Classics in the History of Psychology
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Christopher D. Green
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By E. B. TITCHENER (1896)
First published in Mind, 5, 236-241.
evasions are exceedingly skilful, and the eruptions of polite invective which
usually follow them exceedingly telling.
But those who have followed this discussion with the purpose which I had
in beginning it -- the purpose of finding, if possible, the true explanation of
the results of psychological experiments upon the duration of the simple
reaction -- will refer from his latest paper to mine, and read
comparatively. I shall therefore assume that they have noted the importance of
Professor Baldwin's admissions (e.g.,
p. 81), promises (e.g., p.
85) and qualifications (e.g., p.
89), and proceed at once to the special points emphasised in his argument.
1. As to the Leipsic procedure, I
can only repeat deliberately what I have before deliberately stated: that, so
far as my knowledge goes, no subject who has been found capable of reaction (of
giving approximately the same response to the same stimulus in a, series, say,
of fifteen trials, after practice) has been neglected either in the parent or
in any more recently established laboratory. It was Martius
-- one of the contributors to the Leipsic theory -- who first analysed what is
now known as the " central" form of the
simple reaction, a form which is neither sensorial nor muscular. In the Cornell Study from which Professor Baldwin
quotes the 'disposition view' are given the times of several observers who did
not show the sensorial-muscular difference;
and that although it is expressly stated
that the object of the Study was not to examine and account for these
divergences from the norm. In face of
these and similar facts, the
charge is made that I (and, I suppose -- else the matter would not be important
-- the Leipsic school with me) think that certain results "ought to have
been suppressed," and that certain cases "ought not to have been investigated"!
2. I stated that there were many ways of testing memory type besides
that of the reaction experiment.
Professor Baldwin challenges me to produce my methods, remarking that he
knows of none which are conclusive except those of introspection and pathology. I was referring to the normal mind when I
made the statement; and as all psychological experiments on the normal mind,
the reaction experiment included, follow or should follow the introspective
method, I am afraid that a list of my methods will not broaden Professor
Baldwin's knowledge. However, I recognise
the justness of the challenge, and give the laboratory and other methods
(co-ordinate with the reaction method as sub-forms of introspection) which I
have found useful.
Methods of Investigating Memory Type. (1) I believe the best method for the
determination of memory type to consist in the introspection of a trained
observer at times when consciousness is, so to speak, off its guard. He must
educate himself to take his mind unawares when he is remembering, or failing to
remember. All sorts of rememberings -- cases
referring to all the different sense departments -- must be noted. This, the most direct way in which
introspection can be practised, is also, I think, the most fruitful. I have
employed it for five (not 'one or two') years; and have only refrained from
publishing my results in detail because,
as I said in my previous paper, some facts are still obscure to me. (2) I have
[p. 238] tried to get at memory type by questioning, with as absolute as
possible avoidance of suggestion. This
method can be usefully employed only where the subjects questioned have a
general knowledge of psychology but are ignorant of the doctrine of memory
type. Its results check and are checked
by those of the foregoing and next following methods. (3) Questioning with
suggestion is a method covering all such tests as Mr Galton's
breakfast-table recollection. It has grave dangers, and must be used with great
caution. I have tried to check it by
what is called the "method of reproduction," -- the subject being
required to reproduce his memory image in objective form; and by an error
method,-- the memory image being compared with some
objective standard. Neither check is very easy of application. But my results
lead me to think that a method may be perfected, under this general head, which
will be especially valuable for the estimation
of the relative importance of the different memories in a given
consciousness. (4) Another way of testing the relative importance of memories,
or the fixity of a particular memory, is the following. A series of experiments on memory is made,
with no directions to the subject as to the way in which he is to
memorise. He is encouraged to be as full
as possible in his introspective remarks. From these, checked by special
experiments the experimenter ascertains the type of memory employed, a new set of experiments
is then begun, in which the subject is told to remember in a particular way,
different from the way of least resistance.
The experimental results and the subject's introspection show whether
the shift of type is successful, or only partially or sporadically possible, or
impossible. (5) Sometimes two types are
used in one and the same act of remembrance: introspection reveals the fact,
but cannot say, under the ordinary conditions of memory, which type is the more
indispensable. Experiments by the method
of reproduction, checked by others with voluntary suppression, are again useful. (6) It is very Important
to determine whether non-employment of a type is due to nature or habit and education. I am this year trying to get a reliable
method of investigating the problem, and have obtained good preliminary results
from two forms of the method of reproduction. (7) Another method of testing
type in general I owe to Professor M. Washburn.
Psychological experiments are often made under distraction: the subject
is required to judge of the difference or likeness of impressions while he is
adding numbers, etc. The mistakes made in this addition, etc., are indicative
of type: if one sees the figures to be added, one's mistakes differ from those
made by a subject who hears the numbers spoken as he adds them. (8) Mr A.
Fraser has shown how a writer's memory type can be determined from his writings
(Am.. Journ. of Psych., IV., pp.
230ff.). This is the method which should
replace 'surmise' in the case of Donders.
3. Professor Baldwin wrote of the subjects of his Study as follows (italics mine). "The reagents were, besides the writers (B.
and S.), Mr Faircloth (F.), a student who had had only the experience gained from the
practical work in this subject of
the course in Experimental Psychology. His reactions were ready and unconfused, and from
all appearances he was a
normal and more than usually suitable man for such work. The
fourth, Mr Crawford (C.), is an honour student in this subject
4. I come
to the matter of Professor Baldwin's own reaction times. In his Senses and Intellect he
remarks, in general terms, that he had anticipated Lange's discovery of the
sensorial-muscular difference. Lange
found that the difference averaged one-tenth of a second (Phil. Stud., IV., 494; Wundt, Phys. Psych., 4te Aufl., II., 311).
Many subsequent experiments have confirmed this result (e.g., those published in the Phil.
Stud., VIII., 144; and those of the Cornell Study before alluded to), and
it is now generally accepted by 'the Leipsic people' as the normal difference between the two forms (Wundt, loc.
cit.; Kuelpe, Outlines, 408, 410). If Professor Baldwin anticipated Lange, his
times must have shown an original difference of some 85 to 115s. If
they did not, he did not anticipate Lange.
The differences between the times given for himself in his Study are, as
I said in my earlier paper, 29,
7, 12 and 46s. No one
of these is anything like the sensorial-muscular difference. The 7 and 12 are times no larger than the
average m.v. of the muscular reaction
(about 10s); an m.v, of
30s is not uncommon in the case of the sensorial
form; and 46 would be a typical "central" difference. Either Professor Baldwin is mistaken in
thinking that he anticipated Lange, or his times have changed since he wrote
his Senses and Intellect. S.'s differences are
51, 40, 79 and 40s. Taken as absolute times, these would all be
"central," though one shows an approximation to the true
sensorial-muscular difference. I do not
think, however, that the differences can be treated in this way, since neither
B. nor S. gave what would be ordinarily regarded as a muscular reaction. The times are 171, 149, 164, 138; 195, 184, 158,
are all, in my opinion,-- and I believe that [p. 240] those familiar with chronometrical
results will agree with me,-- more or less "central" or mixed
reactions. The muscular reaction to sound averages 120s.
5. Professor Baldwin resents my method of
appraising his theory. I confess
that, when I am trying to form
a, theory of certain phenomena or to estimate a theory already set up, I like to have the facts 'catalogued,'
ticketed and weighted. Professor Baldwin
objects to bringing facts together: he distributes them sparsely in a matrix of
theory,-- like the infrequent plums in school plum-cake. Then, if the critic complains of the quality of
the compound, he says: But I have
plenty more plums in the pantry. How does that help the present consumer?
The type-theory has
been written about in a medical weekly, a philosophical bi-monthly, a
psychological bi-monthly, and a book. Now we are told that its presentation is
not yet complete. I did not, of
course, know this when I criticised
it. Nevertheless, I do not regret the criticism: since
it may prevent overhasty acceptance of an attractive hypothesis, and may impel
Professor Baldwin to show his full hand to the psychological public.
Something might be said, I think, from the ethical standpoint, of this piecemeal doling-out
of a scientific theory. Had Professor Baldwin's
article left me a shred or two of moral character, I might have made bold to say it.
6. A few minor differences remain to be cleared
up. I deal with them in a foot-note. [p. 241]
In conclusion, I cannot
but express my regret that Professor Baldwin
should have seen fit to write a dialectical and personal rejoinder to my
criticism, without furnishing new facts or reasons for the absence of facts in
earlier publications. A good deal of his
reply, and therefore of this answer to it, might have been disposed of in
private correspondence. Until the promised support is brought up, the theory
remains what it has been,-- a very happy idea, or ingenious
analogy, apparently natural and probable, but (so far as published) based upon
an altogether insufficient substrate of fact.
I also regret Professor Baldwin's
attitude to the "Leipsic people." He is a professor of experimental psychology;
he must know the literary history of reaction theories,--
he must know how much patient work the "Leipsic people" have done,
for how many years,-- how much the different theorists differ, and how the
central theory has advanced,-- how the theory compares with other theories, and how adequately it covers the
ground of ascertained fact. Yet he nowhere meets the Leipsic theory as a
theory, but only questions its norms; he sets its authors contemptuously aside,
as if to have worked at Leipsic meant a biassed view
of psychology in general; he charges "Wundt,
Kuelpe," et id genus omne
in the present instance with "a flagrant argumentum in circulo," and attributes to them an unscrupulous rejection of results
which make against their circulus,-- when some of these results are
published by their own "people," and some even in their own organ! I have tried to write moderately in
this and my previous paper, and have no wish to emulate Professor Baldwin in
the matter of name-calling at the last moment.
But I cannot think that
his attitude to a long line of predecessors in the field is either
scientifically or ethically defensible.
E. B. TITCHENER
 I give one instance of the way in which
Professor Baldwin can parry an objection.
In his Psych. Rev. Study he identified the 'disposition view' with
the Leipsic theory. I urged that the
'view' was not a theory at all; and that the type theory had to meet, not it,
but the Leipsic theory proper,-- something quite
different. He now says, in effect: I
grant that the view is not a theory; but that leaves my theory in a better
position than ever, since it is a theory. To which
course, reply that the rejoinder is formally correct, but that the
objection holds as strongly as it held before, inasmuch as no comparison of the
type theory with the Leipsic theory has been carried out.
 Nine gentlemen took part with me in my
Leipsic Study. I published the results obtained from Dr Meumann,
Mr H. C. Warren and myself. There are consequently seven (not six) to be
accounted for. One devoted almost all his time to the apparatus. One was called
away on military service early in the course of the investigation; the series
which I have from him promise well. One found the apparatus too complex, and
its management too tedious, and withdrew from the research group. One gave such
curiously slow reactions that they were hardly reactions at all. I was advised
by Professor Wundt to continue work with him, but he left the laboratory for a
reason which I cannot recall. One was
found to be colour-blind, and left my group for another in consequence. I have many series from him, which may be
useful some day to compare with those taken from other colour-blind
persons. One was unanimously -- himself included -- referred to the category of incapables
in this department of work. It would
have been interesting to study his irregularity (here I heartily agree with
Professor Baldwin): but that was not the object of my inquiry. It would have demanded simple experiments in
many sense spheres: I was desirous of making complicated experiments in one.
The last participator was the 'odd man' of the group: a very useful
personage, liable to be called upon at short notice to replace an absentee as
experimenter or subject, in order to prevent interruption of the work. His results were good ;
but they were too scanty to be published, and were not intended for publication
Only one of the
seven, then, was rejected on the ground of incapacity: though others might have
been, had they continued with me. And it is surely evident that irregularities
cannot be explained till we have norms whereby to explain them; i.e., that
it was more important to proceed with the original research than to turn aside to examine the single case. This
is to me so obvious, that I almost wonder whether Professor Baldwin and myself
are not using the term "reaction experiment" in two totally different
senses,-- such as those indicated by Dr Rivers, Journ.
of Mental Science, Oct. 1895.
In Nature of
as, I am sure, Professor Baldwin will be sorry that he jumped to an
interpretation of the sentence in my Leipsic Study, which turns out to be very
largely wrong. I must be more accustomed to making mistakes than Professor
Baldwin is; for I find it impossible in that case to work myself up to the height of moral and intellectual indignation
from which he looks down upon my misreading here.
My presumption that
the writers were working definitely upon the type theory from the outset was
based on the statement that one of the "questions set for research"
was that of "the differences of reaction times for different individuals
under identical conditions."
In the paragraph
in which he insists that the greatest reliance was not placed upon the
times of B. and S., Professor Baldwin writes that these times are "very
neutral to the discussion." Yet they
receive quite detailed treatment in his Study in the examinations following the
two Tables. Why?
 Professor Baldwin says that his times
"have only changed in that the distinction is less marked than it used to
be; and this I go [to] the trouble to explain in the same article as probably
due to habit and practice." In my
copy of the Study there is not a word of this explanation. The change in the author's times is not once
referred to. A general statement is made
about habit towards the end of
the Study; I commented on it on p. 514 of my criticism. It does not contain any the most remote trace
of personal reference.
"How can Kuelpe say beforehand that the muscular
form will turn out in each case to be shorter than the sensorial?" If Professor Baldwin will read Kuelpe's Studien articles,-- or if he will even read on for a single page of the
"Outlines," from the place of my quotation,-- he will find Kuelpe's answer to this question. (2) "Is not the fact
that F is a musician
something of an explanation of his auditive 'disposition'?" Not
necessarily; not i.e., if other musicians do not show auditive dispositions
in their reactions. It is just here that
facts are so useful,-- or so obstinate. (3) Defect of
vision might, certainly, lengthen: reaction time. I do not see that this helps to explain the
reaction itself. (4) The rest of the
paragraph which, has called forth these last two
remarks is obscure to me, m spite of many readings. The type theory would
hardly be a theory of the geistige Anlagen which
it presupposes, even if it fitted all the reaction facts. It surely posits
memory type; it does not state the conditions under which one or other type may
be looked for. I fail to see, therefore, how its application can be 'an
investigation of the so-called 'dispositions' to find out what they really
are.' The Study, indeed, dismisses this
problem (p. 78): it is evident, we read, that attention is now motor, now
sensory, differing in individuals with type,-- "apart quite from the
question as to how one of other state of things comes to be as it is in any one case." At the same time, I admit that the incomplete statement
of the theory may account for its obscurity on this point, and shall await the
complete presentation before offering further criticism. (5) I quoted Professor
Cattell's letter, because he allowed me to publish it under his name. I did so altogether unhesitatingly, because
Professor Cattell has taken part in the discussion of the validity of Lange's
distinction (readers of the Studien will
know how rigidly his adverse criticisms were 'suppressed' by Professor Wundt),
and because every jot of direct evidence for or against the type theory was
important to me. When the 'exact figures' and their analysis are published
Professor Cattell's cases will, undoubtedly,
carry greater weight than they can in outline form. The same is
true of Professor Baldwin's cases: "I fear that those mean variations
which "are too complex to be of any value" will still be asked for by
the cataloguing psychologists. (6) M. Inaudi's case tells heavily against the type theory, as
published, for the reasons given on p. 513 of my earlier paper.