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g>tufip fa Scientific 










A.D. 1806 




/ T V HIS attempt to analyze the method em- 
* ployed in the biological sciences arose 
from the belief that the direct study of scientific 
method, as it is illustrated by the works of the 
accepted masters, is worthy of far more careful 
attention than is usually accorded to it. As a 
rule, scientific men are so deeply engrossed in 
their investigations that they rarely undertake 
to discuss method. The logical processes in- 
volved and the nature of the difficulties met 
w r ith in scientific investigation are the same as 
in the practical affairs of life. The fundamental 
processes of reasoning are the same everywhere ; 
and it cannot but be helpful to study those pro- 
cesses as they are actually applied by master 
minds in fields where precision of method is 
peculiarly essential. Even though there may 
be grave question concerning the practical value 
of the study of formal logic, there can be no 

viii PREFACE. 

question concerning the importance of attention 
to the best practice in matters of reasoning. 

Some of the reasons which induced me to 
select Darwin's works as a basis for an analysis 
of scientific method were: (i) the desire to 
confine the discussion to the writings of a single 
author, in order to concentrate the reader's at- 
tention upon a model; (2) the fact that his 
works cover a wide range of subjects, and can 
be read and understood by those who have had 
only a moderate amount of scientific training; 
and (3) above all, the fact that Darwin's inves- 
tigations, and the reasoning based upon them, 
have furnished the biological sciences with their 
dominant principles. 

To facilitate the study of his works from the 
point of view of method, references have been, 
added to nearly all the examples drawn from 
them. A few examples have been mentioned 
or briefly discussed several times, and this may 
detract slightly from the freshness of some parts ; 
but a partial compensation may be found in the 
fact that the repetition of the same example, 
under different divisions of the subject, will 
emphasize more strongly the complex inter- 


dependence of the various logical processes. In 
several instances, particularly those of radicles, 
climbing plants, and electric organs, the discus- 
sions have been carried into considerable detail: 
this has been done for the purpose of show- 
ing what an actual course of investigation and 
reasoning is like, how results, whether true or 
false, are worked out. 

At the same time, no effort has been made to 
make the treatment of Darwin's method exhaust- 
ive, nor has any formal explanation of the vari- 
ous logical processes been made. Those who 
are likely to read this book are already suffi- 
ciently familiar with the terminology of logic and 
the practice of science to understand it easily; 
and extended explanations would require an ex- 
cursion into the domain of formal logic, which 
is not a part of the purpose of the present 

Some of the most important processes have 
been selected, and Darwin's applications of 
them illustrated, in such a way as to confine 
the whole discussion within the narrowest pos- 
sible limits. It is an easy matter to provoke 
differences of opinion in discussing either the 


nature or the names of the logical processes; 
but as far as it lay in my power I have avoided 
setting my foot on controversial ground. There 
are in the book, no doubt, many errors in 
detail, but it is hoped that no serious ones have 
crept in. 

I wish to thank Professor Francis Darwin of 
Cambridge, England, and President David Starr 
Jordan of Stanford University, both of whom 
made important suggestions, and Professor H. 
B. Lathrop of Stanford University, who care- 
fully revised the manuscript. 























Origin of Species, Sixth Edition, 1872. 

Descent of Man and Selection in Relation to Sex, 1871. 

Variation of Animals and Plants under Domestication, 
Second Edition, 1875. 

Expression of the Emotions in Man and the Lower Ani- 
mals, 1872. 

A Monograph of the Cirripedia, Vol. I., 1851 ; Vol. II., 

The Formation of Vegetable Mould through the Action 
of Earthworms, 1881. 

Naturalist's Voyage around the World, 1860. 

Geological Observations on Volcanic Islands and on 

Parts of South America, Second Edition, 1876. 
Structure and Distribution of Coral Reefs, Third Edition, 

Fertilization of Orchids, Second Edition, 1877. 

Effects of Cross- and Self-Fertilization, 1876. 

Different Forms of Flowers on Plants of the same Species, 


Insectivorous Plants, 1875. 
Climbing Plants, 1875. 
Power of Movement in Plants, by Charles and Francis 

Darwin, 1881. 
Life and Letters of Charles Darwin, by Francis Darwin, 

two vols., 1887. 

A SCIENTIFIC discovery is the outcome of an interesting 
process of evolution in the mind of its author. When we are 
able to detect the germs of thought in which such a discovery 
has originated, and to trace the successive stages of the rea- 
soning by which the crude idea has developed into an epoch- 
making book, we have the materials for reconstructing an 
important chapter of scientific history. PROF. J. W. JUDD, 
Critical Introduction to Bettany's Edition of Darwin's "Structure 
and Distribution of Coral Reefs" 





TT is an opinion not uncommon among educa- 
tors that a definition of education which 
would cover all kinds of training is an impossi- 
bility. Such a definition, as it widens for the 
reception of manual training and the study of 
Greek, kindergarten work and the post-graduate 
course, certainly threatens to become " like a 
circle in the water, which never ceaseth to 
enlarge itself till by broad spreading it dis- 
perse to naught." The difficulty in framing it 
ha's apparently increased in recent years, since 
the old standards of value in education have 
had to struggle for existence with all the other 
college and university studies. The old defini- 
tion, "to lead out and train the mental powers," 
is comprehensive enough for all purposes, for 
it tells neither what the mental powers to be 
trained are, nor how they are to be trained ; 


by the change of a word or two it would apply 
equally well to the art of breaking colts. If 
the definition is stated more in detail, it is 
found to lie entirely in the domain of applied 
logic; and education of the intellect, in the 
only sense in which it can cover the whole 
field, is the process of training the intellect in 
the art of reasoning. 

If there is or ever shall be a common aim in 
all phases of education, it will be based upon 
this common element. However important the 
information may be which is conveyed to the 
student in any department of study, his ability 
to retain it and use it for further acquisition 
depends entirely on the method by which he 
acquired it, and the degree to which he has be- 
come master of that method. The facts neces- 
sary for a new investigation are easily brought 
to hand if the intellect has been trained to 
work independently. One of the most strik- 
ing things in Darwin's Autobiography is the 
relative importance, to be mentioned again 
hereafter, which he assigns, in his analysis 
of his own education, 1 to the accumulation of 
facts and to the development of mental habits. 
Probably few minds ever possessed in a higher 

1 Life and Letters of Charles Darwin, by Francis Darwin, 
Vol. I. pp. 51, 52. 


degree the power to collect and utilize facts. 
He said the real education of his mind began 
on the Beagle voyage. And yet he gave a 
very subordinate place to the vast number of 
facts with which he became acquainted on the 
voyage, and assigned supreme importance to 
the habits of incessant industry and concen- 
trated attention which were developed in him, 
and to the necessity of reasoning in the solution 
of geological problems. 

If the most important and only common ele- 
ment in education is the development of the 
power of reasoning, it may seem strange that 
logic, proudly called the science' of sciences, 
should play so obscure a role that in many 
institutions it is practically ignored, and in 
the rest it is tolerated in a very brief course. 
The two most probable reasons for this are, 
first, the general notion that the human mind 
learns to reason as the human body learns to 
walk, that there is no need of teaching; that 
as training in the latter can only produce a 
Delsartean gait, which for practical purposes is 
little superior to an awkward wabble, so train- 
ing in the art of reasoning is likely to produce 
nothing but over-refinement, which accepts 
indifferently postulates foolish and wise, and 
seeks only to draw out their consequences into 


gossamer threads. The second reason is, that 
the logic usually taught is not the logic of 
common life refined by successful scientific 
experience, but "formal logic," emptied of all 
- ^ contents and divested of all covering. Every 
fool can walk, and, as Darwin truly said, any 
fool can generalize and speculate. But the 
secret of originality, ingenuity, skill to seize 
facts, grasp their significance, and anticipate 
consequences, is not hidden here. Not the 
power to reason, but the power to reason 
quickly and unerringly and doggedly and im- 
partially is the basis of success alike for the 
business man and for the man of science. 

If skilful and accurate reasoning constitutes 
so essential an element of education, and if 
logic, as formally taught, is, for the mass of 
students, so barren of results, it is pertinent 
to inquire what provision for logical training 
is made in the general instruction of colleges 
and universities. In the evolution of the col- 
lege curriculum the individuality of the student 
has finally been recognized and provided for, 
and the dignity of the sciences, as subjects 
conducive to mental discipline, has become an 
accepted fact. The material of education has 
by this been both increased and improved. 
Method has also undergone profound changes. 


The laboratory for science, sources of informa- 
tion for history, inventional work in mathe- 
matics, all bear witness that the student has 
been brought into direct contact with the mate- 
rial by means of which his intellect is to be 
trained. The best laboratory hand-books are 
no longer books of directions, but of sugges- 
tion and question ; these books constitute a 
distinct recognition that the art of reasoning is 
the heart of education, that the true student is 
from first to last a discoverer, and that any 
method which makes the discoveries for him is 

There are, however, two very distinct orders 
of reasoning: the order of discovery, which the 
mind follows as it winds its way among facts, 
adopting tentatively hypotheses which are after- 
wards rejected, and groping along the border 
of the unknown in the pursuit of knowledge; 
and the order of proof or argument, used by 
the investigator in his effort to convince his 
hearer or reader of the truth of his results. 
The order of proof may ignore entirely the 
steps by which the discoveries were made, the 
materials collected, and the conclusions drawn. 
The aim is conviction, and the evidence is 
arranged in the most lucid order to support the 
conclusions established at the end of an inves- 


tigation. It is true that sometimes the order 
of discovery is the best for purposes of proof; 
but unless it happen to be so, it is ignored 
after the investigation is completed. 

Logicians insist that their science is the 
science of proof ; that it does not furnish truth, 
but tests by which to determine whether or not 
a supposed discovery is truth. Books and lec- 
tures are invariably built up on the plan of 
proof. In them the question how a conclusion 
was reached is rarely presented, and when it 
does occur, pains is seldom taken to provide 
for its answer. So far, then, as these ele- 
ments of education are concerned, the student 
is made a recipient. He is struck by the lucid 
arrangement of facts, the majestic sweep of the 
argument, and wonders why the world did not 
sooner get hold of truth that seems so conclu- 
sive to him. In the laboratory, the hand-books" 
tell him what to look for and where to find it ; 
and in the lecture-room the facts are arranged 
and the theoretical explanations are made for 
him. Thus in neither of the two practical 
divisions of the art of reasoning is he allowed 
to follow even the untrained impulses of his 
intellect. The average student knows next to 
nothing of the science of reasoning, and is 
largely prevented from practising the art of 


reasoning either from the standpoint of dis- 
covery or from that of proof. 

This general indictment against the college 
curriculum needs to be hedged in by many 
qualifications; but there are none which seri- 
ously break its force. The graduate student is 
left largely to his own resources, and must do 
his own reasoning or go without any. A few 
of the best laboratory hand -books question and 
suggest to the student, so that he is kept from 
dissipating his energy; but they largely compel 
him to make his own discoveries and develop 
independence. ' A few teachers habitually, and 
many teachers occasionally, compel their stu- 
dents to cast their materials into the order of 
proof or argument in topical reports ; but those 
very reports are, as a rule, the best illustra- 
tion of the utter lack of logical insight on the 
part of students. 

Before applied logic secures general recog- 
nition proportionate to its importance, it will 
have to demonstrate its ability to lay in the 
mind of the student the foundation of accurate 
thinking, to furnish him with analyses of mod- 
els of successful reasoning, and criteria by which 
to detect false reasoning. 

It is strange that while the study of our 
mother tongue and of all the sciences has 


undergone so great a revival, the science of 
reasoning should still be lying in the valley of 
dry bones. Fate may have decreed that its 
revival should be the crowning phase of modern 
progress in educational methods. Slowly but 
very surely these methods are drifting in the di- 
rection of a more extended and a more profound 
recognition of the importance of reasoning. 

When educational practice shall have demon- 
strated the importance of the art of reasoning, 
scientific models of the art, for purposes of logi- 
cal study, will be found to be rare, especially 
those that reveal the order of discovery. The 
scientist, after establishing a conclusion to his 
own satisfaction, is not concerned with telling 
other people how he reached it, but with con- 
vincing them of its truth. For this purpose 
he throws his conclusions and facts into the. 
order best suited to form a compact argument. 
In the vast majority of cases it is impossible to 
follow out the original course of thought by a 
study of the results as they are embodied in a 
book. It would probably be difficult for an 
author himself to trace again the windings of 
his thought. Therefore, while there is a fair 
number of models for the study of argument, 
the writers who habitually take their readers 
so far into their confidence as to tell them by 


what steps they arrived at facts and conclusions, 
are extremely rare. 

Several reasons have led to the following 
study of Darwin's method: first, conviction of 
the supreme practical importance of the direct 
study of scientific method; secondly, the fact 
that logicians and scientific philosophers draw 
their illustrations of scientific method almost 
exclusively from the physical sciences; thirdly, 
while those illustrations are fascinating on 
account of their brilliancy and their approach 
toward mathematical certainty, the biological 
sciences are much better adapted to furnish 
models for the average student, because in the 
nature of their logical difficulties they approach 
more nearly to the experiences of common 
life; fourthly,f Darwin's custom of presenting 
all sides of a case very frequently led him to 
expose the original course of his thought and 
the order of his discoveries so clearly as to 
make the reader almost feel that he and Dar- 
win are making the discovery together. Dar- 
win consciously recognized or unconsciously 
felt that there was considerable power to pro- 
duce conviction in an understanding of the 
particular way in which the truth was first 
reached. He so habitually took the reader 
into his confidence that he will probably always 


remain the clearest model in the biological 
world for the study of applied lo^kT^) 

There are two ways open for the logical 
study of Darwin's works: one in which the 
methods of handling material and the differ- 
ent logical processes would be illustrated by 
examples from different parts of his works; 
and the other in which each of his investiga- 
tions would be studied apart from the rest for 
the purpose of noting the part which induc- 
tion, deduction, analogy, and verification play 
in producing the results. The former was 
chosen, because in that way the best examples 
of each of the logical processes could be 
brought together in the smallest compass, 
while the latter would require an elaborate 
summary of the works themselves before their 
logic could be discussed. No epitome, much 
less selected examples, can be made a substi- 
tute for a logical study of the works them- 
selves; it can at most serve as a guide to 
further study. 



IT is necessary to inquire briefly into Dar- 
win's own views of scientific method. 
He has given us the data for the inquiry, both 
in direct statements and indirectly by his 
opinions of the work and ability of other men. 
In connection with this inquiry must be con- 
sidered the intellectual and moral qualities of 
the man himself, and the external influences 
that bore upon him. 

In some quarters the notion is entertained 
that the scientific method leads infallibly to 
the truth, and that it is something quite dis- 
tinct from the logical method of every-day 
life; and yet there is a general haziness as to 
what the scientific method is. The aim of the 
scientist is truth, but he has no special mental 
faculty with which to discover scientific truth. 
He approaches his problem, equipped with the 
same logical processes that the common man 
uses in arriving at facts that are important to 
his success in life. Neglect in applying those 


processes strictly, in either case, results in 
failure, and fidelity to them is the measure of 
success. There is something more than merely 
a weak analogy between the very small pro- 
portion of successful business men and the 
similarly small proportion of really successful 
creative scientific men. The failures on both 
sides are clue to the same kind of intellectual 
errors. Nor are the principles of the scien- 
tific method less clearly understood by success- 
ful business men than by successful scientific 

Darwin has said that the training which he 
got on the Beagle voyage was the first real ed- 
ucation of his mind. 1 His University course 
at Cambridge had been mechanical. He de- 
clared that the study of Paley's ''Evidences" 
and "Natural Theology " gave him as much, 
delight as did Euclid. 2 And he believed at 
the time, and to the end of his life, that the 
study of these works was the only part of his 
academic course that contributed to the educa- 
tion of his mind. He got no inspiration, and 
very little knowledge, from his medical course 
at Edinburgh ; one of the principal records of 
that course is his opinion that there are no 

1 Life and Letters, Vol. I. pp. 51, 52. 

2 Ibid., p. 41. 


advantages and many disadvantages in lectures 
compared with reading. 1 

He has given in his Autobiography the vari- 
ous special subjects that occupied his attention 
on the Beagle voyage. He attended to Zool- 
ogy, Botany, and Geology. After mentioning 
the others, he said that Geology " was far more 
important, as reasoning here comes into play. 
On first examining a new district, nothing can 
appear more hopeless than the chaos of rocks; 
but by recording the stratification and nature 
of the rocks and fossils at many points, always 
reasoning and predicting what will be found 
elsewhere, light soon begins to dawn on the 
district, and the structure of the whole becomes 
more or less intelligible." 2 It is interesting 
to recall that he finally committed the shooting 
of birds to his servant in order that he might 
devote himself to the geology of the districts 
in which he worked. The zoological and 
botanical materials which he collected were 
largely worked up by other scientists after his 
return. On these subjects he collected a vast 
amount of information, which gave birth to 
his great biological theories, and was indis- 
pensable in the work of his later life. But he 

1 Life and Letters, Vol. I. p. 33. 

2 Ibid., pp. 51, 52. 


did not work this information into a system 
and bend his energies upon it. He devoted 
himself to the solution of .geological problems 
in the field; while the biological problems 
only arose in their early shadowy outlines 
during the voyage, and remained in the form 
of questions till long after his return. Thus 
it came about that from an educational point 
of view his biological work was secondary and 
the geological work pre-eminent. Had his 
life-work ended with the reports of the Beagle 
voyage, he would have been rated as a geol- 
ogist. But after his return he exercised upon 
great biological problems the intellectual 
strength and vigor which had been developed 
by the solution of geological problems in the 
field. " The above various special studies were, 
however, of no importance," he said, "compared 
with the habit of energetic industry and of con- 
centrated attention to whatever I was engaged 
in which I 'then acquired. Everything about 
which I thought or read was made to bear 
directly on what I had seen or was likely to 
see." He had problems constantly before him, 
and the time allowed for their solution was 
always limited by his own movements and 
those of the ship; so that energy and concen- 
tration became habitual in a mind already 


strong by nature. His isolation from other 
scientific men and from books doubtless also 
developed in him the habit of using all the 
facts that presented themselves, and directly 
and indirectly getting at their significance. 
He could not lay his hands on ready-made 
explanations of the facts that came before him, 
and was compelled to explain them himself. 
He said of himself, " I think I am superior to 
the common run of men in noticing things 
which easily escape attention, and in observ- 
ing them carefully. . . . From rny earliest 
youth I have had the strongest desire to under- 
stand or explain whatever I observed, that 
is, to group all facts under some general laws." 1 
These natural traits were of necessity strength- 
ened and developed by their incessant exercise 
on the voyage. 

Another prominent trait in Darwin was the 
accuracy with which he made his observations 
and experiments. " He saved a great deal of 
time through not having to do things twice." 
And he always "wished to learn as much as 
possible from an experiment, so that 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 

1 Life and Letters, Vol. I. p. 83. 



was wonderful." 1 Both his accuracy of obser- 
vation and his grasp of all the facts connected 
with an experiment were doubtless made hab- 
itual on the voyage by the never absent con- 
sciousness that there was only one opportunity 
to do whatever he did. 

During that memorable voyage Darwin's 
education went on, unhampered by laboratory 
hand-books with directions for finding the 
facts, or by professors to do the reasoning for 
him either before or after the facts were found. 
In all his work there was the complex and 
incessant interplay of observation, induction, 
deduction, and verification which constitutes 
the scientific method. The necessity of work- 
ing rapidly, accurately, and thoroughly forced 
upon him by the consciousness that his time 
was limited, and that the work could not be 
done over again, coupled with his native energy 
and independence, accounts for the character 
and quantity of his scientific work. 

The mental traits alluded to were coupled 
with remarkable conscientiousness. 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 

1 Life and Letters, Vol. I. pp. 121, 122. 


with far severer penalties in the scientific than 
in the business world. Scientific results are 
used as foundations for further investigations, 
and for this reason they are tested again and 
again; and if any man's work is unreliable 
it is done over by some one else, who reaps 
the permanent credit. But the temptations to 
make statements too broad, to neglect objec- 
tions, to smooth over difficulties superficially, 
are almost infinite. There is apparent through- 
out all of Darwin's work much more than the 
intellectual uprightness that is due to a belief 
in " reward and punishment. " The very grain of 
his scientific character was conscientiousness. 

His educational history, his thoroughness, his 
scientific honesty, his logical power, his power 
of minute observation and broad generaliza- 
tion, the greatness of the problems with which 
he dealt, and the profound influence of his 
views upon the thought of the world, all con- 
spire to make him a model in the study of 
scientific method. Some of his views have 
been rejected, and many may be profoundly 
modified by more accurate knowledge, but 
these things will in no way affect the value 
of Darwin as a type of what education should 
accomplish, and how it must accomplish it. 

Darwin appreciated the humblest scientific 


work, and listened with deference to the sug- 
gestions of others. He never dealt out primi- 
tive justice to his opponents on the principle 
of an eye for an eye and a tooth for a tooth. 
He is morally famous for the forbearance that 
he exercised toward those who attacked him. 
This fame is heightened by the fact that he 
was an acute judge of mental quality. His 
investigations made it necessary for him to 
collect information from all sorts of sources, 
not only at first hand, from Nature herself, 
but at second hand, from many kinds of books, 
made by many kinds of men. He has com- 
plained that it was exceedingly difficult to find 
out what and whom to trust. 1 But his criti- 
cisms of certain kinds of work show how 
definite were his standards of value in measur- 
ing scientific results. 

Perhaps the most savage things Darwin ever 
wrote are contained in letters to Hugh Strick- 
land, and relate to the nomenclature of sys- 
tematic zoology and botany. 2 He expressed 
freely his contempt for describers of species 
who think the honor consists in having one's 
name appended to that of a newly described 
species, and whose work is generally so inac- 

1 Life and Letters, Vol. II. p. 75. 

2 Ibid., Vol. I. pp. 334, 33 8 > 344- 


curate or imperfect, or both, as to be practi- 
cally worthless for any of the higher purposes 
of science. Nor was he satisfied with mere 
details even when they were accurate. In his 
reminiscences of Robert Brown he said that 
Brown seemed to him "to be chiefly remark- 
able for the minuteness of his observations, 
and their perfect accuracy." 1 Darwin often 
took breakfast with Brown, and on those occa- 
sions the latter, according to Darwin, "poured 
forth a rich treasure of curious observations 
and acute remarks; but they almost always 
related to minute points, and he never with 
me discussed large or general questions of 

He has given us an interesting example of 
his opinion of the opposite tendency toward 
speculation, to the neglect of facts. During 
his career as a medical student he admired 
greatly his grandfather Erasmus Darwin's 
" Zoonotnia." 2 "But on reading it a second 
time," he said, "after an interval of ten or 
fifteen years, I was much disappointed, the 
proportion of speculation being so large to the 
facts given." These criticisms of the work 
and methods of others are in perfect accord 

1 Life and Letters, Vol. I. pp. 57, 6b. 


with his own practice. He combined in him- 
self the qualities of both Brown and his own 
grandfather. His works are a series of models 
of the scientific method, because of the rare 
and happy combination of minute and accurate 
observation and daring speculation followed by 
ruthless testing and pruning of his hypotheses. 
He thought it worth while to notice and pene- 
trate into the meaning of the most insignifi- 
cant fact, and was capable of sweeping the 
whole earth for evidence in support of his 
largest theories. He could take the time to 
count twenty thousand seeds of Ly thrum sali- 
caria; 1 and his prophetic philosophical eye 
led him to exclaim, "What a science Natural 
History will be when we are in our graves, 
when all the laws of change are thought one of 
the most important parts of Natural History ! ". 2 
At various times and under various circum- 
stances Darwin expressed fragmentary opinions 
concerning what constitutes scientific method, 
but never tried to make a complete statement of 
it. His notion of what the method is, is shown 
mostly by what he said concerning "deduc- 
tion." For instance, concerning Bastian's 
work, he said, in a letter to Wallace, "I am 

1 Different Forms of Flowers, etc., p. 189. 

2 Life and Letters, Vol. I. p. 439. 


not convinced, partly, I think, owing to the 
deductive cast of much of his reasoning; and 
I know not why, but I never feel convinced by 
deduction, even in the case of H. Spencer's 
writings"; 1 and in a letter to John Fiske, "I 
find that my mind is so fixed by the inductive 
method, that I cannot appreciate deductive 
reasoning; I must begin with a good body of 
facts, and not from principle (in which I always 
suspect some fallacy), and then as much deduc- 
tion as you please." 2 

Now deduction means, in one of its* senses, 
reasoning from the general to the particular, 
from a law, principle, or general fact to a 
particular fact. But in the above quotations 
Darwin meant by deduction, and the deductive 
method, reasoning from postulates the truth of 
which is accepted as beyond dispute. Induc- 
tion, as a logical process, means reasoning 
from particular to general, from facts to laws 
or principles. But induction, or inductive 
method, when used in a sense synonymous 
with scientific method, includes all the logical 
processes, induction, deduction, analogy, veri- 
fication, every way in which the intellect 
passes from fact to fact. This is widely differ- 
ent from what Bacon originally meant by induc- 

1 Life and Letters, Vol. II. p. 346. 2 Ibid., p. 371. 


tive method; but practically no scientific man 
has ever followed Bacon's method. 

The inductive method, as illustrated by Dar- 
win's own work, and as understood by all who 
think clearly on the subject, consists in the 
formation of an hypothesis from the facts by 
induction at the earliest possible moment in 
an investigation, deductive application of the 
hypothesis to known facts, and in the search 
for others that ought to exist if it is true, until 
it proves itself imperfect. By the help of the 
new facts the hypothesis is improved (by in- 
duction) and again applied, until by successive 
approximations it reaches the truth. So that 
in the so-called inductive or scientific method 
deduction is far more extensively used than 
induction. But to say that one of the processes 
is more important than the other would be like 
saying that the female element, for example, 
is more important for reproduction than the 
male element. It is interesting to note in 
this connection that John Stuart Mill, the 
modern logician who has stood out as the 
champion of the inductive method, has incon- 
sistently described the combination "hypoth- 
esis, deduction, and verification," as the 
deductive method. 1 

1 Mill, System of Logic, People's Edition, p. 304. 


The scientific or inductive method as under- 
stood and practised by Darwin begins and 
ends with facts. It takes nothing for granted 
that relates to the matter under investigation, 
and assumes as true only such things as the 
law of causation and the validity of the reason- 
ing processes; while the deductive method, as 
understood by him, starts from principles 
whose truth is not questioned. Regarded 
simply as a logical process, however, deduc- 
tion is equally valid whether the premises are 
assumed to be true or admitted to be hypo- 

The ideal attitude of the scientific mind is 
beautifully described in Darwin's own words 
concerning himself: "I have steadily endeav- 
ored to keep my mind free so as to give up any 
hypothesis, however much beloved, (and I can- 
not resist forming one on every subject,) as 
soon as facts are shown to be opposed to it. 
Indeed, I have had no choice but to act in this 
manner, for, with the exception of the Coral 
Reefs, I cannot remember a single first -formed 
hypothesis which had not after a time to be 
given up or greatly modified. This has natu- 
rally led me to distrust greatly deductive 
reasoning in the mixed sciences." 1 *j> ^ 

1 Life and Letters, Vol. I. p. 83. 


It has been said that deduction, regarded 
merely as a logical process, is equally valid 
whether the premises are assumed to be true 
or are admitted to be hypothetical. If the 
premises are true, the conclusion must be true. 
What brought the old deductive process into 
so general disrepute was not its inadequacy, 
but the using as premises in the process prin- 
ciples that were held to be beyond dispute. 
To this end the a priori reasoner went farther 
and farther back in his philosophical repertory, 
until he reached principles or axioms that he 
felt could not be denied. Then by an irre- 
sistible deductive swoop he reached conclu- 
sions that must likewise be true. In such 
philosophy there is little need of verification. 

In science, and therefore also in the reason- 
ing of practical life, the great question always 
is whether the premises are true, or partly 
true, or false. The old notion was that deduc- 
tion led to certainty, and induction did not. 
But in the scientific method the object is not 
merely to deduce consequences from laws or 
principles, but to establish the truth or falsity 
of those laws or principles themselves. Hence 
there is an incessant interplay of induction 
and deduction. Darwin's distrust of deductive 
reasoning was due to his fear of the premises. 


But he said that all his hypotheses had to 
be abandoned or modified, and they were the 
conclusions of inductions; so that inductive 
reasoning by itself is also absolutely worth- 
less. The truth is, Darwin trusted nothing. 
Induction furnished him hypotheses, and de- 
duction interpreted known facts and led to new 
ones under those hypotheses; but verification 
of his deductions was as indispensable to him 
as sunshine to a plant. 

Darwin himself said, "Any fool can gen- 
eralize and speculate." There has always been 
an over-abundance of reasoning, both inductive 
and deductive. Untrammeled induction is 
largely responsible for the wild and worthless 
beliefs that have burdened the world; and 
untrammeled deduction is as largely respon- 
sible for the dogmatic dry-rot that has pre- 
vented progress in human discovery and beliefs. 
Darwin was one of the most powerful deductive 
reasoners that ever lived; and he was perfectly 
fearless in making inductions, for, as he said 
himself, he made an hypothesis on every sub- 
ject. But the illustrations of the various logi- 
cal processes that have been drawn from his 
works show that even he with his almost 
superhuman powers of observation, his innate 
desire to refer every fact to a general law, his 


rare ability to reason out the consequences of 
his hypotheses, and his unbending determina- 
tion to test his reasoning by ruthless investiga- 
tion made important inductions, deductions, 
and analogies that were not true, and failed to 
make deductions that should have thrust them- 
selves upon him. He rarely, however, fell 
into the old and vicious error of thinking that 
reasoning of any kind is final proof. 

He built up a large inductive structure in 
pangenesis only to see it rejected; he went 
wrong in his deduction concerning the relation 
between high degree of specialization and the 
chances in favor of preservation of a species; 
and was prevented by a bad analogy from 
investigating the effects of cross- and self-fer- 
tilization in plants until the subject was thrust 
upon him by empirical observation. He was 
as productive of hypotheses as Nature is of liv- 
ing things, and, like her, he subjected them 
all to the principle of natural selection. His 
mind was so fertile in guesses and so quick in 
testing them that he called much of his work 
"fool's experiments. " But in this way nothing 
escaped him. 

In recent years there has been made a for- 
mal statement of the reasons why fertility in 
hypotheses should be cultivated, and how they 


should be used. 1 The principle of multiple 
hypotheses is urged, because in the sciences 
it is not generally possible to hit at once upon 
a cause from a study of the facts. As many 
hypotheses as possible should be invented to 
explain the facts under investigation, and as 
fast as possible, as new light comes, other 
hypotheses should be added, in order that the 
mind may, as far as possible, put itself in 
possession of all the possible causes of the 
phenomena. By keeping them all constantly 
before it, it can consider every fact from many 
points of view; and each hypothesis will fur- 
nish its own clews to further evidence. In 
this way, also, the mind can more easily keep 
itself in a judicial attitude. With the increase 
of knowledge some of the hypotheses are shown 
to be inadequate, and by the process of exclu- 
sion their number is reduced until the inves- 
tigation ends in the establishment of the true 
theory of the cause of the facts under inves- 

In actual practice a good many difficulties 
are connected with this method of using 
hypotheses. Among a number of hypotheses 
one will almost invariably have a somewhat 
higher degree of probability than the rest; the 

1 T. C. Chamberlain, in Science, Feb. 7, 1890. 


mind, working along the lines of least resist- 
ance, follows the clews it offers to the neglect 
of the other hypotheses. The more usual prac- 
tice is typified in Darwin's method. He made 
an hypothesis at the earliest possible moment, 
and began to work with it. With increasing 
knowledge it was modified, or rejected and 
replaced by a more likely one. So that there 
was a succession of hypotheses or of improve- 
ments of the original one. 

The method of multiple hypotheses is com- 
mon enough, if it be made to include not only 
the instances in which the same individual 
entertains several hypotheses, but also those 
in which different hypotheses are entertained 
by different people. There are few questions 
on which there are not several opinions; and 
one approaching the subject impartially con- 
siders them together in order to adopt the most 
likely one. The process of exclusion works 
admirably, and the result amounts to demon- 
stration when all the possible hypotheses are 
known, and one needs only to show that one 
of them agrees with the facts and the others 
do not. Newton, in establishing the law of 
gravitation, showed that the orbits and veloci- 
ties of the planets would be what they are if 
the attractive force resided at the centre of the 


system or in the sun, and acted with a force 
varying inversely as the square of the dis- 
tance; and that they could not be what they 
are if the force were located anywhere except 
at the centre. In this instance Newton was 
able to exclude mathematically every theory 
except the true one; and the demonstration 
was made complete by the positive proof that 
the facts accorded with the one hypothesis and 
were at variance with every other. 

Darwin used the principle of exclusion in 
one of his early scientific efforts. There were 
two hypotheses to account for the existence of 
the great terraces called benches, or parallel 
roads, of Glen Roy, in Scotland. It was evi- 
dent enough that they had been formed by the 
action of water; and they must either have 
been formed by the sea, in which case the 
uppermost, for example, must have been after- 
wards elevated more than one thousand feet; 
or they must have been the ancient shores of 
a lake formed by the blocking up of the 
open side of the now empty lake bed. Darwin 
studied the region, and concluded that the 
benches were of marine origin. He could not 
conceive them to be due to barriers of rock or 
detritus. He was then fresh from his studies 
on the geology of South America. On the 


coasts of that continent he had grown familiar 
with the immense scale on which elevations 
take place, and had many opportunities to 
study marine sand and gravel formations that 
are now hundreds of feet above sea level. It 
was therefore as easy for him to conceive a 
marine origin of the terraces of Glen Roy as 
it was difficult for him to believe that they 
were the old shores of an elevated lake that 
had been blocked in. He adopted the method 
of exclusion, proved the one hypothesis prob- 
able and the other improbable. 

But this instance of the principle of exclu- 
sion illustrates well the danger to which the 
investigator is exposed in its use. In geology, 
zoology, etc., in what Darwin calls the mixed 
sciences, one can rarely know whether all 
the possible hypotheses are known. Newton 
could make a rigid demonstration, not simply 
because he could treat his problem mathe- 
matically, but because he was able to treat 
all the possible hypotheses. When the gla- 
cial theory was introduced into the geological 
world the ancient terraces high above sea 
level in the colder temperate zone were ac- 
counted for. Then it was plain that the ter- 
races of Glen Roy had been the shores, not 
of the sea, nor of a lake dammed up by rock 


or detritus, but of a lake dammed up by gla- 
cial ice. 

Darwin was ashamed of his arguments and 
conclusions about Glen Roy. "My error," he 
said, "has been a good lesson to me never to 
trust in science to the principle of exclusion." l 
But it is inevitable that apparently definite 
views should receive just such shocks upon 
the introduction of a great new principle in a 
science. The facts that find their explanation 
under the single newly discovered cause are 
necessarily referred, before the advent of the 
new hypothesis, to very various and unrelated 

On the question of the origin of species 
there were really two hypotheses, creation and 
descent, when Darwin took hold of it; and he 
adopted the process of exclusion in treating 
them. The evidence was all in favor of descent 
by natural selection and opposed to creation. 
But he was himself emphatic in the declaration 
that the origin of species by natural selec- 
tion was not demonstrated. Belief in it must 
be based on general considerations, that 
natural selection is an actually existing cause, 
and that it explains a host of facts and brings 
them under one point of view. One hypothesis 

1 Life and Letters, Vol. I. p. 57. 


was excluded and the other adopted. And the 
one that was accepted was based, not on direct 
proof, but on one of the most magnificent series 
of deductions that the world has ever seen. 

The further discussion of this subject will 
be deferred for the present. In the following 
chapters Darwin's method of treating the prob- 
lems that presented themselves to his mind 
will be analyzed in some detail, and the clos- 
ing chapter will deal with the logical history 
of the principle of natural selection. 



THE starting points of many of Darwin's 
researches were furnished him by other 
intelligent men. In many cases these men not 
only were in possession of the facts, but had 
hit upon their true explanation. With the 
facts thrust upon them, with enough reasoning 
ability to pursue them, they gave away their 
heritage, luckily to one who knew its value. 
In his frank but modest analysis of his own 
mental qualities he said of himself, as already 
quoted, " I think I am superior to the com- 
mon run of men in noticing things which 
easily escape attention, and in observing them 
carefully. . . . From my earliest youth I have 
had the strongest desire to understand or ex- 
plain whatever I observed, . . . that is, to group 
all facts under some general laws." 1 There 
can be no doubt that his great interest in 
apparently little things, and his efforts to make 

1 Life and Letters, Vol. I. p. 83. 


the most of them, were due to his conviction 
that important things were hidden behind them, 
that they were illustrations of general laws. 

Lawson, Vice-Governor of the Galapagos 
Islands at the time of Darwin's visit, knew 
that the tortoises of the different islands dif- 
fered from one another, and even declared to 
Darwin that he could tell from which island 
any tortoise came. 1 He had the time, and 
the material lay at his feet ; but he left it for 
Darwin to make the Galapagos Islands famous 
as illustrations of the local variations of 
species. Darwin himself had to have the evi- 
dence thrust upon him from several directions 
before he grasped its significance, but his 
greater appreciation of the nature and value 
of the facts made him their master. 

After his return from the Beagle voyage, 
Mr. Wedgwood of Maer Hall suggested to 
him that the apparent sinking of superficial 
bodies, ashes, marl, cinders, etc., into the 
earth is due to the action of earth-worms. 2 
Both the facts and the theory were ready at 
hand. To the one man they were probably 
interesting as intellectual playthings; to the 
other they became the starting point for a 

1 Naturalist's Voyage around the World, pp. 393-398. 

2 The Formation of Vegetable Mould, etc., p. 3. 


long investigation. Darwin read one of his 
first papers, " On the Formation of Vegetable 
Mould," before the Geological Society of Lon- 
don, November 1, 1837; and on the same ap- 
parently insignificant subject he published the 
last book of his life. 

While collecting in the Chonos Archipelago, 
Southern Chile, he found numbers of an insig- 
nificant little cirriped, none more than one 
tenth of an inch long, embedded in the shell of 
Concholepas peruviana. 1 The zoological mate- 
rial of his trip was turned over to specialists 
for description, he furnishing the field notes 
and editing the publications. Much zoological 
information was thus given to the world, but 
none of all that material ever served as a start- 
ing point for a great investigation. The little 
abnormal cirriped was left to Darwin himself; 
probably because it was too small an affair to 
be taken charge of by others. In his hands it 
became the germ of a monograph on the Cirri- 
pedia, which is still the classical literature 
of the group. To determine its position he 
studied the structure of as many genera as 
possible. Dr. J. E. Gray, who had already 
collected a large amount of material for a mon- 

1 A Monograph of the Cirripedia, Vol. I., Preface, p. 5 ; 
Vol. II. pp. 566-586. 



ograph of the group, turned it over to Darwin. 
Gray did many things, but none well enough 
to make what he wrote indispensable in the 
study of any subject; he will be remembered 
chiefly as a keeper of the zoological depart- 
ment of the British Museum, and as a bitter 
opponent of Darwin's theory of descent, while 
the latter' s monograph heads the list of cirri- 
ped literature. 

Boitard and Corbie" merely made the obser- 
vation that, when they crossed certain breeds 
of pigeons, birds colored like the Columba 
livia, or common dove-cot, were almost inva- 
riably produced. 1 It drew Darwin's attention 
and led to numerous experiments on rever- 
sion due to crossing. Certainly some, perhaps 
many, scientific men had known that the species 
of sundew (Droserd) catch insects. Darwin 
himself had heard as much. Exhausted by 
his long labors on the Origin of Species, he 
was resting near Hartfield during the summer 
.of 1860, and "was surprised by finding how 
large a number of insects were caught by the 
leaves of the common sundew (Drosera rotundi- 
folid) on a heath in Sussex." 2 The right mind 

1 The Variation of Animals and Plants under Domestica- 
tion, Vol. II. p. 14. 

2 Life and Letters, Vol. I. p. 77. 


had been impressed, and away the giant intel- 
lect started on another long and weary, but suc- 
cessful, search after truth. Mr. W. Marshall 
knew that in the mountains of Cumberland 
many insects adhered to the leaves of Pin- 
guicula; he told Darwin, and Darwin told the 
world. 1 Mr. Holland's statement that water 
insects are often found imprisoned in the 
bladders of Utricularia is interesting, chiefly 
because it led Darwin to investigate the 
genus. 2 

The most fertile suggestions, however, came 
to him from the facts brought out by his own 
work. He did not record the hundredth part 
of the tentative notions that entered his mind; 
but many of the most important and lasting 
had their rise in what to most other men is the 
refuse heap of curious and exceptional little 
facts. Perhaps one of the noblest lessons he 
left to the world is this, which to him 
amounted to a profound, almost religious con- 
viction, that every fact in nature, no matter 
how insignificant, every stripe of color, every 
tint of flowers, the length of an orchid's nec- 
tary, unusual height in a plant, all the infinite 
variety of apparently insignificant things, is 

1 Insectivorous Plants, p. 369. 

2 Ibid., p. 395. 


full of significance. For him it was a histor- 
ical record, the revelation of a cause, the lurk- 
ing place of a principle. 

A typical example of his treatment of little 
exceptional facts is that of "Hero, "the un- 
usual plant in one of the later generations of 
self -fertilized plants of Ipomoea purpurea.^ It 
was a little -larger than the crossed seedlings 
of the same generation, and the first exception 
that had arisen, in his many experiments, to 
the rule that the crossed are superior to the 
self-fertilized seedlings in size and vigor. It 
was a little thing, even for an exception, and 
had occurred only after a very long series had 
established the rule. It was very fit to suffer 
the common fate of exceptions, and to be 
deliberately choked for the benefit of the rule 
to which it was so inconveniently related. By 
other hands it would probably have been re- 
corded and then ignored. Darwin made it the 
parent of a whole race of exceptions. He 
found "Hero" to be exceptional, not only in 
being unusually tall, but in its being highly 
self -fertile, in its great powers of growth, and in 
its descendants which were crossed having no 
advantage over its self-fertilized descendants. 

His aim, as soon as he hit upon a line of 
1 Effects of Cross- and Self-Fertilization, p. 60. 


investigation, was to reach as quickly as pos- 
sible a crucial test or a crucial observation 
that would enable him to determine positively 
whether or not his beliefs were justified. As 
soon as the idea of descent of species took 
definite shape in his mind, he determined, 
after deliberation, to take up the study of 
domestic pigeons. 1 He selected these because 
the variations were more numerous and plainer, 
more of them had arisen in the historical period 
than is usual with animal groups, the material 
was abundant and easily accessible, etc. He 
cnose for his investigation the conditions most 
favorable to success. 

When he discovered that insects are caught 
in large numbers by the common sundew, he 
gathered a number of plants, counted the leaves 
and the number that had caught insects ; and 
compared the results with the accidental de- 
struction of insects by the viscous buds of the 
horse-chestnut, etc. 2 Similar results were pro- 
duced by somewhat similar means; but by the 
comparison he secured preliminary evidence 
that the leaves of the sundew, unlike the buds 
of the horse-chestnut, were excellently adapted 

1 Origin of Species, p. 15; Variation of Animals and 
Plants under Domestication, Vol. I. p. 137. 

2 Insectivorous Plants, pp. 1-3, 63-76. 


for catching insects. To him adaptation for 
insect catching meant that this habit was 
advantageous to the plant; and that it must 
derive nourishment from the captured insects. 
He knew what elements plants required for 
nourishment, and immediately set about mak- 
ing another crucial test. When led to believe 
that the leaves absorbed nutritious matter from 
the insects, he made a crucial experiment by 
immersing numbers of the leaves in nitro- 
genous and non-nitrogenous fluidsW the same 
specific gravity to find whether they would 
act differently in the two cases, taking care 
that the two sets of conditions should be the 
same except in the presence of nitrogenous 
matter in the one and its absence in the other. 
The test confirmed his belief, and is an 
example of the most rigid type of reasoning 
and experiment, a combination of positive 
and negative evidence which Mill called the 
Method of Difference. Darwin's clear notion 
of what constitutes good evidence led him to 
seek demonstrative evidence by the shortest 
way. In the case just described he secured it 
at once, and might have rested content with 
having established the principle; but as soon 
as he found that the nitrogenous fluid alone 
excited energetic movements " it was obvious 


that here was a fine new field for investiga- 
tion." His crucial tests only gave him confi- 
dence that there was more beyond; then he 
began the long series of observations and 
experiments which resulted in the charming 
volume on "Insectivorous Plants." 

It is told elsewhere how he was deterred by 
theoretical considerations from experimenting 
on the effects of cross- and self-fertilization, 
and how the expectation of early results was 
fairly thrust upon him by the difference in size 
and vigor between crossed and self-fertilized 
seedlings. 1 

When once his attention was fixed, he made 
a preliminary experiment on two plants, with 
the effects of cross- and self-fertilization as the 
principal object of investigation. The results 
corroborated his previous observations, and 
he was in possession of the principle. Such 
simple preliminary experiments are interest- 
ing, since, if they do not establish a principle 
fully, they raise up for it a higher degree of 
probability than any succeeding experiments, 
and make it possible to work deductively with 
considerable confidence. 

The introduction of the principle of con- 
tinuity into general scientific thinking has 

1 Effects of Cross- and Self-Fertilization, pp. 6-8. 


made it a normal intellectual process to look 
upon exceptional and isolated phenomena as 
merely extreme instances of much larger 
groups. One of the marked characteristics of 
Darwin's work is that he selected such extreme 
instances, and sought to connect them with the 
more common facts to which they were related, 
by proving, or at least suggesting, their deri- 
vation from the latter. Wherever it was pos- 
sible in his experiments, he varied the amount 
of a cause in order to note the proportionate 
variation in the amount of the effect; and 
where he had to depend upon observation alone, 
he made strenuous efforts to connect extreme 
instances by gradations of character. 

Thus, he and his son Francis, by continuous 
attention to the sleeping movements of plants, 
were able to show that it is not true, as is gen- 
erally supposed, that the leaves move only in the 
evening when going to sleep, and in the morn- 
ing when awaking ; for they found no exception 
to the rule that leaves which sleep continue to 
move during the whole twenty-four hours, only 
moving more quickly when going to sleep and 
awaking than at other times. 1 They were able 
to show that sleeping movements are only 
liighly specialized and exaggerated modifica- 

1 Power of Movement in Plants, p. 403. 


tions of the universal movement of circumnu- 
tation. In his experiments on insectivorous 
plants with phosphate of ammonia he varied 
the proportion of the latter to determine how 
small an amount would affect the tentacles of 
Drosera. 1 He found that excessively minute 
quantities of the latter would produce reac- 
tion. His results were so astonishing that in 
1873 he doubted his own experiments of 1872, 
and in 1874 he again thought that some mis- 
take must have been made, and again repeated 
the experiments, but always with the same 
results. He discussed these remarkable facts 
at some length, tried to make them more cred- 
ible by comparing them with similar cases that 
are equally astonishing but are known to be 
true; and expressed the hope that his experi- 
ments would be repeated, at the same time 
laying down the conditions of success. 

While studying the power of circumnutation 
in plants the Darwins accidentally left some 
of their specimens in several cases exposed to 
oblique light. Before they "knew how greatly 
ordinary circumnutation was modified by a 
lateral light, some seedling oats, with rather 
old and therefore not highly sensitive cotyle- 
dons, were placed in front of a northwest win- 

1 Insectivorous Plants, pp. 154-173., 


dow, towards which they bent all day in a 
strongly zigzag course. On the following day 
they continued to bend in the same direction, 
but zigzagged much less. The sky, however, 
became, between 12 140 and 2 135 P.M., overcast 
with extraordinarily dark thunder-clouds, and 
it was interesting to note how plainly the 
cotyledons circumnutated during this inter- 
val." 1 These observations they considered of 
some value from their having made them while 
they were not attending to heliotropism ; and 
they were led by them "to experiment on 
several kinds of seedlings, by exposing them 
to a dim lateral light, so as to observe the gra- 
dations between ordinary circumnutation and 
heliotropism." An accidental observation led 
to variations in the experiments, which re- 
sulted in demonstrating continuity between two 
apparently distinct classes of movements. 

In some of his remarkable studies on grada- 
tions of characters, where it was impossible to 
make experiments, he sought out and observed 
Nature's own variations. Perhaps the most 
striking instance of the study of gradations of 
character is that connected with the "ocellus " 
on the tail coverts of the peacock. 2 This 

1 Power of Movement in Plants, p. 421. 

2 Descent of Man, Vol. II. pp. 132-145 


feather-mark was properly considered a serious 
difficulty to Darwin's theory because of its 
remarkable character. But with consummate 
ingenuity he undertook to connect it by a 
series of less and less remarkable markings 
with the ordinary feather-markings of the 
group to which the peacock belongs. It is 
impossible to exaggerate the importance of 
studying phenomena in their quantitative and 
qualitative variations, for on it depends the 
establishment of continuity between phenom- 
ena apparently widely separated, and it fre- 
quently leads to results that can be reached in 
no other way. 



THE theories with which Darwin dealt were 
so general, and the facts that had to be 
handled as evidence were so vast in number, 
that probably no man was ever exposed to 
greater temptation to collect his evidence pro- 
miscuously from all quarters, picking up in 
each field what was already known, and sup- 
plementing it by a few test observations. But 
he never contented himself with sketching 
theories and adorning them with dashes of 

He made himself invincible by the exhaust- 
iveness with which he determined the quality 
of his evidence. The great confidence which \ 
scientific men have had in him has been due | 
to the fact that he did not leave it to them to . , 
test the theories which he presented. He con- 
vinced the world of the truth of a doctrine 
which others had striven in vain for fifty years 
to establish. To my mind one of the chief 


characteristic differences between his work 
and that of Lamarck and others, apart from 
differences in the explanations offered, is its 
superb exhaustiveness. It is as impossible 
now to take the ideas of descent and of natural 
selection out of the world as to take a star out 
of the sky. The firm establishment of these 
ideas was due to the quality and quantity of 
Darwin's work, and both of these were deter- 
mined by the same exhaustiveness in method. 

When he started out to describe the single 
little abnormal cirriped from the west coast 
of South America, he was characteristically 
led, as he said, for the sake of comparison, to 
examine the internal parts of as many genera 
as he could procure. This untamed determina- 
tion to find out all there was to know about 
what he was describing was associated with a 
fine contempt for the kind of work that merely 
describes new things without showing all their 
connections. One of the greatest and most 
constant obstacles to his progress was that this 
intellectual quality was so rare or so little cul- 
tivated in other naturalists; so much of the 
scientific material with which he had to deal 
was so superficially or carelessly worked out 
that he never knew what to trust. 

Among the best examples of this spirit of 


exhaustiveness is his study of pigeons. 1 As 
usual, he knew clearly what he was after, and 
this gave him the power of selecting judiciously 
the lines along which to make investigations 
and of using to the best advantage the materials 
he worked on. In his remarks on the search 
for the cause of the modification of species, he 
said, " Believing that it is always best to study 
some special group, I have, after deliberation, 
taken up domestic pigeons." With other ends 
in view, pigeons might be studied in different 
ways. But remembering his purpose, his work 
on pigeons is a model of exhaustiveness as well 
as of reasoning. He not only studied the vari- 
ation of breeds, but sought its explanation by 
a minute study of individual differences. He 
considered the skeleton as well as the feathers, 
and gathered facts and specimens from all over 
the world. 

What is true of his study of pigeons is true 
of his work on orchids. The adaptation of 
flowers for cross-fertilization had interested him 
for many years, and he had collected a large 
mass of observations; but he was true to his 
instinct : " It seemed to me a better plan to 
work out one group of plants as carefully as I 

1 Variation of Animals and Plants under Domestication, 
Chaps. V. and VI., pp. 137-235. 


could rather than publish many miscellaneous 
and imperfect observations." Orchids furnished 
an extreme case ; and his work on them is fas- 
cinating from the nature of the subject, the end 
aimed at, and the ingenuity of the reasoning 
employed. He showed "how admirably these 
plants are constructed so as to permit of, or to 
favor, or to necessitate cross-fertilization " ; but 
the way in which he did it is as admirable from 
a logical point of view as the flowers them- 
selves are in their peculiar adaptation. By 
thus selecting judiciously the most extreme 
special cases for exhaustive examination, he 
threw the strongest light on all the collateral 
evidence, and made it easy for him to under 
stand its significance. On the shoulders of 
such work his theories sat firmly, and it made 
it easy for those who came after him to work 
out the classes of facts which he was not able 
to exhaust. 

In each of the many special studies which he 
carried on there are many models of method in 
the pursuit of details. The following case is 
especially interesting because it illustrates both 
the habitual care of the authors in their experi- 
ments on the movements of plants and the ex- 
treme liability to error that results from a 
wrong start. Since the book on the " Power of 


Movement in Plants " was written, it has been 
shown that the conclusion of the authors that 
"an object which yields with the greatest ease 
will deflect a radicle " is wrong. The whole 
superstructure of reasoning which resulted in 
the notion that the tips of radicles are sensitive 
to contact was therefore built on sand. The 
experiments and reasoning will be discussed 
from the point of view of the authors at the 
time they were made, and afterwards attention 
will be called to the corrections that have since 
been made by others. In their work on the 
movements of radicles, Charles and Francis 
Darwin found that "an object which yields 
with the greatest ease will deflect a radicle." 
Extremely thin tin-foil on soft sand was not at 
all impressed, and deflected the root at right 
angles. Hence, they reasoned, the cause "of 
the deflection could not be mechanical contact. 
A conceivable hypothesis was that " the gentlest 
pressure might arrest growth and the apex grow 
only on one side; but this view leaves unex- 
plained the curvature of the upper part, extend- 
ing for a length of 8-10 mm. . . . We were 
therefore led to suspect that the apex was sen- 
sitive to contact, and that an effect was trans- 
mitted from it to the upper part." 1 By the 

1 Power of Movement in Plants, pp. 131-140. 


exclusion of the other two hypotheses me- 
chanical contact and arrest of growth they 
confined themselves to the last one, sensitive- 
ness to contact. This would have been a fine 
field for a discussion of the known facts fol- 
lowed by a necessary inference. Of the three 
possible hypotheses, two had been excluded, 
and the third must be true. It would seem 
quite clear that the case was logically proved. 
But instead of making this the end, they made 
it the beginning of their work. 

They "thought that any small hard object 
affixed to the tip of a radicle freely suspended 
and growing in damp air, might cause it to 
bend if it were sensitive, and yet would not 
offer any mechanical resistance to its growth." 
The results of their experiments proved remark- 
able. When approaching the subject they made 
a preliminary trial with seven beans at a rather 
cool temperature, and six radicles curved. To 
quote again, "These six striking cases almost 
convinced us that the apex was sensitive, but 
of course we determined to make many more 
trials." As they had noticed that radicles grew 
much more quickly when subjected to con- 
siderable heat, and as they imagined that heat 
would increase their sensitiveness, they made 
five or six dozen trials on more than two dozen 


beans at a temperature of 69-72 F. The 
result was moderately distinct deflection in only 
one radicle; in five other cases slight and 
doubtful deflection. "We were astonished at 
this result, and concluded that we had made 
some inexplicable mistake in the first six experi- 
ments. But before finally relinquishing the 
subject, we resolved to make one other trial, 
for it occurred to us that sensitiveness is easily 
affected by external conditions, and that radi- 
cles growing naturally in the earth in the early 
spring would not be subjected to a temperature 
nearly so high as 70 F." In the vast num- 
ber of successful trials that they made they 
allowed the radicles to grow at a temperature 
of 55-6o F. 1 

Had they stopped with the first trial, they 
would have hit the explanation which they 
finally adopted, and missed the effect of varia- 
tions in temperature. Had they stopped with 
the second, the question would have hung in 
the balance between contradictory results. It 
was very feasible to reason that the results of 
the older experiment were due to some error of 
observation or manipulation. Nothing would 
have been known concerning the effect of tem- 
perature, and nothing concerning the original 

1 Power of Movement in Plants, pp. 141, 142. 


question. Their imagination had led them to 
introduce a new element into the second experi- 
ment; then reason prevented them from suc- 
cumbing before the disturbance in the results, 
and led them to recognize it as a determining 
factor and treat it as such in their subsequent 

The contradictory state in which things would 
have been left at the end of their second experi- 
ment is neatly illustrated by another case in 
connection with the same subject. 1 Ciesielski 
had shown, in his study of geotropic move- 
ments, that roots extending horizontally with 
their tips cut off did not grow downward. " He 
further states that, if the tips are cut off after 
the roots have been left extended horizontally 
for some little time, but before they have begun 
to bend downwards, they may be placed in any 
position and yet will bend as if still acted on 
by geotropism ; and this shows that some influ- 
ence had been already transmitted to the bend- 
ing part from the tip before it was amputated." 
Sachs repeated these experiments, but denied 
the conclusions, because in his experiments 
the roots became distorted in all directions. 
The Darwins undertook to learn the cause of 
the contradiction in the results. After describ- 

1 Power of Movement in Plants, p. 523. 


ing unsuccessful efforts based on reasoning, 
they go on to say, " We next thought that, if 
care were nat taken in cutting off the tips 
transversely, one side of the stump might be 
irritated more than the other, either at first, or 
subsequently during the regeneration of the 
tip, and that this might cause the radicle to 
bend to one side." They amputated some 
radicles obliquely and some transversely, and 
allowed them to grow perpendicularly. There 
was little or no distortion at first; but after 
two or three days, when the new tips began to 
form, the distortion of the obliquely amputated 
radicles became very conspicuous. The new 
tip was probably formed obliquely, causing the 
bending. Sachs probably " unintentionally am- 
putated the radicles not strictly transversely " ; 
and by not attending to this apparently insig- 
nificant condition he produced confusion and 
failed to make a discovery. 

This case is interesting not only because it 
illustrates the difficulties that are met by the 
individual investigator, but because it is a typ- 
ical example of a very large proportion of con- 
tradictions in results with which the literature 
of science is burdened. The contradiction in 
the results obtained by the two men was due, 
not to errors of observation, but to neglect of 


the various conditions under which the experi- 
ments were made. As I have elsewhere shown 
for another more involved case, the disputant 
observers were both right. 1 It was lack of 
exhaustion of the logical conditions of the 
problem that led to the contradiction. Total 
exclusion of error requires that every move- 
ment of the experimenter be fraught with in- 
tention. It is fairly safe to assume that, if two 
observers are competent and upright, their con- 
tradictory results, no matter on what subject, 
will prove essential to the final solution of the 

The publication of the " Power of Movement 
in Plants " was followed by several years of 
active investigation on and discussion of the 
"Darwinian curvature" of radicles. It has 
been shown that radicles, instead of being 
deflected by tin-foil on soft sand, will pene- 
trate mercury and pierce tin-foil even when 
they strike it at a quite high angle. In expla- 
nation of the initial error of the Darwins it has 
been suggested that the radicles upon which 
they experimented were wilted. It has been 
further shown that in the experiments in which 
they attached small hard objects to the tips of 
the radicles to induce them to curve, the curva- 

1 Popular Science Monthly, January, 1894, pp. 373~376 


ture was not due to sensitiveness, but to the 
action of the shellac by means of which the 
objects had been attached. Microscopic exam- 
ination of radicles to which the materials used 
for attachment had been applied showed that 
the cells were affected. In short, the curvature 
of radicles ascribed to sensitiveness to touch 
has been shown to be due to pathological con- 
ditions brought into existence by the experi- 
ments themselves. The reasoning was correct 
enough, but the premises were false. Initial 
errors led to a false conclusion, but the experi- 
ments were all valuable as starting points for 
more searching investigations. The hypothesis 
of sensitiveness has been proved by Wiesner 1 
and others to be untenable, but much more is 
known of the Darwinian curvature now than 
when the Darwins published their conclusions. 
All Darwin's works on plants furnish ex- 
amples of the practically complete develop- 
ment of the conditions of the problem. In 
the opening of the chapter on " Illegitimate 
Offspring of Heterostyled Plants," he said, "I 
give the results of my experiments in detail, 
partly because the observations are extremely 

1 Wiesner, J., Untersuchungen liber die Wachsthumsbewe- 
gungen der Wurzeln (Darwinische und Geotropische Wurzel- 
Kriimmung). Sitz. Akad. Wien, V. 89, I. pp. 223-302. 


troublesome and will not probably soon be 
repeated, thus I was compelled to count under 
the microscope above twenty thousand seeds of 
Lythrum salicaria. "* The whole of his work 
on the same subject is on the same scale, vast 
numbers of observations being condensed into 
each of numerous tables. 

It is elsewhere described how he had fore- 
seen the importance of making comparative 
observations on the effects of cross- and self- 
fertilization in plants; and how he had been 
deterred by a bad analogy, and had finally had 
the subject thrust upon him while making 
experiments on Linaria vulgaris and the carna- 
tion with another end in view. 2 There are 
extant in all biological literature few equally 
fine examples of the clear comprehension of 
the conditions of a problem and of untiring 
attention to them. 3 He began by making a 
preliminary experiment with two plants, and, 
finding that, as in his previous accidental 
observations, the cross-fertilized seedling was 
in every respect superior to the self-fertilized, 
he proceeded to experiment on a very large 

1 Different Forms of Flowers on Plants of the same Species, 
p. 189. 

2 Effects of Cross- and Self-Fertilization, p. 8. 
8 Ibid., pp. 10-27. 


He covered the plants with nets, and cross- 
and self-fertilized them artificially without cas- 
tration, so as to make the cases parallel in all 
respects. The seeds were thoroughly ripened; 
the cross- and self-fertilized seeds were chosen 
in pairs that had germinated simultaneously, 
and were planted on opposite sides of the same 
pot. When one of a pair t became sickly or 
injured, both were thrown away. All the 
seeds which remained after a number of pairs 
were thus planted were sown and left to grow 
up crowded on opposite sides of the same pot. 
The soil was carefully made uniform ; the 
plants on the two sides of a pot were always 
watered at the same time and as equally as 
possible. The plants on the two sides of a pot 
were separated by a partition, but the pot was 
turned so that the two sides would be equally 
lighted. In this way the cross- and self-fer- 
tilized seedlings that competed with each other 
were subjected to as nearly similar conditions 
as human ingenuity could produce. Different 
sets of competing plants were subjected to 
different conditions, to determine whether the 
inequality between the cross- and self-fertilized 
seedlings would show itself only under favor- 
able, or unfavorable, or under all circumstances. 

In making the comparisons the eye alone 


was never trusted. Many plants were measured 
while young, when nearly full grown, and when 
matured. Equal numbers of the two kinds 
were cut down and weighed. Records were 
kept of the rate of germination, of the periods 
of flowering, and of productiveness both as to 
the number of capsules produced and as to the 
average number of contained seeds. Finally, 
the tables of measurements were submitted to 
Francis Galton in order to insure against error 
and to have them examined by the best statis- 
tical methods. Darwin intended at first to 
raise only one generation of crossed and self- 
fertilized seedlings of each kind, but in many 
cases he went as high as ten generations. 
Plants of different generations were exposed to 
different conditions in successive years. He 
started crossed seeds of Ipomcea purpurea (third 
generation) forty-eight hours later than the 
self-fertilized; seeds were sown outdoors late 
in the season, and only one stick given to each 
set to climb on ; two lots were sown in a shady 
and weedy part of the garden ; two other lots 
were sown in a bed of candytuft; seeds from 
the same plant were sown, the crossed in one 
corner and the self-fertilized in another corner 
of a tub in which a Brugmannia had been grow- 
ing, and in which the soil was excessively 


poor; others were transferred from the hot- 
house to the coldest part of the greenhouse; 
all to test the relative vigor of the crossed and 
self-fertilized seedlings. 

He considered the possible sources of error, 
and showed that accidental cross-fertilization 
of plants intended for self-fertilization, and 
accidental self-fertilization of plants intended 
for cross-fertilization, would diminish rather 
than exaggerate his results. It having been 
said that an excess of pollen was injurious, two 
sets of sixty-four each of Ipomcea purpurea 
were tested to find whether the quantity of 
pollen applied to the stigma made any differ- 
ence, and the statement was proved untrue. 
He published the details of his experiments, 
because they extended over eleven years and 
"are not likely soon to be repeated." When 
Darwin said in his conclusion that cross-fertil- 
ized plants are superior to self-fertilized plants 
and have a permanent advantage over them in 
the struggle for existence, and that nature 
abhors perpetual self-fertilization, there was 
no man to gainsay it; his ingenuity had spent 
itself in exhausting the conditions of the prob- 
lem. He could have reached the same conclu- 
sion from his two accidental observations and 
his first direct experiment on the two plants. 


In this way he could have secured for himself 
the priceless gem of "priority of discovery " 
without the tedious years of work; he could 
then have produced what so many scientists in 
prominent positions produce on subjects fit to 
occupy one mind for years, a few pages of 
general discussion and desultory reference to 
scattered and long-known facts. 

The characteristic of exhaustiveness and its 
consequences is well illustrated in his "detail 
work " in the Monograph of Cirripedia. By the 
examination of an enormous number of speci- 
mens he showed how very variable are the spe- 
cies of the genus Balanus, and how, through 
imperfect examinations and want of caution, 
so many nominal species of fossil Balani have 
been described. Discussing dubious species, 
he said, " Bronn does not seem to have been 
aware of the absolute necessity of giving 
minute details in his descriptions of fossil 
cirripeds." 1 Probably in no department of 
the biological sciences has there been more 
superficial and worthless work done than in 
the description of species. This is doubtless 
due to the fact that a spurious fame could be 
acquired by the connection between the author's 
name and that of the species he described. 

1 Monograph of the Cirripedia, Vol. II. pp. 173, 184. 


Even good naturalists have frequently regarded 
a short description sufficient for ordinary pur- 
poses of identification as even preferable to a 
minute enumeration of details. Darwin not 
only gave an example of the permanent worth 
of the latter method of specific description in 
his "Monograph of the Cirripedia," but his 
book on the " Origin of Species " is one of the 
finest examples extant of the fact that a short 
statement of any subject to be valuable and 
forcible must be an abridgment of and be 
based upon a vast mass of details. In a corre- 
spondence with Hugh Strickland he expresses 
himself almost savagely in condemnation of 
the wretchedly poor work of species describers; 
he had unusually good reason to feel aggrieved 
because the nature of his work compelled him 
to use so much of the work of others. But he 
did far less for the improvement of specific 
description by personal example in the Mon- 
ograph of Cirripedia, and by personal condem- 
nation of the poor work of others, than he did 
indirectly by his general theories of descent 
and natural selection. The doctrine that species 
had their origin in varieties and in individual 
variations has changed the purpose of specific 
description. Identification and classification 
have been made processes subsidiary to some- 


thing higher. The establishment of a new 
standard of value for specific work has not only 
directed this work into new channels and the 
careful study of details, but has made many old 
descriptions valueless. 

Intimately connected with the thoroughness 
with which scientific work is done is the length 
of time spent on it. One of the serious objec- 
tions to waiting for better facilities, more evi- 
dence, etc., when the question of closing up an 
investigation arises, is the probability of loss 
of interest in the subject. Promptness in com- 
pleting any line of work seems commendable 
on account of the economy of time, the greater 
certainty of recording results to date, and the 
importance of keeping the coast clear for new 
work. But work "completed" in a short time 
suffers from incompleteness, from whatever 
point of view it is regarded. Nothing can be 
so demonstrative as the relative permanence of 
work that has been done slowly and work that 
has been done with promptness and apparent 
vigor. The latter almost invariably takes a 
very subordinate place in the literature of the 
subject when once that subject is competely 
worked out. 

In these days of competition, when every 
field of biology is ferreted for new subjects of 


investigation, and others are likely to secure 
priority of publication, there is every tempta- 
tion to publish prematurely. Priority having 
been gained by a so called preliminary notice, 
a large proportion of the subjects are dropped 
by the original investigators, and let alone by 
others because they are "old." Time makes 
investigation easier. Where speed is felt to be 
necessary, a vast outlay of energy is frequently 
required to discover what with more time would 
almost come of itself. With the attention 
steadily fixed, time brings to bear multitudes 
of facts that would otherwise be lost. Gaps in 
the evidence, if filled at all, are too often filled 
with "necessary inferences" instead of facts. 

There is perhaps no better case on record to 
illustrate the effect of time on the develop- 
ment of theory than the " Origin of Species/' 
Darwin had already long reflected on the sub- 
ject when he opened his first note-book for 
facts in 1837; and for more than twenty years 
thereafter he labored in analyzing and inter- 
preting the facts of nature by the help of his 
theory in order to test the latter in all its rela- 
tions. By carrying on simultaneously several 
investigations bearing on the general subject, 
he could let each of his studies drag through 
many years, and yet was able to accomplish 


much. Some of the most important explana- 
tions under his theories did not occur to him 
until years after he had begun their study. It 
will be pointed out later that after he once got 
possession of a working hypothesis his work 
was largely deductive; and it will be shown 
how extremely difficult it is to work out all the 
important consequences of such a hypothesis 
even in many years. After it is once done the 
task seems so easy that the wonder is that it 
was not done sooner. But the contemplation 
of the development of a great theory soon re- 
veals the enormous difficulties in the way of 
one or many who seek to work out its conse- 
quences. Darwin did in each of his investiga- 
tions what is usually done for a subject by a 
number of successive workers ; each makes an 
important contribution to the subject, removes 
a serious objection to a theory, explains a sec- 
tion of the evidence, points out an important 
consequence, or modifies the statement of it 
to bring it more clearly in harmony with the 
greater knowledge on the subject. By succes- 
sive approximations many men, working toward 
the same end, originate, build up, and improve 
a theory until it takes its place among perma- 
nently established truths. As far as it was 
possible for one man to do so Darwin did all 


this for his subjects before he gave them to the 
world. His work on the " Expression of the 
Emotions" began in 1838 and closed in 1872; 
"Insectivorous Plants," 1860-1876; "Vegetable 
Mould and Earthworms," 1837-1881. One of 
the most notable legacies that he left to the 
ambitious student is his example of great energy 
and great patience, his incarnation of the truth 
that time, as well as reason, is the handmaid of 

Coupled with the habit of treating exhaust- 
ively the subjects with which he dealt, and 
the willingness to bide his time for publication 
until his views had reached their full maturity, 
was his extreme conscientiousness in giving 
full force to the objections against his. general 
results. The habit of pursuing all the facts to 
their meaning made it possible for him to say 
that he had been able to consider in advance 
all the objections that were afterwards made 
to any of his views. The summing up of his 
experiments on Adonis czstivalis, in the " Effects 
of Cross- and Self-Fertilization," is an example 
of the great length to which he went in record- 
ing facts, especially if they were in any way 
opposed to his conclusions. He said, "The 
results of my experiments on this plant are 
hardly worth giving, as I remarked in my notes 


made at the time, * seedlings from some un- 
known cause, all miserably unhealthy, ' nor did 
they ever become healthy; yet I feel bound to 
give the present case, as it is opposed to the 
general results at which I have arrived." 1 

He did not hesitate to diminish the positive 
results of his experiments or the effect of his 
views by incorporating all exceptions, unless 
they were clearly due to some known extra- 
neous cause. But his inability to leave any 
thing unexplained was so great that he rarely 
left exceptional facts without at least sugges- 
tions of possible explanations. He was ex- 
tremely ingenious in guessing explanations for 
facts that could not be brought under the same 
general explanation as the other facts of their 
class. A good instance of this art of wriggling 
is his attempt to explain the sloping terraces 
of Coquimbo. 2 

1 Effects of Gross- and Self-Fertilization, p. 128. 

2 Geological Observations, etc., pp. 256-258. 



IT would naturally be expected, from Dar- 
win's clear notions of evidence in gen- 
eral, and the necessity that he was under all 
his life of handling vast bodies of complicated 
evidence, that his work would furnish examples 
for the treatment of negative evidence. His 
estimate of its value is well shown by his treat- 
ment of the question whether Primula veris, 
P. vttlgaris, and P. elatior are different forms 
of the same species. 1 After discussing the 
evidence in favor of this view he said, " Nega- 
tive evidence is of little value; but the follow- 
ing facts may be worth giving." Then follows 
the recital of his efforts to determine whether 
the cowslip varies enough to justify the belief. 
He transplanted cowslips from the fields into a 
shrubbery, and then into highly-manured land; 
the next year they were protected from insects, 
artificially fertilized, and seed grown, which 

1 Different Forms of Flowers on Plants of the same 
Species, p. 62. 


was sown in a hot-bed. The young plants 
were set out, some in very rich soil, some in 
stiff, poor clay, some in old peat, and others in 
pots in the greenhouse, seven hundred and 
sixty-five in all. Though they and their parents 
were subjected to all this diversity of treat- 
ment, "not one of them presented the least 
variation except in size." Negative evidence 
is indeed of little value, unless it can be shown 
that it covers the whole ground. In order to 
transform these experiments into proof it would 
be necessary to show that, if the three forms 
belong to one species, the cowslip should have 
varied under the conditions to which it was 
subjected. It is far more difficult to disprove 
a proposition by negative evidence than by 
proving the truth of its contradictory. Darwin 
accordingly demonstrated what several other 
botanists had surmised: that the oxlip is a 
hybrid between the cowslip and the primrose. 

His efforts to determine whether Orchis morio 
secretes nectar also furnish a good illustration 
of his treatment of negative evidence. 1 A 
nectary implies nectar, but Sprengel had thor- 
oughly searched many flowers of O. maculata 
and morio, and could not find a drop. Of 
his own efforts in this direction, Darwin said, 

1 Fertilization of Orchids, pp. 36-41. 


" I have looked to all our common British 
species and could find no trace of nectar; I 
examined, for instance, eleven flowers of O. 
maculata, taken from different plants growing 
in different districts, and taken from the most 
favorable position on the spike, and could not 
find under the microscope the smallest bead of 
nectar." Sprengel believed that these plants 
exhibit an organized system of deception, "for 
he well knew that the visits of insects were in- 
dispensable for their fertilization " ; but Darwin 
could not believe in so gigantic an imposture. 
"Notwithstanding these several facts," he went 
on, " I still suspected that nectar must be 
secreted by our own orchids, and I determined 
to examine O. morio rigorously. As soon as 
the flowers were open I began to examine them 
for twenty-three consecutive days; I looked at 
them after hot sunshine, after rain, and at all 
hours; I kept the spikes in water and examined 
them at midnight and early the next morning." 
He irritated the nectaries with bristles and ex- 
posed them to irritating*vapors. He examined 
flowers whose pollinia had been removed, and 
others which would probably have them soon 
removed. But the nectary was invariably dry. 
Only after he had made the negative evidence 
as complete as it could be made, by examining 


the nectaries of very many flowers from differ- 
ent places under all the possible circumstances 
in which nectar might be secreted, did he feel 
justified in saying, "We may therefore safely 
conclude that the nectaries of the above named 
orchids neither in this country nor in Germany 
ever contain nectar." Even then he restricted 
the negative conclusion to the two countries 
in which the exhaustive examinations had been 

But he did not rest with this negative evi- 
dence. It was strong enough to convince him 
that there was no ordinary nectar, but the 
further evidence that he presents shows how 
quickly negative evidence falls into the back- 
ground in the presence of even the most indirect 
positive evidence. He was thoroughly con- 
vinced that these orchids require the visits of 
insects for fertilization, that insects visit flowers 
for the attractions offered in the way of nec- 
tar, pollen, etc. ; that nature could not deceive 
insects by a permanent imposture, and yet that 
in these orchids the ordinary attraction was 
absent. It was as if a crime had been com- 
mitted, and he were asked to believe there was 
no criminal. 

In examining the nectaries of the several 
species of orchids he was "surprised at the 


degree to which the inner and outer membranes 
forming the tube or spur were separated from 
each other, also at the delicate nature of the 
inner membrane, . . . and, lastly, at the quan- 
tity of fluid contained between the two mem- 
branes." He found the space between the 
membranes of other nectaries quite dry. He 
then examined other forms that do secrete nec- 
tar in the ordinary way, and found the mem- 
branes closely united, instead of separated by 
a space. "I was therefore led to conclude," he 
said, " that insects penetrate the lax membrane 
of the nectaries of the above named orchids and 
suck the copious fluid between the two mem- 
branes. This was a bold hypothesis, for at the 
time no case was known of insects penetrating 
with their proboscides even the laxest mem- 
brane." He afterwards learned that at the 
Cape of Good Hope moths and butterflies pene- 
trate peaches and plums, and in Queensland, 
Australia, a moth penetrates the rind of the 
orange. These facts merely proved his antici- 
pation less anomalous than it had seemed. 
The bees which he saw visiting Orchis morio 
kept their proboscides inserted in the nectaries 
for some time. He opened several nectaries, 
and found brown specks, due, as he believed, 
to punctures made some time before. Herman 


Miiller has since corroborated Darwin's inter- 
pretation, saying, " My own observations have 
confirmed this view, as well as every detail of 
the rest of Darwin's account." 1 The nega- 
tive evidence was, by its very completeness, a 
stumbling-block to Darwin's beliefs. As must 
sooner or later be done with all instances of 
negative evidence, he again set about replacing 
it by positive evidence, which removed the 
necessity of the belief which the negative evi- 
dence destroyed. Until that was done the neg- 
ative evidence increased rather than diminished 
the mystery that needed solution. 

1 H. Miiller, Fertilization of Flowers, pp. 535-538. 



T)ERFORMED consciously or unconsciously, 
*- the act of classification is indispensable 
to and accompanies every scientific inference. 
A mind is orderly or slovenly, according as it 
does or does not habitually and accurately 
classify the facts with which it comes in con- 
tact. The success of an investigation, the 
worth of a conclusion, are in direct proportion 
to the fidelity to this principle and the exhaust - 
iveness with which the process is carried out. 

In nature, constant forces at work upon vary- 
ing materials necessarily produce segregation; 
the like are brought together, and the unlike 
separated. The result is a literally "natural 
classification." This simple result is rarely 
realized. The forces at work are so numerous, 
and have acted so long, that, especially with 
reference to living things, Nature's serial clas- 
sifications in space and time have been broken 
up and thrown into confusion to such an extent 
that they are seldom recognizable. The result 


is a superficial chaos of phenomena. The 
recognition of natural classifications was an 
excessively slow growth; they were finally 
worked out by the slow collection of material 
and successive attempts at a natural arrange- 
ment. In nature's arrangement of living things 
over the earth it has been very difficult to recog- 
nize law, and at first it was possible only where 
isolation has been long continued and the forces 
at work upon living things have been few and 
steady in their action. Even then the recog- 
nition has required extensive travel and a power- 
ful inclination to classify and recognize the 
relations of distant facts to each other. 

It was the recognition of several such arrange- 
rrients or classifications in Nature that first led 
Darwin to reflect on the Origin of Species. 
What immortalized his observations is not the 
simple fact that they were made, but that by 
their cumulative presentation they led Darwin 
to seek an adequate cause for these natural 

After pointing out, in the narrative of his 
voyage, the striking relation between the fossil 
and the living animals of South America, he 
said : " This wonderful relationship in the same 
continent between the dead and the living will, 
I do not doubt, hereafter throw more light on 


the appearance of organic beings on our earth, 
and their disappearance from it, than any other 
class of facts." 1 In passing southward over 
the continent of South America, he recognized 
another of Nature's classifications: he noticed 
the frequent recurrence of the fact that a species 
occupying a given region was replaced to the 
southward by a closely related species, and this 
serial arrangement impressed itself strongly 
upon him. His visit to the Galapagos Islands 
gave him an almost perfect example of sim- 
plicity in the working of Nature's forces. The 
conditions for one of Nature's classifications 
were perfect. When Lawson, the Vice Gover- 
nor, had declared to him that the tortoises from 
the different islands differed from one another, 
Darwin did not see the significance of the fact. 
He mixed up his collections from the various 
islands, and did not dream that there lay before 
him one of the most remarkable facts that 
Nature ever revealed to a naturalist. By some 
happy accident he compared the many speci- 
mens of mocking thrushes shot on Charles 
Island with those from Albemarle Island, and 
was astonished to find that they belonged to 
different species. It was not the fact that 
there were two species of mocking thrush liv- 

1 Naturalist's Voyage around the World, p. 173. 


ing together on the two islands, but that they 
lived apart, each on its own island, and that 
they were closely instead of distantly related, 
that several islands were stocked, each with 
its own species, or perhaps variety, of the same 
kind of animal, that struck him with wonder. 
These facts haunted him, and drove him to look 
for others like them. Upon his arrival at home 
his insect collection proved the same law. He 
had fortunately kept the plants of the different 
islands separate, and Hooker, at Darwin's re- 
quest to see whether the law held good for them, 
found it to be so. 1 Darwin had unwittingly 
carried one of Nature's beautiful classifications 
home to England with him. Keen insight into 
the relation of facts to one another had enabled 
him to recognize three striking examples of 
Nature's arrangements. 

The habit of grouping facts to extract the 
truth from them was indispensable to Darwin's 
work, for he constantly dealt with large bodies 
of facts that were manageable in no other way. 
It will be seen how difficult it is even for a 
powerful observer to see facts for which he is 
not looking, even though they lie under his 
feet. An act of classification, to be worth 
much, must usually be an effort to answer 

1 Naturalist's Voyage around the World, pp. 393-398. 


a direct question. Science has derived very 
little or no benefit from the miscellaneous col- 
lecting and grouping of facts without any pre- 
vious notion of what they are likely to reveal. 
An investigation is usually made for the pur- 
pose of answering a definite question, or of 
verifying an anticipation. With some such 
end in view, with some principle by which the 
classification is guided, the result usually re- 
veals not only what was looked for, but fre- 
quently still more fundamental characteristics ; 
for it is impossible to throw facts into any 
order which reveals one truth without dragging 
others into the light with it. The character of 
Darwin's work required constant recourse to 
lists and tables; he appreciated fully both their 
value and their treachery, and his great ability 
to recognize all the points brought out, no mat- 
ter whether he was looking for them or whether 
they bore directly on the subject which he hap- 
pened to be investigating or not, made them 
enormously useful to him. 

Darwin's original purpose in measuring the 
heights of the gravel-capped plains of Patagonia 
was to ascertain the heights at which recent 
fossil shells occurred. These measurements 
gave him all he sought, a notion of the amount 
of elevation in the recent period. On compar- 


ing his measurements with those of the Beagle 
survey, he was struck with their uniformity. 
He tabulated all the measurements represent- 
ing the summit edges of the plains; and the 
tabulation proved to him that the elevation of 
the land had gone on at a remarkably equable 
rate over a north and south distance of at least 
five hundred miles. 1 There is comparatively 
little danger of throwing away effort in a well 
directed classification. The danger lies in not 
comprehending the vast significance of the 
process both in actual investigation and in the 
presentation of results, and in the lack of per- 
sistent determination to exhaust its resources. 
Darwin himself sometimes owed it to happy 
accident that he did not overlook this powerful 

Guided by deduction to the probable relation 
of the distribution of volcanoes to that of coral 
islands, and to the distribution of fringing and 
barrier reefs and atolls in relation to each other, 
he spent months in mapping them from the 
descriptions of voyagers, surveying vessels, etc. 
From the classification of a vast chaotic mass 
of facts scattered throughout geographic and 
geological literature, he extracted some of the 
most important conclusions of his whole work 

1 Geological Observations, etc., p. 211. 


on coral islands. 1 Time has shown that the 
conclusions reached from this mapping of facts 
is too general. The conclusions that volcanoes 
are invariably absent from the areas which have 
recently subsided or are still subsiding, and are 
commonly present in areas that are rising or 
have recently risen, that fringing reefs lie in 
the areas of elevation and atolls in the areas 
of subsidence, may not be accepted without im- 
portant reservations. But whether time shall 
ultimately substantiate or correct Darwin's con- 
clusions, or shall even destroy some of them, 
his classifications will always remain essential 
to the study of coral islands. 

1 Structure and Distribution of Coral Islands, p. 189. 



A NALOGICAL reasoning plays a very im- 
<L portant part in all scientific work; and 
Darwin frequently availed himself of its help 
in making discoveries and establishing conclu- 
sions. He used every logical device to estab- 
lish and extend his theories, and there is no 
lack of material from which to choose exam- 
ples. But analogy, when used on a large scale, 
proves so treacherous, that it is useful for the 
most part only in giving clues to discoveries. 
There are but few examples of analogical rea- 
soning on a large scale in Darwin's works. 
The most important, perhaps, is his work on 
Insectivorous Plants. 

It has already been told how, while resting 
at Hartfield after years of labor on the Origin 
of Species, he was struck by the number of 
insects caught by the leaves of the common 
sundew. It soon became evident to him that 
" Droseraw&s excellently adapted for the special 
purpose of catching insects, so that the subject 


seemed well worthy of investigation." 1 As 
soon as he began to work on Drosera, and was 
led to believe that the leaves absorbed nutri- 
tious matter from the insects, he began to 
reason by analogy from the well understood 
digestive capacity of animals. One needs but 
to imagine an attempt to do the work without 
any knowledge of animal digestion to under- 
stand at once its impossibility under such con- 
ditions. By connecting his observations with 
the well known animal processes he proceeded 
on a course of rapid discovery that must other- 
wise have remained entirely closed to him. At 
almost every step he drew suggestions from 
and checked his results by reference to animal 
digestion. He made preliminary "crucial" 
experiments by immersing some leaves of 
Drosera in nitrogenous and others in non- 
nitrogenous fluids of the same density to deter- 
mine positively whether the former affected 
the leaves differently from the latter. 2 The 
discovery that Drosera detects "with almost 
unerring certainty the presence of nitrogen " 
in various fluids "led me to inquire," he said, 
''whether Drosera possessed the power of dis- 
solving solid animal matter; the experiments 
proving that the leaves are capable of true 

J Insectivorous Plants, p. 2. 2 Ibid., p. 76. 


digestion, and that the glands absorb the 
digested matter." 1 "These are, perhaps, the 
most interesting of all my observations on 
Drosera, as no such power was before distinctly 
known to exist in the vegetable kingdom." 
Having by analogy established the power of 
true digestion in plants, analogy led him to 
seek in plants the elements that do the work 
of digestion in animals. Bringing together 
what was known of plants, he pointed out that 
the juices of many plants contain an acid, and 
so one element of a digestive fluid was at hand; 
and that all plants possess the power of dis- 
solving albuminous or proteid substances, pro- 
toplasm, chlorophyll, etc., and that "this must 
be effected by a solvent, probably consisting 
of a ferment together with an acid." 2 After 
writing the last quoted sentence he learned 
that a ferment which converted albuminous sub- 
stances into true peptones had been extracted 
from the seeds of the vetch. 

Sachs mentioned the discovery of the fer- 
ment, recorded the fact that peptones had 
themselves been actually found in the seeds of 
the lupine, and added "as we come to know 
the proteinaceous reserve materials of plants 
better, and if we follow their behavior in the 

1 Insectivorous Plants, p. 268. 2 Ibid., p. 362. 



animal body also, it can scarcely be doubtful 
that, in spite of incomplete knowledge, the 
assumption is nevertheless warranted that pep- 
tonizing ferments are perhaps universally dis- 
tributed in plants." 1 "Attention was first 
drawn to the occurrence of peptonizing fer- 
ments in the vegetable kingdom by the re- 
markable phenomena observed in the so called 
insectivorous plants." By analogical reasoning 
a whole new field of study was opened ; a new 
view of the powers of plants was gained, and a 
much closer analogy between plant and animal 
functions was established. But if recent studies 
are taken into account, the question may be 
raised whether this stupendous analogical struc- 
ture has not been undermined. Tischutkin 
contends that the "digestion" of insectivorous 
plants is not accomplished in the same way as 
in animals, but is due to bacteria; that the 
pepsin of the leaves is not a secretion of the 
plant, but a by-product of the activity of the 
bacteria. 2 He proves that bacteria capable of 
dissolving egg albumen are always present in 
the secretion of the leaves; that they come 
principally from the air, that the plant only 
furnishes a medium for them to live in, that 

1 Sachs, Physiology of Plants, p. 344. 

2 Berichte der Deutschen Botanischen Gesellschaft, 1889. 


disintegration of albuminous substances begins 
only after enough micro-organisms are devel- 
oped to do the work, and that the plant simply 
assimilates what these lower organisms have 
set free. The relation between the insectiv- 
orous plants and the bacteria is one of genuine 

If the whole of Tischutkin's contention is 
true, the great body of facts brought out by 
Darwin must still be placed to the credit of 
analogical reasoning. The facts concerning 
plant and animal digestion would still remain 
parallel, both in the succession of the phenom- 
ena and in the results. It would be another 
illustration of the vast importance of analogy 
in scientific method, and of the fact that every 
analogy, the strongest as well as the faintest, 
will sooner or later fail. 

In another instance, analogical reasoning 
from animals to plants actually deterred him 
from discovering the truth to which other logi- 
cal processes might have led him. He states 
the case so clearly himself that it will almost 
suffice to quote him. 1 "The adaptation of 
flowers for cross-fertilization is a subject 
which has interested me for the last thirty- 
seven years. . . . From my own observations 
1 Effects of Cross- and Self-Fertilization, pp. 6-8. 


on plants, guided, to a certain extent, by the 
experience of breeders of animals, I became 
convinced many years ago that it is a general 
law of nature that flowers are adapted to be 
crossed, at least occasionally, by pollen from 
a distinct plant." It was a direct deduction 
from his theory of natural selection that, since 
they are adapted for cross-fertilization, cross- 
fertilization must be advantageous to them. 
Hence it was perfectly natural that he should 
like to verify it. "It often occurred to me," 
he said, "that it would be advisable to try 
whether seedlings from cross-fertilized flowers 
were in any way superior to those from self- 
fertilized flowers. But as no instance was 
known with animals of any evil appearing in 
a single generation from the closest possible 
interbreeding, that is, between brothers and 
sisters, I thought that the same rule would 
hold good with plants, and that it would be 
necessary, at the sacrifice of too much time, to 
self-fertilize and intercross plants during sev- 
eral successive generations, in order to arrive 
at any results. I ought to have reflected that 
such elaborate provisions favoring cross-fertili- 
zation as we see in innumerable plants would 
not have been acquired for the sake of a dis- 
tant and slight advantage, or of avoiding a 

ANALOGY. 10 1 

distant and slight evil. Moreover, the fertili- 
zation of a flower by its own pollen corresponds 
to a closer form of interbreeding than is pos- 
sible with ordinary bisexual animals; so that 
an earlier result might have been expected." 

He had carried the deduction far enough to 
warrant an effort to verify it, but was deterred 
by analogical reasoning from pursuing the 
matter further. Had he clung to his general 
theory and the special facts to be explained 
under it, he would, as he said himself, have 
reached an early result. The analogy, if it 
had served a good purpose, ought to have led 
him to reason that since continuous interbreed- 
ing is harmful among animals, although there 
are no special adaptations to prevent it, or to- 
encourage the opposite, then, surely, the harm- 
ful effects of close breeding and the benefits of 
cross-fertilization ought to be very marked in 
plants, with their striking adaptation for cross- 
fertilization. The analogy had clearly led him 
astray ; and he was finally brought back to the 
subject by a different route. 

" I was at last led to make the experiments 
recorded in the present volume from the follow- 
ing circumstance. For the sake of determin- 
ing certain points with respect to inheritance, 
and without any thought of the effects of close 


interbreeding, I raised, close together, two 
large beds of self -fertilized and crossed seed- 
lings from the same plant of Linaria vulgaris 
(common Toad Flax). To my surprise, the 
crossed plants, when fully grown, were plainly 
taller and more vigorous than the self-fertilized 

"Bees incessantly visit the flowers of this 
Linaria, and carry pollen from one to the 
other; and if the insects are excluded the 
flowers produce extremely few seeds, so that 
the wild plants from which my seedlings were 
raised must have been intercrossed during all 
previous generations. It seems therefore quite 
incredible that the difference between the two 
beds of seedlings could have been due to a 
single act of self-fertilization; and I attributed 
the result to the self-fertilized seeds not hav- 
ing been well ripened, improbable as it was 
that all should have been in this state, or to 
some other accidental and inexplicable cause." 
During the next season he raised two beds of 
carnations (Dianthus caryophyllus) in the same 
way and for the same purpose; the preceding 
generations in this case also must have been 
continuously cross-fertilized; again "the self- 
fertilized seedlings were plainly inferior in 
height and vigor to the crossed." 


" My attention, " he said, " was now thoroughly 
aroused, for I could hardly doubt that the dif- 
ference between the two beds was due to the 
one being the offspring of crossed and the other 
of self-fertilized flowers." After the effects 
of cross- and self-fertilization had been thus 
thrust upon him, he proceeded to make the 
exhaustive examination that ran through many 
years, and finally filled a volume. He foresaw 
the meaning of the adaptations for cross-fer- 
tilization and the character of the results, but 
was deterred by a false analogy from making 
the observations to which a careful study of the 
facts by themselves would have infallibly led 
him; and was finally driven to the subject 
again by the empirical observation of the facts 
that he had anticipated by reasoning. It may 
seem strange that the very consequences which 
theory led him to expect had to be twice forced 
upon the attention of one who was so quick to 
seize Nature's suggestions, before he could be 
brought to investigate them. But the strange- 
ness of such an intellectual phenomenon is all 
due to the afterthought. Even in the sciences 
that are most rigidly deductive it is a common 
thing for the investigator to stumble indirectly 
upon results which he might have foreseen or 
often did more or less perfectly foresee. 


In a more complex case, analogy led to a con- 
clusion which, although it could not be verified, 
possesses great importance in relation to one of 
the principal difficulties in the way of the gen- 
eral theory of natural selection. In the course 
of the investigation on " Different Forms of 
Flowers on Plants of the same Species," he 
noticed the striking parallelism between the 
phenomena of hybridism and those of the 
heterostyled plants which he was studying. 1 
When once the parallelism was established, 
the remarkable and puzzling facts of hybridism 
doubtless furnished a solid analogical basis 
from which to foresee and scrutinize the results 
of crossing the different forms of heterostyled 

Difficulty in uniting two forms and sterility 
of their offspring had been almost universal-ly 
regarded as a test of specific distinctness. 
Darwin showed clearly that this belief, al- 
though very generally true, is by no means 
universally so; and his work on heterostyled 
plants showed that all the phenomena of hy- 
bridism were displayed among forms that 
certainly belonged to the same species. He 
triumphantly overthrew the doctrine that 

1 Different Forms of Flowers on Plants of the same 
Species, pp. 242, 243. 


mutual sterility is a mark of specific distinct- 
ness. But Huxley, in his essay on the "Com- 
ing of Age of the ' Origin of Species,' " said: 
" In my earliest criticisms of the ' Origin' I 
ventured to point out that its logical founda- 
tion was insecure so long as experiments in 
selective breeding had not produced varieties 
which were more or less infertile; and that 
insecurity remains up to the present time." 1 
Such was the serious nature of the facts of 
hybridism which needed explanation. And it 
was the close parallelism between hybridism 
and heterostylism that led Darwin to seek in 
the latter an explanation of the difficulties pre- 
sented by the former. From the study of the 
illegitimate offspring of heterostyled plants he 
drew the conclusion that the sterility is due, 
not to structural differences, but to functional 
differences between the sexual elements; and 
that it is not due directly to natural selection, 
but is an incidental result accompanying the 
adaptation of the sexual elements of the dif- 
ferent forms of plants of the same species to 
fertilize each other. By inverting the analogy 
he transferred the conclusion to the facts of 
hybridism. He said that it was this consider- 
ation, that the sterility of species when first 

1 Life and Letters, Vol. I. p. 551. 


crossed, and of their hybrid offspring, is due 
to functional differences of the sexual elements, 
and not to structural differences between the 
species, that led him to make the many experi- 
ments on the illegitimate offspring of hetero- 
styled plants, and that made the results worthy 
of publication. The great strength of the 
analogy in his mind was doubtless due to the 
fact that the parallelism was so very close as to 
force the conclusion that the two sets of results, 
one within a species, the other between species, 
are due to the same cause. 



A T 7HEN Darwin had once grasped the idea 
* * of the descent of species, and natural 
selection as the cause determining modifica- 
tion, it was inevitable that he should look upon 
all classes of biological facts as consequences 
of these. Accordingly, nearly all the investi- 
gations which he carried on were pursued as 
deductions from his general principles. But 
although the larger outlines and a large part 
of the details of his work were deductive, he 
was frequently obliged to pass by induction 
from facts to the subordinate principles which 
he established 

One of the earliest of the many instances in 
which he felt compelled to re-interpret whole 
groups of facts was that relating to human ex- 
pression. When, in 1838, he read Sir Charles 
Bell's great work on the "Anatomy of Expres- 
sion," the view of the latter that man had been 
created with certain muscles especially adapted 
for the expression of his feelings struck him 


as unsatisfactory. As a deduction from his 
general theory, he believed that the habit of 
expressing our feelings by certain movements 
had been somehow gradually acquired. This 
view required that the whole subject of expres- 
sion should be studied under a new aspect, and 
each expression be given a rational explana- 
tion. 1 This led him to undertake his work on 
the " Expression of the Emotions in Man and 
the Lower Animals." Deduction pointed out 
that expression must fall under the general 
explanation; but it was impossible to foresee 
the principles which governed the develop- 
ment of the various expressions. From 1838 
to 1872 he toiled away at the mass of complex 
facts, and slowly overcame the difficulty of 
bringing the different expressions together 
under one or a few points of view. At last' he 
was able to educe three principles of expres- 
sion, which seemed to him to account for most 
of the expressions and gestures involuntarily 
used by man and animals under the influence 
of various emotions and sensations. These 
principles he arrived at, as he himself says, 
only at the close of his observations. 2 They 

1 Expression of the Emotions in Man and the Lower 
Animals, p. 19. 

2 Ibid., p. 27. 


are: (i) the principle of serviceable asso- 
ciated habits; (2) the principle of antithesis; 
(3) the principle of actions due to the constitu- 
tion of the nervous system, independently from 
the first of the will, and independently to a 
certain extent of habit. It is to be remarked 
of these three principles that they are induc- 
tions, and that they are vague on two accounts: 
they are in part so general that it might prove 
difficult to bring them to a crucial test with 
the hope of proving or disproving them; and 
the only test to which they have been put is 
that of explaining the very facts from which 
they were drawn. They have not been used to 
make further discoveries; they represent well 
the type of inductions based on many carefully 
studied facts, but unsupported by a subsequent 
deductive research. 

A simpler case of induction is his inference 
concerning the age at which characters appear 
which are inherited by one or both sexes. " It 
is in itself probable," he said, "that any char- 
acter appearing at an early age would tend to 
be inherited equally by both sexes, for the 
sexes do not differ much in constitution, before 
the power of reproduction is gained"; and 
went on to point out that characters appearing 
late in one sex would tend to be restricted to 


that sex. " I was led to infer that a relation of 
this kind exists from the fact that whenever 
and in whatever manner the adult male has 
come to differ from the adult female, he differs 
in the same manner from the young of both 
sexes." 1 

The principle that characters appearing at an 
early age are inherited by both sexes, and char- 
acters appearing late in one sex are restricted 
to that sex, is an induction from certain strik- 
ing differences between the adult males and 
females, and between the adult male and the 
young of both sexes in many species. By 
itself, without verification or other deductive 
bracing, it would have been an interesting gen- 
eralization. But Darwin sought to strengthen 
it both by observing whether it held true in 
particular cases, and by deducing it from more 
general laws. In the first of the two quotations 
given above, he pointed out the probability 
that the truth of the principle depends on the 
known changes that take place in the constitu- 
tion of the sexes on approaching maturity. It 
occurred to him to put the principle to a crucial 
test, and to rely on the result. Thereupon fol- 
lowed the investigation on the deer family, 
described elsewhere in more detail. 

1 Descent cf Man, etc., p. 276. 


Inductions are easily made; the test of a 
good investigator, however, is not the number 
of inductions he makes, but his subsequent 
treatment of them. In his study of the amount 
of material brought to the surface of the ground 
by earthworms, Darwin noticed that the sur- 
faces of old worm-castings were often studded 
with coarse particles; and was thence led to 
infer that a good deal of the finest part of 
worm-castings was washed away by the rain. 
Such an induction is so nearly self-evident that 
it would seem superfluous to verify it. Darwin 
.thought otherwise; he mixed fine precipitated 
chalk with the castings, or gently stuck it on 
to them ; the rain washed it away and proved 
him correct. By this little induction, and a 
verification almost childish in its simplicity 
and apparent insignificance, he was able to show 
that the amount of material brought to the 
surface by earthworms is much greater than at 
first appears. 1 It is probably safe to say that 
the majority even of investigators would have 
regarded the induction sufficient unto itself, 
and would not have hesitated to use it without 
verification as evidence in proof of their views. 
We here get a glimpse of how sharply Darwin 
caught the significance of the minutest indica- 

1 The Formation of Vegetable Mould, etc., p. 272. 


tions, and of the patience with which he made 
experiments to prove things which to others 
would seem so simple and self-evident as to 
need no proof. Like his great contemporary, 
Faraday, he " could trust a fact, and always 
cross-examined an assertion." It was his con- 
scientious verification of even his smallest 
inductions that gave the scientific world its 
great confidence in his work. 

Darwin's greatest induction has yet to be con- 
sidered, and will be discussed at some length ; 
because, as well as being his greatest induc- 
tion, it is his most notable speculative failure, 
and will give an opportunity to study the char- 
acteristics of false and true hypotheses. The 
problem of inheritance, the transmission of 
qualities from parent to offspring, had weighed 
upon him during all the years of his work on 
the theories of descent and natural selection. 
Almost at the very start we find him making 
experiments on beds of self- and cross-fertilized 
plants to determine questions of inheritance. 
These experiments possess their greatest inter- 
est, not from having furnished any important 
data for the solution of the problem of inherit- 
ance, but from having finally impressed him 
with the importance of cross-fertilization in 
the plant kingdom. They show how early he 


appreciated the connection between inheritance 
and his general theories, and tried to get an 
experimental basis for inference. 

Darwin, as he himself confessed, had to make 
a theory on every subject, and the intimate 
relation between inheritance and his other 
theories led him irresistibly to form a theory 
on inheritance. Like Newton, he established 
the best of theories, and, like him, "was also 
capable of proposing one of the worst." He 
finally published the hypothesis under the 
title u Pangenesis," in Volume II. of "Varia- 
tion of Animals and Plants under Domestica- 
tion." 1 The reason he gave for forming it was 
to bring the vast number of perplexing facts of 
inheritance together under a single intelligible 
point of view. To do this he assumed the 
existence of minute bodies called gemmules, 
which are cast off by all the living cells of the 
animal or plant body at all stages of its exist- 
ence, and which multiply by division, have the 
power of remaining dormant through an in- 
definite number of generations, possess certain 
remarkable affinities, etc. They were sup- 
posed to collect in the reproductive elements, 
and determine the character of the offspring. 
Darwin endeavored to make the assumption 

i Pages 349-399- 


reasonable by pointing out analogies between 
the gemmules and the reproductive elements, 
between their affinities and those of pollen, 
etc. ; and rebutted the objection of excessive 
minuteness by a comparison with molecules. 
Doubtless the gemmules were a development 
of the idea of reproductive elements, or blood- 
corpuscles, or both ; and their peculiar origin, 
powers, and hypothetical history were deter- 
mined by the various facts that had to be 
explained. It was a clear case of pure induc- 
tion, untainted by any direct or indirect evi- 
dence of the existence of the gemmules, or any 
glimpse of the process by which characters are 
transmitted. Darwin knew how speculative 
the hypothesis was, and justified it because it 
brought all the facts of inheritance together 
under one point of view. 

In his discussion of it he first stated the 
facts to be brought together, and then the 
hypothesis with a working explanation of it, 
and finally tried to show, by reasoning deduc- 
tively from the hypothesis to the facts in which 
it had originated, that it explained them. 

Usually during the effort to reach a cause by 
the road of induction the cause itself is caught 
sight of, either directly or indirectly, and it is 
then possible to formulate at once at least a 


provisional hypothesis. In the case of Pan- 
genesis this was not true. Darwin gave the 
following as the principal reasons for believing 
in natural selection : " (i) It is a true or recog- 
nized cause; (2) from the analogy of change 
under domestication by man's selection, and 
(3) chiefly from this view connecting under an 
intelligible point of view a host of facts." To 
this may be added a fourth, which he men- 
tioned to Huxley in connection with the third, 
as being the reasons why younger scientists 
would choose his theories rather than the doc- 
trine of creation; namely, that it would enable 
them to search out new lines of investigation. 

Let Pangenesis be tried by these four tests. 
In the first place, it was not even claimed that 
there was any proof, either direct or indirect, 
of the existence of the gemmules. As a cause 
which had been actually observed, they had no 
existence. Secondly, while analogy is often a 
strong collateral argument, and was so in the 
case of natural selection, it was a treacherous 
support in the case of Pangenesis. Perhaps as 
many analogies were violated, as was pointed 
out by Delpino and others, by the conception 
of the gemmules as it could muster to its sup- 
port; and one of the first essentials of an 
argument from analogy is that the points of 


similarity shall be more numerous than the 
points of difference. The third and chief 
reason which Darwin gave for belief in natural 
selection, that it connected under an intel- 
ligible point of view a host of facts, is identi- 
cal with the reason which he gave for forming 
and so tenaciously clinging to the hypothesis 
of Pangenesis. And this condition the latter 
fulfilled. It was bound to do so by the very 
terms of its origin. A hypothesis was not 
likely to leave Darwin's hands until it did 
harmonize with the facts from which it had 
taken its rise. 

The fourth reason for belief in a theory, 
namely, that it leads deductively to new inves- 
tigations, and through them to new facts, brings 
up the hypothesis of Pangenesis against a wall. 
A cause may be recognized as a working force"; 
its claim to having produced known effects may 
be supported by analogy; and a vast body of 
phenomena that must be effects of some cause 
may be brought together into harmony under 
it. But it must also be possible to work out 
other consequences of the theory. 

Francis Galton made a determined effort to 
test the hypothesis. He felt the pressing 
importance of doing so, for, as he said, "Its 
postulates are hypothetical and large, so that 


few naturalists seem willing to grant them." 1 
He reasoned that, if the gemmules or bearers of 
inheritable qualities existed in such enormous 
numbers in the body, they must be borne from 
place to place and to the reproductive organs 
by the blood. If this were true, then by inject- 
ing blood from one variety of rabbit into the 
blood-system of rabbits of another variety, the 
gemmules introduced with the foreign blood 
would pass with those proper to the animal 
itself into the repVoductive elements, and 
would modify the character of the offspring. 
He foresaw the practical importance of such a 
result. Slight dashes of blood could be intro- 
duced by breeders to modify a variety; for 
example, greyhounds could have a little of the 
bull-dog instilled into them. At the end of 
his investigation he said, " I have now made 
experiments of transfusion and cross-circulation 
on a large scale in rabbits, and have arrived 
at definite results, negativing, in my opinion, 
beyond all doubt, the truth of the doctrine of 
Pangenesis." Thus ended the only effort ever 
made to test the hypothesis deductively by 
reasoning out its consequences and trying to 
establish them by experiment. 

1 Proceedings of the Royal Society, 1871, Vol XIX. p. 394 
et seq. 


It would seem as if Galton's experiments had 
proved the hypothesis false. Darwin, how- 
ever, met the criticism, and slipped away from 
the results by admitting that he would have 
expected gemmules in the blood; but showed 
that their presence there was no necessary part 
of his hypothesis, because the latter applied 
to the lower animals and to plants, which do 
not have blood. 1 Darwin's modest defence of 
his hypothesis swept away not only Galton's 
experiments, but the possibility of proving or 
disproving it. Lionel Beale remarked, sarcas- 
tically, that it might still be possible to test it 
by cutting out a mass of an animal's flesh, and 
grafting in its place a piece from an animal of 
another variety. 2 Darwin's rejoinder to Galton 
was sound from the former's point of view. 
But the hypothesis was incapable of definite 
proof or disproof. There was no set of facts 
left that could be appealed to as a test. A 
good induction will not only be in harmony 
with and bring under one point of view a host 
of facts, but is likely to be supported by one or 
more of the following lines of proof: (i) inde- 
pendent direct evidence of the existence of the 
cause involved in the induction ; (2) strong and 

1 Nature, April 27, 1871, Vol. III. p. 502. 

2 Nature, May u, 1871, Vol. IV. p. 25. 


independent analogies; (3) the possibility of 
deducing consequences from the hypothesis, 
and verifying them by observation or experi- 
ment; (4) the possibility of deducing the cause 
or principle as an effect of another still more 

Huxley advised Darwin not to publish his 
doctrine of Pangenesis ; but he nevertheless did 
publish it, and gave as his reason the pressing 
importance of co-ordinating the inexplicable 
facts of inheritance. Other hypotheses have 
followed Darwin's with as little success. Dar- 
win did not formulate his hypothesis to support 
his other theories, but its character was at least 
in part determined by the latter. It is interest- 
ing to note that the latest hypothesis of inherit- 
ance, the most aggressive that has yet arisen, 
has been developed as a special support for the 
belief that natural selection acting upon con- 
genital variations is the sole cause in the pro- 
duction of species, and that acquired characters 
are not inherited. The principal evidence on 
which the hypothesis relies for support, apart 
from the refutation of the direct evidence ad- 
duced to support the belief in the inheritance 
of acquired characters, are the karyokinetic 
processes in cell division, and the early stage 
in development at which, in some animals, the 


reproductive elements become distinct from the 
parts which develop into the other organs of 
the body. In this respect Weissmann's hypoth- 
esis has an additional logical support. It has 
provoked earnest discussion, and naturalists 
have taken sides on the subject. Although 
the germ plasm is itself an assumption, and 
the hypothesis owes its existence to the known 
facts of karyokinesis, it has led to further 
investigations in some directions with fruitful 
results. Darwin's hypothesis opened the ques- 
tion under the new light that he had shed upon 
nature, and the more recent hypotheses, like 
his own, owe their existence to the " impelling 
force " of his general theories of descent and 
natural selection. 





DARWIN fell upon the true cause of the 
modification of species so early, that the 
greater number of his special investigations 
took on a deductive cast. 1 His reflections upon 
the known facts and principles of biology took 
the form of efforts to explain them as deduc- 
tions from his theory; and many of his new 
discoveries were foreseen as consequences of 
it. Hence the inductive process does not play 
so important a part in his work as does the 
inverse process of deduction. 

It will not be necessary to dwell long upon 
his success in giving the proper theoretical ex- 
planations to already known facts and empirical 
laws. It had required centuries of painstaking 
research and numberless efforts at classification 
before anything like a natural classification was 

1 See the Chapter on the Logical History of the Principle 
of Natural Selection,/^/, p. 212. 


reached. When, at the beginning of this cen- 
tury, it was finally approached, and the natural 
affinities of plants and animals were brought 
out by it, the doctrine of descent was inevitable; 
and it came. When Darwin had once become 
impressed with its truth, and had found the 
cause of modification, it was first of all neces- 
sary to show that the great bodies of known 
facts harmonized with his doctrines. The facts 
of distribution, palaeontology, embryology, rudi- 
mentary organs, etc., were all reduced. Each set 
of facts presented its own difficulties. 

Up to the present century it was regarded as 
an axiom in taxonomy that the structures of 
most importance to the animals possessing 
them must be of most importance for the pur- 
poses of classification. It is worth while to 
note that this was accepted as self-evident, as 
being beyond the necessity of proof. Systema- 
tists were approaching the "natural arrange- 
ment," and De Candolle discovered empirically 
the rule that there is usually an inverse ra- 
tio between the taxonomic and the functional 
value of a structure ; but he could suggest no 
reason for the paradox. Darwin's theory fur- 
nished the philosophical explanation. 1 The 

1 Origin of Species, pp. 362-373. Romanes, Darwin and 
After Darwin, pp. 34-37- 


organs of the highest functional value are 
under the constant and pressing necessity of 
changing with changes in the environment; 
while those of least functional value remain 
undisturbed, and pass, little or not at all modi- 
fied, from generation to generation. The same 
explanation holds for the rule concerning the 
importance of "aggregates of unimportant char- 
acters " in determining the affinities of animals 
and plants. 

In some parts of the natural system, there 
are what are called "chains of affinities." A 
group, instead of being broken up into well 
separated sub-groups, consists of a chain in 
which the adjacent parts are closely related, 
but the more distant parts have comparatively 
few points in common. It is impossible to 
break up the group without violating the affini- 
ties of adjacent parts, and it is difficult to define 
it in such a way as to include the extremes. 
The Crustacea furnish an example. What was 
a special difficulty under the old views of clas- 
sification is explained under the doctrine of 
descent. 1 

One of the most important principles that 
had been established empirically was the tree- 
like arrangement of species and higher groups 

1 Origin of Species, p. 368. 


in the natural classification. The recognition 
of the principle came only after centuries of 
efforts at classification; and after it was dis- 
covered, no reason could be given for it. Al- 
though so helpful and striking, it remained a 
profound enigma, for there was nothing in the 
nature of the things classified that required this 
peculiarly complex arrangement rather than one 
of several conceivable simpler ones. Darwin's 
explanation of this principle under his theory 
illustrates not only the explanation of empirical 
laws, but the difficulty of doing what, after it 
is done, seems very simple. 

It was not until after he had been at work 
upon the principle of natural selection for 
many years, that the true explanation of this 
law under his principle occurred to him. He 
said, " I suppose I must be a very slow thinker, 
for you would be surprised at the number of 
years it took me to see clearly what some of 
the problems were which had to be solved; 
such as the necessity of the principle of diver- 
gence of character, the extinction of inter- 
mediate varieties, on a continuous area, with 
graduated conditions," etc. 1 After describing 
his earlier sketches of his theory he said, "At 
that time I overlooked one problem of great im- 

1 Life and Letters, Vol. I. pp. 68, 524. 


portance, , . . the tendency in organic beings 
descended from the same stock to diverge in 
character as they become modified." That they 
have thus diverged was proved by their arrange- 
ment into groups within groups. "I can re- 
member," he went on, "the very spot in the 
road, whilst in my carriage, when to my joy 
the solution occurred to me; and this was long 
after I had come to Down." 1 The solution was 
this, "that the modified offspring of all 
dominant and increasing forms tend to become 
adapted to many and highly diversified places 
in the economy of nature." 

It seems very simple now to understand that 
the tree-like arrangement of species must be 
regarded as a direct consequence of the prin- 
ciple of natural selection. It might even seem 
easy to infer the tree-like arrangement as a de- 
duction from the principle, and to discover it, if 
it had not already been discovered empirically. 
It is not because Darwin was so slow a thinker 
that it took him so long to discover the relation 
of cause and effect between natural selection 
and the tree-like arrangement of species; but 
it was because he was a strong and persistent 
thinker that he discovered it at all. The think- 
ing out of such connections is always a slow 

1 Life and Letters, Vol. I. pp. 68-70. 


process. The final mental act may come like 
a flash, as it did in Darwin's case, and be fol- 
lowed by a very rapid and fruitful explanation of 
details ; but such triumphs do not come to the 
mind that will not serve the apprenticeship. 1 

It has been often declared that the work of 
biologists since 1860 has consisted in explain- 
ing known facts as deductions from Darwin's 
theories, and further investigating the conse- 
quences of those theories. The more exten- 
sively a theory has been successfully applied, 
the more easy it is to do what still remains to 
be done. There is profound philosophy in the 
saying, "To him that hath shall be given." It 
was a comparatively easy matter to apply Dar- 
win's theories to all sorts of facts and lines of 
investigation after he had so thoroughly tested 
and illustrated them ; but even then the scien- 
tific world was very long in working out some 
of their striking consequences. It is not to be 
wondered at that Darwin was slow to under- 
stand many things, or that he overlooked others 
entirely. It is rather to be wondered at that 
he accomplished so much single-handed. One 

1 My friend, Prof. G. C. Price, has called my attention to 
the fact that Lincoln was marvellously like Darwin in many 
respects. The former was noted for his efforts to reach funda- 
mental principles in thinking, and was also noted for the 
" slowness " of his mental action. 



of the hardest and most important lessons for 
the majority of investigators to learn is that 
the chances are all against their exhausting 
their subjects, or even putting them into such 
shape that the work will not all have to be 
done over again, unless their work is done 
slowly and continued persistently through long 
periods of time. 

Darwin's great logical power was fortified by 
another rare quality of mind, unusual acute- 
ness in observing all collateral facts that came 
out in his observations or experiments, whether 
they seemed to bear directly upon the subject 
of investigation or not. He was thus put in 
possession of many facts that afterwards proved 
valuable in ways that he could not foresee. 
But with all his ability in these directions he 
experienced difficulty in grasping the full 
significance of facts. 

In discussing Cleistogene flowers, near the 
end of his work on the " Effects of Cross- and 
Self-Fertilization," 1 after giving the reasons for 
the belief he is about to express, he said, "I 
must believe that plants now bearing small and 
inconspicuous flowers profit by their still re- 
maining open, so as to be occasionally inter- 
crossed by insects. It has been one of the 

1 Page 387. 


greatest oversights of my work that I did not 
experimentize on such flowers, owing to the 
difficulty of fertilizing them and to my not 
having seen the importance of the subject." 

Although it is clear that the possession of a 
theory is no guaranty that all its consequences 
will be foreseen, or, if foreseen, observed, or 
even that, if they are both deductively foreseen 
and empirically observed, they will be brought 
into connection with the theory; nevertheless, 
the importance of theory for accurate observa- 
tion cannot be overestimated. However cau- 
tious Darwin was about committing himself 
unreservedly to a hypothesis, he never really 
dispensed with one if he could find one. 
Though he subdued his tendency to speculation 
in the interest of observation, he did not dis- 
pense with at least provisional hypotheses, even 
in accumulating his facts. He felt the want 
when he could not find one, and made it his 
first task to establish some degree of probability 
in favor of one. 

One of his early experiences is a good illus- 
tration of how even trained observers could not, 
without the help of a theory, observe phenom- 
ena on which they actually walked, and which 
obstructed their progress. 1 He has said, "I 

1 Life and Letters, Vol. I. pp. 48, 49. 


had a striking instance of how easy it is to 
overlook phenomena, however conspicuous, be- 
fore they have been observed by any one. We 
spent many hours at Cwm Idwal, examining 
the rocks with extreme care, as Sedgwick was 
anxious to find fossils in them, but neither of 
us saw a trace of the wonderful glacial phe- 
nomena all around us; we did not notice the 
plainly scored rocks, the perched boulders, the 
lateral and terminal moraines, yet these phe- 
nomena are so conspicuous that, as I declared 
in a paper published many years afterwards in 
the Philosophical Magazine (1842), a house 
burnt down by fire did not tell its story more 
plainly than did this valley. If it had been 
filled with a glacier, the phenomena would have 
been less distinct than they now are." 

It may seem strange that two men, one already 
a famous geologist and the other soon to be- 
come one, should have overlooked such evi- 
dence, which has since become so interesting, 
so widely known, and so well understood. The 
secret of their failure is that they were not 
looking for it. It is usually the things that 
men look for that they see; and to look for 
things as yet unseen requires a theory as a 
headlight. Even if they had noticed the mate- 
rial of the moraines, the perched boulders, and 


the parallel scratches, they would certainly not 
have been deeply impressed by them, because 
they become impressive only when their rela- 
tion to one another is understood, and this 
could only be when the glacial theory had 
been imported from a glacier country. 

The importance of the discovery of the theory 
of natural selection to the work of Darwin's life 
will be dwelt upon later. A sigh of relief is 
embodied in the declaration, " Here, then, I 
had at last got a theory by which to work." 1 
Facts cannot be seen without some notion of 
the relation they will bear to each other when 
they are found. The stupendous importance 
of theory for observation is illustrated by the 
effect of Darwin's theories on biological inves- 
tigation in all its phases. Huxley put it thus : 
"The ' Origin' provided us with the working 
hypothesis we sought." 2 The whole biological 
world was waiting for it; and when it came it 
carried the biological sciences into the deduc- 
tive stage, and opened an era of investigation 
unprecedented in the rapidity with which dis- 
covery advanced, and in the accuracy of the 
results reached. 

There are scattered throughout Darwin's 

1 Life and Letters, Vol. I. p. 68. 

2 Ibid., p. 551. 


works numerous illustrations of the importance 
of theory in the investigation even of matters 
of detail. Writing of the trimorphic Lythrum 
salicaria, he said, "The existence of the three 
forms was first observed by Vaucher, and sub- 
sequently by Wirtgen ; but these botanists, not 
being guided by any theory or even suspicion 
of their functional differences, did not perceive 
some of the most curious points of difference 
in their structure." 1 MM. Boitard and Corbie, 
in their study of pigeons, had seen and recorded 
many facts which they could not use, simply 
from lack of a theory. They had stated that 
when they crossed certain breeds of pigeons, 
birds colored like the Columba livia, or the 
common dove-cot, were almost invariably pro- 
duced. 2 Darwin gave significance to these facts 
and many others by the theory of descent. 

In spite of his unusual power of seeing facts 
apparently unconnected with the subject under 
investigation, and his persistent habit of record- 
ing results, whatever they might be, Darwin 
himself, sometimes " not foreseeing the result, 
did not keep a memorandum of all the facts," 
which would afterwards have proved useful. 

1 Different Forms of Flowers on Plants of the same 
Species, p. 138. 

2 Variation of Animals and Plants under Domestication, 
Vol. II. p. 14. 


No one was more thoroughly convinced of the 
necessity of clear-cut theory for accurate obser- 
vation; and he frequently expressed himself to 
that effect. His son says of him, "He often 
said that no one could be a good observer unless 
he was an active theorizer. " 1 He said him- 
self, " I am a firm believer that without specula- 
tion there is no good and original observation." 2 
" It is an old and firm conviction of mine that 
the naturalists who accumulate facts and make 
many partial generalizations are the real bene- 
factors of science. Those who merely accumu- 
late facts I cannot very much respect." 3 

1 Life and Letters, Vol. I. p. 126. 

2 Ibid., p. 465. 

8 Ibid., Vol. II. p. 21. 



A VERY few negative instances have been 
** given to show the importance of theory 
for accurate observation. They illustrate how 
the absence of theory led to the oversight or 
neglect of facts which later, under the sway 
of theory, have become important. Darwin's 
works are full of instances in which he was led 
by his theory to anticipate the facts of nature. 
It was inevitable that, having so early dis- 
covered the theories which covered the whole 
territory in which he worked, he should be 
guided by them in the search for facts, and 
that his work should thenceforth be deductive 
in its character. Examples of this character- 
istic method range from the great deductions 
which led to nearly all his important special 
investigations, and which illustrate the sweep- 
ing consequences of his general theories, to the 
little deductive details which show how swift 
and accurate his prevision became even in the 
matter of minute consequences of these theories. 


The minor instances will be given first, and 
will be followed by the more general ones. 
Then will follow deductions which he made, 
but which are still unverified, or have been 
verified by others; and lastly will be given 
some of the instances in which he went clearly 
wrong in his deductions. 

The instance about to be given may well be 
placed first, for the purpose of raising a mooted 
question in logic. Mill took the position that 
typically the process of inference consists in 
reasoning directly from one particular case to 
another; whereas the older and more generally 
accepted view is that inference must pass by 
induction from particulars to a general law, and 
then by deduction from the general law to other 
particulars. Darwin had found silicified wood 
in certain tufaceous formations in Patagonia 
and on the island of Chiloe on the west coast 
of South America. He afterwards crossed the 
Andean Cordillera in an east and west direc- 
tion, and again found tufaceous formations. 
In his description of the geological section of 
the Uspallata range he said: "Many of these 
tufaceous beds resemble, with the exception of 
being more indurated, the upper beds of the 
great Patagonian Tertiary formation, especially 
those variously colored layers high up the river 


Santa Cruz, and in a remarkable degree the 
tufaceous formations at the northern end of 
Chiloe. I was so much struck with this re- 
semblance, that I particularly looked out for 
silicified wood, and found it under the follow- 
ing extraordinary circumstances." 1 

We are not told whether he gained his first 
knowledge of the connection between silicified 
wood and tufaceous formations from his geo- 
logical researches in South America; nor if he 
did, whether he had come to the general con- 
clusion that silicified wood is likely to be found 
in tufaceous formations, and therefore it ought 
to be found in the beds of the Uspallata range, 
or whether he simply reasoned that because 
silicified wood is found in the tufaceous beds of 
Chiloe, therefore it will be found in the very 
similar tufaceous beds of the Uspallata range. 
It is known that the two are found in connec- 
tion in different parts of the world, and there 
is a causal connection between them. The 
peculiar conditions under which tufaceous beds 
are deposited, and the subsequent processes of 
mineral solution, etc., are such that, if wood 
was present at the time of the deposition 
of such beds, it would probably be silicified. 
Whether Darwin knew of this causal connec- 

1 Geological Observations, etc., p. 526. 


tion or only knew empirically that the two are 
often found in connection, if he reasoned from 
a belief that the two are likely to be found 
together, the Uspallata case is one of deduc- 
tion. It would be interesting to have a com- 
plete record of the mental operations in this 
case; but from Darwin's mental habit of leap- 
ing quickly to hypotheses, even where the 
connection between facts appeared altogether 
empirical, there cannot be much doubt about 
the deductive character of the process, even 
if it be held that the process of inference is 
typically from one particular case to another. 

In his studies of coral islands he laboriously 
gathered information concerning the distribu- 
tion of atolls, barrier reefs, and fringing reefs, 
and indicated each kind by a different color on 
the map, distinguishing fringing reefs with red. 
He had reached the conclusion that atolls and 
barrier reefs lie in areas of subsidence, and 
fringing reefs in areas of elevation. So far as 
he could learn from records, Banks Islands and 
some others apparently had no fringing reefs, 
although they lie in what he had designated 
the zone of elevation. He pointed out the 
fact that most of the information concerning 
coral reefs and islands had been collected and 
recorded in the interests of navigation, and 


from this point of view narrow fringing reefs 
would be insignificant, and likely to be over- 
looked. He said, " I do not doubt that several 
of these islands, now left uncolored [on his 
map], ought to be red." Bonney, in his revised 
edition of Darwin's "Coral Reefs," says, on 
the authority of Captain Wharton, that Banks 
Islands are fringed in parts. 1 

The data from which he had compiled the 
map of the distribution of coral reefs and 
islands had been recorded for a purpose entirely 
different from that for which he wished to use 
them ; hence much information that was impor- 
tant for him was left out. The imperfect data 
verified his principle of distribution; and he 
was able to infer deductively that there were 
small fringing reefs in existence where they 
had not been observed or recorded. 

In pursuit of the same subject he studied 
carefully the charts of the Great Chagos Bank, 
which he had not seen himself. He saw from 
a study of the chart that, as he said, " On the 
eastern side of the atoll some of the banks are 
linear and parallel, like islets in a great river, 
and they pointed directly towards a great breach 
on the opposite side of the atoll. I inferred 
from this that strong currents sometimes set 

1 Structure and Distribution of Cpral Reefs, p. 220. 


directly across this great bank; and I hear 
from Captain Moresby that this is the case." 1 
The causal relation between currents of water 
and linear parallel islets was known to him; 
from this law and the particular arrangement 
of the banks he deduced the existence of cur- 
rents, and verified the anticipation. 

Some of these instances are so simple as 
almost to require apology for their insertion ; 
but their very simplicity makes them typical 
of the most common of the logical processes. 
The variety of consequences to be deduced 
from principles or laws is so great, that induc- 
tions by which those laws or principles are 
reached are few compared with the deductions 
by which their consequences are developed. 

Darwin's studies of the fertilization of flowers 
are full of examples of deduction and verifica- 
tion ; and some of these are very curious. The 
principle of advantage from cross-fertilization 
lay at the root of these deductions; and it was 
by incessant application of it that he was able 
to interpret the most complex arrangements in 
orchidaceous flowers. He studied the structure 
of Listeraovata, and experimented on the action 
of its parts, until he felt sure that he under- 
stood the manner in which insects enter the 

1 Structure and Distribution of Coral Reefs, p. 150. 


flower and free the pollinia. After watching 
flowers for hours to see Nature at work, he was 
rewarded with a verification of his interpreta- 
tion. 1 In the description of another case he 
said, " From the large size of the flower, more 
especially of the viscid disk, and from its won- 
derful power of adhesion, I formerly inferred 
that the flowers were visited by large insects, 
and this is now known to be the case." 2 He 
was well acquainted with the general interaction 
of the parts and their relation to visiting insects. 
From this and the size, etc. of the parts, he 
was able to deduce the size and strength of the 
insect. He had been convinced by theoretical 
considerations that the pollen of Hedychium is 
removed by the wings of hovering butterflies, 
and wrote to India to have the butterflies ob- 
served in action. Two years later Fritz Miiller 
observed the process itself. 

Probably no other of Darwin's works illus- 
trates so well the variety of results which may 
be deduced from a general principle by inge- 
nuity and skill in interpretation as does that on 
the " Fertilization of Orchids." When once 
he had laid down the proposition that the 
flowers of many plants are adapted for cross- 

1 Fertilization of Orchids, pp. 119, 120. 

2 Ibid., p. 190. 


fertilization, he set himself the task of inter- 
preting the complex arrangement of parts in 
orchidaceous flowers in relation to the visiting 
insects in accordance with that proposition. 

One of the most interesting and successful 
applications of this principle is the following. 
He has described various excrescences, warts, 
ribs, ridges, etc. on the labellum, or large odd 
petal of different orchids, the flowers of which 
do not secrete nectar. He was haunted by 
the question of the meaning of these absurdly 
insignificant and irregular things, their rela- 
tion to the other parts and to the visiting in- 
sects. He said, " From the position relatively 
to the viscid disk [by means of which the pol- 
len is removed by visiting insects] which these 
excrescences occupy, and from the absence of 
any free nectar, it formerly seemed to me higlrly 
probable that they afforded food, and thus 
attracted either Hymenoptera or flower-feeding 
Coleoptera. . . . Nevertheless it was a bold 
speculation that insects were attracted to the 
flowers of various orchids in order to gnaw the 
excrescences or other parts of the labella; and 
few things have given me more satisfaction 
than the full confirmation of this view by Dr. 
Cruger, who has repeatedly witnessed in the 
West Indies humble-bees of the genus Euglossa 


gnawing the labellum of Catasetum, CoryantJius, 
G angora, and StanJiopea. " 1 

When his attention was first attracted to the 
cowslip (Primula veris), and he noticed the 
different forms of flowers on different plants, 
some with longer pistils, rougher stigmas, and 
smaller pollen grains, and some with shorter 
pistils, longer stamens, and larger pollen grains, 
he inferred that the species was tending to 
become dioecious. Later he became convinced 
that the differences between the forms were for 
the purpose of securing cross-fertilization, and 
proved this to be the case. In his discussion 
of the positions of the flower organs in the long- 
styled and short- styled forms he said: "The 
anthers in the one form stand nearly, but not 
exactly, on a level with 'the stigma of the 
other. ... It follows from the position of the 
organs that if the proboscis of a dead humble- 
bee, or a thick bristle, or a rough needle be 
pushed down the corolla, first of one form and 
then of the other, as an insect would do in visit- 
ing the two forms growing mingled together, 
pollen from the long-stamened form adheres 
around the base of the object, and is left with 
certainty on the stigma of the long-styled form ; 
whilst pollen from the short stamens of the 

1 Fertilization of Orchids, pp. 269, 270. 


long-styled form adheres a little way above the* 
extremity of the object, and some is generally 
left on the stigma of the other form. In ac- 
cordance with this observation I found that 
the two kinds of pollen, which could easily be 
recognized under the microscope, adhered in 
this manner to the proboscides of the two 
species of humble-bees and of the moth which 
were caught visiting the flowers." l 

From these apparently insignificant deduc- 
tions and verifications he passed on to show 
that the short-styled form was far more likely 
to be self-fertilized than the long-styled form. 
For when he inserted a bristle or other object 
into the corolla of the short-styled form, he 
had to pass it between the anthers seated round 
the mouth of the corolla, and some of the 
pollen was almost invariably carried down arid 
left on the stigma. His inferences concerning 
adaptation for cross-fertilization in these forms 
were completely verified, so far as it could be 
done from a study of the relative positions of 
the parts of the flowers and the action of insects 
upon them. The proof was strong enough to 
support the principle. But for Darwin it was 
merely made the starting point for further 
verification from the physiological side. "The 

1 Different Forms of Flowers, etc., pp. 18-24. 


several foregoing facts led me to try the effects 
of the two kinds of pollen on the stigmas of 
the two forms." This "trial" consisted of a 
long series of experiments to establish the 
effects of legitimate and illegitimate unions of 
the two forms. The reward of this effort to 
establish the principle by physiological evi- 
dence is summed up in his own words: "From 
the facts now given the superiority of a legiti- 
mate over an illegitimate union admits of not 
the least doubt ; and we have here a case to 
which no parallel exists in the vegetable, or 
indeed in the animal kingdom." 1 

It had long been known that if pollen from 
a distinct species is placed on the stigma of a 
plant, and afterwards (sometimes many hours 
afterwards) pollen from its own species is 
placed on the same stigma, the latter obliter- 
ates the effects of the former, and the plant 
will be fertilized by the pollen of its own 
species. He had shown that the two forms of 
flowers of the cowslip were beautifully adapted 
in structure for cross-fertilization, and that it 
was essential to the vigor of the species that 
there be cross-fertilization between the two 
forms, and that cross-fertilization between 
flowers of the same form, or fertilization of a 

1 Different Forms of Flowers, etc., p. 28. 


flower by its own pollen, should be prevented. 
But he had also shown that there is a mechan- 
ical liability to self-fertilization in the short- 
styled form by the pollen being carried down 
from the stamens to the pistil. These facts 
led him to the belief that the pollen of the 
other form is prepotent over the pollen of the 
same form as that to which the stigma belongs, 
when they are placed on it together. He said, 
" There can hardly be a doubt that with hetero- 
styled dimorphic plants, pollen from the other 
form will obliterate the effects of the pollen 
from the same form, even when this has been 
placed on the stigma a considerable time before. 
To test this belief I placed on several stigmas 
of a long-styled cowslip plenty of pollen from 
the same plant, and twenty hours later pollen 
from a short -styled dark red polyanthus" (va- 
riety of cowslip). Of the thirty seedlings, all 
bore reddish flowers, showing that they were 
the result of the cross. 1 

It is not surprising that, after he had verified 
his general inference concerning prepotency in 
heterostyled dimorphic plants by the experi- 
ments with the highly specialized flowers of 
the cowslip, he should take another step and 
test the inference by a species in which there 

1 Different Forms of Flowers, etc, p. 31. 


was much less difference between the two 
forms. After describing the two forms of 
Linum grandiflorum, which differ only in the 
length of their pistils, he said that he had in 
his garden two fine long-styled plants, sep- 
arated by a considerable distance and some 
evergreens from plants of the other form. He 
marked twelve flowers on these two long-styled 
plants, and put some short-styled pollen on 
them ; but they, and the rest of the vast num- 
ber of flowers on these two plants, had their 
stigmas already covered with their own pollen, 
and it was late in the season (September 15). 
The pollen of the two forms could not be distin- 
guished under the microscope. "Altogether," 
said Darwin, "it seemed almost childish to 
expect any result. Nevertheless, from my ex- 
periments on Primula I had faith, and did not 
hesitate to make the trial, but certainly did 
not anticipate the full result that was obtained. 
The germens of the twelve flowers swelled, and 
bore six good capsules (the seed of which germi- 
nated) and two bad ones; only four falling off. 
All the other flowers were absolutely barren; 
not even their germens swelled." 1 Not con- 
tent with this striking result, he hunted down 
this absolute sterility of the long-styled plants 

1 Different Forms of Flowers, etc., p. 83. 


with their own form pollen, which his experi- 
ments of 1 86 1 had brought out, by carrying 
through a long series of experiments which, as 
he said, were so curious that he gave them in 
detail. His conclusion from the experiments is 
that although the pollen of the two forms is iden- 
tical under the microscope, "taking fertility as 
a criterion of distinctness, it is no exaggeration 
to say that the pollen has been brought to a de- 
gree of differentiation, with respect to its action 
on the stigma of the same form, corresponding 
with that existing between the pollen and stigma 
of species belonging to distinct genera." l 

An excellent illustration of the relation 
between induction and deduction in the scien- 
tific method is furnished by Darwin's study of 
the expression of grief. During several years, 
he said, no expression seemed to him so utterly 
perplexing as this one. Why should the inner 
ends of the eyebrows be raised when a person 
feels the emotion of grief? Or, in other words, 
what is the cause of the obliquity of the eye- 
brows under suffering? "Why should grief or 
anxiety cause the central fasciae alone of the 
frontal muscle, together with those round the 
eyes, to contract?" 2 Here was a little induc- 

1 Different Forms of Flowers, etc., pp. 87-90. 

2 Expression of the Emotions, etc., pp. 188-192. 


tive problem: the effects given, to find the 
cause, without any hint as to its nature. Sev- 
eral years would seem long enough for a mind 
like Darwin's. 

He had seen Duchenne's photograph of a 
young man contracting the grief-muscles while 
looking up at a strongly illuminated surface, 
but had entirely forgotten the picture. The 
problem remained unsolved. One day while 
on horseback, with the sun behind him, he met 
a young girl whose eyebrows as she looked 
up at him became extremely oblique, with the 
proper furrows on her forehead. He had been 
unable to reach the cause by contemplation 
of the effects. Now he had observed a cause 
producing effects identical with those which 
puzzled him. There was now a basis for ex- 
periment He went home and caused three of 
his children, without their knowing why, to 
look up at the top of a tall pine against a 
bright sky. "With all three," he said, "the 
orbicular, corrugator, and pyramidal muscles 
were energetically contracted, through reflex 
action " to protect the eyes against the light. 
But they wanted to see, and a " curious struggle 
arose between these muscles, that tended to 
lower the brows and close the lids and all or 
only the central fasciae of the frontal muscle, 


causing obliquity of the brows with puckering 
and swelling of their inner ends, so that the 
exact expression, in every detail, of grief or 
anxiety was assumed " 

"When children scream they contract the 
orbicular, corrugator, and pyramidal muscles, 
primarily for the sake of compressing their 
eyes, and thus protecting them from being 
gorged with blood." By observation on the 
little girl and his own children he found that 
the peculiar expression characteristic of grief 
was the combined result of the reflex contrac- 
tion of the muscles around the eye to protect it 
by closing it, and the voluntary contraction of 
other muscles to keep it open. In children the 
unrestrained expression of suffering called into 
action only one set of these muscles. These 
were the factors in his possession for the solu- 
tion of the problem. He knew that the eleva- 
tion of the inner ends of the eyebrows was due 
to the effort to keep the eyes open. " I there- 
fore expected to find with children," he said, 
"that when they endeavored either to prevent 
a crying-fit from coming on, or to stop crying, 
they would check the contraction of the above- 
named muscles, in the same manner as when 
looking upwards at a bright light; and conse- 
quently that the central fasciae of the frontal 


muscle would often be brought into play." He 
himself observed children with reference to 
this point, and had others, including physi- 
cians, do so. He soon found that the "grief- 
muscles " were very frequently brought into 
very distinct action, and has given a number 
of cases. The crying-muscles act in children, 
and have acted for countless generations. The 
pyramidal muscles are least under the control 
of the will, and can be counteracted only by 
the voluntary contraction of the central fasciae 
of the frontal muscle ; and that is the expression 
of grief. 

This instance of the solution of an inductive 
problem is by its apparent smallness a striking 
example of the difficulties of scientific investi- 
gation, and of the necessity of appealing to all 
the logical processes. After the explanation is 
once made, it would seem an easy matter to ana- 
lyze the complex effect called the expression 
of grief, and discover its causes in the involun- 
tary contraction of one set, and the voluntary 
contraction of another set of muscles; but the 
apparent simplicity is all due to the explana- 
tion itself. It will be remarked, in the discus- 
sion of the logical history of the principle of 
natural selection, that the causes of any set of 
facts are rarely discovered by a direct study 


of the effects. Sooner or later a cause is ob- 
served to produce the effect of which an ex- 
planation is desired; then by an induction the 
cause is applied to the whole class of effects, 
and the induction is established by subsequent 
deduction and verification. 

One of the most interesting examples of 
reasoning recorded in Darwin's works is that 
concerning the colors of caterpillars. Although 
Darwin put the problem and Wallace solved it, 
it is inserted here because it illustrates the 
devices used to secure explanations of facts. 
Darwin had undertaken to explain the beauty 
of butterflies by the principle of sexual selec- 
tion, but knew that it was foolish to think that 
the beauty of the mature animal was thus ex- 
plained unless the equally beautiful colors of 
many caterpillars, in whose case sexual selec- 
tion certainly could not act, were explained in 
some special way. 1 Here was another set of 
facts that could not be reduced under his 
theory; and again appears the almost insuper- 
able difficulty of passing directly from facts to 
their causes. He whom many regarded as a 
master in the art of "wriggling" was unable to 
devise an explanation, and appealed to Wallace, 

1 Descent of Man, etc., Vol. I. pp. 202-204 ; Life and Letters, 
Vol. II. p. 276. 


who, he said, had an innate genius for solving 
difficulties. Wallace, by a pretty paradox, re- 
ferred this anomalous set of facts to the well 
known principle of protective coloring. He 
said most caterpillars require protection, as 
may be inferred from some kinds having spines 
or hairs, others being colored like leaves and 
twigs. But in known cases in which the color- 
ing served to protect the larva it did so by con- 
cealing the animal from its enemies. Gaudy 
colors would expose it to the sharp sight of 
every foe ; how, then, could they serve to pro- 
tect it? By reasoning from these considera- 
tions "Mr. Wallace thought it probable that 
conspicuously colored caterpillars were pro- 
tected by having a nauseous taste." But as 
they are tender, a peck from a bird's beak 
would be fatal. "Distastefulness alone," said 
Wallace, "would be insufficient to protect a 
caterpillar unless some outward sign indicated 
to its would-be destroyer that its -prey was 
a disgusting morsel." Darwin presented the 
reasoning to the Entomological Society, and 
it was supported by statements of the members, 
and afterwards verified by Jenner Weir's ex- 
periments with his birds. The smooth green 
and twig-like larvae were devoured by the 
birds; and the spinous and brightly colored 


ones were rejected with signs of distaste- 

The correlation of brilliant colors and dis- 
tastefulness was thus anticipated as a conse- 
quence of natural selection, the principle of 
protective coloring and the belief that animals 
so protected by obscure colors are attractive to 
their enemies. Darwin immediately seized on 
this result as an opening for further investiga- 
tions, and said : " This view will, it is probable, 
be hereafter extended to many animals which 
are colored in a conspicuous manner." The 
study of animal coloration under Darwin's 
principle of natural selection and the subordi- 
nate principles of mimicry, etc., has been car- 
ried to such a length, or rather the effort to 
explain coloration under these and similar prin- 
ciples has been carried to such a length, that 
one prominent zoologist has felt justified in 
characterizing the speculations of recent years 
on the coloration of animals as a mild form of 
scientific lunacy. There has been an enormous 
amount of wild deduction and half-digested 
observation ; but what is most needed is more 
light on the physiological causes at work within 
the animal and producing and determining the 
distribution of colors. 

It has been mentioned in another place that 


Darwin had concluded that characters inherited 
by both sexes appear early in life, and that char- 
acters restricted to one sex appear late. He 
said, " I was led to infer that a relation of this 
kind exists, from the fact that whenever and in 
whatever manner the adult male has come to 
differ from the adult female, he differs in the 
same manner from the young of both sexes." 
This induction he proceeded to strengthen by 
deduction at both ends. He deduced the law 
from a still more general one, as follows : " It 
is in itself probable that any character appear- 
ing at an early age would tend to be inherited 
equally by both sexes, for the sexes do not 
differ much in constitution, before the power 
of reproduction is gained " ; and in the same 
way characters appearing late in one sex would 
tend to be restricted to that sex. l 

From the other side, he sought to test the 
law by an examination of its consequences; and 
chose the deer family as a crucial instance, upon 
which he felt he could rely. 2 In some species 
of this family the males alone have horns, and 
in one species both sexes have them. If the 
law were true, horns should appear late in 
the species in which they are restricted to the 

1 Descent of Man, etc., Vol. I. p. 276. 

2 Ibid., p. 278 et seq. 


males, and early in the species of which both 
sexes have horns. He found that in seven 
species with horns only on the males the horns 
appear late, at nine months, or even later. 
In the reindeer, which alone has horns on both 
sexes, the horns appear in both sexes at the age 
of four or five weeks. His investigations took 
a somewhat wider range, and he gave other 
illustrations and some exceptions to the law 
among horned animals. 

One of the most striking of his minor efforts 
was his explanation of the origin of the remark- 
able color patterns called " ocelli " on the tail 
of the peacock. 1 He had adopted the theory 
of sexual selection for the explanation of the 
beauty of birds, etc., which did not seem to 
him to admit of explanation under natural selec- 
tion. There are other naturalists who do not 
believe that sexual selection plays the part in 
nature which Darwin ascribed to it. But what- 
ever view is taken of it, it furnished him with 
the indispensable working hypothesis by means 
of which to explain known facts and search for 
others that ought to follow as consequences of 
the hypothesis. It was characteristic of Dar- 
win to select for investigation and explanation 
extreme instances that would put his beliefs to 

1 Descent of Man, etc., Vol II. pp. 132-145. 


the most rigorous test. The ocelli on the tail 
of the peacock furnished such an instance. The 
problem was how to explain the origin of these 
ocelli from the ordinary feather markings of 
the group to which the peacock belongs. 

First, his belief that the colotf patterns of 
many birds are due to sexual selection led him 
to explain the absence of ocelli from the tail- 
feathers of the two species of peacock by the 
fact that these feathers are covered up and con- 
cealed by the long tail-coverts. The theory 
required that the patterns due to sexual selec- 
tion should be exposed to the gaze of the 
females. "In this respect," he said, "they 
differ remarkably from the tail-feathers of Poly- 
plectron, which in most of the species are orna- 
mented with larger ocelli than those on the 
tail-coverts." According to theory, the ocelli 
had disappeared from the tail-feathers and 
been remarkably developed on the tail-coverts 
because the latter by enormous development 
had covered the former. In Polyplectron, in 
which the tail-coverts are not so enormously 
developed, the ocelli were larger on the tail- 
feathers than on the coverts. By the theory, 
however, the markings of the Polyplectron are 
more generalized, and some indications of 
gradations between these two extremes ought 


to exist. " Hence," he said, " I was led to care- 
fully examine the tail-feathers of the several 
species of Polyplectron in order to discover 
whether the ocelli in any of them showed any 
tendency to disappear, and, to my great satis- 
faction, I was successful." His whole study of 
these ocelli is remarkable for the ingenuity 
with which he worked out the consequences of 
his theory and verified them ; and explained the 
intricate pattern as a modification and speciali- 
zation of more general feather-marking. 

Darwin's theory of descent led him to regard 
species as only more strongly marked varieties. 
"From looking at species as only strongly 
marked and well defined varieties, I was led to 
anticipate that the species of the larger genera 
in each country would oftener present varieties 
than the species of the smaller genera." He 
tested this deduction by an extensive tabulation 
of plants and Coleoptera; "and it has invariably 
proved to be the case that a larger proportion 
of the species on the side of the larger genera 
presented varieties than on the side of the 
smaller genera. " 1 

When once he had got hold of natural selec- 
tion as the cause that had brought about the 
adaptations in nature, it was an essential part of 

1 Origin of Species, p. 44. 


the doctrine that only variations favorable to 
the species could be preserved. It was an 
inevitable inference from the nature of the 
cause of adaptations that there could be no 
such thing in nature as an adaptation for the 
exclusive benefit of any other species than the 
one possessing it. Darwin was so confident 
of this deduction, although it could never be 
rigidly verified by observation, that he boldly 
staked the fate of his whole theory on the 
truth of the inference. " If it could be proved 
that any part of the structure of any one species 
had been formed for the exclusive good of 
another species, it would annihilate my theory, 
for such could not have been produced through 
natural selection." 1 He could never know 
from direct observation that there were no such 
cases in existence, but he was driven to the 
assertion of their non-existence by the nature 
of the cause of adaptations. Doubtless this 
deduction gave the severest blow that was ever 
dealt to the belief in general benevolence in 
Nature, and it has proved the final blow. It 
was the apparently awful consequences of this 
inevitable deduction that roused the bitter 
opposition of the religious forces of the world. 
It seemed to establish forever the doctrine that 

1 Origin of Species, p. 162. 


advantage to self is the only invariable motive 
of all the striving in the universe. The moral 
consequences of the theory seemed to outrage 
all the noble ideals that had ever been cherished 
in the world. 

Since the time he made the declaration, there 
have been up for discussion numerous cases of 
adaptation which seemed of no value, or even 
hurtful, to the species possessing them. These 
difficulties have caused a vast amount of stren- 
uous explanatory wriggling under the name 
symbiosis; but there has as yet been no case 
found which can be positively regarded as an 
example of what Darwin said could not exist. 
He had long studied adaptations carefully; but 
the nature of the cause, after he had discovered 
it, helped him to understand more clearly the 
nature of adaptations. 

Good testimony for the necessity of a theory 
of some kind to enable him to work effectively 
is what Darwin wrote to Asa Gray about 
cleistogamic flowers, which are self-fertilized 
and do not open at all. He said, "The tem- 
porary theory which I have formed on this class 
of dimorphism, just to guide experiment, is 
that the perfect flowers can only be perfectly 
fertilized by insects, and are in this case abun- 
dantly crossed; but that the flowers are not 


always, especially in early spring, visited 
enough by insects, and therefore the little 
imperfect self-fertilizing flowers are developed 
to insure a sufficiency of seed for present genera- 
tions. " This temporary theory is now generally 
accepted as the true one. 1 

1 Life and Letters, Vol. II. p. 482. 



IT has been said that a large proportion of 
Darwin's special investigations were started 
as deductions from the general theories of 
descent and natural selection for the purpose 
of corroborating or testing them, and otherwise 
working out their consequences. But before 
turning to these it will be well to notice a 
piece of deductive work not connected with 
those theories; for it is important, both on 
account of his using it himself as an illustra- 
tion of his method and on account of the more 
recent views that have arisen in opposition 
to it. 

The hypothesis concerning the formation of 
coral reefs took its rise as a special application 
of the general rule that depositions are made 
over sinking areas to the coral limestones of 
the west coast of South America. 

The main outlines of his work on coral 
islands were deductive, and so were many of 
the special investigations of details. He spoke 


of the theory of the formation of coral islands 
as the only one of his many hypotheses which 
he had not to modify afterwards, and asserted 
that therefore his study of coral islands was 
more deductive in spirit than any other of his 
investigations. 1 After the theory had held 
sway for forty years in the geological world as 
a complete explanation of coral reefs, it was 
called in question by John Murray, who sought 
to replace it by another which seemed to him 
more reasonable. Murray has found some ad- 
herents; the war of the two theories has been 
waged more or less hotly ever since, and both 
views are still in the field. Darwin's theory 
is not superseded, 2 nor is it likely to be; but 
it will nevertheless be somewhat modified to 
adjust it to the greater knowledge 'of the 
present. Indeed, if Darwin had lived to issue 
another edition of his book, he would have 
taken the new facts into account, as he did in 
his latest correspondence. Here, again, he had 
considered in advance many of the objections 
that have since been raised against his theory. 
But the chief interest of this case is derived 

1 Life and Letters, Vol. I. pp. 58, 83. 

2 Structure and Distribution of Coral Reefs, 3d edition, 
Appendix by Prof. T. G. Bonney; Ibid., Bettany's edition, 
Critical Introduction by Prof. John W. Judd. 



from the facts that he regarded it as the most 
deductive in spirit of all his work, and as the 
only hypothesis which he was not obliged to 
modify, and that scientists have since attacked 
it more severely perhaps than any of his other 

Darwin's approach to the subject of the ex- 
pression of the emotions has already been 
described under Induction. He said, "When I 
read Sir C. Bell's great work [On the Anat- 
omy of Expression], his view, that man had 
been created with certain muscles specially 
adapted for the expression of his feelings, 
struck me as unsatisfactory." 1 This was be- 
cause he had become convinced of the truth of 
evolution, which required him to believe that 
the habit of expressing our feelings by cer- 
tain movements had been somehow gradually 
acquired. This view required that the whole 
subject of expression should be studied under 
a new aspect; "and each expression," he said, 
"demanded a rational explanation. This belief 
led me to attempt the present work." In this 
case the general theory led him only to the 
conviction that there must be some rational 
explanation for each emotional expression; and 
left him to find out inductively the particular 

1 Expression of the Emotions, p. 19. 


nature of the explanations. It will be recalled 
that he reached three principles of expres- 
sion; but only when he had completed his 

Darwin's botanical work was almost entirely 
done under the influence of the theory of evolu- 
tion. His special investigations in this field 
were based on corollaries from the general 
theory. Writing to Mr. Murray, his publisher, 
concerning his book on the "Fertilization of 
Orchids," he said, "It will perhaps serve to 
illustrate how natural history may be worked 
under the belief of the modification of species. " 1 
Equipped with the belief that all adaptations 
are useful to the species possessing them, 
and that innumerable flowers, among them the 
orchids, are adapted for cross-fertilization, he 
studied orchids and the effects of cross- and 
self-fertilization in the same spirit in which he 
had studied coral islands. 

One of the most interesting of the many 
investigations that arose out of his general 
theories was that on climbing plants. As has 
been said, he selected as subjects for special 
research some of the principal difficulties that 
presented themselves for explanation. He did 
this because, if the theories were true, they 

1 Life and Letters, Vol. II., Letter to Murray. 


ought to lead to the right explanations, and 
because he always regarded it as better to 
work out a single typical case or a few typ- 
ical cases thoroughly, in proof of his theories, 
than to offer miscellaneous suggestions on 
many cases. 

Climbing plants offered a case of special 
importance. When once the principles of 
descent and natural selection are adopted as 
working hypotheses, it is a comparatively easy 
matter to explain how a group of closely related 
animals or plants come to possess one or more 
striking characteristics in common. In such a 
case they are all supposed to have inherited the 
characters in question from a common ancestor. 
For example, all the woodpeckers, with their 
peculiar feet and tail and tongue, the last 
with its remarkable apparatus of hyoid-bone 
and muscle, or the various oaks with their 
acorns and cupules, their flowers and leaves, 
are believed to have descended from a com- 
mon stock. The individuals of these groups 
have a great many characters in common. But 
climbing plants are found throughout the plant 
kingdom. Some families contain several or 
many closely related climbers, and these offer 
no special difficulty so far as their mutual pos- 
session of the power to climb is concerned. 


But other large families, normally composed of 
non-climbers, contain one or a few climbing 
species, as, for example, the hop in the nettle 

The power to climb is so striking a charac- 
ter, and is so plainly useful to the plant pos- 
sessing it, that Darwin's theories would be 
taxed with failure if they did not explain its 
origin. But climbing plants are found through- 
out the plant kingdom ; and they are not 
descended from a common climbing ancestor, 
for they possess nothing in common except 
this one power to climb. ''Plants, "he said, 
"become climbers in order, it may be pre- 
sumed, to reach the light, and to expose a 
large surface of leaves to its action and to 
that of the free air. This is effected by the 
climbers with wonderfully little expenditure of 
organized matter in comparison with trees, 
which have to support a load of heavy branches 
by a massive trunk. Hence, no doubt, it arises 
that there are in all quarters of the world so 
many climbing plants belonging to so many 
different orders." The very great advantage 
offered to the climber has acted as a powerful 
premium for the development of the capacity 

1 Journal of the Linnean Society, 1865; Botany, Vol. IX. 
pp. 107, 108. 


wherever variation offered the materials out of 
which natural selection could produce it. 

The first thing to be established in proof of 
the derivation of climbing plants from non- 
climbers was the existence of gradations in the 
power of climbing, and of intermediate stages 
between the different methods of climbing, 
by twining of the stem, by leaf-stalks, and by 
tendrils; just as he connected the ocelli of the 
peacock's tail by a series of gradations with 
the more ordinary feather-markings of related 
birds. But another unknown element was the 
source of the variations upon which natural 
selection could work to produce climbers. In 
his arguments to prove his theories of descent 
and natural selection Darwin showed that 
variations do occur, and that when they occur 
natural selection will inevitably preserve the 
favorable and destroy the unfavorable. But he 
could do little or nothing in the direction of 
pointing out the cause of variations. He has 
been incessantly twitted about this by his 
opponents, especially because of the false 
notion that he ascribed to chance all variations 
whose causes were not known. Ignorance of 
the sources of variation is no obstacle what- 
ever to belief in Darwin's theories; but this 
is true only when the species having a certain 


character in common are proved by many other 
characters to be descended from a common 
stock. In the case of climbing plants the same 
kind of variation must have occurred indepen- 
dently in all parts of the plant kingdom, or 
there must have been a common source or ten- 
dency which served as a starting point for the 
development of the power to climb. 

In his work on climbing plants, first pub- 
lished as a paper in the Linnean Journal, 1 he 
worked out in a masterly way the gradations in 
the power to climb, and between the different 
methods of climbing, showing that all are mod- 
ifications of the method of climbing by twining 
of the stem/ Near the end of his work he said, 
"We have seen how diversified are the move- 
ments of climbing plants. . . . They belong to 
many and widely different orders. . . . When 
we reflect on this wide serial distribution of 
plants having this power, and when we know 
that in some of the largest well defined orders, 
such as the Compos itae, Rubiaceae, Scrophu- 
lariaceae, Liliaceae, etc., two or three genera 
alone out of a host of genera in each, have this 
power, the conclusion is forced on our minds 
that the capacity of acquiring the revolving 

1 Journal of the Linnean Society, 1865, Botany, Vol. IX., 
" On the Movements and Habits of Climbing Plants." 


power on which most climbers depend is 
inherent though undeveloped in almost every 
plant in the vegetable kingdom." 1 

It will be interesting to try to analyze the 
conditions under which he made this definite 
prediction. In his work on climbing plants he 
showed that the power to climb depends on two 
quite distinct powers: (i) the power of spon- 
taneous circumnutation, and (2) sensitiveness to 
touch, and the consequent bending toward the 
side touched. 

Without the theory of descent, the question 
of the origin of the above mentioned sensitive- 
ness could never have arisen at all. With the 
theory of descent, and with natural selection as 
a cause, and a belief in the existence of varia- 
tions for it to work upon, it might have been 
possible to infer some general power or tendency 
in plants as the source of that sensitiveness to 
touch; but it was not done, and from what has 
been said elsewhere it is not likely that it 
would have been done, at least without great 
difficulty, from a knowledge of the highly 
specialized effects. Darwin said, " If we in- 
quire how the petiole of a leaf, or the peduncle 
of a flower, or a branch, first becomes sensitive, 
and acquires the power of bending toward the 

1 Journal, p. 117. 


touched side, we get no certain answer. Nev- 
ertheless, an observation by Hofmeister well 
deserves attention, namely, that the shoots and 
leaves of all plants, whilst young, move after 
being shaken; and it is almost invariably young 
petioles and young tendrils, whether formed of 
modified leaves or flower-peduncles, which move 
on being touched; so that it would appear as 
if these plants had utilized and perfected a 
widely distributed and incipient capacity, which 
capacity, as far as we can see, is of no service to 
ordinary plants." l 

Darwin was in search of a source of the sen- 
sitiveness of plants, and Hofmeister had pro- 
vided it by empirical observation. Darwin's 
relation to this explanation was exactly the 
same as it was in the discovery of the principle 
of natural selection. It will be seen that in 
the latter case he had studied very carefully the 
effects (adaptations) to be accounted for, and 
variations as the material upon which the un- 
known cause might act; then by accidental 
reading of Malthus the cause was presented 
to him, and he brought it and its effects into 
relation with each other by interpreting the 
latter as results of the action of the former. In 
the case of the sensitiveness to touch in plants, 

1 Journal, p. 112. 


he was in possession of the cause (natural selec- 
tion), and the specialized effects and the belief 
that these are the results of the action of natural 
selection upon variations ; Hofmeister furnished 
the material which natural selection could de- 
velop, by the observation that all young plants 
are slightly sensitive to disturbance. 

Now what was the logical setting for Darwin's 
prediction that the capacity of revolving would 
be found inherent, though undeveloped in almost 
every plant in the vegetable kingdom ? If there 
were no evidence to the contrary, it would be 
supposed that he had been able to make the 
prediction from the knowledge that climbing 
plants occur throughout the plant kingdom, 
and that therefore the source of the variation 
must be a general tendency in plants. Such an 
inference seems easy enough to make, as has 
been shown in other cases, after it has been 
made. In this case Darwin had the help of an 
analogy upon which he could depend with con- 
fidence. Hofmeister had furnished, by obser- 
vation, a general source of the sensitiveness of 
climbing plants in the slight sensitiveness of 
young leaves and shoots in general. Sensitive- 
ness to touch and power of circumnutation are 
inseparable in climbing plants; what was more 
natural, therefore, than the inference that the 


power to revolve had its source in an unknown 
general tendency, just as sensitiveness to touch 
had its source in a known slight general sen- 
sitiveness, each power having been developed 
and specialized in climbing plants by natural 
selection? Such an inference would seem al- 
most inevitable. But in addition he was in 
actual possession of a case in which the power 
of revolving was imperfect and functionless. 

He said that when he made the prediction he 
"knew of only one imperfect case, namely, of 
the young flower-peduncles of a Maurandia^ 
which revolved slightly and irregularly, like 
the stems of twining plants, but without mak- 
ing any use of the habit." l In the discussion 
of Maurandia semperflorens, in his original 
paper on climbing plants, he gave the follow- 
ing interesting bit of history : " I should not 
have noticed the present species, had it not 
been for the following unique case. Mohl says 
that the flower-peduncles, as well as the petioles, 
are wound into tendrils." Darwin proved that 
the flower-peduncles do not act as tendrils ; but 
that they nevertheless, whilst young, exhibit 
feeble revolving powers, and are slightly sen- 
sitive to a touch. He observed nine vigorous 
plants, and it was certain to him that neither 

1 Origin of Species, p. 197. 


the slight spontaneous movements nor the slight 
sensitiveness of the flower-peduncles were of 
any service to the plants in climbing. He 
gave reasons for believing that these imperfect 
powers are not relics of former functional power, 
and that correlation of growth did not transfer 
them imperfectly from the internodes and young 
petioles to the flower-peduncles; and said that, 
by whatever means acquired, the case was inter- 
esting to him because these useless capaci- 
ties, by being a little perfected, would make 
the flower-peduncles of this plant as useful for 
climbing as are those of Vitis and other plants. 1 
The important part which the case of Mau- 
randia played in the reasoning is shown by 
what he said concerning it. What he had said 
of the source of sensitiveness to touch he almost 
literally repeated of the power of circumnuta- 
tion : " If we further inquire how the stems of 
petioles, tendrils, and flower-peduncles of climb- 
ing plants first acquire their power of spontane- 
ously revolving, or, to speak more accurately, 
of successively bending to all points of the 
compass, we are again silenced, or at most can 
only remark that the power of movement, both 
spontaneous and from various stimuli, is far 

1 Journal of the Linnean Society, 1865; Botany, Vol. IX. 
pp. 38-40. 


more common with plants, as we shall presently 
see, than is generally supposed to be the case 
by those who have not attended to the subject. 
There is, however, the one remarkable case of 
the Maurandia semperflorens, in which the 
young flower-peduncles spontaneously revolve 
in very small circles, and bend themselves when 
gently rubbed to the touched side; yet this 
plant profits in no way by these two feebly 
developed powers. A rigorous examination of 
other young plants would probably show some 
slight spontaneous movements in the peduncles 
and petioles, as well as that sensitiveness to 
shaking observed by Hofmeister. We see, at 
least in the Maurandia, a plant which might, 
by a little augmentation of qualities which it 
already possesses, come first to grasp a support 
by the flower-peduncles, as with Vitis and Car- 
diospermum, and then by the abortion of some 
of its flowers acquire perfect tendrils." 1 At 
this point he made the prediction already 

To sum up, Darwin based his conclusions 
concerning the source of the power of revolving 
upon the following data: (i) detailed knowledge 
of the nature and extent of the climbing power 
in the plant kingdom ; (2) proof that there are 

1 Journal, p. 113. 


many gradations of structure and function 
between simple twiners and tendril bearers; 
(3) the conviction that all such highly special- 
ized functions and structures are extreme de- 
velopments of more general but less obvious 
phenomena, or of slight variations whose source 
is unknown ; (4) the almost perfectly analogous 
case of sensitiveness to touch in climbing plants, 
which is inseparably connected with the power 
of revolving, and which he had connected with 
the general though slight sensitiveness of plants 
observed by Hofmeister; (5) and one of the 
most important of the data mentioned, the 
actual case of imperfect and functionless power 
of revolving in Maurandia semperflorens, which 
might by a little augmentation become useful 
in climbing. 

The final verification of the prediction is 
embodied in the volume on the " Power of 
Movement in Plants," by Charles and Francis 
Darwin. The sweeping character of the verifi- 
cation cannot be better indicated than by quot- 
ing their own statement of what they intended 
to show in that volume ; it will serve, too, as a 
summary of results, for they completely estab- 
lished what they claimed : " In the course of 
the present volume it will be shown that ap- 
parently every growing part of every plant is 


continually circumnutating, though often on a 
small scale. Even the stems of seedlings be- 
fore they have broken through the ground, as 
well as the buried radicles, circumnutate as far 
as the pressure of the surrounding earth permits. 
In this universally present movement we have 
the basis or groundwork for the acquirement, 
according to the requirements of the plant, of 
the most diversified movements. Thus the great 
sweeps made by the stems of twining plants and 
by the tendrils of other climbers result from a 
mere increase in the amplitude of the ordinary 
movements of circumnutation. The position 
which young leaves and other organs ultimately 
assume is acquired by the circumnutating move- 
ment being increased in some one direction. 
The leaves of various plants are said to sleep 
at night, and it will be' seen that their blades 
then assume a vertical position through modified 
circumnutation, in order to protect their upper 
surfaces from being chilled through radiation. 
The movements of various organs to the light, 
which are so general throughout the vegetable 
kingdom, and occasionally from the light, or 
transversely with respect to it, are all modified 
forms of circumnutation; as, again, are the 
equally prevalent movements of stems, etc. 
towards the zenith, and of roots towards the 


centre of the earth. In accordance with these 
conclusions, a considerable difficulty in the way 
of evolution is in part removed, for it might 
have been asked, How did all their diversified 
movements for the most different purposes first 
arise ? As the case stands, we know that there 
is always movement in progress, and its ampli- 
tude or direction, or both, have only to be mod- 
ified for the good of the plant in relation with 
internal or external stimuli. " 1 

Thus the great work of observation and rea- 
soning began with an effort to explain the power 
of climbing among plants under the theories of 
descent and natural selection; passed on to the 
prediction of the universal movement of cir- 
cumnutation and its verification; and closed by 
explaining all the other highly specialized and 
remarkable movements 'of plants and plant or- 
gans as modifications of the same general but 
unapparent movement. The principal difficulty 
at first was the fact that climbers were found 
throughout the plant kingdom, and could not 
have been descended from a common climbing 
ancestor. By the investigations of Darwin and 
his son, not only were the different methods of 
climbing shown to be modifications of the twin- 
ing movements of the stem, but it and all the 

1 Power of Movement in Plants, p. 4. 


other movements of plants were shown to be 
modifications of a universal movement. What 
was at first a difficulty in the way of evolu- 
tion became, like the structure of the flowers 
of orchids, the ocelli of the peacock,, and the ex- 
pression of the emotions, one of the strongest 
supports of the theory. 




EVERY apparently insignificant fact was 
full of meaning to Darwin; and he made 
it the occasion for what he used to call "fool's 
experiments." His speculative powers em- 
ployed themselves as actively and energetically 
on the details of his investigations as on their 
larger outlines; but he was as ruthless in test- 
ing and rejecting his speculations as he was 
facile in making them. When, however, he 
had once established a principle, he followed 
out the deductions from it with as much confi- 
dence as if he had already secretly seen the 
facts whose existence he suspected or thought 
probable. It is important to note the caution 
with which he usually stated his anticipations, 
and to contrast with it the energy and confi- 
dence with which he sought and worked out 
the facts. He spent his life establishing the 
consequences of his theories, but with all his 
fidelity and persistence he had to leave many 
things unproved; some for lack of time, others 


because of the inaccessibility of the facts. He 
had the satisfaction of living to see the whole 
biological world applying itself to the work of 
bringing out the consequences of his theories. 
It is not a part of the present purpose, even if it 
were possible, to follow out the logical history 
of the subsequent work based on those theo- 
ries. But it will be of interest to notice a few 
instances in which he made deductions which 
he could not verify. Some of these have been 
since verified by others, and some still remain 
unverified. They vary all the way from confi- 
dent predictions to vague expressions of a wish 
that some one would make observations that he 
thought would bear fruit. 

There is one instance of a difficulty in the 
way of Darwin's theories which is of especial 
importance. He outlined a possible explana- 
tion, but the difficulty has proved itself so stub- 
born that even some of his adherents feel that 
his theories could not face many of the same 
kind. The problem is almost exactly similar 
to that of climbing plants, and its interest is 
increased by some recent work that has been 
done towards its solution. 

Electric organs occur in various unrelated 
species of fishes, and differ so widely in their 
position in the body, their mode of innervation, 


etc., that they could not possibly have been 
derived from a single primitive electric organ. 
In this respect the difficulty was exactly similar 
to that of the climbing power in plants. After 
pointing out that the electric organs of the 
different electric fishes are not homologous, 
that they occupy different parts of the body, 
are differently innervated, etc., Darwin said 
that the problem which remains is "by what 
graduated steps these organs have been devel- 
oped in each separate group of fishes. " In the 
case of climbing plants he had been able to 
show many gradations of structure and function, 
that even when not fully developed the power 
to climb was serviceable to plants. He said, 
" The electric organs of fishes offer another case 
of special difficulty; for it is impossible to con- 
ceive by what steps these wondrous organs have 
been produced. But this is not surprising, for 
we do not even know of what use they are." l 

Darwin mentioned, however, as factors for 
the solution of the problem, the great differ- 
ences in the strength of the shocks, the close 
analogy, as he called it, between the electric 
organs and muscular tissue, the electrical phe- 
nomena of ordinary muscle; and called atten- 
tion to our ignorance of the habits and structure 

1 Origin of Species, pp. 150, 151. 


of the progenitors of electric fishes, and added, 
" It would be extremely bold to maintain that 
no serviceable transitions are possible by which 
these organs might have been gradually devel- 
oped." Nevertheless, the subject was unap- 
proachable for him; and his opponents have 
used the electric fishes as one of the greatest 
stumbling-blocks in the way of natural selec- 
tion. Even Romanes felt that the electric 
fishes present so serious an obstacle that if 
there were many such he would have to hold in 
abeyance his belief in the theory. 1 Darwin 
believed that the facts, because they could not 
be explained, did not therefore militate against 
the theory. The much greater difficulty of 
explaining the case of the electric organs com- 
pared with that of climbing plants is due to two 
important facts. In the latter there were at 
least some gradations of structure and function 
known ; and even when both were imperfect, it 
could be shown that they were useful, so that 
natural selection could act upon them. But 
there were no imperfectly developed electric 
organs in fishes which could be appealed to as 
the source from which the perfect organs might 
be developed; and what was still more impor- 
tant, in some of the electric fishes the organs, 

1 Romanes, Darwin and After Darwin. 


though perfect in structure, were apparently 
functionless; they were not known to give off 
any electrical discharge. 

Darwin left the problem unsolved except for 
the suggestions he offered, and it still remains 
unsolved in part. Among the reasons for this 
state of the subject are these : that the habits of 
the electric fishes have been but little known, 
that the powers of the electric organs are but lit- 
tle understood, and that both are very difficult 
to investigate. 

The present state of the subject is made 
interesting by the recent studies of Professor 
Fritsch. 1 From the first the electric organs 
have been regarded as modified muscular tissue. 
They occupy the place of what in other fishes 
is common muscle. The Pacinian law of the 
direction of the current in electric organs -is 
that at the instant of the shock the side of the 
electric plate on which the nerve enters is neg- 
ative, and the opposite side positive; and in 
this important respect such of them as are of 
undoubted muscular origin agree with the com- 
mon muscular tissue and its electrical phenom- 
ena. Fritsch' s interesting recent studies on 

1 Gustav Fritsch, Archiv fiir Anatomic und Physiologic, 
Supplement Band, 1892; Nature, Jan. 19, 1893, Vo1 - XLVII. 
p. 271. 


the Mormyrida of the Nile have removed the 
objection based on the existence of structurally 
perfect electric organs which do not give off 
electric discharges. He showed that these deli- 
cate little fishes, hitherto regarded as pseudo- 
electric, are really capable of giving off shocks 
that can be felt by the hand and can be easily 
measured with instruments. He has also shown 
that in these fishes a part of the organ is in 
a state of transition from muscular to electric 
tissue. At the posterior end the electric organ 
is sharply set off from the muscular tissue; 
but at the anterior end it graduates more or 
less perfectly into the muscular tissue, and the 
organ seems to be actually developing in that 

A special difficulty lay in the fact that in 
MalapteruruS) an African fish, in which the 
electric organ lies beneath the skin and encases 
the body like a sheath, the electric current does 
not obey the Pacinian law, but takes the oppo- 
site direction. Fritsch removed the whole diffi- 
culty by giving reasons for the belief that in 
this case the organ is not of muscular but of 
cutaneous origin, and represents the cutaneous 
glands that are so plentiful in some parts of 
the body. Such an exception, without the ex- 
planation of Fritsch, would confuse the whole 


problem of the relation between muscle and 
the electric organs. With the explanation, it 
furnishes a good example of how investigation 
dissolves difficulties. 

It is a common saying that the solution of 
one problem leads to new and frequently more 
difficult ones. It may almost be said an inves- 
tigation should be viewed with suspicion if it 
does not leave more new problems than it started 
out to solve. The belief of Fritsch that the 
electric organs of Malapterurus are homologous 
with the cutaneous glands opened up a new 
phase of the general problem of the origin of 
electric organs. Another difficulty presented 
itself to Fritsch in the process of solving the 
original problem which he set before himself. 
In his study of the innervation of the electric 
organs of Mormyrus he found that the nerves 
which supply the electric organs decussate, or 
cross from one side of the body to the other, 
after leaving the spinal cord as anterior roots, 
much as the optic nerves form the optic 
chiasma within the brain-case. There is no 
similar case known of nerve fibres crossing 
from one side of the body to the other after 
they have left the central nervous system ; and 
Fritsch properly thinks it to be more difficult 
to explain by gradual variation and natural 


selection than the origin of the electric organs 
themselves. He has suggested that this re- 
markable peculiarity has been developed to 
insure perfect co-ordination between the elec- 
tric organs of the two sides of the body, with- 
out which there could not be perfect unity of 
action in the electric discharge, whereas while 
the tissue is merely muscular it is important 
that the organs of the two sides should act 
independently of each other. 

Fritsch has also called attention to the fact 
that the sluggish powerfully electric fishes are 
carnivorous, and the active feebly electric spe- 
cies are at least mostly herbivorous. 

More recently still, Professor Engelmann, 1 
of Utrecht, in a histological study of the elec- 
tric organs in embryos of Raja clavata, etc., 
has established in detail the genetic relations 
between some of the elements of cross-striped 
muscle-fibre and the lamellae of the so called 
meandrine or striped layer which, lying be- 
neath the nerve end-plate in most species of 
Raja, forms one of the principal constituents of 
the electric organs in the tail of these fishes. 
Hitherto little more had been known than that 

1 Th. W. Engelmann, Archiv fur die Gesammte Physiolo- 
gic des Menschen und der Thiere, Band LVII. pp. 149-180, 
June 1 6, 1894. 


such relations existed. The whole problem has 
advanced much farther toward a solution on the 
morphological than on the physiological side; 
but, as might have been expected, the demon- 
stration of the exact relations between the 
various elements of muscle-fibre and those of 
the electric organs has enabled Engelmann to 
indicate some very important and fruitful lines 
for physiological experiment. 

Although the homology of cross-striped mus- 
cle-fibre and the constituents of the electric 
organ has been proved even to many histo- 
logical details, and the morphological changes 
by which the former has been transformed into 
the latter have become quite clear, the diffi- 
culty of explaining the development of electric 
organs from muscular tissue by means of natural 
selection is as great as ever. Engelmann has 
significantly suggested the existence of func- 
tions that we are entirely ignorant of; and 
refers, by way of illustration, to the recent 
remarkable discoveries of the effects of the 
removal, partial and complete, and grafting of 
the thyroid gland, 1 and to Brown-Sequard's 
demonstration of the existence of an extremely 
important "internal secretion" in the renal and 

1 Archives de Physiologic Normale et Pathologique, 1890- 
1894, and elsewhere. 


other glands. 1 He has marked out a new field 
of physiological research on the problem of 
electric organs by the suggestion that the 
marine biological laboratories be taken advan- 
tage of to study the effects which the partial or 
total removal, or destruction, transplantation, 
etc. of those organs in various stages of onto- 
genetic and phylogenetic development will have 
on the normal functions of the animal. He 
believes that it might thus be quickly shown 
that these so called useless organs do serve an 
important function in the animal economy, and 
that it might be made clear what that function 
is ; or that it might at least be shown what injury 
their absence entails upon the animal. 

It must be remembered that the problem of 
electric organs has not yet been attacked in any 
such way as that in which Darwin attacked the 
problem of climbing plants. Fritsch by two 
brief visits brought to light many important 
facts; on the morphological side contributions 
are steadily made, but the knowledge on the 
subject up to date has been brought out piece- 
meal. Before the mode of development of elec- 
tric organs can be fully understood, there will 
have to be not only knowledge of the electrical 

1 Ibid., Series V., Vol. V. pp. 778-786, October, 1893, and 


phenomena of muscle in general, but a thorough 
investigation of the normal electrical phenom- 
ena of fish-muscle, and of the efficacy of slight 
shocks in water; the habits and environments 
of the electric fishes, their enemies and their 
prey, need to be carefully studied. When the 
investigation is set going on a large enough 
scale, and along all the lines on which there 
is at present little more than dense ignorance, 
there will be in the minds of those who have 
attended closely to the principal biological 
investigations of recent years no doubt about 
the outcome. The logical processes involved 
in the solution of such problems under the 
influence of a general theory are practically the 
same, whether the work is done by one man or 
by a number of men who attack the problems 
simultaneously or in succession. 

The unverified deduction in the following 
example is interesting on several accounts, 
(i) The prediction involved what seemed to 
many entomologists an improbability. (2) The 
prediction has not been verified, but the im- 
probability has been removed. (3) It has been 
often quoted even by naturalists as a case of 
verified prediction. Angrczcum scsquipedale, 
an orchid native to Madagascar, has a long 
whip-like nectary. On several flowers -Darwin 


found it eleven and a half inches long, with 
only an inch and a half of nectar at the bottom. 
He proved to his own satisfaction, by a study of 
the structure of the flower, that it is fertilized 
by moths that thrust their proboscides and heads 
down into the flower to the utmost, and declared 
that moths with proboscides long enough to 
reach the nectar must exist in Madagascar. 
"This belief of mine," he said, "has been ridi- 
culed by some entomologists ; but we now know 
from Fritz Miiller that there is a sphinx moth 
in South Brazil which has a proboscis of nearly 
sufficient length, for when dried it was between 
ten and eleven inches long. When not pro- 
truded, it is coiled up into a spiral of at least 
twenty windings." The moth with the long 
proboscis has not yet been discovered in Mada- 
gascar; but the fact that there are moths else- 
where with proboscides as long as the one 
required in- the case of Angrcecum has removed 
the improbability from the prediction. But the 
point to be borne in mind is this, that the firm 
conviction that orchids are fertilized by insects, 
and that the flowers and insects are co -adapted 
in structure, led Darwin to believe firmly in an 
" improbable thing.*' l 

The questions raised in Darwin's mind by 

1 Fertilization of Orchids, pp. 162-166. 


his own theories were innumerable; some of 
them he answered by the great investigations 
already mentioned, others he left unanswered 
for various reasons. Only about two months 
before his death he pointed out new lines of 
investigation. Among other things he said 
that there were many inconspicuous flowers not 
known to be visited by insects during the day, 
and the natural inference is that they are self- 
fertilized. And he pointed out the desirability 
of finding out whether these flowers are visited 
at night by the innumerable individuals of the 
many species of minute moths. If they are not 
so visited, why do they expand at all ? Why 
are they not cleistogamic ? He suggested, as a 
mode of procedure, smearing the flowers with 
viscid matter and then looking for insect scales; 
but gave the caution that it would be necessary 
to prove that the matter employed was not in 
itself attractive to insects. 1 

It is a fascinating study to follow out the 
suggestions that came to him and that he made 
to others, to note the various degrees of success 
with which the investigations were made by 
others, to compare the spirit and methods with 
which they were made with Darwin's own spirit 

1 Miiller, Fertilization of Flowers, Prefatory Note, by 
Charles Darwin. 


and method. He knew the importance of study- 
ing the speech of monkeys in relation to his 
belief in the descent of man, and expected valu- 
able results from it. "I wish," he wrote to 
Asa Gray, " some one would keep a lot of the 
noisiest monkeys, half free, and study their 
means of communication." 1 Mr. Garner has 
recently written magazine articles and a book 
on the subject, and has even visited the ape 
country in Africa with elaborate arrangements 
for studying the speech of monkeys in their 
native haunts. It is too early to forecast re- 
sults, but this case illustrates well how different 
phases of Darwin's theories have attracted dif- 
ferent types of men, and how caution or the 
want of it may make or break confidence in the 
results of their investigations. 

1 Life and Letters, Vol. II. p. 183. 



CONSIDERED simply as a logical process, 
^-^ deduction is no more interesting in the 
hands of the modern investigator than it was 
in the hands of the mediaeval schoolman. The 
scientist uses it, apart from its importance in 
proof, or effort to convince others, merely as an 
instrument with which to test what is known, 
and to develop its unknown consequences. The 
infallibility of the process is altogether hypo- 
thetical. The conclusion is true only if "the 
premises are true; and since the truth of the 
premises is oftener the matter in question than 
even the investigator dreams, the effort to get 
at new truth by anticipating the consequences 
of theory often results in false conclusions. 
This must especially be the case when there is 
no apparent reason to question the truth of the 
premises ; when they would seem to have been 
permanently established by repeated crucial 
tests. In a number of instances Darwin went 


clearly wrong in his deductions. Some of them 
he corrected himself, for some he accepted the 
corrections of others ; and some have never yet 
been corrected directly, but only by the adop- 
tion of the contrary principle from a study of 
facts similar to those on which Darwin went 
wrong. When his attention had become fixed 
upon the cowslip (Primula veris), he found that 
there were two forms of flowers on plants of 
this species. He said, "The first idea which 
naturally occurred to me was, that this species 
was tending towards a dioecious condition; that 
the long-styled plants, with their longer pistils, 
rougher stigmas, and smaller pollen grains, were 
more feminine in nature, and would produce 
more seed; that the short-styled plants, with 
their shorter pistils, longer stamens, and larger 
pollen grains, were more masculine in nature." 1 
Nothing would seem more natural than that the 
structural differences between the flowers should 
indicate differences in sexual function. The 
knowledge of dioecious plants and belief in the 
modification of species could plainly suggest but 
one interpretation of the structural differences of 
the two kinds of flowers. Either they indicated 
what was inferred from them, or they could 

1 Different Forms of Flowers on Plants of the same 
Species, pp. 18-21. 



indicate nothing at all. Had his conclusion 
been left at this point, it would probably have 
been accepted as both interesting and quite cer- 
tain. The degree of certitude with which such 
an inference is received depends on the number 
of facts involved, their relation to each other, 
and the degree to which they act as convergent 
evidence toward the one conclusion. In these 
respects the facts were all that could be desired. 
It would seem that, if it is possible to make any 
inferences at all concerning function from the 
structure of plants, it would have been so in this 

For Darwin, as for every true student of 
nature, deductions exist only to be verified. 
The indirect evidence from structure he supple- 
mented by experiments on the actual produc- 
tion of seed by the two forms. He might have 
pointed with pride to the cowslip as a plant in 
an actual state of transition, as a fine illus- 
tration of his theory. But after describing in 
detail the differences of structure in the two 
forms of flower in the cowslip, he said, "The 
question seems well worthy of careful investi- 
gation." He made preliminary experiments 
which of themselves would have been conclu- 
sive, but used them to lay a basis for his much 
more extensive experiments; they suggested 


methods, furnished cautions, and brought out 
facts enough to determine the most important 
directions of investigation. He marked a few 
plants of each form in his garden, in a field, 
and in a shady wood, and gathered and weighed 
the seed. In all the lots the short-styled plants 
yielded, contrary to his expectation, most seed. 
He gave tables of results, and added that "by 
all these standards of comparison the short- 
styled form is the more fertile." In 1861 he 
made fuller and fairer trials, and found that 
the same result also held good for some other 
species of Primula. " Consequently my anticipa- 
tion that the plants with longer pistils, rougher 
stigmas, shorter stamens, and smaller pollen 
grains would prove to be more feminine in 
nature, is exactly the reverse of the truth." 

The facts on which his first inference was 
based were easy to observe; they corroborated 
each other in a remarkable way, and harmonized 
perfectly with what was well known concerning 
dioecious plants. There was no reason to sus- 
pend judgment, for there were no facts that 
obtruded themselves as objections to the infer- 
ence. Now if under such circumstances an 
inference turns out to be exactly the reverse of 
the truth, what guaranty is there that a conclu- 
sion will be correct in any case ? The answer 


was given in Darwin's researches. The evi- 
dence was not all in. The structural evidence, 
instead of serving as a basis for a true inference 
concerning the functions of the organs, was 
found to be in contradiction with them. Darwin 
showed that both sets of facts were dependent 
on a hitherto altogether unknown phenomenon, 
the differentiation of the flowers of a species 
into distinct sets with marked structural differ- 
ences for the purpose of making cross-fertiliza- 
tion almost absolutely certain. 

The following case is perhaps as interesting 
as it could be made, to illustrate the danger of 
accepting as truth inferences that fall short of 
demonstration, and only represent a high degree 
of probability. In all the books that Darwin 
had consulted Enonymus Europeans (spindle- 
tree) is called hermaphrodite. But he found 
from an examination of the species that about 
half of the individuals had both stamens and 
pistils of normal size, and were therefore her- 
maphrodite; and that the remaining half had 
pistils of the normal size, but short stamens with 
rudimentary anthers without pollen, and were 
therefore properly females. The ovules were 
of equal size in the two forms. There could 
not possibly be any other conclusion from the 
structure of the flowers than the one he sug- 


gested, that half of the plants, with perfect 
flowers, were hermaphrodite, and the other half, 
with rudimentary stamens and anthers and no 
pollen, were female. What were the centuries 
of study on plant structure worth, if it was not 
safe to accept the conviction that female organs 
of normal size are present for the bearing of 
seed? Darwin said, "The most acute botanist, 
judging only from structure, would never have 
suspected that some of the bushes were in func- 
tion exclusively males." 1 As in the previous 
example, he sought to verify his inference by 
watching the fruit. He watched thirteen bushes, 
eight females and five " hermaphrodites. " 
The females yielded abundant fruit, and a 
single branch two or three feet long from one 
of them yielded more than any one whole bush 
among the "hermaphrodites." The inference 
from structure was almost completely reversed. 
The species seemed to be practically dioecious, 
with the stamens aborted in the females, but 
the pistils apparently normal in the individuals 
that were almost exclusively male in function. 
He might here again have rested the case, and 
recorded the spindle-tree as dioecious. 

But hear him : " I now determined to observe 
more carefully during successive seasons some 
1 Different Forms of Flowers, etc., pp. 287-292. 


bushes growing in another place about a mile 
distant." He did so, and found some variability 
among the females in the power of producing 
fruit and seed, and great variability in the 
"hermaphrodites," the latter never producing 
as much or as fine seed as the other. At this 
third stage it was clear that the plants of the 
spindle-tree are neither part of them female and 
part hermaphrodite, nor part of them female and 
the rest, with both sets of organs, practically 
male in function. The truth lay between the 
two extremes, the variations in the one or other 
direction depending even on the character of 
the season. He said, " This case appears to me 
very interesting, as showing how gradually an 
hermaphrodite plant maybe converted into a 
dioecious one." The final result of the long 
drawn out investigation was in harmony with 
his general doctrine of the descent of species, 
and is an illustration of some of the best evi- 
dence that has yet been adduced in its support. 
To him it was interesting, because it showed 
how gradually an hermaphrodite plant may be 
converted into a dioecious one. To the student 
of scientific method it is interesting as an 
example of how an investigation, by stopping 
short of exhaustion of the field, may lead, not 
only to imperfect, but to false conclusions. 


In the work on the Fertilization of Orchids 
Darwin's sagacity found full play in the inter- 
pretation of the structure of orchids in ac- 
cordance with the principle of adaptation for 
cross-fertilization. Confident that all the mar- 
vellously complex structures of orchidaceous 
flowers were adaptations for cross-fertilization, 
he regarded each case only as presenting a 
question with regard to the particular mode of 
the mutual action of the insect and the flower 
organs. He was frequently able to predict this 
mutual action in the case of particular species. 
He never for a moment lost faith in the prin- 
ciple; but in at least one case he went wrong in 
his interpretation by not applying the principle 
rigorously enough. 

In the Cypripedium t or Lady's Slipper, there 
are two small orifices near the anthers and one 
large opening in the labellum or odd petal. 1 
After discussing the structure of the flower he 
said, " Formerly I supposed that insects alighted 
on the labellum and inserted their proboscides 
through either of the small orifices close to the 
anthers " to extract the nectar. This inference 
seemed plausible enough; the small orifices 
seemed well adapted to accomplish cross-fertil- 
ization because they were close to the anthers, 

1 Fertilization of Orchids, pp. 229-231. 


and an insect would inevitably remove the pol- 
linia if it inserted its head into one of them. 
But he had not clung closely enough to his 
general principle. Darwin himself accepted 
the correction of his inference as follows : 
"Delpino, with much sagacity, foresaw that 
some insect would be discovered " to remove 
the pollinia by entering the labellum by its 
large opening, and crawling out through one of 
the orifices near the anthers; "for he argued 
that if an insect were to insert its proboscis, as I 
f had supposed, from the outside through one of 
the small orifices, the stigma would be liable 
to be fertilized by the plant's own pollen; and 
in this he did not believe, from having con- 
fidence in what I have often insisted on, 
namely, that all the contrivances for fertiliza- 
tion are arranged so that the stigma shall 
receive pollen from a distinct flower or plant. 
But these speculations are now superfluous ; for, 
owing to the admirable observations of Dr. H. 
Miiller, we know that Cypripedium calceolus, in 
a state of nature, is fertilized in the manner 
just described." 

Darwin's error in this case consisted in not 
considering one of the important elements of 
his principle of adaptation for cross-fertiliza- 
tion, namely, the importance, not only of 


favoring cross-fertilization, but of protecting 
the stigma against self-fertilization. When this 
is considered, the direction in which the insect 
entered would appear much more important 
than comparative ease in getting at the nectar 
or proximity of the orifices to the stamens. 

One of the most remarkable cases of over- 
sight in Darwin's work occurred in connection 
with the Venus' Fly-trap. This plant is re- 
stricted to a very narrowly limited locality in 
North Carolina, and its organs are highly differ- 
entiated for the purpose of catching insects. 
Darwin could not reconcile the very limited 
range of so highly specialized an insectivorous 
plant with his general belief that the best 
adapted plants and animals spread over the 
earth and survive. In his discussion of Dioncea, 
(Venus' Fly-trap), he said, " It is a strange fact 
that Dion&a, which is one of the most beauti- 
fully adapted plants in the vegetable kingdom, 
should apparently be on the high road to ex- 
tinction. This is all the more strange as the 
organs of Dioncea are more highly differentiated 
than those o f Drosera." l 

All the studi^ of forty years had borne out 
the conviction that the adaptations of animals 
and plants to their environment were the result 

1 Insectivorous Plants, p. 358. 


of natural selection acting upon variations, and 
preserving those that conduced to the preserva- 
tion of the species. Following this principle, 
it seemed almost self-evident that the more 
highly specialized the organs of a plant or 
animal are, and the more minutely adapted to 
its surroundings and mode of life they become, 
the more certain would the species be of con- 
tinued existence and of success in the race of 
life. He never, so far as I know, recognized 
the inevitable consequence of extreme special- 
ization. Had he pursued the deduction to the 
end, he must have recognized the fact that a 
high degree of specialization for a particular 
mode of life is the mess of pottage for 
which the birthright of the species has been 

Darwin was familiar with, and recognized 
the value of Agassiz's generalization that the 
progenitors of the greater animal and plant 
groups have been generalized forms. He him- 
self deduced from his general theory the prin- 
ciple that the species of the larger genera, 
the wide ranging, much diffused, and common 
species vary most, that they are more closely 
related to each other, and that in this respect 
they more nearly resemble varieties than do the 
species of the smaller genera with restricted 


distribution. 1 It is clear that the wide range 
of a species, instead of depending on a high 
degree of specialization for any one environ- 
ment, depends rather on the absence of it. He 
clearly recognized and pointed out the danger 
of extinction to a species of limited range, but 
nowhere recognized explicitly the connection, 
on the one hand, between a high degree of 
specialization for a particular environment or 
mode of life and restriction of the species to 
that particular environment, or the relation, on 
the other hand, between wide range over the 
earth and generalized characters which give 
some general advantage that would be useful 
under all or nearly all circumstances into which 
the species might be thrown. 

He said: "If we ask ourselves why this or 
that species is rare, we answer that something 
is unfavorable in its conditions of life; but 
what that something is we can hardly ever tell." 
He insisted that the improved and modified 
forms would crowd out and exterminate the less 
well adapted forms; but did not hit upon the 
truth that, the more beautifully adapted a 
species is to a definite locality and set of con- 
ditions, the less it is adapted to enter into a 
general competition for the possession of the 

1 Origin of Species, pp. 42-44. 


earth. Both Agassiz's empirical generaliza- 
tion that the progenitors of the principal plant 
and animal groups were generalized forms, 
and the deductive consequences of Darwin's 
own theory of natural selection would indicate 
that the highly differentiated forms are forever 
handicapped. They have a present advantage 
in having intensified their adaptation to a cer- 
tain environment; but in the long run they 
are doomed because they have lost the power 
of adaptability to new conditions in direct 
proportion to their present gain. 

It is curious that Darwin had before him, 
and mentioned in the same sentence, a case of 
each kind: Dioncea, with its extreme adapta- 
tions for insect catching, with only a single 
species in the genus, restricted to a very small 
locality, on the verge of extinction ; and Drostra, 
with the same general advantage of catching 
insects, but with no extreme adaptations, with 
a vast number of species in the genus, dis- 
tributed all but everywhere over the earth. It 
is as great a surprise that he did not see the 
connection between extreme specialization and 
extinction on the one hand, and general advan- 
tage and wide distribution on the other, as he 
says it was to him that Dioncza is on the verge 
of extinction. It is clearly inferable from 


these cases and the general principle of natural 
selection that Nature has pronounced the sen- 
tence of death upon highly specialized forms; 
that they have passed out of the royal line of 
descent for a special advantage; that if they 
vary at all it can only be within the restricted 
lines along which they have already gone so 
far; and that the birthright belongs to forms 
which have some general advantage, but are 
not hampered by special adaptations. These 
spread over the earth and from them branch 
off the numerous closely related and variable 
species that occupy all the environments of the 
earth. Thus Drosera, with its power to catch 
insects, is yet a plant like others, and has gone 
forth with its advantage to possess the earth. 
Vitis, with its climbing power, has scattered 
its species by the hundred over the earth. It 
is the modification that opens up to the species 
a large area, which makes it possible for the 
species to send out its kind into the whole 
earth to be everywhere modified by local influ- 

The principle that has been discussed is now 
one of the well understood corollaries of the 
principle of natural selection. I do not know 
who first called attention to it. It has prob- 
ably occurred to many minds independently. 


Darwin, so far as I know, never recognized it. 
The earliest clear statement of it that I have 
seen is by Prof. Joseph Le Conte in an article 
on "Instinct and Intelligence," 1 published in 
1875, on ly a f ew months after the publication 
of Darwin's " Insectivorous Plants. " He said, 
"Instinct, therefore, is accumulated experi- 
ence, or knowledge of many generations fixed 
M permanently and petrified in brain-structure. 
All such petrifaction arrests development, be- 
cause unadaptable to new conditions. They are 
J ound, therefore, only in classes and families 
J^jJjjy^ widely differentiated from the main stem of evolu- 
tion, from the lowest animals to man. Instincts 
are, indeed, the flower and fruit at the end of 
these widely differentiated branches, but flower- 
ing and fruiting arrest onward growth." In 
1877, Marsh, in a discussion of the suilline 
type, stated the true principle when he said 
that ambitious offshoots have perished, while 
the generalized or rather unspecialized forms 
continue the line of life with true suilline 
stubbornness. 2 

1 Popular Science Monthly, October, 1875, P- 664. 

2 American Journal of Science, XIV. (III.), pp. 362-364. 



DARWIN'S general discussions of the 
various subjects that he worked out in 
such minute detail are models both of clearness 
and of exhaustiveness. The reasoning of the 
second volume of the "Variation of Animals 
and Plants under Domestication " is long sus- 
tained and characterized by the use of enor- 
mous numbers of facts. The latter is one of 
the chief characteristics of his reasoning. He 
was frequently compelled, as in the case of 
the "Origin of Species," by the limits within 
which he was obliged to condense his materials, 
to substitute general statements for long series 
of facts. The generalizations were condensa- 
tions of the detailed facts, which were too 
bulky for his pages. This is the reason why his 
discussions leave the impression of an almost 
infinite reserve of evidence; and rightly seem 
to convey much more to the reader than is 
actually written on the page. 

Among Darwin's many exhaustive discus- 


sions of the materials which he had collected, 
some of the most striking are his chapters on 
pigeons, 1 in which he considered the variation 
of breeds, individual differences, and skeletal 
differences; the discussion in the second volume 
of the "Variation of Animals and Plants under 
Domestication " ; the exhaustive analysis of his 
materials in reaching his general conclusions 
on the effects of cross- and self-fertilization; 
and his repeated discussions of the cement 
glands of Cirripedia, and of the parasitic and 
complemental males on the hermaphrodite 
"females," and the reasons for regarding them 
as such rather than as independent forms. 2 
But the general discussion that is typical both 
from the general interest of the subject and 
the compactness and symmetry of the argument 
is the work on the " Origin of Species."" It 
would be impossible to analyze such a far- 
reaching argument without restating it. Doubt- 
less criticisms could be made against the 
arrangement of materials and the order of dis- 
cussion, and against the nature of the evidence 
adduced. It is not intended here to raise the 

1 Variation of Animals and Plants under Domestication, 
Vol. I. pp. I37-235- 

2 Monograph of Cirripedia, Vol. I. pp. 38, 180-293, Vol. II. 
pp. 23-30, 151. 


question whether his argument as a whole is 
sound and carries conviction with it, but simply 
to repeat that, considering the materials that 
Darwin had to work with and the difficulties 
under which he labored, the argument is 
finished, and will always serve as a type of 
probable proof. 

Darwin himself has given the reasons for 
this state of his great discussion. He has com- 
plained that he must be a very slow thinker; 
and doubtless the truth in this complaint 
accounts for the fact that his thinking was 
always so thorough. He also bewailed the fact 
that he experienced great difficulty in writing. 1 
He felt that he had great ability to get things 
wrong end foremost in his expression, and said 
that he spent a great deal of time in arranging 
the matter in his larger works. From one 
point of view it is a paradox that such a man 
should accomplish so much that has proved 
of permanent value. But the lack of natural 
felicity of expression and inability to think 
rapidly, together with his persistence, insured 
him against the vice of saying things nimbly, 
and furnished the guaranty that whatever he 
did would be thorough. It is safe to say that 
a far larger proportion of false and inaccurate 

1 Lifs and Letters, Vol. I. p. 80. 


statements and arguments with fatal flaws in 
them are made by writers who express them- 
selves easily, than by writers whose rhetorical 
inability compels them to be painstaking. 
When the expression is laboriously evolved by 
an intellect that is otherwise strong, the thought 
comes during the process to be regarded from 
more points of view. In details there is greater 
assurance of accuracy, and the proper relative 
importance is more likely to be assigned to the 
different phases of the truth. Given two intel- 
lects equally conscientious, the slower moving 
and more deliberate one will always hit upon 
more phases of the truth than the quicker one. 
Darwin attributed the success of the " Origin 
of Species" to the way in which it was devel- 
oped. Only when he had spent a number of 
years in investigation, after he had got hold of 
the theory of natural selection, did he allow 
himself, in 1842, to draw up a brief thirty-five 
page sketch of it. In 1844 he wrote a larger 
sketch of two hundred and thirty pages. Then 
followed years of laborious investigation, the 
vast results of which were cast into an abstract 
which, if it had been published, would have 
been a very large work. Upon the urgent 
advice of his friends, Lyell and Hooker, he 
decided not to delay publication any longer; 


but the large work was not in condition for 
publication. An abstract of it was made; and 
this abstract was the " Origin of Species." He 
had written two condensed sketches, and finally 
abstracted a much larger manuscript which was 
itself an abstract. 1 Probably no work was ever 
better tempered and tested before it reached 
the public eye. 

1 Life and Letters, Vol. I. p. 70. 



T^vARWIN'S own views of method, his treat- 
L ^ ment of evidence, and some of the 
various logical processes which he employed in 
his investigations, having been discussed and 
illustrated by examples from his many works, 
it now remains necessary to trace the logical 
history and examine the present logical status 
of the principle of natural selection, which gave 
inspiration to and lay at the basis of his life- 
work. The theory of natural selection has per- 
meated and colored modern thought more deeply 
than perhaps any other scientific theory, and 
this fact alone makes the study of its logical 
history extremely interesting. 

The scientific influences, both in the form 
of teachers and of books, to which Darwin was 
exposed during and after his university life, 
were opposed to the already well known doc- 
trine of the descent of species. Various reasons 
have been assigned for the failure of the doc- 


trine to impress itself upon scientific men. 
The difficulty did not lie in the circumstance 
that the facts of botany and zoology were 
opposed to it; for it first took its rise out of 
them. The affinities of species and of the 
higher groups, and the facts of embryology, 
distribution, and palaeontology by themselves 
were sufficient to force the conviction that 
species are derived, and the doctrine would 
doubtless have won its way at once had it not 
had to make head against the imported belief 
in creation. Had the doctrines of descent and 
creation been for the first time presented to the 
scientific mind as alternative beliefs, there can 
be no doubt that the former would have been 
chosen as the true explanation of the facts, 
even though no force capable of producing the 
effects had been assigned. The cause would 
still remain to be investigated, while the facts 
would be brought together under a single point 
of view. With the adoption of creation as an 
explanation, an efficient cause is provided, but 
the facts remain worthless either to prove or 
to disprove the doctrine. It is not enough that 
a cause should be capable of producing given 
effects, but it should produce the given effects 
and be incapable of producing any other set 
of effects. In short, by the former view the 


special character of the facts is accounted for, 
but from the latter it is impossible to deduce 
the specific character of any phenomena. Any 
other set of facts exhibiting a plan or purpose 
of any kind could be deduced with equal ease 
from the doctrine of creation. 

When Darwin started on the Beagle voyage 
he was orthodox on the question of the ori- 
gin of species. As he travelled, and as his 
knowledge of zoology and palaeontology became 
wider and deeper, the doctrine of descent began 
to take hold of him. The relation of the liv- 
ing animals to the fossil species in South 
America, the manner in which closely allied 
animals replaced one another as he proceeded 
southward over the continent, the South Amer- 
ican character of the productions of the Gala- 
pagos archipelago, and especially the slight 
but distinct differences of the flora and fauna 
on neighboring islands of the archipelago, im- 
pressed him so strongly with the peculiar char- 
acter of the facts and the necessity of a definite 
mode of origin that he began to see the differ- 
ence in the logical characters of the doctrines of 
creation and descent 1 The facts were better 
explained by the latter than by the former; and 
he connected them at least tentatively with the 

1 Life and Letters, Vol. I. p. 67 ; Origin of Species, p. 2. 


old doctrine of descent. But as he himself 
remarked, a naturalist might be convinced by 
affinities, embryology, distribution, etc., that 
species are derived by descent; but the conclu- 
sion, though correct, would be unsatisfactory 
until it was shown how it was brought about. 

Lamarck had assigned causes for the modifi- 
cation of species ; but Darwin insisted positively 
that he derived no help whatever from him. 
Logically, the failure of the former's doctrines 
to win over the scientific world was due to his 
connecting the doctrine of descent, which had 
strong evidence in its favor, with hypothetical 
causes which he did not subject to rigid de- 
ductive tests in explanation of the facts. What 
kept Darwin longest orthodox were the facts 
of adaptation. No cause could be considered 
adequate which did not account for the exqui- 
site adaptation to environment found through- 
out the animal and plant kingdoms. As he 
said himself, " I had always been much struck 
by such adaptation, and until these could be 
explained it seemed to me almost useless to 
endeavor to prove by indirect evidence that 
species have been modified." 1 He distin- 
guished clearly in his own mind between the 
two propositions which he undertook to prove 

1 Life and Letters, Vol. I. p. 67. 


in the " Origin of Species " : first, that species 
are derived by modification from other species, 
and, secondly, that Natural Selection is the 
chief cause of this modification. He did not 
originate the former; the logical relation of his 
work to it is deductive, and largely took the 
form of an answer to the question, Do the facts 
of Nature harmonize with the hypothesis? 

The cause of the modification of species could 
not even be raised as a question until the fact 
of modification had been accepted, at least ten- 
tatively. He recognized the cause of specific 
modification as a problem to be solved, a prin- 
ciple to be discovered by induction from the 
effects it produced in the form of adaptations. 
To quote his own words: "My first note-book 
was opened in July, 1837. I worked on true 
Baconian principles, and without any theory 
collected facts on a wholesale scale, more 
especially with respect to domesticated pro- 
ductions," etc. 1 He had rejected Lamarck's 
suggestions, and it would seem impossible to 
imagine a more interesting or more purely 
inductive problem than that which presented 
itself to him. There was for him no clew to 
the cause which he wished to discover except 
in the vast wealth of material which he regarded 

i Life*nd Letters, Vol. I. p. 68. 


as its effects. To have discovered the cause 
by an analysis of the effects would indeed have 
been a triumphant inductive discovery. 

He selected wisely the material on which 
to concentrate the investigation ; he said : " I 
soon perceived that selection was the keystone 
of man's success in making useful races of 
animals and plants. But how selection could 
be applied to organisms living in a state of 
nature remained for some time a mystery to 
me." In his study of domestic races he ob- 
served both the effects (races) and the cause 
(selection), and did not, except perhaps in 
details, reason deductively from the cause to 
discover the effect, or inductively from the 
effects to discover the cause. The effort to 
extend the principle of selection by induction 
to animals and plants in a state of nature failed 
because it was impossible to see how the prin- 
ciple could be applied. The inductive problem 
was apparently as far from solution as at the be- 
ginning; he was still groping in the dark. It 
would be a bootless speculation to try to answer 
the question whether Darwin could ever have 
solved by a study of adaptations the problem 
which he set for himself. It would be hardy 
to hold that a man with Darwin's intellectual 
and moral resources, with his clear conception 


of the problem and the data from which it was 
to be solved, could not have derived the cause 
from an analysis of the effects ; and yet very 
few problems like this were ever solved by 
pure induction. It may be possible to infer 
the nature of a cause from the nature of the 
effects, but nearly always observers manage to 
catch a glimpse of the cause at work. Then, 
by a generalization, the cause is extended to all 
the other effects of the same kind. 

In October, 1838, at the end of fifteen 
months of work on Baconian principles, with- 
out any theory, he read Malthus on Population 
for amusement. 1 There had been much dis- 
cussion in the eighteenth century concerning 
the vice and misery in human society. It 
was quite commonly believed that they were 
due to the organization of society, and tha-t 
they could be eliminated by reorganization of 
society according to some ideal. The father 
of Malthus shared this view; but the son, in 
discussion with him, took the position that, no 
matter how society might be organized, vice and 
misery would follow inevitably from the fact 
that the human race naturally increases more 
rapidly than the means of subsistence. This 
notion was finally developed into the " Prin- 

1 Life and Letters, Vol. I. p. 68. 


ciple of Population," which fell into Darwin's 
hands. The purpose of Malthus in this work 
was to investigate the causes that had hitherto 
impeded the progress of mankind toward hap- 
piness. After establishing the principle that 
population has a tendency to increase in geo- 
metrical ratio, while the food supply can at best 
increase only in arithmetical ratio, he pointed 
out that the ultimate check to the increase of 
population is lack of food; and that all the 
immediate checks could be included under three 
heads, moral restraint, vice, and misery, and 
urged moral restraint as a check to population, 
because by it alone could vice and misery be 
driven out of the world. 1 

Malthus stated with perfect clearness "the 
constant tendency in all animated life to in- 
crease beyond the nourishment prepared for 
it," and the consequent struggle for existence; 
and insisted that in every country, speaking of 
the human family, some of the checks to popu- 
lation are, with more or less force, in constant 
operation. 2 He recognized both artificial and 
natural selection as results of the struggle for 
existence. In the chapter on the " Checks to 
Population among the American Indians," he 

1 Malthus, Principle of Population (gth edition), pp. 1-8. 

2 Ibid., p. 9. 


"As the parents are frequently exposed to 
want themselves, the difficulty of supporting 
their children becomes at times so great that 
they are reduced to the necessity of abandon- 
ing or destroying them. Deformed children 
are very generally exposed ; and among some 
of the tribes in South America, the children of 
mothers who do not bear their labors well ex- 
perience a similar fate from a fear that the off- 
spring may inherit the weakness of its parent. 

"To causes of this nature we must ascribe 
the remarkable exemption of the Americans 
from deformities of make. Even when a mother 
endeavors to rear all her children without dis- 
tinction, such a proportion of the whole number 
perishes under the rigorous treatment which 
must be their lot in the savage state, that prob- 
ably none of those who labor under any original 
weakness or infirmity can attain the age of 
manhood. If they be not cut off as soon as 
they are born, they cannot long protract their 
lives under the severe discipline that awaits 
them. In the Spanish provinces, where the 
Indians do not lead so laborious a life, and 
are prevented from destroying their children, 
great numbers of them are deformed, dwarfish, 
mutilated, blind, and deaf." 1 

1 Principle of Population, Chap. IV. pp. 20, 21. 


It seems almost astounding that Malthus did 
not recognize the importance of this principle 
of natural selection based on the struggle for 
existence and develop it deductively. Had he 
worked out the principle of the survival of the 
fittest among human beings after he so clearly 
recognized it, it would have borne rich fruit 
for the happiness doctrine. It would have re- 
moved much of the gloom from his principle of 
population, by showing that much permanent 
good much more, in fact, than from moral 
restraint arises from the struggle for exist- 
ence by its preserving those best fitted to enjoy 
life. From another point of view, the fact that 
he did not develop the principle of natural 
selection, at least within the human race, after 
he had so plainly recognized both its action 
and its effects, is not even remarkable. When 
one has once made a study of the deductive 
powers of such a man as Darwin, and finds that 
with his great logical strength he sometimes 
failed altogether, and was often very long in 
reaching deductively the consequences of his 
theory, it is not to be wondered at that Malthus 
did not grasp one of the most important features 
of his principle. 

Since he failed to apply the principle of 
natural selection within the human species, 


after he had himself stated clearly its action 
and results, there is no cause for wonder at his 
not applying it to the derivation of species. 
In fact, there was a good reason why he should 
not do the latter. He expressed himself vigor- 
ously in opposition to the belief that a species 
can vary by an indefinite amount in any given 
direction; and denied Condorcet's theory of 
the indefinite perfectibility of the human race. 1 
He admitted only a limited amount of varia- 
tion within a species. Malthus. had worked out 
the struggle for existence and recognized its 
selective action, at least within a limited range; 
and as a natural theologian he must have been 
acquainted with numerous adaptations. But 
he did not connect them as cause and effect, 
because he did not admit general variability 
of species, without which there could be no 
material for the cause to act upon. 

When the work of Malthus fell into Darwin's 
hands, the latter was in possession of the doc- 
trine of descent, and many facts in harmony 
with it, and hence the convi.ction in his mind 
that there was an efficient cause for these facts. 
The adaptations found in nature seemed the 
most difficult facts to explain under the theory 
of descent, and Darwin was already widely 

1 Principle of Population, p 270. 


acquainted with these. He had recognized, as 
did others before him, specific variations as 
material out of which new species must be 
made, and had gone to work systematically to 
study variations, especially in domestic pigeons, 
the most favorable group of animals that could 
have been selected ; and had recognized selec- 
tion as the key to man's success in the produc- 
tion of races. His study hitherto had helped 
him to a wider knowledge and clearer notion 
of adaptations, the effects that had to be 
explained; and a better understanding of the 
nature and range of variations, the materials 
upon which the cause must have acted to pro- 
duce the effects. And in the case of domestic 
productions he was in full possession of the 
cause, the materials on which the cause acted, 
and the results, in selection, variations, and 
races. As he himself said, he had been fully pre- 
pared by his long study of the habits of animals 
to appreciate the struggle for existence which 
everywhere goes on. " It at once struck me," he 
said, "that under these circumstances favorable 
variations would be preserved and unfavorable 
ones destroyed. The result of this would be 
the formation of new species. Here, then, I had 
at last got a theory by which to work." 1 

1 Life and Letters, Vol. I. p. 68. 


It is not recorded at what point in his read- 
ing of Malthus it struck him that the struggle 
for existence, by working upon variations, would 
produce new species. Probably with his mind 
so thoroughly imbued with the subject that 
everything he read was made to bear upon the 
problem he almost instantaneously caught the 
significance of the principle. Malthus himself 
stated the principle clearly in the first few 
pages of the book, and already on pages 21, 22, 
of the ninth edition stated its action and effects 
upon the American Indians. The significance 
of these details is great from the logical point 
of view. All the years of the Beagle voyage 
had prepared Darwin to appreciate the principle. 
The time since his return had strengthened his 
belief in the descent of species, and his efforts 
to reach the cause of modification inductively 
had brought him detailed knowledge of both 
variations and adaptations. What he had not 
hitherto been able to discover by induction 
came to him by accident, if it can be said that 
anything can come by accident to a mind so 
much on the alert for it. It would have been 
one of the most fascinating chapters in scien- 
tific discovery if he had recorded in detail the 
mental activity and the feelings that must have 
flooded him from the moment the discovery was 


made. There was an intellectual explosion, a 
flash of the mind, and from that moment his 
life-work was devoted to elaborating the conse- 
quences of the principle. The facts which he 
had been gathering and reflecting upon were 
explained as the effects of the cause which 
Malthus presented, and gathered a new sig- 
nificance from it. 

" Here, then, I had at last got a theory by 
which to work," he said. The groping was at 
an end. His future work was outlined. The 
confession in that sentence can be appreciated 
only by one who has in his own experience 
passed from the mental strain and perplexity 
of a purely inductive effort to the solid ground 
afforded by even a fairly probable hypothesis. 
Doubtless his work was thenceforth many times 
more rapid than it could otherwise have been; 
for with so vast a number of facts to be con- 
sidered the theory itself was the only pathfinder. 
Only after the discovery of the principle could 
the work of gathering up and classifying known 
facts and of searching for new ones, of reducing 
exceptions and apparently unexplainable groups 
of facts, go on apace. The logical process by 
which adaptations, variations, and the struggle 
for existence were brought together into the 
relation of cause and effect was deductive; and 


the principle of Natural Selection still de- 
pends for its logical support upon that power of 
deductive explanation which Darwin recognized 
in it the day he read Malthus on Population. 
It has penetrated every field of thought, but in 
the field in which it first gathered strength it 
is still without direct demonstration. It has 
been made the basis for countless deductive 
operations, but it leans for support on the very 
structures thus erected. Writing to Bentham, 
in 1863, concerning the proofs of natural selec- 
tion and the descent of species, Darwin said, 
"Belief in natural selection must at present be 
grounded entirely on general considerations : 
(i) on its being a vera causa from the struggle 
for existence; ... (2) from the analogy of 
change under domestication by man's selection; 
(3) and chiefly from this view connecting 
under an intelligible point of view a host of 
facts. " 1 To Huxley he said, in December, 
1860, "I can pretty plainly see that, if my 
view is ever to be generally adopted, it will 
be by young men growing up and replacing the 
old workers, . . . and finding out that they can 
group facts and search out new lines of inves- 
tigation better on the notion of descent than on 
that of creation." 2 

1 Life and Letters, Vol. II. p. 210. 2 Ibid., p. 147. 


From a logical point of view the work of the 
last thirty years in the various fields of biology 
has been a series of deductions and verifica- 
tions of the original propositions laid down 
by Darwin. He saw from the beginning that 
belief in his theory must rest on general con- 
siderations, the chief of which was its power 
to facilitate deductive investigation; and there 
it still rests. At this late day the chief apostle 
of natural selection says that it is really diffi- 
cult to imagine the process of natural selection 
in its details, and that it is impossible to this 
day to demonstrate it in any one point. 1 It 
is the logical relation of the principle to the 
facts that makes it invaluable in modern 
thought. The whole logical history of Dar- 
win's principles illustrates what Mill said of 
the deductive method. "To the Deductive 
Method thus characterized in its three con- 
stituent parts, Induction, Ratiocination, and 
Verification, the human mind is indebted for 
its most conspicuous triumphs in the investiga- 
tion of nature. To it we owe all the theories 
by which vast and complicated phenomena are 
embraced under a few simple laws, which, con- 
sidered as the laws of these great phenomena, 

1 Weissmann, Contemporary Review, September, 1893, Vol. 
LXIV. p. 322. 


could never have been detected by their direct 
study." Writing of the celestial motions as 
an illustration, he continued, "How could we 
ever have ascertained the combination of forces 
on which the motions of the earth and planets 
are dependent by merely comparing the orbits 
or velocities of different planets or the different 
velocities and positions of the same planet ? " 

Darwin himself did not discover the cause by 
the direct study of the effects ; but his efforts 
to reach a cause inductively gave him such an 
insight into variations and adaptations that he 
could prosecute vigorously the other two steps, 
deduction and verification, when once the cause 
was given. What Mill said of celestial motions 
could be almost literally quoted of adaptations. 
It would hardly be going beyond the facts to 
say that the history of theories proves that 
usually not even preliminary hypotheses con- 
cerning causes are worked out directly from an 
analysis of effects; but the causes are usually 
caught in action during the effort to discover 
them inductively, or are reached in a round- 
about way. 



MUCH might be said concerning the per- 
sonal qualities of the man that did so 
much scientific work of such uniformly high 
character. The moral force that overcame life- 
long physical suffering, that stood through 
many years of silent toil face to face with the 
certainty of abuse for its reward, that never 
knew defeat and remained calm during the 
years of victory, has a powerful influence on 
the student of Darwin. The utter lack of 
partisanship for any idea, the rare judicial 
temper that made truth seem better than any 
theory, the penetration, the power of concen- 
tration, the firm mental grasp, the inability to 
leave anything unexplained, all these high 
qualities have their silent evidence in the char- 
acter of Darwin's scientific work. But his 
intellectual and moral traits have been touched 
upon here only in so far as was necessary in 
order to discuss clearly his use of the logical 
processes. The effectiveness of these processes 


must always be entirely dependent on the char- 
acter of the individual using them. 

Darwin's views on method can be summed 
up in the assertion that he was afraid of every 
statement or hypothesis until it was tested, 
and indeed regarded an unverified belief as 
worthless. The starting points of his investi- 
gations were frequently what seemed to other 
men interesting, but unimportant or incon- 
venient exceptional facts. When he sought 
explanations he seemed to be trying to get a 
conclusion by the shortest and easiest route, 
with as little labor as possible. But when he 
had once got an hypothesis he dragged it before 
all the multitude of facts that could be made 
to bear witness to its truth or falsity, until it 
seemed as if he were trying to make the inves- 
tigation last as long as possible. Time seemed 
no longer worth considering. He always used 
the isolated phenomena which were most diffi- 
cult to explain as tests of the validity of his 
hypotheses. )/ By considering all possible objec- 
tions during the progress of the development 
of his conceptions, he threw a merciless light 
on the weaknesses of his theories, and thus 
gave them, in their final form, as high a degree 
of probability as was possible. In his treat- 
ment of negative evidence he never lost sight 


of its comparatively small value, and continued 
the investigation until, by careful observation 
of all collateral facts, he was able to combine 
them into a body of positive evidence in sup- 
port of a different or supplemental theory. 

Classification was with him an invaluable 
instrument for extracting information from 
bodies of facts. His works teem with compar- 
ative tables and statements of results derived 
from them. Analogical reasoning, with all its 
strength and weakness, was utilized as a power- 
ful instrument of suggestion. Induction was 
constantly active in the formation of hypoth- 
eses. He could leave nothing unexplained. 
He made an hypothesis for everything, and 
then tested it unmercifully by deduction. He 
appreciated the immense importance of theory 
to good observation, explained in the light of 
his general theories great bodies of facts and 
principles which had been discovered empiri- 
cally, and anticipated many important conse- 
quences of those theories. Whenever it was 
possible he undertook to verify those anticipa- 
tions ; but did not hesitate to make predictions 
that he could not verify. And with all his 
vast and accurate knowledge of facts and his 
logical power, he frequently fell into erroneous 


The processes employed in scientific inves- 
tigations, although some of them have been 
treated in separate chapters, have a vital inter- 
dependence. Darwin did not and could not use 
one process until its resources were exhausted, 
and then turn to another. It was the very 
swiftness with which different processes were 
successively brought to bear upon his problems 
that made it possible to digest so thoroughly 
every set of facts with which he dealt. What- 
ever may be the future of the particular con- 
clusions which Charles Darwin reached, the 
general method which he employed and the 
general drift of his conclusions will have a 
permanent value. All his efforts tended toward 
the unification of knowledge. All his induc- 
tions became corollaries of one great theory; 
all his deductions had to do with efforts "to 
test and prove the truth of that theory. The 
subordination of all the devices of the intellect 
to one great comprehensive purpose has given 
a unity of aim to all the great works of his life, 
has made his general method conspicuously 
lucid, and has knit the products of his intellect 
into one great logical whole. 


E c f T! B ^vN 

IT KT T \r -r- T^ ^\ 



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