FIVE
The outcOIne probleIn
in psychotherapy
HANS EYSENCK
Introduction
As I have pointed out in two autobiographical sketches (Eysenck 1990a;
1990b), my connection with psychotherapy has been along three main lines.
The first was an initiation of the debate, still continuing, concerning the
efficacy of psychotherapy; the second was playing a part in the establishment
of behaviour therapy, and writing its first textbook (Eysenck and
Rachman 1965); and the third was the setting up of clinical psychology as
a profession in the United Kingdom. These three contributions are not of
course independent. The first step in the sequence was my being given the
task of setting up clinical psychology as a profession in the United Kingdom;
as a result I got interested in the degree to which psychotherapy might
be considered to be useful in the treatment of neurosis, and as a consequence
of my discovery that there was no evidence to support the view that psychotherapy
had any beneficial consequences, as opposed to no treatment, or
placebo treatment, I was led to investigate the possibilities of behaviour
therapy, originally adumbrated by Watson and Rayner (1920), Jones (1924)
and others, as discussed by Kazdin (1978) and Schorr (1984). Thus in my
connection with clinical psychology the outcome problem was absolutely
crucial, and my feeling was and is that this problem has never been properly
addressed by clinical psychologists, and forms the weakest part of our argument
to be a socially useful profession.
In the late 1940s and early 1950s, when I became involved in this field,
certain things were generally taken for granted. It was widely believed and
The outcome problem in psychotherapy 101
taught that psychoanalysis was the only acceptable method of treatment for
neurotic patients, being the only Inethod that concerned itself with causes
rather than merely with symptoms; that symptomatic treatment might be
superficially successful, but that it would soon!be followed by a recurrence
of symptoms, or symptom substitution; that 'ideep', 'psychodynamic' and
long-lasting investigations by trained psychoan~lystswere required to produce
stable and long-lasting cures; and that such cures could be effected
only by analysts who had themselves been psybhoanalysed. Diagnoses and
cures might be helped by psychodynamically oriented projection tests, like
the Rorschach or the Thematic Apperception Test (TAT); the emphasis of
both tests and treatment were unconscious causes, transference phenomena,
and early childhood experiences reconstructed through analysis of dreams
and other types of 'dynamic' evidence.
Few knowledgeable psychologists or psychiatrists would now deny that
there was no objective evidence for any of these beliefs. There were no
clinical studies comparing the progress of neurotic patients under psychoanalysis
with that of similar patients receiving no treatment, or placebo
treatment; it was often suggested that it would be unethical to withhold
such obviously beneficial treatment as psychoanalysis from patients, disregarding
the fact that of all the people suffering from severe neurotic illness
in the United States, less than 0.01 per cent would in fact receive psychoanalytic
treatment! The superiority of psychoanalysis was simply assumed
on the basis of pseudo-scientific arguments, without there being any evidence
in its favour. It was often suggested that the cases treated and described by
Freud provided such evidence, but apart from the obvious point that there
were no controls involved in his work, and no follow-ups, it is now well
known that Freud was very economical with the truth, as far as description
of his famous cases is concerned, and that the alleged 'cures' in fact were
not cures at all (Eysenck 1985b). Thus the famous 'Wolf Man' was not in
fact cured as claimed, but continued with the self-same symptoms from
which Freud claimed to have relieved him for the next sixty years of his life,
being under constant treatment during this time (Obholzer 1982). Similarly,
the famous 'cure' of Anna O. by Breuer, which was supposed to constitute
the beginnings of psychoanalytic treatment, was shown by historians to
have been a misdiagnosis and the 'cure' a fraud (Thornton 1983). Anna O.
was not a hysteric, but suffered from tuberculous meningitis: she was not
cured, but lived for many years with the self-same symptoms in a hospital
(Hirschmuller 1989). The 'Rat Man' was far from a therapeutic success as
claimed, and Freuďs process notes deviate notably from his final account
(Mahony 1986). It would be difficult to adduce these and other cases treated
by Freud as evidence .of psychoanalytic successes (Eysenck 1985b).
The outcome problem, then, was being completely disregarded, and the
only kind of clinical studies to be done were concerned with problems
internal to the analytic process, it being assumed that psychoanalysis was
not only the best, but also the only method of treatment. It seemed to me
from the beginning that this was entirely the wrong way to look at the
102 Hans Eysenck
whole problem of psychotherapy. Both from the theoretical and the practical
points of view, the outcome problem was the most important and critical
of all; if psychoanalysis, or psychotherapy if. general, which was then as it
is now, largely based on Freudian assumptions, did not in fact do better than
placebo treatments or no treatment at all, then clearly the theory on which
it is based was wrong. Similarly, if there were no positive effects of psychoanalysis
as a therapy, then it would be completely unethical to apply this
method to patients, to charge them money for such treatment, or to train
therapists in these unsuccessful methods. The practical importance of the
issue will be clear without any great discussion, but the theoretical implications
have been debated for a long time; it has been asserted that
even if the therapy itself did not work, the theory might nevertheless be
correct. I took it for granted that if a treatment method based on theory does
not work, then this suggests that the theory itself must be mistaken.
Grunbaum (1984) has argued the case in considerable detail, and has come
to a very similar conclusion. I shall return to this point presently.
Effectiveness of psychoanalysis
In order to satisfy myself concerning the alleged efficacy of psychoanalysis,
I carried out an analysis of all the published material concerning recovery
from neurotic illness after psychoanalysis, after psychotherapy, and after no
treatment of a psychiatric nature at all; the results were published in an
article which has been referred to as 'the most influential critical evaluation
of psychotherapy' (Kazdin 1978: 33). In this article (Eysenck 1952) I examined
a number of outcome studies that primarily evaluated treatment of
neurotic patients. I attempted to assess the effects of psychotherapy by
comparing its outcome with an estimate of improvements in patients that
occurred in the absence of therapy. I concluded that approximately 67 per
cent of seriously ill neurotic patients recover within two years, even in the
absence of formal psychotherapy. If we regard this as an approximate baseline
against which treatment can be evaluated, then we can compare therapy
outcome with it, and I found a cure rate of approximately the same magnitude.
Thus remissions with no treatment ('spontaneous remission') appear
to be as effective as psychotherapy and psychoanalysis. The dissatisfaction
with psychotherapy expressed in this conclusion was shared by many others
who published similar articles around the same time (e.g. Denker 1946;
Landis 1937; Salter 1952; Wilder 1945; Zubin 1953L all of whom came to
very similar conclusions, although they tended to express them less definitively
and perhaps less clearly than I had done.
The paper produced a plethora of replies, all of which, interestingly enough,
criticized me for saying something I had not said, namely that the evidence
proved psychoanalysis and psychotherapy to be ineffective. The quality of
the papers surveyed, it was stated, was too poor to allow such a conclusion
to be substantiated. This, of course, is true; the evidence is methodologically
and statistically inadequate, but my conclusion had been rather different,
The outcome problem in psychotherapy 103
namely that the evidence was not sufficient to prove that psychoanalysis
and psychotherapy were instrumental in mediating recovery. The poorer the
evidence, the stronger this conclusion is; if the studies surveyed are so poor
that no conclusions can be drawn, then they cannot be used to support the
idea that psychoanalysis and psychotherapy have a positive effect!
In case it might be thought that I am making a special case for my own
view, or that the issue is not a serious and important one, readers are
recommended to read an article by Erwin (1980) who, as a trained philosopher,
has exhaustively looked at the argument (also treated in his previous book:
Erwin 1978). His conclusion agrees with me th~t the issue is important, and
that the critics of my original thesis were mistaken.
It is interesting, in view of other criticisms that I have to make, that the
critics of my paper had to resort to misrepresentation in order to enable
them to put up some kind of argument. It is also interesting that neither the
referees nor the editors of the journals concerned noted this misrepresentation.
., I took up the topic again in 1960 and in 1965, summarizing the large
number of articles that had appeared, partly as a consequence of the stress
on the importance of the outcome problem which we had insisted on. The
results were not very dissimilar, as the following quotation from my 1960
paper will illustrate:
1 When untreated neurotic control groups are compared with experimental
groups of neurotic patients treated by means of psychotherapy,
both groups recover to approximately the same extent.
2 When soldiers who have suffered a neurotic breakdown and have not
received psychotherapy are compared with soldiers who have received
psychotherapy, the chances of the two groups returning to duty are
approxinlately equal.
3 When neurotic soldiers are separated from the service, their chances
of recovery are not affected by their receiving or not receiving
psychotherapy.
4 Civilian neurotics who are treated by psychotherapy recover or improve
to approximately the same extent as similar neurotics receiving
no psychotherapy.
5 Children suffering from emotional disorders and treated by psychotherapy
recover or improve to approximately the same extent as
similar children not receiving psychotherapy.
6 Neurotic patients treated by means of psychotherapeutic procedures
based on learning theory improve significantly more quickly than do .
patients treated by means of psychoanalytic or eclectic psychotherapy,
or not treated by psychotherapy at all.
7 Neurotic patients treated by psychoanalytic psychotherapy do not
improve more quickly than patients treated by means of eclectic
psychotherapy and may improve less quickly when account is taken
of the large proportion of patients breaking off treatment.
8 With the single exception of the psychotherapeutic methods based
104 Hans Eysenck
on learning theory, results of published research with military and
civilian neurotics, and with both adults and children, suggest that
the therapeutic effects of psychotherapy are small or non-existent
and do not in any demonstrable way add to the non-specific effects
of routine medical treatment, or to such events as occur in the
patients' everyday experience.
(Eysenck 1960: 719-20)
In these writings I made a number of other points, which have not always
been considered by critics. Thus I emphasized the need for carefully controlled
therapy research that not only took into account spontaneous remission,
but also controlled for non-specific treatment effects, that is the inclusion
of placebo treatment in assessment. I also pointed out that showing that
therapy is superior to no treatment is not sufficient to demonstrate that any
particular technique or ingredient of therapy is effective; non-specific treatment
effects such as attending treatment and meeting with the therapist
would still have to be ruled out to argue for specific benefits of treatment
(Eysenck 1966). Arguments for and against were taken up by many contributors
whose points of view are summarized by Kazdin (1978) and Schorr
(1984). It would not be useful to take up these arguments here again, but it
may be worthwhile to look at more recent surveys of the burgeoning literature,
and try and see to what extent more recent studies have validated or
invalidated my original conclusions.
Before turning to this task, however, let us consider the degree to which
psychoanalysts have responded to the widespread criticism voiced concerning
the efficacy of their treatment. Following the principle that criticism
should be directed at what is regarded the best, rather than the worst project
in the area, we may look at the Menninger Clinic project (Kernberg 1972;
1973), a lavishly financed study published after eighteen years of work. The
aim of the project was to 'explore changes brought about in patients by
psychoanalytically oriented psychotherapies and psychoanalysis' (Kernberg
1972: 3). Forty-two adult neurotic patients were studied, those in psychoanalytic
therapy receiving an average of 835 hours of treatment, and those
in psychoanalytically oriented psychotherapy receiving an average of 289
hours. A detailed criticism of the project has been made by Rachman and
Wilson (1980). Listing such obvious faults as contamination, non-random
allocation, absence of any control, and so on, we find that the authors of the
Menninger report themselves admit that the most severe limitation of their
study was its 'lack of formal experimental design' (Kernberg 1972: 76). They
point out that it was not possible:
(i) To list the variables needed to test the theories;
(ii) To have methods of quantification of the variables, preferably
existing scales which would have adequate reliability and validity;
(iii) To be able to choose and provide controlled conditions which
would rule out alternative explanations for the results.
The outcome problem in psychotherapy 105
(iv) To state the hypothesis to be tested; or finally,
(v) To conduct the research according to the design.
(Kernberg 1972: 75)
As Rachman and Wilson correctly point out,
This astonishing conclusion can have few equals ... one is left with a
study that is so flawed as to preclude any; conclusions whatsoever.
Whilst the honesty of this self-appraisal is highly commendable, one
cannot help wondering how the authors sucrieeded in persuading large
and reputable foundations to provide them with financial support
extending over many years. How does one persuade a foundation to
uphold research which, in the words of the authors themselves, lacks
a formal experimental design, or methods of quantification, or hypotheses?
And which cannot be conducted 'according to the design'?
(Rachman and Wilson 1980: 73)
(Over $1 million was spent on the project, at a time when this was a
considerable amount of money.)
Did this waste of time and money induce in the authors of the report a
suitable feeling of humility? Malan (1976: 21) states: 'When I met Dr. Kernberg
at the meeting of the Society for Psychotherapy Research in Philadelphia, in
1973, he said that the problem of measuring outcome on psychodynamic
criteria was essentially solved, and I could only agree with him.' It is difficult
not to resort to a quotation: 'Quem Jupiter vult perdere dementat
prius' (Whom Jupiter wants to destroy, he first renders mad). Clearly
psychoanalysts have learned nothing and forgotten nothing! They have no
intention of submitting their beliefs to any kind of empirical proof: they
prefer assertion to demonstration. Anyone seriously interested in this topic
ought to read the detailed critique of Rachman and Wilson (1980) to discover
how far intellectual vacuity can go.
It is sometimes said that no proper clinical trial of psychoanalytic therapy
has been carried out because of the expense involved. This is not true. The
Menninger study failed because of incompetence, complacency and a daunting
lack of elementary methodological sophistication, not because of lack of
funding. Or consider another example. Many years ago a large grant-giving
body offered Sir Aubrey Lewis $1 million to organize a clinical trial to compare
psychoanalytic treatment and behaviour therapy. He asked the Tavistock
Clinic, the leading psychoanalytic institution in Britain, to take part, offering
them a leading role in the design and organization of the clinical trials, and
the evaluation process. (Sir Aubrey was quite neutral between the rival
claims made at the time for these methods of treatment.) The Tavistock
Clinic turned down the offer, presumably because they feared the outcome
would be unfavourable to their claims. My colleagues and I welcomed it,
but of course the offer was contingent on both sides agreeing, and was
withdrawn when no psychoanalysts could be found to take up the challenge.
Am I being too hard in my interpretation? As Anthony Storr, one of the
best known psychoanalysts in Britain, wrote in 1966:
106 Hans Eysenck
The American Psychoanalytic Association, who might be supposed to
be prejudiced in favour of their own speciality, undertook a survey to
test the efficacy of psychoanalysis. The results obtained were so disappointing
that they were withheld from publication.... The evidence
that psychoanalysis cures anyone of anything is so shaky as to be
practically non-existent.
(quoted by Wood 1990)
If a soi-disant 'scientific' organization can behave in this fashion to prevent
the public from knowing that their'science' was worthless, we should not
be surprised at anything done by psychoanalysts to protect their religion.
Rachman and Wilson (1980) provide us with so far the best and most
honest survey of the literature, and it is reassuring that their verdict is not
very different from that I arrived at thirty years before. A quotation makes
clear their overall evaluation:
The need for strict evaluations of the effects of various forms of therapy
arises from several observations. In the first place, there is clear evidence
of a substantial remission; as a result any therapeutic procedure
must be shown to be superior to 'non-professionaľ processes of change.
Closely allied to this point is the wide range of therapeutic procedures
currently on offer and the competing and often exclusive claims for
effectiveness. The lengthy business of separating the wheat from the
chaff can only be accomplished by the introduction of strict and rational
forms of evaluation. One important function of strict evaluation would
be to root out those ineffective or even harmful methods that are being
recommended. The availability of incisive methods of evaluation might
have averted the sorry episode during which coma treatment was given
to a large number of hopeful but undiscriminating patients.
The occurrence of spontaneous remissions of neurotic disorders provided
a foundation stone for Eysenck's (1952) sceptical evaluation of
the case for psychotherapy. His analysis of the admittedly insufficient
data at the time led Eysenck to accept as the best available estimate
the figure that roughly two-thirds of all neurotic disorders will remit
spontaneously within 2 years of onset. Our review of the evidence that
has accumulated during the past 25 years does not put us in a position
to revise Eysenck's original estimate, but there is a strong case for
refining his estimate for each of a group of different neurotic disorders
the early assumption of uniformity of spontaneous remission rate~
among different disorders is increasingly difficult to defend.
Given the widespread occurrence of spontaneous remissions, and it
is difficult to see how they can any longer be denied, the claims made
for the specific value of particular forms of psychotherapy begin to
look exaggerated. It comes as a surprise to find how meagre is the
evidence to support the wide-ranging claims made or implied by
psychoanalytic therapists. The lengthy descriptions of spectacular
improvements achieved in particular cases are outnumbered by the
The outcome problem in psychotherapy 107
descriptions of patients whose analyses appear to be interminable. More
important, however, is the rarity of any form of controlled evaluation
of the effects of psychoanalysis. We are unaware of any methodical
study of this kind which has taken adequat~ account of spontaneous
changes or, more importantly, of the con,tribution of non-specific
therapeutic influences such as placebo effects, expectancy, and so on.
In view of the ambitiousness, scope, and influence of psychoanalysis,
one might be inclined to recommend to one's scientific colleagues an
attitude of continuing patience, but for the fac;t that insufficient progress
has been made in either acknowledging thei need for stringent scientific
evaluations or in establishing criteria of outcome that are even
half-way satisfactory. One suspects, however, that consumer groups
will prove to be far less patient when they finally undertake an examination
of the evidence on which the claims of psychoanalytic
effectiveness now rest.
(Rachman and Wilson 1980: 259)
The rather negative evaluation of psychoanalysis, and indeed other forms of
psychotherapy, to which Rachman and Wilson are finally forced contrasts
spectacularly with conclusions arrived at by authors like Bergin (1971), Bergin
and Lambert (1978) and Luborsky et al. (1975). The latter, in a memorable
phrase, summarized their comparative studies of psychotherapies in the
quotation that 'Everyone has won, and all must have prizes'. This will
illustrate the Alice's Adventures in Wonderland atmosphere of this whole
field, as do the equally optimistic conclusions of Bergin and his colleagues.
Let us first consider the argument advanced by Luborsky and his colleagues,
which is also put forward by Smith et al. (1980) in a meta-analysis
of all published data, to the effect that all types of therapy are equally
effective, and that this proves the correctness of the views of those who
support the effectiveness of psychotherapeutic research, and the theories on
which this is based. Let us assume that it is true that different methods of
psychotherapy (let us call them TIJ T2, T3 ˇˇ. Tn) have indeed been shown to
be equally effective in reducing or abolishing the neurotic illnesses for which
they have been recommended. It should be obvious that such an outcome
would not support the hypotheses or theories on which the treatments were
based (let us call them H l , H2, H3 ˇˇ. Hnl, but would completely disprove
them. Let us consider psychoanalysis as Tl . This is based on HlJ which asserts,
as we have seen, that only psychoanalytic methods can produce a proper cure,
and that all other methods must inevitably fail to do so. But according to
Luborsky, T2, T3 .ˇ. Tn are equally successful as T l ; this clearly demonstrates
that HI is incorrect, because it predicted the opposite, namely that T2,
T3  .. Tn would have no effect, or at most, a markedly weaker effect, than T l .
Much the same can be said for all the other types of treatment - clientcentred,
Gestalt, 'primal therapy', etc. They are all based on specific hypotheses
which would assert that the respective methods of treatment should be
superior to all others; if they are not, then surely the theories themselves
108 Hans Eysenck
cannot be correct. If it can also be shown, as we shall see, that placebo treatments
are as effective as genuine treatments, then it should become plain
that the outcome of all these studies must be that it is non-specific factors,
such as discussing one's troubles with a friendly person, receiving advice,
relieving one's tensions through receiving positive reactions, etc. which are
effective in mediating therapeutic success, rather than the specific methods
derived from the various theories in question. If indeed all have won, and
all must have prizes, then that surely spells the definite rebuttal to all the
theories psychotherapists have fought so earnestly to elaborate and establish.
As far as Bergin and Lambert (1978) are concerned, their main argument
rests on the assertion that Eysenck's original suggestion of a spontaneous
remission rate of about two-thirds is incorrect, and that this figure should
be very much lower. As they say, 'It can be noted that the two-thirds estimate
is not only unrepresentative but is actually the most unrealistic figure
for describing the spontaneous remission rate or even rates for minimal
treatment outcomes' (Bergin and Lambert 1978: 147, original emphasis).
Eysenck's estimate had been based on data published by Landis (1937) and
Denker (1946), which gave an estimate of spontaneous remission effects of
something like two-thirds; Bergin (1971) compiled a table containing fourteen
studies, and provided percentage improvement rates for each. The rates
vary from 0 per cent to 56 per cent and 'the median rate appears to be in
the vicinity of 30 per cent!' Although his figures 'have their weaknesses',
Bergin nevertheless felt that 'they are the best available to date' and rest
'upon a much more solid base' than the Landis-Denker data. In the face of
such a large discrepancy, which is obviously vital in coming to any conclusions,
it is essential to study the figures and arguments in detail. This
has been done very carefully by Rachman and Wilson (1980), and the reader
is referred to their discussion. We shall quote only brief excerpts to illustrate
the essential dishonesty of the Bergin and Lambert argument:
Before commencing the close examination of what Bergin presents as
the best available data, two points should be borne in mind. In the first
place it seems to be a curious procedure in which one rediscovers data
and then calculates a median rate of improvement, while ignoring the
data on which the original argument was based. The new data (actually
some of them are chronologically older than those of Landis-Denker)
should have been considered in conjunction with, or at least in the
light of, the existing information. The second point is that although
Bergin considered some new evidence, he missed a number of more
satisfactory, and indeed more recent, studies which are more pertinent
to the question of spontaneous recovery rates. His estimate of a 30%
spontaneous recovery rate is based on the fourteen studies which are
incorporated in Table 8 of his work. It will be noticed that the list
omits some of the studies discussed earlier in this chapter, which
antedate Bergin's review.
(Rachman and Wilson 1980: 41)
The outcome problem in psychotherapy 109
Rachman and Wilson now give a list of the fourteen studies cited in Bergin's
review, and then go on to a detailed discussion of each. Let us consider as
an example the spontaneous remission rate of 0 per cent given by Bergin for
a study by Cappon (1964). Here is what Rachman and Wilson have to say
about this study:
The first surprise is its title - 'Results of psychotherapy'. Cappon reports
on a population consisting of 201 coqsecutive private patients
'who underwent therapy between 1955 and 1~60'. Their diagnoses were:
psychoneurosis 56%, psychopathic personality 25 %, psychosomatic
reactions 8%, and others 3%. As 163 had ended their therapy in 1960,
'this was the operative sample'. Cappon describes his treatment as
being'applied Jungian'. The results of the treatment were'admittedly
modesť, and the follow-up was conducted by mail. Unfortunately,
only 53% of the patients returned their forms, and the follow-up
period varied from 4 to 68 months. In addition, the follow-up sample
'was biased in that these patients did twice as well at the end of
therapy, as rated by the therapist, as those who did not return the
forms'. It was also noted that 'the operative patient sample (n = 158)
was still different (sicker) from a controlled normal sample, at the time
of the follow-up. Patients showed more than 4 times the symptoms of
normals. This ensured the fact that the sample was indeed composed
of patients'.
Cappon states that 'the intention of this work was not so much to
prove that results were actually due to psychotherapy as to show some
of the relationships results. Consequently, there was no obsessive preoccupation
with "controls" as the sine qua non dictate of science.' We
seem in the midst of all this to have strayed from the subject of
spontaneous remissions. In fact, Cappon did make some brief COlTIments
on the subject. He argued that 'if worsening rather than improvement
were rated, 4 to 15 times as many patients changed (got
worse) in the follow-up (control) period combined with the therapeutic
(experimental) period, depending on the index useď. As the follow-up
period averaged some 20 months and the therapeutic period some
61/2 months, 'this fact alone casts great doubt on Eysenck's data on
spontaneous remission which led him to the false conclusion that
patients did better without treatment than with treatmenť. Leaving
aside the fact that Cappon unfortunately lost approxilTIately half of his
sample between termination of treatment and follow-up, we can perhaps
leave uncontested his conclusion that many of the patients got
worse after treatment. Cappon's report adds slender support to the
belief that some patients get worse after psychotherapy. It tells us
nothing at all about spontaneous remission rates, and far from giving
a spontaneous remission rate of 0%, Cappon does not provide any figures
on which to calculate a rate of spontaneous remission.
Bergin's figure of a 0% spontaneous remission rate appears to be
110 Hans Eysenck
drawn from Cappon's introductory description of his patients, in which
he says that they 'had their presenting or main problem or dysfunction
for an average of 15 years before the treatmenť (original italics).
Clearly, one cannot use this single-sentence description in attempting
to trace the course of neurotic disorders or to determine their spontaneous
remission rate. Nearly half of Cappon's patients apparently
had disorders other than neurotic; we are not aware that they had been
untreated prior to attending Cappon; we cannot assume that their
diagnosis at the beginning of treatment would correspond with their
condition in the years prior to treatment; we do not know whether
the 201 patients constitute 90% of the relevant population or even
0.00001 % of that population. Without labouring the point, this incidental
sentence cannot be taken as evidence for or against the occurrence
of spontaneous remissions. Bergin's use of the information is
unjustified. His introduction of Cappon's report, coming from someone
who complains of the 'irrelevance' and 'inadequacy' of the studies
by Landis, Shepherd, and others, is baffling. In any event, the occurrence
of therapeutic failures, and of a large minority (33 %?) of unremitting
neuroses, are consistent with the Eysenckian argument. A
special collection of therapeutic failures no more demonstrates a spontaneous
remission of 0% than a similar collection of patients who
have recovered without treatment (easy to compile) would demonstrate
a spontaneous remission rate of 100%. The matter rests on the
proportion of neurotic patients who show marked improvements within
2 years of the onset of their disorder - or if one prefers a longer or
shorter period of study, then a modified hypothesis can be put forward.
(Rachman and Wilson 1980: 41)
Rachman and Wilson continue:
Bergin also gives a 0% spontaneous remission rate for the paper by
O'Connor et al. (1964). Once again, the title - 'The effects of psychotherapy
on the course of ulcerative colitis' - is surprising as the
subject under discussion is the spontaneous remission rate in neurotic
disorders. Ulcerative colitis is defined by O'Connor and his co-authors
as 'a chronic non-specific disease characterized by inflammation and
ulceration of the colon and accompanied by systemic manifestations'.
(Rachman and Wilson 1980: 42)
According to O'Connor et al. (1964)
'its course is marked by remissions and exacerbations, its aetiology is
considered multifactorial, and it has been variously attributed to infections,
genetic, vascular, allergic and psychological phenomena'.
(quoted in Rachman and Wilson 1980: 42)
Rachman and Wilson further note the following:
It will not pass unnoticed that 'psychological phenomena' are only one
in ::I li.<;:t nf f1vp tvnp<;: of !Jttrihlltinn nnr 'nrl",,,,rl ..hn" ..h~ ~~,,_~~ ~r. -,-1.._
The outcome problem in psychotherapy III
disease is 'marked by remissions'. The observation that patients who
have ulcerative colitis can show remissions is of interest to gastroenterologists.
The study compares the progress made by fifty-seven
patients with colitis who received psychotherapy and fifty-seven
patients who received no such treatment. The patients in both groups
continued to receive medical and even surgical treatment, and those
who had psychotherapy are said to have progr~ssedbetter. In the treated
group, '19 patients were diagnosed as schizophrenic, 3 were psychoneurotic,
34 were diagnosed as having personality disorders, and 1
received no diagnosis'. In the control group, however, '3 of the patients
were diagnosed as schizophrenic, 3 as psychoneurotic, and 14 as having
personality disorders. The remaining 37 control patients were not diagnosed
because of the lack of overt psychiatric symptOlns'. As only
three of the control group were diagnosed as psychoneurotic, the spontaneous
remission rate over the fifteen-year period would have to be
expressed as the number of spontaneous remissions for a group with
an N of 3. Bergin's use of the data in this report also raises a methodological
point. He quotes the spontaneous remission rate for colitis
patients as 0 per cent over fifteen years. In fact no percentage rate can
be obtained from the report as all the results are given as group means
- it is possible, and indeed likely, that numbers of patients experienced
remission even though the group mean showed little change. The study
leaves us in no position to determine the spontaneous remission rate
in three neurotic patients with ulcerative colitis.
(Rachman and Wilson 1980: 42-3)
Another report quoted by Bergin is equally irrelevant as Rachman and
Wilson report thus:
Orgeľs (1958) report on fifteen treated cases of peptic ulcer is quoted
as showing a 0% remission rate. Bergin appears to argue that because
the patients had suffered from stomach ulcers for 4 to 15 years prior
to entering treatment, this indicates a remission rate of O. Factually,
Bergin is incorrect in stating that the peptic ulcers 'had persisted from
4 to 15 years without change'. Several of the patients had experienced
remissions prior to entering psychoanalytic treatment. Furthermore,
some of them experienced remissions and recurrences during the
treatment. Far more serious, however, is Bergin's asslunption that these
fifteen ulcer cases are representative of the relevant population. Moreover,
the introduction of material on the 'natural history' of patients
with peptic ulcer into a discussion on spontaneous remissions in neurotic
disorders is not justified.
(Rachman and Wilson 1980: 43)
The relnaining studies examined by Rachman and Wilson (1980) are equally
irrelevant to the issue in question:
For reasons that are not explicit, neither Bergin nor Lambert (separ~
.. ~lTT ~_ ~~~_ ...lTT\ ~ __ ~ __ -'-~ 1.. __ .ˇ;11; __ -,- D __ L1..; , ˇ _ .1-_
112 Hans Eysenck
question in hand} i.e. the rate of spontaneous remission in neuroses.
They repeatedly introduce irrelevant information - on the effects of
treatment} on recovery rates in surgical patients} on remissions in
schizophrenia} on the fate of delinquents} and so on. Lambert (1976:
116) took this inexplicable process one step further and objected to
analyses that are confined to untreated neurotic disorders. Contrary to
the drift of his argument, the inclusion of studies should not be dictated
by caprice} but rather should be an exercise in applying firm
standards of selection. It is, after all, simple - if you wish to determine
the rate of remission in neurotic disorders, then study data on neurotic
disorders.
(Rachman and Wilson 1980: 48)
Above all else, however, the evidence gathered since the original estimate
was attempted} emphasizes the need for more refined studies and more
accurate statistics. In particular, one can now postulate that the gross spontaneous
remission rate is not constant across different types of neurotic
disorders. For example, obsessional disorders probably have a lower rate of
spontaneous remission than anxiety conditions. Future investigators would
be well advised to analyse the spontaneous remission rates of the various
neuroses within} rather than across, diagnostic groupings. If we proceed in
this manner it will be possible to make more accurate estimates of the
likelihood of spontaneous remission occurring in a particular type of disorder
and, indeed, for a particular group of patients.
Although the gross spontaneous remission rate has thus far been based on
a two-year period of observation (and this serves well for many purposes),
attempts to understand the nature of the process will be facilitated by an
extension of the periods of observation. The collection of reliable observations
on the course of spontaneous remissions will} among other things, greatly
assist in making prognoses.
Readers will be able to form their own opinion on whether these excursions
by Bergin and Lambert into the higher realms of imagination constitute
an honest appraisal of the evidence; Rachman and Wilson (1980) leave little
doubt on the point. Unfortunately, it has to be said that most writers on
the topic prefer the conclusions provided by Luborsky, by Bergin and by
Lambert to the much more realistic appraisal offered by Rachman and
Wilson; the reasons for this preference are not far to seek in people whose
professional advancement and livelihood depend on the popular acceptance
of the kinds of psychotherapy they provide. Whether such a procedure is
ethically defensible} and scientifically meaningful is of course another
question.
The relevance of meta-analysis
Where Luborsky, Bergin and Lambert at least pretend to some kind of
scientific objectivity, a much praised book by Smith et al. (1980) provides
The outcome problem in psychotherapy 113
the seeds of destruction within itself, without requiring any aid from outside
critics. The contents of this book, which essentially aims at a meta-analysis
of all published studies to date, amount to an essential contradiction of the
conclusions I drew in 1952} and which have been virtually unchanged in the
review by Rachman and Wilson (1980). To illustrate this conclusion, let
me quote first of all the general conclusion~ drawn by the authors from
their data. They assert that
Psychotherapy is beneficiaL consistently iSO and in many different
ways. Its benefits are on a par with other ~xpensive ambitious interventions,
such as schooling and medicink. The benefits of psychotherapy
are not permanent, but then littl~ is.
(Smith et al. 1980: 183, original emphasis)
They go on to say that
The evidence overwhelmingly supports the efficacy of psychotherapy
... psychotherapy benefits people of all ages as reliably as schooling
educated them, medicine cures them} or business turns a profit.
(Smith et al. 1980: 183)
Apparently psychotherapy sometimes seeks the same goals as education and
medicine, and when it does, psychotherapy performs cOlnmendably well:
We are suggesting no less than that psychotherapists have a legitimate,
though not exclusive, claim} substantiated by controlled research, of
those roles in society, whether privately or publicly endowed, whose
responsibility is to restore to health the sick, the suffering, the alienated,
and the disaffected.
(Smith et al. 1980: 183)
Smith et al. then go on to repeat the Luborsky view that
Different types of psychotherapy (verbal or behavioural; psychodynamic,
client-centred, or systematic desensitization) do not produce different
types or degrees of benefit.
(Smith et al. 1980: 184)
Allied to this odd conclusion is another one, to wit that
differences in how psychotherapy is conducted (whether in groups or
individually, by experienced or novice therapists, for long or short
periods of time, and the like) make very little difference in how beneficial
it is.
(Smith et al. 1980: 188) original emphasis)
As we have already noted, if indeed all different methods of psychotherapy
give pretty much the same results} then this disproves conclusively all the
theories on which the different methods of therapy are based. Actually
of course the data presented in their Table 5.1 completely contradict their
own conclusions; they found average effect sizes of 0.28 for undifferentiated
114 Hans Eysenck
counselling, for instance, and of 0.14 for reality therapy, with figures like
1.82 for hypnotherapy and 2.38 for cognitive therapies. This does not suggest
equality of outcome! They also fail to note a very important conclusion
from the same table that placebo treatment (effect size 0.56) is as effective
as Gestalt therapy (0.64), client-centred therapy (0.62) or psychodynamic
therapy (0.69). Clearly, their own conclusions force us to argue that all the
vaunted effects of psychotherapy are simply placebo effects, a conclusion
also arrived at by the much more meaningful analysis carried out by Prioleau
et al. (1983). It is curious that almost none of the reviewers of the book saw
this obvious contradiction between data and conclusions, or commented on
the devastating effects this must have on the claims for efficacy of psycho-
therapy.
Much the same must be said about the final conclusion of the book
quoted above, to the effect that for the effectiveness of therapy it makes
very little difference if it is done by an experienced or an inexperienced
therapist, or for long or short periods of time. If that is true, then clearly
claims by psychoanalysts that their discipline requires a lengthy training,
and a lengthy time to establish and then resolve transference relations, are
completely unjustified. Obviously what we should do is to train therapists
for just one hour, and restrict treatment to one hour's duration; clearly, if
we can rely on Smith, Glass and Miller, this should make no difference to
the outcome! To keep up with our Alice's Adventures in Wonderland story,
we should apparently have followed the practice of the Red Queen to believe
as many as six impossible things before breakfast. To believe the conclusions
of Smith et al. (1980) would certainly constitute good practice for that.
Smith et al. curiously enough do discover that behaviour therapy is more
effective than psychotherapy, but they try to argue this conclusion out of
existence by a rather specious argument which this is not the place to
discuss. Eysenck and Martin (1987) have discussed this question in some
detail, and have come to the conclusion that not only is a learning theory
of neurosis the only scientific theory available at present, but also the
methods of treatment to which it gives rise are the only ones which show
a significant improvement over no treatment or placebo treatment. Thus
the 'spontaneous remission' objection does not apply to behaviour therapy;
Rachman and Hodgson's (1980) book presents an excellent example. The
failure of psychotherapy to achieve a similar status, alas, does not seem to
have reduced the ardour with which many therapists still proclaim its virtues,
and foist it on innocent victims.
Have more recent studies suggested that my estimate was wrong? Garfield
and Bergin (1986) have reviewed the field, but I still do not see a single study
which would meet what I consider minimum requirements of a meaningful
comparison between no treatment, placebo treatment of an acceptable kind,
psychoanalysis or closely specified psychotherapy, and behaviour therapy
carried out by a properly qualified behaviour therapist, using appropriate
methods. If we are dealing with obsessive handwashing, for instance, flooding
with response prevention works very well, while desensitization, in our
I
I,
Ii
II
The outcome problem in psychotherapy 115
experience, does not (Rachman and Hodgson 1980); it would be easy to
make behaviour therapy do no better than psychotherapy by choosing the
wrong method. Also, many people call themselves behaviour therapists
without any proper training; one would need to be assured on this point.
Ideally studies should be set up by a supervisory group comprised of leading
exponents of the methods under compari~on, free to select the therapists
using their type of treatment. Alas, no sqch study is familiar to me.
Two objections are often made to the claims of psychotherapeutic lack
of effectiveness. The first is that clients qften report satisfaction with the
outcome of the treatment, even if symptom-removal failed to occur. Cognitive
dissonance theory would lead us to expect precisely this; patients
who have spent four years or more in treatment, and spent upwards of
$100,000 on fees, would not be human if they willingly acknowledged that
it was all for nothing. There is also the suggestion constantly reiterated by
analysts that if the patients are no better it is all their own fault -'resistance'
and all that! Finally, there is the hello-and-goodbye phenomenon; all mental
disorders have their ups and downs, and therapy is usually entered in a
down phase, and left in an up phase. Anyone making claims of this kind
would have to make a proper study of the proportions of satisfied customers,
then eliminate possible causes like those mentioned, and finally set the
results against the number of dissatisfied customers. Nothing of the kind
has yet been done.
The other argument concerns 'market forces' - why, if behaviour therapy
is so nluch more successful, do people not choose it in preference to the
discredited psychotherapy? Such an argument is clearly disingenuous. There
are still very few properly qualified behaviour therapists, so there can be no
.proper choice. Few people have heard of the alternatives, so can hardly
make a choice. They are not told of the evidence favouring behaviour therapy,
so cannot make a meaningful choice. 'Market forces' require an open market
where buyers and sellers know what the conditions governing the sale
are; this is demonstrably not so in the psychiatric field. Patients are sent to
the hospital by a general practitioner who has probably never beard of behaviour
therapy, and are seen by a psychiatrist who has been brought up in
the psychotherapeutic tradition, and regards the psychologists who use behaviour
therapy as rivals whose lack of a medical background disqualifies
them from treating patients altogether.
But above all there is the Semmelweiss effect. Semmelweiss was a Hungarian
physician in Vienna who reduced the mortality of women giving
birth in hospital from something like 30 per cent to something like 2 per
cent by asking his colleagues to wash their hands when going from one
woman to another, thus avoiding the infections which were the killers. The
effect was obvious, and so huge, that no argument would seem necessary.
However, his colleagues laughed him out of court, refused to follow his
advice, and finally forced him to go back to Budapest in disgrace. I recall
giving a lecture on behaviour therapy in the university there which bears
his name - honoured centuries after the event. New methods make their
116 Hans Eysenck
way slowly in medicine; there is an immense resistance to change, and
arguments concerning facts, experiments and clinical trials tend to fall on
deaf ears. Psychologists should know better than anyone that human beings
are seldom motivated by rational considerations; in the long run psychoanalytic
notions will be recognized as the oddities they are, but this time
is not yet (Eysenck 1985b). When that happens, behaviour therapy will be
the universal method of choice, and historians will wonder about our
medieval superstitions.
Negative effects of psychoanalysis
It should not be assumed that the term 'victims' has been chosen inadvisedly
in any of the preceding paragraphs. There is ample evidence that psychoanalysis
is not an innocent, if ineffective, method of talking to people. As
Mays and Franks (1985) have shown, there is frequently a negative outcome
in psychotherapy, so that instead of improving the neurotic disorders from
which patients suffer, it actually makes them worse. Not only is there good
evidence that this is true, but also I have suggested a mechanism, derived
from the general theory of neurotic illness in terms of learning theory,
which explains why this is so, and why it would have been expected on a
theoretical basis (Eysenck 1976a; 1976b; 1977; 1982; 1985a). Those who
praise the wonderful effects of psychotherapy customarily disregard or dismiss
the negative effects, the evidence for which is much more impressive.
This is completely irresponsible of course; the essence of the Hippocratic
Oath enjoins us not to harm our patients.
The suggestion that some of the psychological effects of psychoanalysis
may be negative, and harm the patients rather than cure them is often
rejected as being relatively unimportant, the assumption being that negative
consequences cannot be very serious. However, recent work has suggested
that not only are they serious psychologically, but also they may involve
psychoanalysis as a risk factor in cancer and coronary heart disease (GrossarthMaticek
and Eysenck 1990). These data, as well as those suggesting that
behaviour therapy is a very powerful prophylactic aid in avoiding cancer and
coronary heart disease, may not be known to all readers, and hence may
deserve a special mention, illustrating the wide generality of the positive
effects of behaviour therapy, and the negative effects of psychoanalysis.
The work of Eysenck (1987a; 1987b; 1988b; 1989) and of Grossarth-Maticek
and Eysenck (1989) and Grossarth-Maticek et ai. (1988) has demonstrated
very clearly two things. The first is that in large-scale prospective studies,
in which healthy probands were tested for personality, smoking, drinking,
cholesterol levels, blood sugar and blood pressure at the beginning of the
study, and were then followed up for ten years or more, specific personality
reactions to stress were found to be highly predictive of cancer, while other
types of reactions were found to be highly predictive of coronary heart
disease. Personality/stress reactions were six times as predictive of these
The outcome problem in psychotherapy 117
diseases as were smoking, cholesterol level and the other Inedical predictors,
and deaths from cancer and coronary heart disease were very significantly
more frequent in people who were stressed than in people who were
not stressed.
It was also demonstrated that a special type of behaviour therapy used in
changing the behavioural pattern of cancer-prone and coronary heart diseaseprone
probands was highly effective in pireventing death from cancer or
coronary heart disease thirteen years later. When therapy groups were
compared with carefully matched control groups, it was found that out of
fifty controls, sixteen died of cancer, while in the therapy group none died
of cancer. Similarly, out of forty-six controls, sixteen died of coronary heart
disease, while in the therapy group only three died of coronary heart disease.
These results were obtained with thirty hours of individual therapy; similar
results were obtained with group therapy, and with bibliotherapy accompanied
by short-term individual therapy (Grossarth-Maticek and Eysenck
1991; Eysenck and Grossarth-Maticek 1991).
In another study an attempt was made to see whether psychoanalysis,
which is generally regarded as a very stressful procedure, would add to the
stress suffered by cancer-prone and coronary heart disease-prone healthy
probands, and would be associated with an increase in mortality from these
causes. Studies were Inade of some 7,000 inhabitants of Heidelberg who
were first interviewed in 1973. In 1977 probands were asked whether they
had been under any form of psychotherapy, and notes were made at the time
concerning duration and type of treatInent. In 1986 the participants were
followed up, and death and cause of death established by reference to
the death certificates of those who had died.
Two groups of physically healthy probands who were under psychoanalytic
treatment of an orthodox kind, for mild psychiatric disorders in the
main, constituted our therapy groups. One group had been treated for between
one and two years, and had then discontinued treatment. Group 2 had been
in treatment for two years or more, and had not broken off treatment. Two
control groups were created from a large pool of probands so that they could
be matched closely with the two treatment groups on age, sex, personality
type and cigarette consumption. Matching was person-to-person, thus guaranteeing
equality of means and SDs (a measure of variability). A final control
group was created to match the two groups together overall.
Table 5.1 shows the final results of our study. The results make certain
conclusions very clear (at a high level of statistical significance). Cancer, as
expected, is the most frequent cause of death in Type 1 (cancer-prone) persons,
coronary heart disease in Type 2 (CHD-prone) persons. Cancer and coronary
heart disease are most frequent in the group that had psychoanalysis for
over two years, less frequent in those who had psychoanalysis for less than
two years, and least in the control groups whose members were not treated
by psychoanalysis. There is thus in this table clear evidence that psychoanalysis
acts as a stressor, and is a strong risk factor for cancer and coronary
heart disease.
Hans Eysenck
The outcome problem in psychotherapy 119
118
Table 5.1 Mortality from cancer, coronary heart disease ~nd.other cau.ses for These results ought to give pause to those who still advocate the use of
controls and probands treated by psychoanalysis for psychlatnc complamts psychoanalysis as a treatment for neurotic disorders; not only does the literature
suggest that negative consequences of a psychological kind may
Therapy Status Type 1 Type 2 Type 3 Type 4 often follow, but also as we have seen t4ere is now evidence that quite
% % % %
serious health consequences may also follow. Conversely not only is behavCancer
11 7.1 4 4.6 5 4.8 1 100.0 iour therapy superior in curing neurotic patients, but also it can be used as
(1) Up to two years
CHD 7 4.5 5 5.8 6 5.7 0 0 a prophylactic aid in preventing cancer and coronary heart disease. These
of psychoanalysis,
Other 7 4.5 5 5.8 6 5.7 0 0 facts ought to, but probably will not, be instrumental in making therapists
then terminated
Living 129 83.7 72 83.7 87 83.6 0 0 think twice about using the discredited methods introduced by Freud and
Omitted 8 4.9 4 4.4 5 4.5 0 0 his colleagues so many years ago.
Total 162 90 109 1
% % % % Psychoanalysts reply
(2) Psychoanalysis for Cancer 9 9.3 3 6.5 8 7.7 1 33.3
What is the reaction of advocates of psychoanalytic treatment to these
CHD 8 8.2 6 13.0 8 7.7 1 33.3
rather grave charges? Their major reaction has been one of disregarding alllonger than two years,
8.2 5 10.8 7 6.7 1 33.3
not terminated Other 8 criticisms, and discrediting the critics by appealing to the concept of 'resistLiving
72 74.2 32 69.5 81 77.8 0 0
ance'; critics cannot and should not be taken seriously because their critiOmitted
5 14.9 0 0 4 3.7 0 0
Total 102 46 108 3 cisms are based on neurotic motivations of a very subtle kind which only
a psychoanalyst is capable of understanding. It hardly needs a philosopher
% % % % of science to see through this attempt at side-tracking criticism; it is not the
(3) Control group for Cancer 2 1.3 1 1.2 0 0 0 0 motivation of the critics that is at issue, but the truth or otherwise of the
Group I, matched on CHD 1 0.6 2 2.4 0 0 0 0 criticisms made. These require to be answered, regardless of the Illotives of
age, sex, type and Other 3 1.9 2 2.4 3 2.7 0 0 the critics. Furthermore of course the psychoanalysťs answer to the critic
amount of smoking Living 149 96.1 80 94.1 100 95.2 1 100.0 presupposes what has to be proved, namely the correctness of psychoanaOmitted
7 4.3 5 5.5 5 4.6 0 0
lytic theories, including that of 'resistance'. As we know, there is no such
Total 162 90 108 1
evidence (Grunbaum 1984; Eysenck and Wilson 1973).
% % % % Another argument frequently adduced, following Freud, is that neurotic
(4) Control group for Cancer 1 1 1 2.2 0 0 0 0 states are so complicated that it is impossible for any IIIatching to be made
Group 2, matched on CHD 1 1 1 2.2 1 0.9 0 0 between therapy and control groups, so that statistical comparisons and
age, sex, type and Other 1 1 3 6.6 5 4.6 0 0 clinical trials become meaningless and impossible. This arguillent leaves
amount of smoking Living 94 96.9 40 88.8 98 95.1 3 100.0 out the essential feature of all clinical trials, nan1ely the power of random
Omitted 5 4.9 1 2.1 5 4.6 0 0 assignment to eliminate differences between groups. Psychoanalysts have
Total 102 46 109 3 made no attempt to answer this counter-argument and thus their research
% %
has resulted in such absurd and meaningless studies as the Menninger one
% % cited previously.
(5) Control group for Cancer 1 0.6 1 0.5 0 0 1 0.9
A third argument often propounded is that critics assess the success or
Groups 1 and 2 CHD 2 1.2 2 1.0 1 0.9 0 0
failure of treatment merely by looking at the elimination or persistence of
5 2.9 5 2.7 2 1.8 2 1.8
combined, matched Other symptoms, while psychoanalysis aims at a complete restructuring of perLiving
166 95.4 180 95.7 107 96.4 107 97.3
on age, sex,
Omitted 13 6.9 9 46.6 10 8.3 6 5.2 sonality. As Erwin (1978) and Grunbaum (1984) have pointed out, there are
and cigarette
Total 187 197 120 116 two counter-arguments. In the first place, the elimination of symptoms is
consumption
necessary, although it may not be a sufficient criterion for success of
treatments. Second, there is no evidence at all for the success of psychoanalysts
in 'restructuring' personalities, and no proper criteria are offered for
testing this alleged change. Until and unless this is provided, there clearly
is no answer to the criticism that psychoanalysts have no evidence to offer
supporting their claims.
120 Hans Eysenck
It is also frequently adduced that these matters are too complex and
difficult to allow any natural science approach or answer; this argument is
often produced by those who would turn psychoanalysis into a hermeneutic
discipline. However difficult it may be to prove the efficacy of psychoanalysis,
claims have been made in that direction, and require proof. If this proof
is too difficult to obtain, then the claim should be withdrawn until methods
have been elaborated to substantiate it. All scientific advances are difficult
and require complex reasoning and experimentation; claims for success are
not made until such success can be substantiated and replicated.
The final argument originally proposed by Freud, and enthusiastically
adopted by his followers, is what Grunbaum (1979; 1980) has called the
'Tally Argumenť. This argument is based on the premise that 'clinical
data', that is findings coming from within the psychoanalytic treatment
sessions, substantiate all the claims of psychoanalysis. Grunbaum (1984)
suggests that this argument is the basis for five claims made by psychoanalysts,
each of which is of the first importance for the legitimation of the
central parts of Freuďs theory. These five claims are the following:
1 Denial of an irremediable epistemic contamination of clinical data by
suggestion.
2 Affirmation of a crucial difference, in regard to the dynamics of therapy,
between psychoanalytic treatment and all rival therapies that actually
operate entirely by suggestion.
3 Assertion that the psyc.hoanalytic method is able to validate its major
causal claims - such as its specific sexual aetiologies of the various psychoneuroses
- by essentially retrospective methods without vitiation by post
hoc ergo propter hoc, and without the burdens of prospective studies employing
the controls of experimental inquiries.
4 Contention that favourable therapeutic outcome can be warrantedly attributed
to psychoanalytic intervention without statistical comparisons
pertaining to the results from untreated control groups.
5 Avowal that, once the patienťs motivations are no longer distorted or
hidden by repressed conflicts, credence can rightly be given to his or her
introspective self-observations, because these data then do supply
probatively significant information.
It is Grunbaum's (1984) very detailed and competent destruction of this
argument which forms the basis of his book, and his argument has not been
refuted by any philosophers or psychoanalysts, as far as I know. I will not
try to undertake a detailed discussion here as this would obviously be out
of place.
Summary and conclusions
We may now try to see what conclusions can be drawn from this lengthy
discussion. It is sometimes suggested by historians of behaviour therapy
The outcome problem in psychotherapy 121
like Kazdin (1978) and Schorr (1984) that the major contribution of behaviour
therapy has been an insistence on the importance of the outcome
problem, and an attempt to investigate it in relation to the different methods
of behaviour therapy. This is no doubt true in part, but it would seein
that many, too many, behaviour therapist~ have followed the temptations
of. Lazarus (1967; 1971) to go along the primrose path of 'eclectic' therapy
- In other words, to indulge in an arbitrary and subjective mish-mash of
theories, practices and therapies without r~gard to strict outcome nleasures
empirical guidance or experimental contrql. This, taken together with th~
unsc.ientific and arbitrary handling of data by writers such as Luborsky,
BergIn, Lambert, Smith, Glass and Miller, has tended to hide the truth
behind the veil of inaccurate and tendentious assertions and claims.
Rachman and Wilson have made it only too clear that there is still no
good evidence that psychotherapy is any more effective than any reasonable
placebo treatment. As the latest publication by the National Institute of
Me~tal Health Treatment of Depression Collaborative Research Program
(Ellun et al. 1989) makes clear, even after all this time, we are still faced
with a virtual equivalence of lauded programmes of psychotherapy and
placebo treatments. No doubt this study, like all the others showing negative
effect~, will be silently consigned to the oubliette where so many other
negatIve reports are secreted, and there will be no slowing down of claims
for the. wonders that psychotherapy can perform! The people suffering from
neurotIC symptoms whom we are supposed to help will not thank us for
disregarding all the evidence, in continuing to claim successes where no
successes exist. Only behaviour therapy can be exempted from this accusation;
as even Smith et al. (1980) are forced to admit, as a result of their
meta-analysis:
In. those studies in which behavioral therapies were compared directly
WIth developmental therapies, the former were vastly superior. In the
direct comparison of verbal and behavioral therapies, behavioral therapy
has produced reliably larger effects. .
(Smith et al. 1980: 107)
Perhaps future generations will pay more attention to empirical facts than
has been customary over the past half-century; this certainly is a consummation
devoutly to be wished.
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Studies 14: 25-47.
Eysenck, H.J. (1990a) Rebel With a Cause (autobiography). London: W.H. Allen.
The outcome problem in psychotherapy 123
Eysenck, H.J. (1990b) Maverick psychologist, in E. Walker (ed.) History of Clinical
Psychology in Autobiography. Pacific Grove, Calif: Brooks-Cole.
Eysenck, H.J. and .Grossarth-Maticek, R. (1991) Creative novation behaviour therapy
as a prophylactlc treatment for cancer and coronary heart disease. II. Effects of
treatment. Behavior, Research and Therapy 29: 17-31.
Eysenck, H.J. and Martin, 1. (eds) (1987) Theoretical Foundations of Behavior
Therapy. New York: Plenum. I
Eysenck, H.J. and Rachman, S. (1965) Causes and pures of Neurosis. London: Routledge
& Kegan Paul. I
Eysenck, H.J. and Wilson, G.D. (1973) The Expeid.mental Study of Freudian Theories.
London: Methuen. i
Garfield, S. and Bergin, A (1986) Handbook of Psychotherapy and Behavior Change,
3rd edn. New York: Wiley.
Grossarth-Maticek, R. and Eysenck, H.J. (1989) Length of survival and lymphocyte
percentage in women with mammary cancer as a function of psychotherapy.
Psychological Reports 65: 315-21.
Grossarth-Maticek, R. and Eysenck, H.J. (1990) Prophylactic effects of psychoanalysis
of cancer-prone and coronary heart disease-prone probands, as compared with control
groups and behaviour therapy groups. Journal of Behaviour Therapy and Experimental
Psychiatry 21: 91-9.
Grossarth-Maticek, R. and Eysenck, H.J. (1991) Creative novation behaviour therapy
as a prophylactic treatment for cancer and coronary heart disease: 1. Description of
treatment. Behavior, Research and Therapy 29: 1-16.
Grossarth-Maticek, R., Eysenck, H.J. and Vetter, H. (1988) Personality type, smoking
habit and their interaction as predictors of cancer and coronary heart disease.
Personality and Individual Differences 9: 479-95.
Grunbaum, A (1979) Epistemological liabilities of the clinical appraisal of psychoanalytic
theory. Psychoanalysis and Contemporary Thought 2: 451-526.
Grunbaum, A (1980) Epistemological liabilities of the clinical appraisal of psychoanalytic
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Grunbaum, A (1984) The Foundations of Psychoanalysis: A Philosophical Critique.
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Kernberg, O. (1973) Summary and conclusions of 'Psychotherapy and Psychoanalysis',
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124 Hans Eysenck
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Prioleau, 1., Murdoch, M. and Brody, N. (1983) An analysis of psychotherapy versus
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RESPONSE - Sol Garfield
There is little question that Hans Eysenck was, and remains, the staunchest
and foremost critic of psychotherapy, and of psychoanalysis in particular.
Despite the rather significant increase in research on outcome in psychotherapy
in the past thirty years, the results secured haven't caused Eysenck
to change the view he first espoused in 1952, namely that the effectiveness
of psychotherapy has not yet been demonstrated. Thus he exhibits an amazing
consistency in his point of view. In what follows, I shall offer my
appraisal of Eysenck's consistently critical view of the outcome problem in
psychotherapy.
The outcome problem in psychotherapy 125
Earlier responses to Eysenck
There is no question that Eysenck's 1952 article in the Journal of Consulting
Psychology, 'The effects of psychotherapy: an evaluation', created
quite a stir mTIong clinical psychologists,l a number of whom hastened to
publish critiques of the article (DeChar~s et al. 1954; Luborsky 1954;
Rosenzweig 1954). Not only has this article become the most frequently
cited article on outcome in psychotherfPY, but also Eysenck kept the
controversy alive by additional publicat,ions in which he continued to
maintain, and even to increase, his criti~al evaluation of psychotherapy.
(Eysenck 1961; 1966).
My own response to Eysenck's 1952 article was much more positive than
was true of the responses of most of the clinical psychologists I knew. Even
though I could see the important limitations in the 'control groups' used by
Eysenck in his appraisal and in his subsequent estimate of the spontaneous
remission rate of neurotic individuals, I responded positively to his emphasis
on the need to evaluate the effects of psychotherapy. To me, this was an
important and needed emphasis. However, the data presented by Eysenck
did not provide a truly adequate basis upon which to rest his case. Conceivably,
he might have pointed to the need for research in a way which did
not alienate clinicians and that would not be viewed as 'overkilľ.
In my 1957 text on clinical psychology, for example, I had a section entitled
'Evaluation of psychotherapy'. In this section I mentioned the need for
research on outcome and the limitations in the existing research at that
time. I also referred to Eysenck's paper, gave a brief summary of it, and
made the following comment:
At first glance the material presented by Eysenck appears quite damaging
to the entire field of psychotherapy, and, indeed, it is so presented.
However, before accepting such a drastic conclusion, it is worth
discussing at greater length the problems encountered in the evaluation
of therapy.
(Garfield 1957: 334)
In my view, and in the view of many others, Eysenck did not fully evaluate
the limitations in the research reviewed and in the assumptions made for
the two so-called control groups. Once he reached his conclusion about the
effects of psychotherapy, it seemed as if he were reluctant to consider other
alternatives. Certainly, serious questions could be raised about the comparability
of the patients treated in the various studies, the suitability of the
control groups, and the criteria of improvement used. The classification of
patients into the broad classification of 'Neurosis' is an overly broad and
unreliable one on which to base serious conclusions.
Despite the various critiques offered of Eysenck's 1952 article, he continued
to hold to his original conclusions in his later presentations (Eysenck
1961; 1966) and in the present chapter. As I have already indicated, I believe
that Eysenck was fully justified in asserting in his earlier work that the
126 Hans Eysenck
efficacy of psychotherapy had not been demonstrated. Clearly, the existing
research was of poor quality and the rates of improvement reported ranged
rather widely, from 39 per cent to 67 per cent for psychoanalysis and from
41 per cent to 77 per cent for so-called eclectic therapy. However, both the
quantity and quality of research on psychotherapy has increased since the
mid-1950s, and there is a much larger body of data available at present to
be evaluated and from which at least tentative conclusions can be drawn
that do not necessarily agree with those of Eysenck. However, before discussing
this material a few other comments can be offered.
Eysenck's critical pronouncements on psychQtherapy did appear to stimulate
a greater awareness on the part of others to conduct research and to
present evidence in response to his critiques. Meltzoff and Kornreich (1970)
and Bergin (1971) published reviews that included studies not mentioned by
Eysenck and that presented a more favourable view of outcome in
psychotherapy. Bergin, in particular, responded to Eysenck's interpretations
and included a re-analysis of some of the data on psychoanalysis that had
b~en mo~ified and reinterpreted by Eysenck. This led him to offer very
dIfferent Interpretations. In turn, Bergin was rather strongly criticized by
Eysenck's colleague, Rachnlan (1973), and by Eysenck in the present chapter.
There is little question that such heated controversies tend to create
polarization and at times to diminish objectivity. As I have pointed out
elsewhere, 'Whereas Eysenck (1952) came up with a 39 per cent improvement
rate for the Berlin Institute, Bergin (1971) came up with a 91 per cent
rate of improvement! Clearly, no scientific conclusions are possible from
such data' (Garfield 1974: 388).
Since the early 1970s, additional comprehensive and critical reviews of
research on outcome have appeared which are based on a larger number of
studies than those reviewed earlier by Eysenck and that are not alluded to
in his current chapter. Rather than list a series of such references I shall
simply refer to the review by Lambert et al. (1986) which not only e~aluates
the recent literature but also includes a table that summarizes all or
practically all of the meta-analytic reviews that have dealt with outcome in
psychotherapy. Although one can criticize some of the studies included in
the individual meta-analyses, the overall pattern is relatively clear, and
clearly positive. There is a median effect size of 0.82 which does indicate a
positive effect for the psychotherapies evaluated. Interpretations of this effect
size may vary (Rosenthal 1983; Smith et al. 1980), but the direction is clear.
Since Eysenck has questioned this type of finding and its interpretation,
some elaboration is required. According to Smith, Glass and Miller an effect
size of 0.85 signifies that the average treated patient at the end of treatment
is better off than 80 per cent of untreated controls. This is considered to be
a large effect according to Cohen (1977) and such results 'suggest that the
assignment to treatment versus control conditions accounts for some 10 per
cent of the variation in outcome assessed in a typical study' (Lambert et al.
1986: 159). My own interpretation based on a variety of clinical reports and
studies is that about 65 per cent of patients who receive psychotherapy
The outcome problem in psychotherapy 127
show some improvement and that perhaps 10-20 per cent of this group
show marked improvement. Since Eysenck himself has reported an improvement
rate of about 65 per cent for psychotherapy, we agree on this
estimate. However, the interpretation of :this estimate is another matter,
and, therefore, I want to discuss several ar~as where we definitely disagree.
The placebo response
I
One basic disagreement concerns the intel1Pretation of the placebo response
and the role of the placebo as a control in ,psychotherapy research. Eysenck
believes it is a desirable control whereas I and some others see placebos as
by no means 'inerť or comparable to a no-treatment group. Although a
placebo may be appropriate for studies of pharmacological agents, it is not
a meaningful control for psychotherapy. People do respond to a placebo for
a variety of reasons and thus it would appear to have 'psychologicaľ properties.
It-mirrors certain general features that probably constitute some of the
components of the psychotherapeutic process such as the generation of hope,
the support received from the placebo therapist, the feeling that one is doing
something about one's problem, and the like. Thus, in my view it is not an
appropriate control for evaluating psychotherapy outcome per se and some
individuals have referred to it as the 'powerful placebo'. When some forms
of psychotherapy perform little better than some placebos, it may be that
the former rely on the same general factors as the placebo without offering
much in addition. It is well to remember that the placebos used in the
different studies have varied widely (Garfield 1983a). In any event, although
some studies may not show statistically significant differences between a
form of psychotherapy and a placebo, in most of them psychotherapy secures
a visibly larger number who show positive gains.
The recently completed collaborative study of the treatment of depression
co-ordinated by our National Institute of Mental Health is also worth referring
to here (Elkin et al. 1985; 1989). In this study, 239 patients in three medical
centres were assigned randomly to one of four treatment groups: CognitiveBehaviour
Therapy (CBT), Interpersonal Psychotherapy (IPT), Imipramine
plus Clinical Management (IMI-CM) and a Pill Placebo plus Clinical
Management (PLA-CM). Although the placebo group was selected to be a
control for the Imipramine group, comparisons were made with all groups.
The patients studied all met specific criteria of unipolar depression, therapy
manuals were used for training the therapists to ensure the integrity of the
therapies, the therapy sessions were monitored and were conducted in centres
not associated with the developers of the therapies studied, and a variety of
standard measures were used.
The results obtained at the end of treatment are quite similar to those
obtained in many studies (Elkin et al. 1989)- no significant differences were
obtained between the two forms of psychotherapy. Actually, there were few
significant differences among the four treatInent groups although the patients
128 Hans Eysenck
in all groups showed significant improvement over the course of treatment.
In terms of the patients considered 'recovereď at the end of treatment on
the basis of securing a score of six or less on the Hamilton Rating Scale of
Depression, the percentage reaching this level ranged from 51 per cent to 57
per cent for the three treatment conditions and was 29 per cent for the PLAeM
condition. These findings were for those patients who completed treatment.
Although there was a trend toward a statistically significant difference,
the group findings were not statistically significant. Nevertheless, the pattern
obtained is quite comparable to the pattern secured by Smith et aI. (1980)
in their meta-analysis of 475 studies on outcome and deserves some additional
comment.
In the Smith et al. review, the overall effect size (ES) for psychotherapy
was 0.85 whereas the ES for placebos was 0.56. Thus, the ES for the placebo
treatments was somewhat more than half the ES secured for psychotherapy.
In the NIMH study, the ratio of the 'recovery' rate for the pill placebo plus
clinical management to the rate for the two psychotherapies is approximately
the same. In other words, as indicated previously, the so-called placebo used
in many studies is not an inert stimulus, but conceivably contains a number
of the factors that are common to inost of the psychotherapies. In the
NIMH study, for example, each of the patients in the pill-placebo plus
clinical management condition received an intensive diagnostic appraisal
and were seen by a psychiatrist for twenty to thirty minutes throughout the
sixteen weeks designated for the study. Without question, this experience
was beneficial for a certain percentage of patients, but the number was clearly
less than the number helped by the two psychotherapies or Imipramine.
Psychotherapy and behaviour therapy
It is quite evident that Eysenck sharply differentiates behaviour therapy
from psychotherapy, or, preferably, from all other forms of psychotherapy.
He believes firmly that behaviour therapy is effective, and that psychotherapy
is not. I do not know if this is a widely held view in Britain or not,
but I believe most of us in the United States tend to view behaviour therapy
as one form of psychotherapy, and there is currently an organized movement
to attempt some integration of various forms of psychotherapy (Goldfried
and Newman 1986). Be that as it may, there is considerable interaction
among behaviourally oriented clinical psychologists and clinical psychologists
of other theoretical persuasions.
Of more importance, however, is the fact that there have been studies
that compared behaviour therapy with other forms of psychotherapy. Eysenck
does not mention the very well-known study of Sloane et al. (1975) that
compared behaviour therapy and brief psychoanalytically oriented psychotherapy.
This study was distinguished by the fact that the therapists used
were for the most part very experienced and well-known therapists. Joseph
The outcome problem in psychotherapy 129
Wolpe and Arnold Lazarus, for example, were two of the three behaviour
therapists employed in the study and the analytically oriented therapists
were of comparable experience and distinction. Overall, in terms of most of
the group comparisons, there were no ilnportant differences among the two
forms of psychotherapy. In terms of the: primary criteria of change, the
target symptoms of each patient, both the*pies secured significantly better
results than a wait-list control group, and were not significantly different
from each other. Furthermore, of particular interest was the finding that at
the end of therapy, 'The successful patients in both therapies placed primary
importance on more or less the same iteJ:tls, (Sloane et aI. 1975: 206).
As I have noted elsewhere, 'The Society for Psychotherapy Research in
1980 awarded Sloane and his colleagues its first award for an outstanding
research study in. the area of psychotherapy' (Garfield 1981: 39). Although
the study was criticized by several behavioural psychologists (Bandura 1978;
Kazdin and Wilson 1978; Rachman and Wilson 1980), similar findings have
been reported by others (Berman et al. 1985; Thompson et aI. 1987; Zeiss
et al. 1979). Space limitations preclude additional elaboration.
Concluding comments
As I indicated previously, despite inadequacies in the evaluation made by
Eysenck in his 1952 article, I responded very positively to his emphasis on
the need to evaluate the effects of psychotherapy. 'There is little question
that this was an important event historically and helped focus attention on
the need to evaluate the effectiveness of psychotherapy' (Garfield 1983b: 35).
I also felt his criticisms of psychoanalysis had justification and I, too, offered
a strong criticisln of the eighteen-year Menninger study (Garfield 1981).
However, my current view of the research on outcome in psychotherapy
diverges from that of Eysenck. His view has remained unchanged since 1952
and apparently the accumulated research over forty years has had little
impact on him. In my opinion, Eysenck has adhered too fixedly to his views
concerning spontaneous remission, the placebo response and the complete
superiority of behaviour therapy over all other forms of therapy. Because of
this, he has not been able to accept the fact that even if neurotic patients
recover in two years without treatment, they may be helped more rapidly
by means of psychotherapy. In a similar fashion, although behaviour therapy
may be the most effective for such disorders as phobias, compulsions and
infantile autism, there is considerable comparability in outcomes for behaviour
therapy and other forms of therapy for a variety of other problems and
this does suggest the possibility of important common factors among the
psychotherapies (Garfield 1980; Lambert et aI. 1986). We shall not settle our
differences here and both of us most likely won't be around when these
issues may be settled more conclusively on the basis of better research in
the future.
130 Hans Eysenck
References
Bandura, A. (1978) On paradigms and recycled ideologies. Cognitive Therapy and
Research 2: 79-104.
Bergin, A.E. (1971) The evaluation of therapeutic outcomes, in A.E. Bergin and S.L.
Garfield (eds) Handbook of Psychotherapy and Behavior Change: An Empirical
Analysis. New York: Wiley.
Bergin, A.E. and Lambert, M.J. (1978) The evaluation of therapeutic outcomes, in S.L.
Garfield and A.E. Bergin (eds) Handbook of Psychotherapy and Behavior Change:
An Empirical Analysis, 2nd edn. New York: Wiley.
Berman, J.S., Miller, R.C. and Massman, P.J. (1985) Cognitive therapy versus systematic
desensitization: is one treatment superior? Psychological Bulletin 97: 451-61.
Cohen, J. (1977) Statistical Power Analysis for the Behavioural Sciences. New York:
Academic Press.
DeCharms, R., Levy, J. and Wertheimer, M. (1954) A note on attempted evaluations
of psychotherapy. Journal of Clinical Psychology 10: 233-5.
Elkin, 1., Parloff, M.B., Hadley, S.W. and Autry, J.H. (1985) National Institute of
Mental Health Treatment of Depression Collaborative Research Program: background
and research plan. Archives of General Psychiatry 42: 305-16.
Elkin, 1., Shea, M.T., Watkins, J.T., Imber, S.D., Sotsky, S.M., Collins, J.F., Glass,
D.R., Pilkonis, P.A., Leber, W.R., Docherty, J.P., Fiester, S.J. and Parloff, M.B.
(1989) National Institute of Mental Health Treatment of Depression Collaborative
Research Program: general effectiveness of treatments. Archives of General Psychiatry
46: 971-82.
Eysenck, H.J. (1952) The effects of psychotherapy: an evaluation. Journal of Consulting
Psychology 16: 319-24.
Eysenck, H.J. (1961) The effects of psychotherapy, in H.J. Eysenck (ed.) Handbook of
Abnormal Psychology. New York: Basic Books.
Eysenck, H.J. (1966) The Effects of Psychotherapy. New York: International Science
Press.
Garfield, S.L. (1957) Introductory Clinical Psychology. New York: Macmillan.
Garfield, S.L. (1974) Clinical Psychology: The Study of Personality and Behavior.
Chicago: Aldine.
Garfield, S.L. (1980) Psychotherapy: An Eclectic Approach. New York: Wiley.
Garfield, S.L. (1981) Psychotherapy: a 40-year appraisal. American Psychologist 36:
174-83.
Garfield, S.L. (l983a) Commentary. Does psychotherapy work? Yes, No, Maybe?
Behavioral and Brain Sciences 6: 292-3.
Garfield, S.L. (1983b) The effectiveness of psychotherapy: the perennial controversy.
Professional Psychology 14: 35-43.
Goldfried, M.R. and Newman, C. (1986) Psychotherapy integration: an historical
perspective, in J.c. Norcross (ed.) Handbook of Eclectic Psychotherapy. New York:
Brunner/Mazel.
Kazdin, AE. and Wilson, G.T. (1978) Evaluation of Behavior Therapy: Issues, Evidence,
and Research Studies. Cambridge, Mass: Ballinger.
Lambert, M.J., Shapiro, D.A and Bergin, A.E. (1986) The effectiveness of psychotherapy,
in S.L. Garfield and AE. Bergin (eds) Handbook of Psychotherapy and Behavior
Change, 3rd edn. New York: Wiley.
Luborsky, L. (1954) A note on Eysenck's article, 'The effects of psychotherapy: an
evaluation'. British Journal of Psychology 45: 129-31.
The outcome problem in psychotherapy 131
Meltzoff, J. and Kornreich, M. (1970) Research in Psychotherapy. New York: Atherton
Press.
Rachman, S. (1973) The effects of psychologiq.al treatment, in H.J. Eysenck (ed.)
Handbook of Abnormal Psychology. New Yqrk: Basic Books.
Rachman, S.J. and Wilson, G.T. (1980) The Effeqts of Psychological Therapy: Second
enlarged edition. New York: Pergamon. i
Rosenthal, R. (1983) Assessing the statistical ifnportance of the effects of psychotherapy.
Journal of Consulting and Clinical Psychology 51: 4-13.
Rosenzweig, S. (1954) A transvaluation of psychotherapy: a reply to Hans Eysenck.
Journal of Abnormal and Social Psychology 49: 298-304.
Sloane, R.B., Staples, F.R., Cristol, A.H., Yorkston, N.J. and Whipple, K. (1975)
Psychotherapy versus Behavior Therapy. Cambridge, Mass: Harvard University Press.
Smith, M.L., Glass, G.Y. and Miller, T.1. (1980) The Benefits of Psychotherapy. Baltimore,
Md: Johns Hopkins University Press.
Thompson, L.W., Gallagher, D. and Breckenridge, J.S. (1987) Comparative effectiveness
of psychotherapies for depressed elders. Journal of Consulting and Clinical
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Zeiss, A., Lewinsohn, P. and Munoz, R. (1979) Nonspecific improvement effects in
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REBUTTAL - Hans Eysenck
I am not at all convinced that Garfield and I differ all that much with
respect to answers; we may well differ with respect to questions.
This may mirror our respective major commitments to therapy and
science. Garfield sees large numbers of people suffering from neurotic
disorders; his major interest is in what may help them. I see a scientific
problem of discovering why neurotics fall prey to neurotic disorders, why
they seem to recover without treatment, or with placebo treatment, whether
any of the treatlllents based on some form of theory does better than
placebo treatment, or any alternative form of treatment, and to what extent
results bear out theoretical preconceptions. My emphasis thus has been to
build a lllodel which would incorporate the major en1pirical findings. On
these findings Garfield and I seem to agree for the most part, but there is
a curious lack of response by Garfield to my interpretation of these findings.
I have tried to show that if 'all have won, and all must have prizes' is
really true; that is if different forms of treatment based on different theories
have the same effect, then all these theories must be wrong. Each theory
predicts that the treatment based on it will be significantly more successful
than treatments based on other (false) theories; if that prediction fails, then
the theory fails. The result would seem to be that all theories concerning
psychotherapy are wrong (I am here sharply divorcing psychotherapy from
behaviour therapy). Garfield does not tell us whether he agrees with this
conclusion, but it seems to me incontrovertible, and highly damaging to the
132 Hans Eysenck
whole enterprise seen as a scientific endeavour to build a proper model of
therapeutic effectiveness.
The placebo response, I believe, is particularly important in this discussion.
I fully agree with Garfield that placebos are by no means inert, but
have 'psychologicaľ properties. I would go even further than that and say
that what a 'non-treatment controľ does to alleviate a person's suffering
(consult a priest, discuss his or her problems with a friend, talk over worries
and anxieties with a family member) has the same psychological properties,
and explains the'spontaneous remission' which has been found so successful.
If there is a grading from 'spontaneous remission' through placebo treatment
to psychotherapy and finally to behaviour therapy, I would explain this in
tenns of a model which makes desensitization and other methods of behaviour
therapy the fundamental ingredients in successful treatment (Eysenck
1980). The differential effectiveness of their methods would be explained in
terms of the deliberate use of these methods, least for spontaneous remission,
most for behaviour therapy. It should be remembered that nearly all these
encounters contain some personal interaction between patient and therapist
- friend-priest-relative, in which friendly acceptance facilitates desensitization.
The only exception would be psychoanalysis along classical lines in
which such sympathetic aid and friendly interaction is neglected in favour
of dogmatic neutr~llity and 'interpretation' (Sutherland 1976). It is this that
probably accounts for the 'negative outcome in psychotherapy' (Mays and
Franks 1985) that Garfield fails to mention.
Garfield is right in thinking that I make a firm distinction between behaviour
therapy and psychotherapy, and he is also right in saying that in the
United States there is some attempt to produce some integration between
them. Seeing how different the theories are on which behaviour therapy and
psychotherapy are based, it will be interesting to see how such reconciliation
is produced. My own interpretation would be that what is sought is simply
an eclectic mish-mash of theories (Eysenck 1970) signifying nothing, and
completely untestable scientifically. I am certainly unaware of any demonstration
that a treatment based on such a confabulation has been shown
significantly superior to behaviour therapy. To some this may read like
dogma; I have elsewhere argued that behaviour therapy is applied science,
not dogma, and that science is not well served hy eclectic committee decisions,
but only by firm theorizing and experimental testing of deductions
(Eysenck 1976).
It is sometimes suggested that behaviour therapy, based on deductions
from learning theory, has been displaced by cognitive behaviour therapy,
which admits cognitive elements. This, it is suggested, brings behaviour
therapy and psychotherapy closer together.
This argument is completely fallacious (Eysenck and Martin 1987). Learning
theory from Pavlov onwards has always included cognitive elements,
and these are absolutely fundalnental (Mackintosh 1984). Criticisms based
on the aberrations of Watson or Skinner are irrelevant; in my definition of
behaviour therapy as being based on modern learning theory, I laid special
The outcome problem in psychotherapy 133
emphasis on the relevant theories being modern, not anchored in the early
1920s. The term 'cognitive behaviour therapy' is either an oXylnoron or a
tautology, and it should be eliminated from meaningful scientific discourse.
One final comment. Garfield cites some meta-analyses which at times
seem to contradict my conclusions based on other meta-analyses. But disagreements
between meta-analysts are no les~ frequent than those between
reviewers prior to the advent of this particular type of analysis. Wittman
and Matt (1986), for instance, in a meta-analysis of the large body of German
studies, found, contrary to Smith et al. (1980) that quality of study did
make a large difference, and that the effects of different types of psychotherapy
did differ with therapies of behavioural orientation showing the highest
effects. (Riedel and Schneider-Duker (1991) criticize and extend this discussion.)
What all this suggests to me is that in the presence (still!) of gross
disagreement between experts (Rachman vs Bergin; Wittman and Matt vs
Smith, Glass and Miller; Wolpe vs Lambert), it would be premature to dismiss
my original conclusion that the superiority of psychoanalytic treatment
or psychotherapy over (credible) placebo treatment had not been proved
beyond reasonable doubt. (The average effect size of placebo treatment is
badly affected by placebos which lack credibility.) For behaviour therapy I
would claim a more positive conclusion; such advances as those demonstrated
by Rachman and Hodgson (1980) over all previous therapeutic interventions
in the treatment of obsessive-compulsive disorders show what
can be done when we take theories seriously, and base our methods of
treatment on modern learning theory. But above all I agree with Garfield on
the need for better research in the future; this alone will settle any differences.
References
Eysenck, H.J. (1970) A mish-mash of theories. International Tournai of Psychiatry
9: 140-6.
Eysenck, H.J. (1976) Behaviour therapy - dogma or applied science?, in M.P. Feldman
and A. Broadhurst (eds) The Theoretical and Experimental Foundations of Behaviour
Therapy. London: Wiley.
Eysenck, H.J. (1980) A unified theory of psychotherapy, behaviour therapy and spontaneous
remission. Zeitschrift fUr Psychologie 188: 43-56.
Eysenck, H.J. and Martin, I. (eds) (1987) Theoretical Foundation of Behaviour
Therapy. New York: Plenum.
Mackintosh, N.J. (1984) Conditioning and Associative Learning. Oxford: Clarendon.
Mays, D.T. and Franks, C.M. (1985) Negative Outcome in Psychotherapy. New York:
Springer.
Rachman, S. and Hodgson, R. (1980) Obsessions and Compulsions. Englewood Cliffs,
NJ: Prentice-Hall.
Riedel, H. and Schneider-Duker, M. (1991) Kontextbedingungen 'Kontrollierter' und
'Unkontrollierter' Psychotherapieforschung. Psychologische Rundschau 42: 19-28.
Smith, M.L., Glass, G.V. and Miller, T.I. (1980) The Benefits of Psychotherapy. Baltimore,
Md: Johns Hopkins University Press.
134 Hans Eysenck
Sutherland, S. (1976) Breakdown. London: Weidenfeld &- Nicolson.
Wittman, W.W. and Matt, G.E. (1986) Meta-Analyse als Integration von Forschungsergebnissen
am Beispiel deutschsprachiger Arb,~iten zur Effektivitiit von Psychotherapie.
Psychologische Rundschau 37: 20-40.
SIX
I
The tnytn of therapist
expertise i
KATHARINE MAIR
Psychotherapists of the 1990s are in many ways in a silnilar position to the
physicians of eighty years ago. Their patients have faith in their expertise
and expect them to say what is wrong and how to put it right. Psychotherapists'
understanding of patients' problems, and knowledge about how they
can be remedied is, however, very much less than they imagine. It is also
less than therapists imagine. They have been through a training which
claims to give them a model by which to understand their patients, and
methods by which to treat them. Physician and psychotherapist alike believe
in their models and methods because they see them work. I hope to
demonstrate that, although psychotherapy can be a valuable means of helping
people, its efficacy is not due primarily to the models and methods that
it uses (which may be as irrelevant to the patienťs problems as the application
of leeches was to the curing of a fever eighty years ago), and that too
blind a faith in them may actually interfere with therapists' ability to help
their patients. George Bernard Shaw voiced his scepticism of the doctors of
his day in his preface to The Doctor's Dilemma in 1911. His comments seem
appropriate to this argument.
The expert healer
I presume nobody will question the existence of a widely spread popular
delusion that every doctor is a man of science.
(Shaw 1911)