wallace
making a very small discovery :

" None but a naturalist," wrote Wallace, " can understand the
intense excitement I experienced when at last I captured it
[a new species of butterfly]. My heart began to beat violently,
the blood rushed to my head, and I felt much more like fainting
than I have done when in apprehension of immediate death. I
had a headache the rest of the day, so great was the excitement
produced by what will appear to most people a very inadequate

cause."®

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THE ART OF SCIENTIFIC INVESTIGATION

Referring to the elation he felt after demonstrating the feasibility
of protecting people against smallpox by vaccination, Edward
Jenner wrote :

" The joy I felt at the prospect before me of being the instru-
ment destined to take away from the world one of its greatest
calamities . . . was so excessive that I sometimes found myself
in a kind of reverie."^"

Louis Pasteur and Claude Bernard made the following comments
on this phenomenon :

" When you have at last arrived at certainty, your joy is one
of the greatest that can be felt by a human soul."^^

" The joy of discovery is certainly the liveliest that the mind of
man can ever feel."^^

The discoverer has an urge to share his joy with his colleagues
and usually rushes into a friend's laboratory to recount the event
and have him come and see the results. Most people get more fun
and enjoyment out of new developments if they are able to share
them with colleagues who are working on the same subject or are
sufficiently closely related to be genuinely interested.

The stimulus of a discovery immediately wipes out all the
disappointments of past frustrations and the scientist works with
a new-found vigour. Furthermore, some stimulus is felt by his
colleagues and so one discovery makes the conditions more pro-
pitious for further advances. But unfortunately things do not
always turn out like this. Only too often our joy is short-Uved
and found to be premature. The consequent depression may be
deep, and here a colleague can help by showing understanding
and encouragement. To "take it" in this way without being
beaten is one of the hard lessons the young scientist has to learn.

Unfortunately research has more frustrations than successes
and the scientist is more often up against what appears to be an
impenetrable barrier than making progress. Only those who have
sought know how rare and hard to find are those little diamonds
of truth which, when mined and polished, will endure hard and
bright. Lord Kelvin wrote :

" One word characterises the most strenuous of the efforts for
the advancement of science that I have made perseveringly
during fifty-five years; that word is failure."

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SCIENTISTS

Michael Faraday said that in the most successful instances less
than one in ten of the hopes and preliminary conclusions are
realised. When one is depressed, some cold comfort might be
derived from the experience of those two great scientists. It is well
for the young scientist to realise early that the fruits of research
are not easily won and that if he is to succeed he will need
endurance and courage.

The ethics of research

There are certain ethical considerations which are generally
recognised among scientists. One of the most important is that,
in reporting an investigation, the author is under an obligation
to give due credit to previous work which he has drawn upon and
to anyone who has assisted materially in the investigation. This
elementary unwritten rule is not always followed as scrupulously
as it should be and offenders ought to realise that increased credit
in the eyes of the less informed readers is more than offset by the
opprobrium accorded them by the few who know and whose
opinion really matters. A common minor infringement that one
hears is someone quoting another's ideas in conversation as though
they were his own.

A serious scientific sin is to steal someone's ideas or preliminary
results given in the course of conversation and to work on them
and report them without obtaining permission to do so. This is
rightly regarded as little better than common thieving and I have
heard a repeated offender referred to as a " scientific bandit ".
He who transgresses in this way is not likely to be trusted again.
Another improper practice which unfortunately is not as rare
as one might expect, is for a director of research to annex most
of the credit for work which he has only supervised by publishing
it under joint authorship with his own name first. The author
whose name is placed first is referred to as the senior author,
but senior in this phrase means the person who was responsible
for most of the work, and not he who is senior by virtue of the
post he holds. Most directors are more interested in encouraging
their junior workers than in getting credit themselves. I do not
wish to infer that in cases where the superior officer has played
a real part in the work he should withhold his name altogether,

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THE ART OF SCIENTIFIC INVESTIGATION

as over-conscientious and generous people sometimes do, but
often it is best to put it after that of the younger scientist so
that the latter will not be overlooked as merely one of "and
collaborators". The inclusion of the name of a well known
scientist who has helped in the work is often useful as a guarantee
of the quality of the work when the junior author has not yet
established a reputation for himself It is the duty of every
scientist to give generously whatever advice and ideas he can
and usually formal acknowledgment should not be demanded for
such help.

Some colleagues and myself have found that sometimes what
we have thought to be a new idea turns out not to be original at
all when we refer to notes which we ourselves made on the subject
some time previously. Incomplete remembering of this type
occasionally results in the quite unintentional annexing of another
person's idea. An idea given by someone else in conversation may
subsequently be recalled without its origin being remembered and
thus be thought to be one's own.

Complete honesty is of course imperative in scientific work.
As Cramer said,

" In the long run it pays the scientist to be honest, not only
by not making false statements, but by giving full expression to
facts that are opposed to his views. Moral slovenliness is visited
with far severer penalties in the scientific than in the business
world." 26

It is useless presenting one's evidence in the most favourable light,
for the hard facts are sure to be revealed later by other
investigators. The experimenter has the best idea of the possible
errors in his work. He should report sincerely what he has done
and, when necessary, indicate where mistakes may have arisen.

If an author finds out he cannot later substantiate some results
he has reported he should publish a correction to save others either
being misled or put to the trouble of repeating the work them-
selves, only to learn that a mistake has been made.

When a new field of work is opened up by a scientist, some
people consider it courteous not to rush in to it, but to leave the
field to the originator for a while so that he may have an
opportunity of reaping the first fruits. Personally I do not see
any need to hold back once the first paper has been published.

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SCIENTISTS

Hardly any discovery is possible without making use of a
knowledge gained by others. The vast store of scientific knowledge
which is to-day available could never have been built up if
scientists did not pool their contributions. The publication of
experimental results and observations so that they are available
to others and open to criticism is one of the fundamental
principles on which modem science is based. Secrecy is contrary
to the best interests and spirit of science. It prevents the individual
contributing to further progress; it usually means that he or his
employer is trying to exploit for their own gain some advance
made by building on the knowledge which others have freely
given. Much research is carried out in secret in industry and in
government war departments. This seems to be inevitable in the
world as it is to-day, but it is nevertheless wrong in principle.
Ideally, freedom to publish, provided only that the work has
sufficient merit, should be a basic right of all research workers.
It is said that occasionally, even in agricultural research, results
may be suppressed because they are embarrassing to government
authorities.^^ This would seem to be a dangerous and shortsighted
policy.

Personal secrecy in laboratories not subject to any restrictions
is not infrequently shown by workers who are afraid that someone
else will steal their preliminary results and bring them to fruition
and publish before they themselves are able to do so. This form
of temporary secrecy can hardly be regarded as a breach of
scientific ethics but, although understandable, it is not commend-
able, for free interchange of information and ideas helps hasten
the advance of science. Nevertheless information given in confi-
dence must be respected as such and not handed on to others. A
travelling scientist visiting various laboratories may himself be
perfectly honourable in not taking advantage of unpublished
information he is given, but may inadvertently hand on such
information to a less scrupulous individual. The traveller can best
avoid this risk by asking not to be told anything that is wished
to be kept confidential, for it is difficult to remember what is for
restricted distribution and what not.

Even in the scientific world, unfortunately, one occasionally
encounters national jealousies. These are manifest by lack of
appreciation or acknowledgment of work done in other countries.

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THE ART OF SCIENTIFIC INVESTIGATION

Not only is this to be deplored as a quite indefensible breach of
ethics and of the international spirit of science, but it rebounds
on the offenders, often to the detriment of themselves and their
country. The person failing to appreciate advances in science
made elsewhere may be left in the backwater he deserves, and
he shows himself a second-rate scientist. Among the great majority
of scientists there exists an international freemasonry that is one
of the main reasons for faith in the future of mankind, and it is
depressing to see this marred by petty selfishness on the part of a
few individuals.

Different types of scientific minds

Not all minds work alike. Attempts are often made to divide
scientists broadly into two types, but the classification is arbitrary
and probably the majority fall somewhere between the two
extremes and combine many of the characteristics of both.

W. D. Bancroft,^" the American chemist, calls one type the
" guessers " (using the word guess in the sense of making a shrewd
judgment or hypothesis in advance of the facts) : these follow
mainly the deductive or Aristotehan methods. They get their
hypothesis first, or at any rate early in the investigation, and then
test it by experiment. The other type he calls the "accumulators"
because they accumulate data until the generalisation or hypo-
thesis is obvious; these follow the inductive or Baconian method.
However, the terms inductive and deductive, and Aristotelian
and Baconian can be confusing and have sometimes been misused.
Henri Poincare^^ and Jacques Hadamard^" classify mathemati-
cians as either "intuitive" or "logical" according to whether
they work largely by intuitions or by gradual systematic steps.
This basis of classification seems to agree with Bancroft's. I will
use the terminology "speculative" and "systematic" as this seems
the simplest way of indicating the principal difference between
the two types.

Charles Nicolle®^ distinguished (a) the inventive genius who
cannot be a storehouse for knowledge and who is not necessarily
highly intelligent in the usual sense, and {b) the scientist with a
fine intelligence who classifies, reasons and deduces but is,
according to NicoUe, incapable of creative originality or making

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original discoveries. The former uses intuition and only calls on
logic and reason to confirm the finding. The latter advances
knowledge by gradual steps like a mason putting brick on brick
until finally a structure is formed. Nicolle says that intuitions were
so strong with Pasteur and Metchnikoff that sometimes they
almost published before the experimental results were obtained.
Their experiments were done mainly to reply to their critics.
Bancroft gives the following illustrations of the outlook of the
diflferent types of scientist. Examples of the systematic type are
Kelvin and Sir W. Hamilton, who said,

" Accurate and minute measurement seems to the non-
scientific imagination a less lofty and dignified work than looking
for something new, yet nearly all the grandest discoveries are
made this way ",

" In physical sciences the discovery of new facts is open to any
blockhead with patience and manual dexterity and acute senses."

Contrast this last statement with one made by Davy :

" I thank God I was not made a dextrous manipulator; the
most important of my discoveries have been suggested to me
by my failures."

Most mathematicians are the speculative type. The following
remarks are attributed to Newton, Whewell and Gauss respec-
tively :

" No great discovery is ever made without a bold guess,"

" Advances in knowledge are not commonly made without
some boldness and licence in guessing,"

" I have the result but I do not yet know how to get it."

Most of the outstanding discoverers in biology have also been of
the speculative type. Huxley wrote :

" It is a popular delusion that the scientific enquirer is under
an obligation not to go beyond generalisation of observed facts
. . . but anyone who is practically acquainted with scientific work
is aware that those who refuse to go beyond the facts, rarely
get as far."

The following two comments, made on different occasions, reveal
Pasteur's views on this point :

" If someone tells me that in making these conclusions I have

H9

THE ART OF SCIENTIFIC INVESTIGATION

gone beyond the facts, I reply : ' it is true that I have freely put
myself among ideas which cannot be rigorously proved. That is
my way of looking at things.' "

" Only theory can bring forth and develop the spirit of inven-
tion."

W. Ostwald classifies scientists slightly differently.'*^ He distin-
guishes the classicist whose main characteristic is to bring to
perfection every discovery and is systematic, and the romanticist
who has a multitude of ideas but has a certain amount of super-
ficiality in dealing with them and seldom works them out com-
pletely. Ostwald says the classicist is a bad teacher and cannot
do anything in front of others, while the romanticist gives away
his ideas freely and has an enormous influence on his students.
He may produce some outstanding students but sometimes spoils
their originality. On the other hand, as Hadamard points out,
highly intuitive minds may be very obscure. Kenneth Mees
considers that practical scientific discovery and technology
embrace three different methods of working : {a) theoretical
synthesis, (b) observation and experiment, (c) invention. It
is rare, he says, for one man to excel in more than one
of these activities, for each requires a different type of mind.^^

The systematic type of scientist is probably more suited to
developmental research and the speculative type to exploratory
research; the former to team work and the latter either to
individual work or as leader in a team. Dr. E. L. Taylor describes
the organisation of a large commercial research organisation
which employed men of the speculative type to play about with
their ideas, but as soon as they hit on something that promised
to be of value it was taken out of their hands entirely and given
to a systematic worker to test and develop fully. ^°

The speculative and systematic types, however, represent
extremes and probably most scientists combine some of the
characteristics of both. The student may find that he has natural
tendencies toward one type or the other. Bancroft considers that
often one type cannot be converted to the other. It is probably
best for each to follow his natural tendencies and one wonders
if many scientists have not been unduly influenced by the teacher
under whose influence they happened to fall. The important
thing is for us not to expect everyone to think the same way as

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we do ourselves. It is a great pity for a young scientist who is
naturally the speculative type to come under the influence of a
systematic type and be misguided into believing that his imagina-
tion should be suppressed to the extent that it is crushed. The
man who gets ideas of his own and wants to try them out is
more likely to be attracted by research, to contribute more to it,
and to get more from it than the man lacking in imagination and
curiosity. The latter can do useful work on research but probably
does not get much enjoyment out of it. Both types are necessary
for the advancement of science for they tend to be comple-
mentary.

As is mentioned elsewhere, it is a common error among
philosophers and writers of books on the scientific method to
believe that discoveries are made by the systematic accumulation
of data until the generalisation is a matter of plain logic, whereas
in fact this is true in probably a minority of cases.

The scientific life

Some comment on the personal aspects of research might be
helpful to the young man or woman contemplating taking up a
scientific career.

The young scientist on reading this book might be alarmed at
the demands made on him and, unless he is one of those rare
individuals who is willing to give his whole life to "a cause", he
may be put off research if some further comment is not offered.
Let me reassure him at once that this is a counsel of perfection
and one can become a good research worker without sacrificing
all other interests in life. If one is willing to regard research as
a calling and to become what Einstein calls a tiTie devotee, all to
the good, but there are plenty of examples of great and successful
scientists who have not only lived normal family lives but have
managed also to find time for many outside interests. Until recent
times research was carried on only by the devotees, because the
material rewards were so poor, but nowadays research has
become a regular profession. However, it cannot be conducted
successfully on a strict 9 a.m. to 5 p.m. basis and some evening
study is a practical necessity. One needs to have a real interest in
science and it must be part of one's life and looked upon as a
pleasure and a hobby.

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THE ART OF SCIENTIFIC INVESTIGATION

Research work progresses in an irregular manner and only
occasionally is the scientist hotly pursuing a new discovery. It is
then he needs to pour all his energies into the work and think of
it day and night. If he has the true scientific spirit he will want
to do this and it is crippling if circumstances prevent it. The
research man's family usually understand that if he is to be a
creative scientist, there are times when it is most important for
him to be spared other responsibilities and worries as much as
possible; and likewise his colleagues at the laboratory usually try
and help with any other commitments he may have in the way
of routine work or administration. This help is not Hkely to be a
burden on his associates or family because these spurts are all too
rare with most people. Perhaps two to six intervals each of a
week or two every year might be average, but they will vary
enormously from one individual to another. However, these
remarks should not be misconstrued as an encouragement to
develop an "artistic temperament" and lack of responsibility in
everyday affairs !

When Simon Flexner was planning the Rockefeller Institute he
was asked "are you going to allow your men to make fools of
themselves at your Institute?" The implication was that only
those who would risk doing so were likely to make important
discoveries. The research man must not be put off his ideas by
fear of being ridiculous or being said to have "a bee in his
bonnet". It sometimes requires courage to put forward and follow
up a novel idea. It will be remembered that Jenner confided his
proposals about vaccination to a friend under a bond of secrecy
for fear of ridicule.

When I asked Sir Alexander Fleming about his views on
research his reply was that he was not doing research when he
discovered penicillin, he was just playing. This attitude is typical
of many bacteriologists who refer to their research as "playing
about" with this or that organism. Sir Alexander believes that
it is the people who play about who make the initial discoveries
and the more systematic scientists who develop them. This
expression, "playing about", is significant for it clearly means
that the scientist is doing something for his own enjoyment, to
satisfy his own curiosity. However, with the incompetent person
"playing about" may amount to nothing more than ineffectual

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pottering in which nothing is followed up. Sir Henry Dale,
speaking at a Congress held in Cambridge in 1948 in honour
of Sir Joseph Barcroft, said that the great physiologist always
regarded research as an amusing adventure. Speaking at the
same Congress, Professor F. J. W. Roughton said that for
Barcroft and for Starling, physiology was the greatest sport in
the world.

The great pioneers of science, although they have defended
their ideas feH^ently and often fought for them, were mostly at
heart humble men, for they realised only too clearly how puny
were their achievements compared to the vastness of the as yet
unknown. Near the end of his life Pasteur said : " I have wasted
my life" as he thought of the things he might have done to
greater profit. Shortly before his death Newton is reported to
have said :

" I know not what I may appear to the world, but to myself I
appear to have been only like a boy playing on the sea-shore, and
diverting myself in now and then finding a smoother pebble or a
prettier shell than ordinary, whilst the great ocean of truth lay
all undiscovered before me."

Diversion and holidays are very much a question of individual
requirements but freshness and originality may be lost if the
scientist works unremittingly for too long. In this connection a
good maxim has been coined by Jowett : "Don't spare; don't
drudge." Most of us require recreation and variety in interests
to avoid becoming dull, stodgy and mentally constipated. Simon
Flexner's attitude to holidays was the same as Pierpont Morgan's
— who once remarked that he could do a full year's work in nine
months but not in twelve months. Most scientists, however, do not
require as much as three months' annual vacation.

Mention has already been made of the disappointments so
often met in research and the need for understanding and encour-
agement from colleagues and friends. It is recognised that these
continual frustrations sometimes produce a form of neurosis
which Professor H. A. Harris calls "lab. neurosis", or they may
kill a man's interest in research. Interest and enthusiasm must
be kept alive and this may be difficult if the worker is obliged
to plod along on a line of work which is not getting anywhere.

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THE ART OF SCIENTIFIC INVESTIGATION

In most walks of life it is possible to get into a groove, or to go
"stale", but it is a more serious problem in research than in most
other occupations, because practically all the research worker's
activities must be initiated from within his own brain. He gets
stimulus from his work only when he is making progress, whereas
the business man, the lawyer and the physician are constantly
receiving stimulus both from their clients and from the fact that
they are able to effect something.

Frequent discussion of one's work with associates who show
an interest in it is helpful in avoiding "lab. neurosis". The great
value of "mental catharsis" in neurosis is well known, and
similarly telling others of one's problems and sharing one's dis-
appointments can help the baffled research worker from suffering
unduly from worry.

"Lab. neurosis" is most likely to arise in scientists devoting all
their time to one research problem. Some individuals find
sufficient relief if they have two problems under investigation at
the same time. For others it is better to spend a portion of their
time in teaching, routine diagnostic work, administration or
similar occupation which enables them to feel they are doing
something effectively and contributing something to the com-
munity even if getting nowhere with the research. Each case needs
to be considered individually, but if effective research is to be
accomplished the scientist nevertheless has to devote the major
portion of his time to it.

With regard to this latter point W. B. Cannon waxes eloquent :

" This time element is essential. The investigator may be made
to dwell in a garret, he may be forced to live on crusts and wear
dilapidated clothes, he may be deprived of social recognition,
but if he has time, he can steadfastly devote himself to research.
Take away his free time and he is utterly destroyed as a contri-
butor to knowledge." ^^

It is little use to squeeze research into an hour or two of spare
time during a day occupied in other duties, especially if the other
duties are of a nature that require a lot of thought, for, apart
from time at the bench, research requires peace of mind for
reflection. Furthermore, to achieve results in research it is some-
times necessary to drive oneself in the face of frustrations and
it may be a disadvantage to have a too ready alternative "escape"

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SCIENTISTS

activity. F. M. Burnet considers that part-time research is usually
"of relatively unimportant character".

Piatt and Baker suggest that a research worker may have to
choose between having a reputation as being good natured and
easily accessible to visitors but mediocre, or on the other hand
temperamental but successful. Visitors to laboratories who are
merely scientific sightseers ought to be severely discouraged, but
most research workers are glad to make time to talk to visitors
who have a genuine and serious interest in their work.

Just before his death Pavlov wrote :

" What can I wish to the youth of my country who devote
themselves to science? Firstly, gradualness. About this most
important condition of fruitful scientific work I can never speak
without emotion. Gradualness, gradualness, gradualness . . .
never begin the subsequent without mastering the preceding . . .
But do not become the archivist of facts. Try to penetrate the
secret of their occurrence, persistently searching for the laws
which govern them. Secondly, modesty ... do not allow haughti-
ness to take you in possession. Due to that you will be obstinate
where it is necessary to agree, you will refuse useful and friendly
help, you will lose your objectiveness. Thirdly, passion. Remem-
ber that science demands from a man all his life. If you had two
lives that would not be enough for you. Be passionate in your
work and your searching."

68

Enthusiasm is one of the great motivating forces, but, like any-
thing associated with emotion, it can be fickle. Some people are
given to bursts of intense enthusiasm which are short-lived,
whereas others are able to sustain their interest for long periods,
usually at a more moderate intensity. It is as well to learn as much
as possible about oneself in this, as in other respects. Personally,
when I feel myself in the grip of an enthusiasm, warned by past
experience, I try to assess the situation objectively and decide
if there is a solid foundation for the enthusiasm or if it is hkely
to burn itself out leaving that deflated feeling from which it is
difficult to rouse further interest in the subject. One help in
sustaining interest in a subject is to share that interest with
colleagues. This also helps to sober one up and check ill-founded
bursts of enthusiasm. Young people are especially liable to get
excited about their ideas and be impatient to try them out without

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THE ART OF SCIENTIFIC INVESTIGATION

giving them sufficient critical thought. Enthusiasm is a most
valuable stimulant but, like most stimulants, its use needs to be
tempered with a proper understanding of all its effects.

If the young scientist succeeds within a year or two of
graduation in establishing a profitable Une of work, it is as well
for him to pursue it to the exclusion of other subjects, but
generally it is wise for him to gain some breadth of experience
before devoting all his time to one field. Similarly with his place
of work : if he is fortunate enough to find his colleagues and the
circumstances of his position such that he is well satisfied with
his advances, well and good, but often, especially if the scientist
feels he is getting into a groove, a change of position is very
helpful owing to the great stimulus that is to be had from fresh
mental contacts and different scientific fields. I have been struck
by this myself and others have told me that they also have
experienced it. Perhaps every three to five years the scientist
under forty should examine his position in this light. A change
of subjects also is often beneficial, for working too long on the
same problem can produce intellectual sterility.

It is usually difficult or undesirable for senior scientists to
change their posts; for them the sabbatical year's leave provides
the opportunity for a change of mental climate, while another
method is to arrange a temporary exchange of scientists between
institutes.

It is rare for a person to carry within himself enough drive
and interest to be able to pursue research for long if he is isolated
from people with similar interests. Most scientists stagnate when
alone, but in a group have a symbiotic-like effect on one another,
just as to culture some bacteria it is necessary to have a number
of individual organisms or to start a fire several sticks are
necessary. This is the main advantage of working in a research
centre. The fact that there one can get advice and co-operation
from colleagues and borrow apparatus is of secondary impor-
tance. Scientists from the more outlying parts of the world get
great benefit from coming to one of the great research centres
for a period of work, and also from paying brief visits to various
research centres. Similarly, the main value of scientific congresses
is the opportunity they provide for scientists to meet informally
and discuss topics of mutual interest. Great stimulus is to be

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SCIENTISTS

derived from meeting people who are interested in the same things
as ourselves, and subjects become more interesting when we see
how interested others are in them. Indeed few of us are sufficiently
strong-minded and independent to be enthusiastic about a subject
which does not interest others.

Nevertheless there are the rare individuals who have sufficient
internal drive and enthusiasm not to stagnate when alone and
even perhaps to benefit from the forced independence and wider
interests that the isolated worker is obliged to take up. Most of
the great pioneers had to work out their ideas independently and
some — Mendel in his monastery and Darwin during the voyage
of the Beagle — worked in scientific isolation. A present-day
example is H. W. Bennetts who has worked in comparative
scientific isolation in Western Austraha. He has to his credit the
discovery of the cause of entero-toxaemia of sheep and copper
deficiency as a cause of disease in sheep and cattle as well as other
important pioneer contributions to knowledge.

Lehman has collected some interesting data about man's most
creative time of life.^^ He extracted data from sources such as
A Series of Primers of the History of Medicine and An Intro-
duction to the History of Medicine, and found that the maximum
output of people bom between 1750 and 1850 was during the
decade of life 30 to 39 years. Taking this as 100 per cent, the
output for the decade 20—29 years was 30—40 per cent; for 40-49
years, 75 per cent; 50-59 years, about 30 per cent. Probably
man's inventiveness and originality begins to decrease at an early
age, possibly even in the 20s, but this is offset by increased
experience, knowledge and wisdom.

Cannon says that Long and Morton began the use of ether as
an anaesthetic when they were both 27 years of age; Banting
was 31 when he discovered insulin; Semmelweis recognised the
infectiousness of puerperal fever when he was 29 ; Claude Bernard
had started his researches on the glycogenic function of the liver
when he was 30 ; van Grafe devised the operation for cleft palate
and founded modem plastic surgery when he was 29. When
von Helmholtz was only 22, barely emerged as an undergraduate
medical student, he published an important paper suggesting
that fermentation and putrefaction were vital phenomena and
thus paved the way for Pasteur.^* Robinson considers 28 is a

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THE ART OF SCIENTIFIC INVESTIGATION

critical age, as many great scientists have published their most
important work at that age. On the other hand, some individuals
continue to do first-rate research till they are past 70. Pavlov,
Sir Frederic Gowland Hopkins and Sir Joseph Barcroft are good
examples.

The fact that a person has not made a significant contribution
by the time he is 40 does not necessarily mean he never will,
for such cases have occurred, though not often. With advancing
age most minds become less receptive to new ideas suggested by
others and probably also arising from their work or thinking.
William Harvey stated that no man over forty accepted the idea
of the circulation when he first advanced it. The reason why
many lose their productivity about middle age is often simply
due to their having taken on administrative responsibilities that
do not allow time for research. In other cases indolence develops
with middle age and security, and drive is lost. Contact with
young minds often helps to preserve freshness of outlook. What-
ever the reasons for the frequent falling off of productivity after
middle age, its occurrence shows that accumulation of know-
ledge and experience is not the main factor in successful research.

W. Ostwald considered that the frequent decrease of product-
ivity with increasing age is due to too long familiarity with the
same subject. The way in which accumulated information
handicaps originality was discussed in the first chapter of this
book. For scientists past middle age who have lost originality,
Ostwald advocated a radical change of field of work. In his
own case he was evidently successful in refreshing his mind by
this means when he was over fifty years of age.

The research scientist is fortunate in that in his work he can
find something to give meaning and satisfaction to life. For
those who seek peace of mind by sinking their personality in
something bigger than themselves, science can have a special
appeal, while the somewhat more material-minded can get
gratification from the knowledge that his achievements in
research have an immortality. Few callings can claim to have
as much influence on the welfare of mankind as scientific
research, especially in the medical and biological sciences.
Brailsford Robertson said : " The investigator is the pathfinder
and the pioneer of new civilisations."^* The human race has

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SCIENTISTS

existed and been accumulating knowledge for only about a million
years, and civilisation started only some 10,000 years ago. There
is no known reason why the world should not remain habitable
for hundreds of milHons of years to come. The mind staggers at
the thought of what will be accomphshed in the future. We have
scarcely begun to master the forces of nature.

But more urgent than finding out how to control the world's
climate, to draw on the heat stored under the crust of the earth,
or reaching out through space to other worlds, is the need for
man's social development to catch up with his achievements in
the physical sciences. And whose fancy can guess at the shape
of things to come when mankind finds the collective will and
courage to assume the tremendous but ultimately inescapable
responsibility of deliberately directing the further evolution of
the human species, and the greatest tool of research, the mind
of man, becomes itself the subject of scientific development?

SUMMARY

Curiosity and love of science are the most important mental
requirements for research. Perhaps the main incentive is the
desire to win the esteem of one's associates, and the chief
reward is the thrill of discovery, which is widely acclaimed as
one of the greatest pleasures life has to offer.

Scientists may be divided broadly into two types according
to their method of thinking. At one extreme is the speculative
worker whose method is to try to arrive at the solution by use
of imagination and intuition and then test his hypothesis by
experiment or observation. The other extreme is the systematic
worker who progresses slowly by carefully reasoned stages and
who collects most of the data before arriving at the solution.

Research work commonly progresses in spurts. It is during
the " high spots " that it is almost essential for the scientist
to devote all possible energy and time to the work. Continual
frustrations may produce a mild form of neurosis. Precautions
against this include working on more than one problem at a
time or having some other part-time occupation. A change of
mental environment usually provides a great mental stimulus, and
sometimes a change of subject does too.

There is real gratification to be had from the pursuit of
science, for its ideals can give purpose to life.

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APPENDIX

FURTHER EXAMPLES OF DISCOVERIES
IN WHICH CHANCE PLAYED A PART

(i) It was not a physicist but a physiologist, Luigi Galvani,
who discovered current electricity. He had dissected a frog and
left it on a table near an electrical machine. When Galvani left
it for a moment someone else touched the nerves of the leg with
a scalpel and noticed this caused the leg muscles to contract. A
third person noticed that the action was excited when there was
a spark from the electric machine. When Galvani's attention was
drawn to this strange phenomenon he excitedly investigated it and
followed it up to discover current electricity. ^^^

(2) In 1822 the Danish physicist, Oersted, at the end of a
lecture happened to bring a wire, joined at its two extremities
to a voltaic cell, to a position above and parallel to a magnetic
needle. At first he had purposely held the wire perpendicular
to the needle but nothing happened, but when by chance he
held the wire horizontally and parallel to the needle he was
astonished to see the needle change position. With quick insight
he reversed the current and found that the needle deviated in
the opposite direction. Thus by mere chance the relationship
between electricity and magnetism was discovered and the path
opened for the invention by Faraday of the electric dynamo.
It was when telling of this that Pasteur made his famous remark :
" In the field of observation chance favours only the prepared
mind." Modem civilisation perhaps owes more to the discovery
of electro-magnetic induction than to any other single
discovery. ^^

(3) When von Rontgen discovered X-rays he was experiment-
ing with electrical discharges in high vacua and using barium
platinocyanide with the object of detecting invisible rays, but
had no thought of such rays being able to penetrate opaque
materials. Quite by chance he noticed that barium platino-

160

APPENDIX

cyanide left on the bench near his vacuum tube became fluores-
cent ahhough separated from the tube by black paper. He
afterwards said : " I found by accident that the rays penetrated
black paper."*

(4) When W. H. Perkin was only eighteen years old he tried
to produce quinine by the oxidation of allyl-o-toluidine by
potassium dichromate. He failed, but thought it might be
interesting to see what happened when a simpler base was
treated with the same oxidiser. He chose aniline sulphate and
thus produced the first aniline dye. But chance played an even
bigger part than the bare facts indicate : had not his aniline
contained as an impurity some p-toluidine the reaction could
not have occurred.*

(5) During the first half of the nineteenth century it was
firmly believed that animals were unable to manufacture carbo-
hydrates, fats or proteins, all of which had to be obtained in
the diet preformed from plants. All organic compounds were
believed to be synthesised in plants whereas animals were thought
to be capable only of breaking them down. Claude Bernard
set out to investigate the metabolism of sugar and in particular
to find where it is broken down. He fed a dog a diet rich in
sugar and then examined the blood leaving the liver to see if
the sugar had been broken down in the liver. He found a
high sugar content, and then wisely carried out a similar
estimation with a dog fed a sugar-free meal. To his astonish-
ment he found also a high sugar content in the control animal's
hepatic blood. He realised that contrary to all prevailing views
the liver probably did produce sugar from something which is
not sugar. Thereupon he set about an exhaustive series of
experiments which firmly established the glycogenic activity of
the liver. This discovery was due firstly to the fact that Bernard
was meticulous in controlling every stage of his experiments, and
secondly, to his ability to recognise the importance of a result
discordant with prevailing ideas on the subject and to follow
up the clue thus given.^^

(6) A mixture of lime and copper sulphate was sprayed on
posts supporting grape vines in Medoc with the object of
frightening away pilferers. Millardet later noticed that leaves
accidentally sprayed with the mixture were free from mildew.

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THE ART OF SCIENTIFIC INVESTIGATION

The following up of this clue led to the important discovery
of the value of Bordeaux mixture in protecting fruit trees and
vines from many diseases caused by fungi. ^^

(7) The property of formalin of removing the toxicity of
toxins without affecting their antigenicity was discovered by
Ramon by chance when he was adding antiseptics to filtrates
with the object of preserving them/^

(8) The circumstances leading to the discovery of penicillin
are widely known. Fleming was working with some plate cultures
of staphylococci which he had occasion to open several times
and, as often happens in such circumstances, they became con-
taminated. He noticed that the colonies of staphylococci around
one particular colony died. Many bacteriologists would not
have thought this particularly remarkable for it has long been
known that some bacteria interfere with the growth of others.
Fleming, however, saw the possible significance of the observa-
tion and followed it up to discover penicillin, although its
development as a therapeutic agent was due to the subsequent
work of Sir Howard Florey. The element of chance in this
discovery is the more remarkable when one realises that that
particular mould is not a very common one and, further, that
subsequently a most extensive, world-wide search for other anti-
biotics has failed to date to discover anything else as good. It
is of interest to note that the discovery would probably
not have been made had not Fleming been working under
" unfavourable " conditions in an old building where there was
a lot of dust and contaminations were likely to occur."^

(9) J- Ungar^^ found that the action of penicillin on
certain bacteria was slightly enhanced by the addition to the
medium of paraminobenzoic acid (PABA). He did not explain
what made him try this out but it seems likely that it was
because PABA was known to be an essential growth factor for
bacteria. Subsequently, Greiff, Pinkerton and Moragues'*' tested
PABA to see if it enhanced the weak inhibitory effect which
penicillin had against typhus rickettsiae. They found that
PABA alone had a remarkably effective chemotherapeutic action
against the typhus organisms. " This result was quite unex-
pected," they said. As a result of this work PABA became
recognised as a valuable chemotherapeutic agent for the typhus

162

APPENDIX

group of fevers, against which previously nothing had been
found effective.

In the chapter on hypothesis I have described how
salvarsan and sulphanilamide were discovered following an
hypothesis that was not correct. Two other equally famous
chemotherapeutic drugs were discovered only because they
happened to be present as impurities in other substances which
were being tested. Scientists closely associated with the work
have told me the stories of these two discoveries but have asked
me not to publish them as other members of the team may not
wish the way in which they made the discovery to be made
public. Sir Lionel Whitby has told to me a story of a slightly
different nature. He was conducting an experiment on the then
new drug, sulphapyridine, and mice inoculated with pneumo-
cocci were being dosed throughout the day, but were not treated
during the night. Sir Lionel had been out to a dinner party
and before retuminsr home visited the laboratorv to see how the
mice were getting on, and while there lightheartedly gave the
mice a further dose of the drug. These mice resisted the
pneumococci better than any mice had ever done before. Not
till about a week later did Sir Lionel realise that it was the
extra dose at midnight which had been responsible for the
excellent results. From that time, both mice and men were
dosed day and night when under sulphonamide treatment and
they benefited much more than under the old routine.

(lo) In my researches on foot-rot in sheep I made numerous
attempts to prepare a medium in which the infective agent would
grow. Reason led me to use sheep serum in the medium and
the results were repeatedly negative. Finally I got a positive
result and on looking back over my notes I saw that, in that
batch of media, horse serum had been used in place of sheep
serum because the supply of the latter had temporarily run out.
With this clue it was a straightforward matter to isolate and
demonstrate the causal agent of the disease — an organism which
grows in the presence of horse serum but not sheep serum !
Chance led to a discovery where reason had pointed in the
opposite direction.

(ii) The discovery^ that the human influenza virus is able to
infect ferrets was a landmark in the study of human respiratory

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THE ART OF SCIENTIFIC INVESTIGATION

diseases. When an investigation on influenza was planned,
ferrets were included among a long list of animals it was
intended to try and infect sooner or later. However, some time
before it was planned to try them, it was reported that a colony
of ferrets was suffering from an illness which seemed to be
the same as the influenza then aflfecting the people caring for
them. Owing to this circumstantial evidence, ferrets were
immediately tried and found susceptible to influenza. Afterwards
it was found that the idea which prompted the tests in ferrets
was quite mistaken for the disease occurring in the colony of
ferrets was not influenza but distemper ! ^

( 1 2) A group of English bacteriologists developed an effective
method of sterilising air by means of a mist made from a
solution of hexyl-resorcinol in propylene-glycol. They conducted
a very extensive investigation trying out many mixtures. This
one proved the best; the glycol was chosen merely as a suitable
vehicle for the disinfectant, hexyl-resorcinol. Considerable
interest was aroused by the work because of the possibility of
preventing the spread of air-borne diseases by these means.
When other investigators took up the work they found that the
effectiveness of the mixture was due not to the hexyl-resorcinol
but to the glycol. Subsequently, glycols proved to be some of
the best substances for air disinfection. They were only intro-
duced into this work as solvents for other supposedly more active
disinfectants and were not at first suspected as having any
appreciable disinfective action themselves."

(13) Experiments were being conducted at Rothamsted
Experimental Station on protecting plants from insects with
various compounds, when it was noticed that those plants treated
with boric acid were strikingly superior to the rest. Investigation
by Davidson and Warington showed that the better growth had
resulted because the plants required boron. Previously it had
not been known that boron was of any importance in plant
nutrition and even after this discovery, boron deficiency was for
a time thought of as only of academic interest. Later, however,
some diseases of considerable economic importance — " heart-
rot " of sugar beet for example — were found to be manifesta-
tion of boron deficiency. ^"^

(14) The discovery of selective weed-killers arose unexpectedly

164

APPENDIX

from studies on root nodule bacteria of clovers and plant
growth stimulants. These beneficial bacterial nodules were found
to exert their deforming action on the root hairs by secreting a
certain substance. But when Nutman, Thornton and Quastel
tested the action of this substance on various plants, they were
surprised to find that it prevented germination and growth.
Furthermore they found that this toxic effect was selective, being
much greater against dicotyledon plants, which include most
weeds, than against monocotyledon plants, which include grain
crops and grasses. They then tried related compounds and found
some which are of great value in agriculture to-day as selective
weed-killers.^^

(15) Scientists working on the technicalities of food preserva-
tion tried prolonging the " life " of chilled meat by replacing
the air by carbon dioxide which was known to have an inhibitory
effect on the growth of micro-organisms causing spoilage.
Carbon dioxide, at the high concentration used, was found to
cause an unpleasing discoloration of the meat and the whole
idea was abandoned. Some time later, workers in the same
laboratory were investigating a method of refrigeration which
involved the release of carbon dioxide into the chamber in
which the food was stored, and observations were carried out
to see whether the gas had any undesirable effect. To their
surprise the meat not only remained free from discoloration
but even in the relatively low concentrations of carbon dioxide
involved it kept in good condition much longer than ordinarily.
From this observation was developed the important modem pro-
cess of "gas storage" of meat in which 10—12 per cent carbon
dioxide is used. At this concentration the gas effectively prolongs
the " life " of chilled meat without causing discoloration.^^

(16) I was investigating a disease of the genitalia of sheep
known as balano-posthitis. It is a very long-lasting disease and
was thought to be incurable except by radical surgery. Affected
sheep were sent from the country to the laboratory for investiga-
tion but to my surprise they all healed spontaneously within a
few days of arrival. At first it was thought that typical cases
had not been sent, but further investigation showed that the
self-imposed fasting of the sheep when placed in a strange
environment had cured the disease. Thus it was found that

165

THE ART OF SCIENTIFIC INVESTIGATION

this disease, refractory to other forms of treatment, could in
most cases be cured by the simple expedient of fasting for a
few days.

(17) Paul Ehrlich's discovery of the acid- fast method of stain-
ing tubercle bacilli arose from his having left some preparations
on a stove which was later inadvertently lighted by someone. The
heat of the stove was just what was required to make these
waxy-coated bacteria take the stain. Robert Koch said " We
owe it to this circumstance alone that it has become a general
custom to search for the bacillus in sputum." ^^^

(18) Dr. A. S. Parkes relates the following story of how he and
his colleagues made the important discovery that the presence of
glycerol enables living cells to be preserved for long periods at very
low temperatures.

" In the autumn of 1948 my colleagues. Dr. Audrey Smith and
Mr. C. Polge, were attempting to repeat the results which
Shaffner, Henderson and Card (1941) had obtained in the use of
laevulose solutions to protect fowl spermatozoa against the effects
of freezing and thawing. Small success attended the efforts, and
pending inspiration a number of the solutions were put away in
the cold-store. Some months later work was resumed with the
same material and negative results were again obtained with all
of the solutions except one which almost completely preserved
motility in fowl spermatozoa frozen to -79 °C. This very curious
result suggested that chemical changes in the laevulose, possibly
caused or assisted by the flourishing growth of mould which had
taken place during storage, had produced a substance with sur-
prising powers of protecting living cells against the effects of
freezing and thawing. Tests, however, showed that the mysteri-
ous solution not only contained no unusual sugars, but in fact
contained no sugar at all. Meanwhile, further biological tests had
shown that not only was motility preserved after freezing and
thawing but, also, to some extent, fertilizing power. At this point,
with some trepidation, the small amount (10—15 ml.) of the
miraculous solution remaining was handed over to our colleague
Dr. D. Elliott for chemical analysis. He reported that the solution
contained glycerol, water, and a fair amount of protein ! It was
then realised that Mayer's albumen — the glycerol and albumen
of the histologist — had been used in the course of morphological
work on the spermatozoa at the same time as the laevulose solu-
tions were being tested, and with them had been put away in the
cold-store. Obviously there had been some confusion with the
various bottles, though we never found out exactly what had

166

APPENDIX

happened. Tests with new material very soon showed that the
albumen played no part in the protective effect, and our low
temperature work became concentrated on the effects of glycerol
in protecting living cells against the effects of low tempera-

tures." ^^^

(19) In a personal communication Dr. A. V. Nalbandov has
given the following intriguing story of how he discovered the
simple method of keeping experimental chickens ahve after the
surgical removal of the pituitary gland (hypophysectomy).

" In 1940 I became interested in the effects of hypophysectomy
of chickens. After I had mastered the surgical technique my
birds continued to die and within a few weeks after the operation
none remained alive. Neither replacement therapy nor any other
precautions taken helped and I was about ready to agree with
A. S. Parkes and R. T. Hill who had done similar operations in
England, that hypophysectomized chickens simply cannot live.
I resigned myself to doing a few short-term experiments and
dropping the whole project when suddenly 98% of a group of
hypophysectomized birds survived for 3 weeks and a great many
lived for as long as 6 months. The only explanation I could find
was that my surgical technique had improved with practice. At
about this time, and when I was ready to start a long-term experi-
ment, the birds again started dying and within a week both
recently operated birds and those which had lived for several
months, were dead. This, of course, argued against surgical pro-
ficiency. I continued with the project since I now knew that they
could live under some circumstances which, however, eludea me
completely. At about this time I had a second successful period
during which mortality was very low. But, despite careful
analysis of records (the possibility of disease and many other
factors were considered and eliminated) no explanation was
apparent. You can imagine how frustrating it was to be unable
to take advantage of something that was obviously having a pro-
found effect on the ability of these animals to withstand the
operation. Late one night I was driving home from a party via a
road which passes the laboratory. Even though it was 2 a.m. lights
were burning in the animal rooms. I thought that a careless
student had left them on so I stopped to turn them off. A few
nights later I noted again that lights had been left on all night.
Upon enquiry it turned out that a substitute janitor, whose job
it was to make sure at midnight that all the windows were closed
and doors locked, preferred to leave on the lights in the animal
room in order to be able to find the exit door (the light switches
not being near the door). Further checking showed that the two
survival periods coincided with the times when the substitute

167

THE ART OF SCIENTIFIC INVESTIGATION

janitor was on the job. Controlled experiments soon showed that
hypophysectomized chickens kept in darkness all died while
chickens lighted for 2 one-hour periods nightly lived indefinitely.
The explanation was that birds in the dark do not eat and develop
hypoglycaemia from which they cannot recover, while birds
which are lighted eat enough to prevent hypoglycaemia. Since
that time we no longer experience any trouble in maintaining
hypophysectomized birds for as long as we wish."

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174

INDEX

Accidental discoveries, 33
Acid-fast staining, 166
Age, creative, 156
Agglutination, 29
Air sterilisation, 164
Analogy, 94
Anaphylaxis, 28
Aniline dye, 161
Anthrax, 96
Applied research, 126
Attributes for research, 139

Bacon, Francis, 3, 6, 57, 82, 118,
Baker, J. R. 74
Balano-posthitis, 165
Bancroft, W. D., 25, 148
Barcroft, Sir Joseph, 11, 153
Bartlett, Sir Frederic, 60
B.C.G. Vaccination, 17
Bennets, H. W., 46, 157
Bernard, Claude, x, 2, 42, 49, 76,

96, 144, 161
Bessemer, 2

Biographies of scientists, 7
Biometrics, 6, 19
Blowfly attack, 97
Broaching the problem, 8
Bordeaux mixture, 162
Boron deficiency, 164
Burnet, Sir MacFarlane, 8, 57,

75, 104, 155
Butterfield, H., 106
Byron, Lord, 2

Cannon, W. B., 68, 71, 117, 154

Celsus, 137

Chamberlain, T. C, 50

Chance, 27

Change of post, 156

Chemotherapy, 32, 44

Chilled meat, 165

Choosing the problem, 8

Clue. 34

Columbus, Christopher, 41

Committees, 122

Competing interests, 6

Conferences, scientific, 7

Congresses, 156

Copper deficiency, 45

Cramer, F., 146

Creative age, 157

Curiosity, 6i

136

89.

59>

Dai^, Sir Henry, 28, 33, 79, 153
Darwin, Charles, 25, 59, 69, 85, 92,

97, 103, 140
Davidson & Warington, 160
Davy, Humphry, 59, 149
Defining problem, 10
Descartes, Rene, 74, 83
Dewey, J., 53, 59
Diabetes, 28
Diamidine, 45
Difficulties, 106
Diphtheria toxin, 41
Discussion, 63, 156
Domagk, G., 45
Duclaux, E., 27
Dunn, J. Shaw, 28
Durham, H. E., 29

Edwards, J. T., 35
Ehrlich, Paul, 44, 141, 166
Einstein, Albert, 56, 60, 137, 141, 143
Electricity, discovery, 160
Electro-magnetic induction, i6o
Enthusiasm, 155
Errors, 115
Ethics, 144
Examinations, 140
Experiments, 13

definition, 13

fool's, 89

misleading, 23

multiple factor, 21

negative, 25

pilot, 15

planning, 19, 125

recording, 17

screening, 15

sighting, 15
Extrasensory perception, 108
Evolution, 69

Fallacy, 19, 22, 23, 116, 117

False trails, 58

Faraday, Michael, 58, 86, 112, 136,

145
Farmers, 10

Fisher, Sir Ronald, 19, 21, 49, 108

Fleming, Sir Alexander, 35, 37, 93,

152, 162

Flexner, Simon, 152, 153

Florey. Sir Howard, 37, 93, 136, 162

175

THE ART OF SCIENTIFIC INVESTIGATION

Foot-rot, 163
Fowl cholera, 27
Freedom in science, 121
Frustrations, 144

Galvani, L., 160

Gas storage, 165

Gauss, 70, 149

George, W. H., 57, 60, 90, 99, 100,

138
Glycogen, synthesis, 161
Gram's stain, 28
Graphs, 23
Gregg, Alan, 33, 103
GriefF, D., et al., 162

Hadamard, Jacques, 59, 68, 70

Haemagglutination, 30

Hamilton, Sir W., 149

Harding, Rosamund E. M., 55, 57

Harvey, William, 106, 107, 112, 153

Herd instinct, 109

Herodotus, 99

Hirst, G. K., 30

History of science, 7

Holidays, 152

Hopkins, Sir F. Gowland, 29

Hunter, John, 23, 62

Huxley, Thomas, 50, 59, 149

Hypothesis, 41

illustrations, 41

multiple, 50

precautions, 48

use, 46

Illustrations, 27
Imagination, 53
Impasse, 134
Incentive, 60, 141
Index, card, 5
Indexing, journals, 9
Influenza virus, 161
Inspiration, 68
Intuition, 54, 68

psychology of, 73
Isolated workers, 156

Jackson, Hughlings, 10, 75, 92
Jenner, Edward, 38, 144
Jowett, 153

Keen, B. A., 51
Kekule, F. A., 56
Kelvin, Lord, 144, 149
Keogh, E. v., 31
Kettering, Charles, 2
Koch, R., 118, 166
Kropotkin, Prince, 69, 143

176

Lab. neurosis, 153
Landsteiner, 37
Languages, 5
Lister, 59
Loeb, Jacques, 64
Loewi, Otto, 71
Luck, 32

McClelland, L. &: Hare, R., 30

Malthus, 69

Mees, C. E. K., 150

Mendel. Gregor, 49, 108

Metchnikoff, Elie, 70, 149

Method, transfer, 129

Milk fever, 43

Millardet, 161

Minds, scientific, 148

Minkowski, 28

Monkey trial, 113

Mules, 97

Mules' operation, 24

Nalbandov, a. v., 167

National jealousies, 147

Natural history, 141

Needham, 23

Neufeld, 37

Newton, 149

Nicolle, Charles, 11, 148

Noguchi, 10

Note taking, 77

Nutman, P. S., et al., 165

Observation, 96

induced, 102

spontaneous, 102
Observations, recording, 17, 104
Occam, William of, 87
Oersted, 160
Opportunities, 34

exploiting, 36

lost, 34
Opportunism, 33
Opposition to discoveries, 111
Ostwald, W., 5, 79, 150, 158
Outsiders, 3

Pairing, 20

Paraminobenzoic acid, 162

Pavkes. A. S.. 166

Pasteur, Louis, 27, 33, 96, 97, 140,

144, 149
Pavlov. I. P., 62, 155
Penicillin, 162
Periodicals, scientific, i
Perkin, W. H., i6i
Planck, Max, 55, 60
Planning, 19, 121

categories, 121

attack, 10

INDEX

Planning and organising, 121

Piatt, W. & Baker, R. A., 68, 72, 77,

150
Poincare, H., 68, 70, 85
Precursory ideas, 36
Preparation, 1
Psychology of intuition, 73
Publication, 136
Pure research, 126

Quinine, 130

Ramon, 162
Randomisation, 21
Rationalise, 90
Reading periodicals, 3
Reason, 82

safeguards, 86
Reasoning, deductive, 84

inductive, 84
References, 9

Research institutes, size, 126
Research, borderline, 128

developmental, 128

exploratory, 128

pot-boiling, 128

types, 126
Resistance to new ideas, 106
Reward, 141, 158
Richet, Charles, 28
Ringer's solution, 29
Robertson, T. Brailsford, 158
Rontgen, 35, 160
Roux, Emile, 41
Rush. B.. 51
Russian genetics, 113

Salvarsan, 44

Schiller, F. C. S., 83, 84, 110, 132

Schmidt, J., 43

Scientific bandit, 145

Scientific life, 152

Scientists, 139

speculative, 150

systematic, 150
Scott, W. M., 74
Secrecy, 147

Semmelweis, Ignaz, 111, 116
Skim-reading, 4
Smith, Theobald, 16, 37, 89, 113

Spencer, Herbert, 5
Spurts, 152
Staining, 166
Steinhaeuser, 37
Stimulus, 156
Strategy, 121
Study, I, 152
Sulphanilamide, 45
Suiphapyridine, 163

Tactics, 131
Taste, scientific, 78
Taylor, E. L., 55, 150
Team work, 123, 124
Teleology, 62
Text-books, 9
Thinking, conditioned, 64

productive, 53

subjective, 81
Topley, W. W. C, 122
Transfer method, 129
Trotter, Wilfred, 84, 90, 109, 112
Twins, 20

Tyndall, J., 58, 109, 134
Typhus diagnosis, 30

Ungar, J., 162

Vaccination, 37

Vesalius, 107

von Bruecke, 62

von Helmholtz, Hermann, 60, 157

von Mering, 28

Wallace, A. R., 69-70, 143
Wallas, Graham, 68, 75
Wassermann, 44
Waterston, J. J., 112
Weed-killers, 164
Weil & Felix, 30, 37
Whewell, 149
Whitby, Sir Lionel, 163
Wilson, G. S., 17
Winslow, C. E. A., 117
Wright, Sir Almroth, 16
Writing scientific papers, 6, 91

X-rays, 160

Zinsser, Hans, 57, 93, 111

177

ACKNOWLEDGEMENTS

For their kind permission to reproduce paintings and photo-
graphs in this book, the Author wishes to thank the following :

The National Portrait Gallery, for Michael Faraday and
Edward Jenner.

The Royal Society, for Sir F. Gowland Hopkins.

The Director of the Pasteur Institute, Paris, for Louis

Pasteur.

Messrs. Macmillan and Co., Ltd., for Thomas Huxley (from
Memoirs of Thomas Huxley, by M. Foster).

Messrs. Allen and Unwin, Ltd., for Gregor Mendel (from
Life of Mendel, by Hugo litis).

Picture Post, for Claude Bernard.

Harper's Magazine, for Charles Darwin.

Martha Marquardt, for Paul Ehrlich (from her Paul Ehrlich,
published by Heinemann).

The editor. The Journal of Pathology, for Theobald Smith.

Mrs. W. B. Cannon, for Walter B. Cannon.

Messrs. J. Russell and Sons, for Sir Henry Dale and Sir
Howard Florey.

Topical Press, for Sir Alexander Fleming.

Lotte Meitner-Graf, for Max Planck.

178

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