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Placebo Effects in Psychotherapy: A Flawed Concept and a Contorted History

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In this article, we examine the history and controversy of the placebo in psychotherapy. In medicine, beginning in the 1950s, the use of the placebo in double-blind randomized trials has allowed the identification of specific treatments. It seemed logical to researchers that this strategy could be fruitfully adapted for studying psychotherapy. However, Rosenthal and Frank (1956) noted that the analogy would likely fail because there is no such thing as an “inert psychotherapy.” Notwithstanding the problems with psychotherapy placebos, psychotherapy research moved forward with efforts to make inferences about specificity using placebo types control groups. The discussion of specificity and the therapeutic value of the common factors raise the issue of whether psychotherapy is in and of itself a placebo.
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Placebo Effects in Psychotherapy: A Flawed Concept
and a Contorted History
Bruce E. Wampold
University of Wisconsin–Madison and Modum Bad
Psychiatric Center, Vikersund, Norway
Nickolas D. Frost and Noah E. Yulish
University of Wisconsin–Madison
In this article, we examine the history and controversy of the placebo in psychotherapy.
In medicine, beginning in the 1950s, the use of the placebo in double-blind randomized
trials has allowed the identification of specific treatments. It seemed logical to research-
ers that this strategy could be fruitfully adapted for studying psychotherapy. However,
Rosenthal and Frank (1956) noted that the analogy would likely fail because there is no
such thing as an “inert psychotherapy.” Notwithstanding the problems with psycho-
therapy placebos, psychotherapy research moved forward with efforts to make infer-
ences about specificity using placebo types control groups. The discussion of specificity
and the therapeutic value of the common factors raise the issue of whether psycho-
therapy is in and of itself a placebo.
Keywords: common factors, placebo, psychotherapy, specificity
The pharmacopoeias of European medicine of
the 17th century contained such substances as
Vigo’s plaster (viper’s flesh with live worms and
frogs), fox lungs, moss from the skulls of victims
of violent death, Gascoyne’s powder (Bezoar, am-
ber, pearls, crab’s eyes and claws, and coral),
human urine, various sexual organs, excreta (from
many different sources), human placenta, saliva
from fasting individuals, and wood lice (Shapiro
& Shapiro, 1997b). However, as science and the
scientific method were evolving in Europe in the
Cartesian context, it became apparent that most of
the substances in the pharmacopoeias were not
effective. Indeed, only a very few seemed to be
effective for particular diseases (e.g., foxglove for
congestive heart conditions and cinchona bark for
malaria) (Shapiro & Shapiro, 1997b). We now
call the inert substances given to please the patient
placebos. But the concept of the placebo, and its
related concept the placebo effect, are complex
and have a rather contorted history.
In 1785 the term placebo entered the medical
lexicon and was applied to treatments that were
known to be ineffective physiochemically but sat-
isfied the patient’s desire to be treated (Shapiro &
Shapiro, 1997b). The term, according to Walach
(2003), originated from the Latin psalm verse,
“Placebo Domino in regione vivorum” (“I shall
please the Lord in the land of the living”), which
was sung in the Middle Ages as a prayer at the
deathbed. Because others were often paid to do
the singing, the term placebo became associated
with a “nearly fraudulent replacement of the real”
(Walach, p. 178). A placebo, since its origin, has
carried a tainted connotation—those who admin-
istered a substance simply to please the patient
became repugnant and those who claimed that a
“placebo” was curative would risk being labeled a
charlatan. Nevertheless, the effects of placebos are
real and now constitute a legitimate area of inquiry
(see, e.g., Benedetti, 2011,2014;Price, Finniss, &
Benedetti, 2008).
(Very) Brief History of Placebo Effects and
Placebo Control Groups in Medicine
The use of randomized designs in medical
and psychological research are so ingrained in
Bruce E. Wampold, Department of Counseling Psychol-
ogy, University of Wisconsin–Madison, and Modum Bad
Psychiatric Center, Vikersund, Norway; Nickolas D. Frost
and Noah E. Yulish, Department of Counseling Psychology,
University of Wisconsin–Madison.
Correspondence concerning this article should be ad-
dressed to Bruce E. Wampold, Department of Counseling
Psychology, 335 Education Building, 1000 Bascom Mall,
University of Wisconsin, Madison, WI 53705. E-mail:
bwampold@wisc.edu
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Psychology of Consciousness: Theory, Research, and Practice © 2016 American Psychological Association
2016, Vol. 3, No. 2, 108–120 2326-5523/16/$12.00 http://dx.doi.org/10.1037/cns0000045
108
our minds that many of us forget that they are
relatively recent inventions. Early examples of
rudimentary designs using blinding, and pla-
cebo type groups date back at least to efforts to
discredit Mesmer around 1784 (see Kaptchuk,
1998 for a thorough review of the history of
these designs). In the early twentieth century
significant methodological and statistical ad-
vances were made to the randomized design to
increase the validity of the inferences of these
designs and these advances were utilized in
three areas. The first application involved ex-
amining procedures in education, where in the
early 1920s the treatment group design was
“being sold to American school superintendents
as the ‘control experiment’ and touted as a key
element in comparing the ‘efficiency’ of various
administrative measures” by the American Psy-
chological Association (Danziger, 1990,p.
114). The scientific bases of these designs were
developed and presented in McCall’s (1923)
volume How to Experiment in Education. Dur-
ing the same period, Sir Ronald Fisher, who was
developing methods to study agricultural prac-
tices, developed further the notion of random-
ization and derived various statistical methods
for making inferences from the data produced
by such designs, the best known of which is the
analysis of variance (Danziger, 1990;Gehan &
Lemak, 1994;Shapiro & Shapiro, 1997b). Fish-
er’s volumes Statistical Methods for Research
Workers (Fisher, 1925) and The Experimental
Design (Fisher, 1935) formed, with little mod-
ification, the bases for all randomized designs in
medicine and the social sciences.
Medicine needed to take randomized design
one step further. The goal of modern medicine
was to establish that the benefits of any medical
treatment were attributable to the physiochemi-
cal properties of the interventions and not to the
patient’s expectations, hopes, or other psycho-
logical processes, thereby establishing the speci-
ficity of the purported active ingredients of the
procedures. To rule out threats to validity attrib-
utable to these psychological factors, researchers
in the late 1930s began to use double-blind pla-
cebo studies in the United States and the United
Kingdom, but the method did not take root, ap-
parently because placebo carried a negative con-
notation (Gehan & Lemak, 1994;Shapiro & Sha-
piro, 1997a,1997b). Gradually however, the
acceptance of the randomized double-blind pla-
cebo design spread. Harry Gold, a pharmacologist
and one of those given credit for the development
of the placebo control group design in medicine
the United States, participated in several confer-
ences at Cornell University on the subject in the
late 1940s and early 1950s and he became the first
professor of Clinical Pharmacology, a new disci-
pline (Kaptchuk, 1998;Shapiro & Shapiro,
1997b). As noted by Shapiro and Shapiro (1997b):
Gold advocated a comparison between “an allegedly
potent agent and a blank of such physical properties as
to render a distinction between the two impossible
except through some pharmacologic potency which
may exist...[the recommended] double-blind proce-
dure which calls for an investigation in which neither
the patient nor the doctor is aware of the identify of the
two agents until the results are in and analyzed. This is
imperative to avoid the influence of subconscious bias”
(Gold, 1954, p. 724). The statement by Gold culmi-
nated 20 years of pioneering study of methods with
which to reliably and validly evaluate the effectiveness
of new drugs (p. 148).
The work of Gold as well as others became
the basis for the procedures used by the United
States Food and Drug Administration (FDA) to
approve drugs for marketing the drug for a
specific disorder (Shapiro & Shapiro, 1997b).
The logic of the design is understood by exam-
ining Figure 1, where patients hypothetically
were randomly assigned to three conditions: no
treatment, a pill placebo, and active medication.
Let’s assume the study is conducted well in that
blinding is accomplished to the extent possible,
the measures are psychometrically sound, and
the analysis is correctly conducted. The course
of the disorder for those assigned to no treat-
ment (ideally) represents the natural history of
the disorder as well as other possible effects
(e.g., regression toward the mean). Indeed, pa-
tients in no treatment groups seem to improve
over time (e.g., depression; Minami, Wampold,
Serlin, Kircher, & Brown, 2007). Taking a pill
placebo has an effect for many disorders—the
separation between the outcome for patients
taking the placebo versus the outcome for pa-
tients taking no medication or receiving no in-
tervention is what is commonly called the pla-
cebo effect, the size of which is an issue which
will be discussed shortly. The separation be-
tween the active medication and the placebo can
be labeled as the specific treatment effect—this
is the effect that medicine cherishes. Indeed, as
part of the approval process, the FDA requires
109PLACEBO EFFECTS IN PSYCHOTHERAPY
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at least two trials that show the drug is superior
to a pill placebo (Spielmans & Kirsch, 2014).
1
In medical clinical trials, inclusion of a no
treatment control group is uncommon, as the
placebo’s therapeutic effect is of no interest. It
is the effects of the drug that are attributable to
the active ingredients that are of interest in
medicine—the goal is to rule out effects attrib-
utable to hope, expectation, the ritual of taking
a medication, conditioning, and so forth. A pre-
ponderance of the substances in the pharmaco-
poeias of European medicine of the 17th cen-
tury mentioned earlier would fail under the
scrutiny of the FDA requirements, and with
good reason.
Despite the lack of interest in, or even the
disdain of placebos, there have been attempts in
medicine to estimate the size of the placebo
effect. In an oft cited study, Beecher (1955)
reviewed many studies and concluded that the
placebo “had a high degree of therapeutic ef-
fectiveness in treating subjective responses” in
about a third of patients (p. 1606), justifying the
title of the article “The Powerful Placebo.”
However, in a meta-analysis of studies that con-
tained a placebo condition and a no-treatment
condition, with the title “Is the placebo power-
less?” which was used to foreshadow the re-
sults, Hróbjartsson and Gøtzsche (2001)
claimed, “We found little evidence in general
that placebos had powerful clinical effects” (p.
1594; see also Hróbjartsson & Gøtzsche, 2004).
However, these results were challenged in a
reanalysis of the same trials based on concep-
tual and statistical grounds, with the conclusion,
again in the title, “The Placebo is Powerful”
(Wampold, Minami, Tierney, Baskin, & Bhati,
2005), creating a bit of a contentious inter-
change between the various authors (see Hrób-
jartsson & Gøtzsche, 2006;Hróbjartsson &
Gøtzsche, 2007;Wampold, Imel, & Minami,
2007a,2007b). As well, Vase, Riley, and Price
(2002) noted that clinical studies are not de-
signed to detect placebo effects and con-
firmed this conjecture in a meta-analysis that
showed that placebo experiments (i.e., studies
designed to investigate the placebo effect)
produced larger effects than clinical studies.
Moreover, the experimental studies have pro-
duced evidence of neurological and physio-
logical effects as well as subjective reports of
placebos (Benedetti, 2014;Price et al., 2008).
Finally, Kirsch and colleagues have provided
convincing evidence that to a great extent the
effects of antidepressants are placebo effects
(Kirsch, 2000,2002,2009;Kirsch, 2010;
Kirsch, Moore, Scoboria, & Nicholls, 2002;
Kirsch & Sapirstein, 1998).
Having a general notion of placebos and pla-
cebo effects as well as the designs using placebo
controls in medicine, we turn our attention to
these topics in the context of psychotherapy.
Placebos and Psychotherapy—The
Beginning
In the 1950s when Gold was discussing pla-
cebos in medicine, the idea of the placebo, as a
means to understand how psychotherapy works
and as a control condition to establish specific-
ity, came to the attention of psychotherapy re-
searchers. In 1956, two prominent psychother-
1
Actually, superiority to pill placebo is not required, but
typically most such comparisons form the basis of the
evidence submitted to the FDA by the manufacturer.
Figure 1. Conceptualization of natural history, placebo effects, and specific treatment
effects.
110 WAMPOLD, FROST, AND YULISH
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apy researchers, David Rosenthal, of the
National Institute of Mental Health, and Jerome
Frank, of the School of Medicine at Johns Hop-
kins, authored a seminal article entitled “Psy-
chotherapy and the Placebo Effect.” This article
foreshadowed the issues that were to bedevil
psychotherapy research for the coming de-
cades—all too often we repeat mistakes because
we neglect literature that we might classify as
“ancient.”
Rosenthal and Frank (1956) understood the
nature of placebos and the emerging placebo
control group in medicine: “The relief of any
particular complaint by a given medication is
not sufficient evidence for the specific effect of
the medicine on this complaint unless it can be
shown that the relief is not obtained as a placebo
effect” (p. 296). Analogously to medicine, “psy-
chotherapists have theories of personality and
psychotherapy and therapeutic actions in the
belief that these are the active agents which
produced the desired results” (p. 296). Conse-
quently, Rosenthal and Frank indicated that pla-
cebo controls could be used to establish speci-
ficity in psychotherapy:
To show that a specific form of [psychotherapy] pro-
duces more than a nonspecific placebo effect it must be
shown that its effects are stronger, last longer, or are
qualitatively different from those produced by the ad-
ministration of placebos, or that it affects different
types of patients (p. 297). If we do not control for
nonspecific factors like the placebo effect, we cannot
know whether effects predicted from a theory lead to
or result from improvement based on the nonspecific
effect (p. 299).
They went in a more prescriptive fashion to
explain what was needed:
1. A theory of personality and psychological
distress (neurosis, maladjustment, etc.).
2. Predictions of effects in the patient or cli-
ent consequent to psychotherapy, in ac-
cord with the theory.
3. Demonstration of a relationship between
the predicted effects and some criterion of
improvement.
4. Demonstration that the predicted effects
and their relationship to the improvement
criterion are not primarily attributable to
the patient’s conviction that therapy will
help him. This will permit greater confi-
dence that the relationship found is spe-
cific to the therapeutic technique derived
from the theory (p. 299).
On the face of it, it would seem that
Rosenthal and Frank (1956) were suggesting
that psychotherapy research follow the medical
model in that the placebo control group could be
used to establish the specificity of various psy-
chotherapeutic approaches. But this was not the
case. They realized that the effectiveness of
psychotherapy may indeed be related to the
ways in which the placebos work: “It may well
be that the efficacy of any particular set of
therapeutic operations lies in their analogy to a
placebo in that they enhance the therapist’s and
patient’s conviction that something useful is
being done” (p. 296). They went on to say
emphatically that these conditions could not be
met, especially the fourth condition:
The fourth condition has not been met in any research
of which we are aware. It is not possible to set up an
experiment precisely analogous to comparison of a
medication with a placebo because there is no such
thing as inert psychotherapy in the sense that placebos
are pharmacologically inert.
Since 1956 when Rosenthal and Frank laid
out the dilemma about using placebo control
groups in psychotherapy, there have been em-
pirical and logical analyses of the problems with
using psychotherapy placebos (Bowers &
Clum, 1988;Colloca & Benedetti, 2009;Critelli
& Neumann, 1984;Grünbaum, 1981;Horvath,
1988;Kirsch, 1997;Shapiro & Morris, 1978;
Wampold & Imel, 2015;Wampold et al., 2005;
Wilkins, 1983,1984). The problems with pla-
cebo controls are many, including the lack of
blinding, the fact that the active treatment and
the psychological placebo are distinguishable,
the logical impossibility of creating a placebo
with inert ingredients, the fact that the active
ingredients depend on relationship factors for
their delivery, among others (see Kirsch,
Wampold, & Kelley, 2016). Despite these prob-
lems, researchers in psychotherapy continue to
put their faith in establishing specificity with
placebo type control groups, a topic to which
we know turn.
Placebo Type Controls and a History of
Improper Inference
Shortly after Rosenthal and Frank’s (1956)
article on the use of placebos in psychotherapy
111PLACEBO EFFECTS IN PSYCHOTHERAPY
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research, psychotherapy researchers began to
design control groups to establish the efficacy
and specificity of treatments. These placebo
treatments, labeled in various ways, were used
first, it seems, by behavior therapists, primarily
in the area of systematic desensitization. A brief
review of a few studies from this era is infor-
mative historically.
Systematic desensitization (SD) was devel-
oped by Joseph Wolpe (Wolpe, 1958) as a treat-
ment for phobias and is based theoretically on
the mechanism of reciprocal inhibition. In this
procedure the patient is imaginally exposed to
the feared stimulus when in a state that is in-
compatible to fear, such as when relaxed. The
initial step of the procedure involves the cre-
ation of a hierarchy of feared situations, from
least to most threatening. Next the patient is
assisted to acquire relaxation skills (i.e., the
incompatible response). Finally the patient pro-
gresses through the developed hierarchy by
imagining their feared situation while relaxed
and only ascending the hierarchy when the cur-
rent situation is tolerated without anxiety. There
is some debate about whether an anxiety com-
peting response to the stimulus is needed or
whether the absence of an aversive consequence
to the stimulus is sufficient (i.e., an extinction
explanation). A number of studies in the early
1960s demonstrated that SD was an effective
and efficient treatment for phobias. However,
there were disagreements about what the ev-
idence demonstrated in terms of how SD
worked, and these disagreements rested
largely on the nature of placebo-type control
groups.
Gordon Paul investigated the mechanisms of
SD using performance anxiety created by public
speaking. In a series of studies, Paul and col-
leagues (see Paul & Shannon, 1966) compared
SD with an alternative treatment (insight ori-
ented psychotherapy) and an “attention-placebo
treatment,” the latter of which was included to
“determine the degree of improvement which
might be attributed to nonspecific treatment ef-
fects such as: expectation of relief; attention,
warmth, and interest of the therapist (therapeu-
tic relationship; suggestion, and ‘faith’” (p.
127). Participants in the placebo condition were
told the treatment was a method of training for
working under stress and were given a pill pla-
cebo described as having a tranquilizing effect
at the beginning of every session. Participants
were then given what was described as a stress-
ful task (e.g., identifying particular sounds in an
audio tape) and the therapists, who did not
interact with the participants, purportedly re-
corded the patient’s responses. The SD par-
ticipants improved to a greater extent than the
participants in the insight oriented and the
attention-placebo control group, supporting
not only the efficacy of SD, but the mecha-
nisms of change, as purportedly the attention-
placebo treatment controlled for nonspecific
factors.
About the same time as Paul’s investigation,
Lang, Lazovik, and Reynolds (1965) compared
SD with relaxation and hypnotic states as the
counterconditions to anxiety, to “pseu-
dotherapy,” and no treatment controls. Psue-
dotherapy was “an effort...toinvolve the
subject in a treatment procedure that was ther-
apeutically neutral except for the therapist-
client relationship” (p. 396). Effort was made
for the pseudotherapy to be similar in several
respects to the SD, including providing a cogent
explanation for the procedure, creation of the
hierarchy, and involvement of relaxation and
hypnotic states. However, the therapist in this
condition prevented the patient from phobic re-
actions in the session by steering the conversa-
tion away from material related to the phobia.
The sessions consisted mainly of using the
items in the hierarchy to begin a conversation
about the patient’s life that did not elicit anxi-
ety. The results showed that SD was superior
to no-treatment and pseudotherapy; moreover
pseudotherapy was not more effective than no
treatment. The authors concluded, “These re-
sults imply that the reduction in fear follow-
ing desensitization does not stem from a sug-
gestion to change implicit in being ‘in
therapy’” (p. 400).
The results of the two experiments on SD
described here, as well as other studies at the
time, seemed to support not only the efficacy of
SD but the conditioning mechanisms hypothe-
sized to be responsible for the benefits. How-
ever, the results of these studies generally ig-
nored the credibility of placebos as well as the
expectations created by the treatments, two
processes that were thought to be critical to
success of psychotherapy by some theorists
(e.g., Frank, 1961). These processes were of
interest to Kirsch, who set out to examine
credibility and expectations as alternative ex-
112 WAMPOLD, FROST, AND YULISH
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planation for the efficacy of SD (Kirsch &
Henry, 1977;Kirsch, Tennen, Wickless, Sac-
cone, & Cody, 1983).
In one study Kirsch and Henry (1977) explic-
itly tested whether the benefits of SD were
attributable to extinction, a hypothesized mech-
anism of SD, or attributable to the credibility of
the treatment. The effort to test the alternative
hypothesis (viz., that credibility of the treatment
was responsible for the benefits of SD) provided
guidance for the design of the control groups for
SD. In this study of treatments for speech anx-
iety, two control groups were designed to be as
credible as SD and credibility was assessed as a
mediating variable. The first control group, la-
beled “operant desensitization,” was designed
to rule out extinction as an explanation by fol-
lowing presentation of the stimulus with elec-
trical shocks, which theoretically should in-
crease anxiety. However, the subjects were told
that the shocks served to “punish” the anxiety.
The second control group, labeled “systematic
ventilation,” involved having the participant de-
scribe neutral situation in the participants’ his-
tory (e.g., first pet) by free associating, and was
described to the participants as a “combination
of ‘directed attention’ and ‘free association’ to a
series of childhood incidents that ‘recent re-
search has established as being related to stage
freight” (p. 1054). Credibility ratings did not
differ among the three groups, ruling out a
threat due to differential credibility. Moreover,
no differences on the outcomes variables were
found, indicating that the two control groups
were as effective as SD, despite one group (viz.,
operant desensitization) that should have failed
if extinction was explanatory. Finally, and im-
portantly, credibility scores for the participants
predicted reduction of fear in all three groups.
Clearly, to be a viable comparison, placebo-
type controls need to be credible (see Borkovec
& Nau, 1972).
In another study, Kirsch and colleagues
(Kirsch et al., 1983) examined the role of ex-
pectations in producing the benefits of SD. In
this study of snake phobias, the authors differ-
entiated expectancies for improvement, self-
efficacy a` la Bandura (Bandura, 1977), and re-
sponse expectancies (i.e., expectations that one
will experience fear). The goal was to design a
treatment which would produce comparable re-
sponse expectancies but contain no procedures
that would produce benefits by any known psy-
chological theory. SD was compared to with
condition designed to induce positive response
expectancies using a variation of the “system-
atic ventilation” used in the previous study, and
to a waiting list control group. Participants in
the expectancy modification group benefited as
much as SD participants, and both groups were
superior to the waiting list control group. More-
over, within each treatment, expectancies were
correlated with improvement, and to a greater
extent than credibility ratings. It appeared, from
these results, that response expectancies ex-
plained the results better than either condition-
ing or self-efficacy.
Over the years, SD has fallen away as treat-
ment for anxiety, but not because it was not
effective (i.e., it was never shown not to be
superior to no treatment). Although difficult to
know, perhaps the demonstration that the con-
ditioning mechanism was faulty led to this de-
cline. Nevertheless, this brief review of SD lit-
erature shows how important the design of the
placebo-type controls in psychotherapy studies
are for making proper conclusions. Indeed,
when poorly designed, SD was superior to pla-
cebo type comparisons, but when well de-
signed, with an alternative explanation in mind,
SD was not superior to the credible and expec-
tation producing comparisons. Kirsch’s efforts
to design placebo groups that test alternative
hypotheses are important historically, but ap-
parently did not serve to be a model for the
design of placebo type controls in psychother-
apy research.
Beginning in the 1980s, a concerted effort
was made to establish various psychotherapies
as scientific by the use of randomized, clinical
trials (RCTs) (Goldfried & Wolfe, 1998), as
exemplified by the National Institute of Mental
Health Treatment of Depression Collaborative
Research Program (Elkin, Parloff, Hadley, &
Autry, 1985;Elkin et al., 1989). Notwithstand-
ing the cautions raised by Rosenthal and Frank
(1956), and the example set by Kirsch and col-
leagues, a number of researchers attempted to
design psychotherapy treatments that were de-
signed to have no purported active ingredients
but failed to adequately control for alternative
hypotheses. These conditions were given vari-
ous names, including psychological placebos,
attention controls, alternate treatments, or sup-
113PLACEBO EFFECTS IN PSYCHOTHERAPY
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portive counseling.
2
A few examples from the
PTSD literature will illustrate the difficulties
inherent in designing these psychological pla-
cebos.
Foa, Rothbaum, Riggs, and Murdock (1991)
investigated the efficacy of two cognitive–
behavioral treatments (CBT), prolonged expo-
sure and stress inoculation training for the treat-
ment of PTSD in rape victims, by comparing
them to a treatment called supportive counsel-
ing and a no treatment control group. Support-
ive counseling “was included to control for non-
specific therapy effects” (p. 716). The challenge
was to design supportive counseling so that it
contained no cognitive– behavioral procedures,
including exposure and cognitive restructuring,
as well as any other purportedly active ingredi-
ent of any other known treatment for PTSD.
Accordingly, supportive counseling contained
the following procedures:
Patients were taught a general problem-solving tech-
nique. Therapists played an indirect and uncondition-
ally supportive role. Homework consisted of the pa-
tient’s keeping a diary of daily problems and her
attempts at problem solving. Patients were immedi-
ately redirected to focus on current daily problems if
discussions of the assault occurred. No instructions for
exposure or anxiety management were included.
Patients were not allowed to talk about being
raped, a prohibition some would think unethi-
cal, because that would involve imaginal expo-
sure (imagining the rape while in a relaxed
state). Although patients were taught a possible
coping strategy, it was not individualized to the
patient, no feedback was given to the patient,
homework was not integrated into the treat-
ment—that is, as intended the patients were not
given any strategies or asked to conduct any
actions that might be useful. Consequently, the
treatment lacked many of the components that
are common to all treatments, such as viable
and cogent explanation for the patient’s disor-
der, agreement between patient and therapist
about the goals and tasks of treatment (i.e., the
components of the working alliance), a plan for
overcoming one’s difficulties, and so forth
(Wampold & Imel, 2015)—most likely support-
ive counseling would not be credible to a patient
seeking to work on her problems, expectations
that the treatment would be efficacious would
be low, and the attribution that the patients
efforts in therapy were responsible for improve-
ment would be nonexistent. Moreover, these
problems were exacerbated by the fact that the
therapists were aware of the treatments being
delivered and were knowledgeable about
whether they were giving the active treatments
or the placebos. Clearly, supportive counseling
as a placebo control for the two active treat-
ments was not analogous to comparing a drug
with a pill placebo. Nevertheless, this study
found that the two active treatments were supe-
rior to supportive counseling for PTSD symp-
toms, although not for “nonspecific” distress,
and it was concluded that the treatments acted
specifically.
But the use of placebo controls in psycho-
therapy research becomes even more complex,
as illustrated again by the PTSD literature. A
treatment called present centered therapy (PCT)
has been used in PTSD trials to “provide a
credible therapeutic alternative to control for
nonspecific therapeutic factors so that observed
effects of prolonged exposure could be attrib-
uted to its specific effects beyond the benefits of
good therapy” (Schnurr et al., 2007, p. 823).
PCT, similar to supportive counseling used by
Foa et al. (1991), intentionally omits prolonged
exposure and cognitive restructuring, but PCT
was more deliberate by intentionally addressing
maladaptive relationship patterns, providing
psychoeducation about PTSD, and teaching the
use of problem solving therapy. PCT was
guided by a manual and involved therapists who
were trained to deliver the treatment faithfully
(Frost, Laska, & Wampold, 2014). Even though
PCT did not contain what are thought to be the
necessary ingredients of beneficial PTSD treat-
ments (viz., exposure and cognitive restructur-
ing), it has been found to be as effective as CBT
containing those ingredients (Frost et al., 2014).
That is to say, when the treatment had structure,
contained a proper rationale that could be ex-
plained cogently to patients, had ingredients
that the patients could believe were remedial,
and were given by therapists who believed that
2
Supportive counseling or supportive therapy are ambig-
uous terms, as sometimes they are used to apply to placebo
type controls, and as such have no coherent treatment ra-
tionale and no therapeutic actions, other than empathic
responding. However, the term is also used to refer to a
psychodynamic treatment. Attention is needed to know
whether supportive counseling is purportedly inert (i.e., a
control) or a purportedly active treatment (Budge, Baards-
eth, Wampold, & Flu˝ ckiger, 2010).
114 WAMPOLD, FROST, AND YULISH
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the treatment was remedial, the treatment was as
effective as the canonical evidence-based treat-
ments, a finding that has been established meta-
analytically (Baskin, Tierney, Minami, &
Wampold, 2003). Indeed there are other accepted
evidence-based treatments that originated as treat-
ments designed to be control conditions without
hypothesized specific ingredients (e.g., behavioral
activation and interpersonal therapy for depres-
sion).
One of the problems for psychotherapy re-
searchers is that any psychotherapy contains
many ingredients. For example, examination of
PTSD treatments yields a multitude of possibly
beneficial ingredients (Wampold et al., 2010),
including the following:
Cogent psychological rationale that is ac-
ceptable to patient
Systematic set of treatment actions consis-
tent with the rationale
Development and monitoring of a safe, re-
spectful, and trusting therapeutic relation-
ship
• Collaborative agreement about tasks and
goals of therapy
Nurturing hope and creating a sense of self
efficacy
Psychoeducation about PTSD
Opportunity to talk about trauma (i.e., tell
stories)
Ensuring the patient’s safety, especially if
the patient has been victimized as in the
case of domestic violence, neighborhood
violence, or abuse
Helping patients learn how to avoid revic-
timization
• Identifying patient resources, strengths,
survival skills, and intra- and interpersonal
resources and building resilience
Teaching coping skills
Examination of behavioral chain of events
• Exposure (covert in session and in vivo
outside of session)
• Making sense of traumatic event and pa-
tient’s reaction to event
Patient attribution of change to his or her
own efforts
Encouragement to generate and use social
supports
Relapse prevention
Of course some treatments would emphasize
some of these ingredients more than others, but
it is impossible to design a comparison treat-
ment without any of these ingredients, in the
manner that a placebo pill in medicine contains
no ingredients that could possibly be remedial
for the disorder being studied.
Interestingly, there is a perspicuous example
of a control condition in the panic treatment
literature that harkens back to Kirsch’s studies
of SD. Often panic patients are taught to stop or
reduce hyperventilation in panic-inducing situ-
ations. In a study of breathing and panic, Kim,
Wollburg, and Roth (2012) manipulated breath-
ing. One group was taught to raise partial pres-
sure of carbon dioxide to counteract hyperven-
tilation using a feedback device; a second group
used the same device to lower the partial pres-
sure of carbon dioxide. These two conditions
were compared with a no-treatment control
group. Both breathing training protocols re-
duced panic severity compared to the no-
treatment group (i.e., no differences between
the two breathing interventions). The authors
concluded, “Clinical improvement must have
depended on elements common to both breath-
ing therapies...[including ] changed beliefs
and expectancies, exposure to ominous bodily
sensations, and attention to regular and slow
breathing” (p. 931).
Clearly placebo type controls have obvious
problems—and for that reason they have been
called pseudoplacebos (Wampold & Imel,
2015), a term we use from now on. Despite
these problems, researchers have over the years
insisted that pseudoplacebos are legitimate con-
trols to establish specificity, in the same manner
as in medicine. Various meta-analyses have
shown that legitimate treatments, a concept we
discuss below, are superior to pseudoplacebos,
which in turn are superior to no treatments
(Lambert & Bergin, 1994;Stevens, Hynan, &
Allen, 2000). However, as illustrated above,
when the pseudoplacebo begins to resemble a
legitimate treatment, it becomes as effective as
the “active” treatment (Baskin et al., 2003;Frost
et al., 2014). Moreover, removing the active
ingredient of treatments in dismantling designs
does not attenuate the benefits of the treatments,
a conclusion reached in two meta-analyses (Ahn
& Wampold, 2001;Bell, Marcus, & Goodlad,
2013).
The problems continue, to an absurd extent.
Recently, Honyashiki et al. (2014) conducted a
meta-analysis of CBT versus what they called
psychological placebos and concluded, despite
115PLACEBO EFFECTS IN PSYCHOTHERAPY
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very small and for the most nonsignificant dif-
ferences, that “the present study strongly sug-
gested a non-null specific component of CBT”
(p. 249). One of the psychological placebos in
the meta-analysis was a “talking control,”
which was described as follows:
Dysfunctional beliefs were not challenged; however,
the therapists were asked to show interest and warmth,
encouraging participants to discuss neutral topics such
as hobbies, sports, and current affairs. No advice or
problem solving was given, and there was little focus
on emotional issues. No suggestions for behavioral
tasks were offered (p. 256).
As innocuous as that sounds, the talking con-
trol was indeed a miserable form of therapy:
consider that the therapist was instructed to
respond, for example, to the statement “My
daughter does not like me as she never comes to
visit me” with “How many children do you
have?” (p. 256), a response no reasonably
trained psychotherapist would make. The fact
that CBT is superior to the “talking control”
does not, in our view, support a specificity con-
clusion. Moreover, such controls deviate greatly
from the cleverly designed treatments that
Kirsch used to test alternative explanations for
the benefits of SD.
There has been another problem interwoven
into this fabric that has historically led to some
specious conclusions. As we have seen, pseu-
doplacebos are not appropriate logically or em-
pirically for establishing specificity in psycho-
therapy trials. However, another issue in
psychotherapy research is whether one type of
psychotherapy is superior to another. Unfortu-
nately, the pseudoplacebo has played a nefari-
ous role here as well. Claims of superiority
often are based on comparative trials, in which
two (or more) treatments are compared in a
head-to-head manner. These comparative trials
have been summarized in meta-analyses to
make conclusions about classes of therapies.
For example, Gloaguen, Cottraux, Cucherat,
and Blackburn (1998) found that CBT was su-
perior to “other therapies.” However, the cate-
gory “other therapies” contained legitimate
therapies, such as psychodynamic therapies, but
also several others which were intended to be
controls (i.e., were pseudoplacebos). This prob-
lem was identified early on by Lambert and
Bergin (1994):
There is a strong trend toward no difference between
techniques in amount of change produced, which is
counterbalanced by indications that, under some cir-
cumstances, cognitive and behavioral methods are su-
perior even though they do not generally differ in
efficacy between themselves. An examination of se-
lected exemplary studies allows us to further explore
this matter. Research carried out with the intent of
contrasting two or more bona fide treatments show
surprisingly small differences between the outcomes
for patients who undergo a treatment that is fully in-
tended to be therapeutic (p. 158; emphasis added).
To address this problem, Wampold et al.
(1997) proposed a set of criteria for differenti-
ating treatments intended to be therapeutic (la-
beled as bona-fide) and those that were pseudo-
placebos. When these criteria were applied to
the “other” therapies in Gloaguen et al. (1998),
it was found that CBT was not superior to
treatments intended to be therapeutic but were
superior to those that were not bona fide thera-
pies (Wampold, Minami, Baskin, & Tierney,
2002). This distinction is critical to understand-
ing whether some treatments for PTSD are more
effective than others (see Benish, Imel, &
Wampold, 2008;Ehlers et al., 2010;Wampold
et al., 2010 for an interchange about this issue).
Is Psychotherapy a Placebo?
From the beginnings of psychotherapy,
claims have been made that the factors common
to all psychotherapies are what produces the
benefits (Rosenzweig, 1936), a conjecture that
has had many advocates over the years (Frank
& Frank, 1991;Garfield, 1992;Wampold,
2001;Wampold & Imel, 2015). The lists of
what might constitute common factors vary, but
a short list would contain the relationship with
the psychotherapist, expectations, instillation of
hope, the provision of a reasonable and accept-
able explanation for one’s difficulties, a thera-
peutic set of actions that the patient believes
will be helpful, and the therapeutic alliance.
Indeed, there is good evidence that the common
factors, rather than the specific ingredients of
psychotherapy, are what make therapy work
(Laska, Gurman, & Wampold, 2014;Wampold
& Imel, 2015). Not coincidentally, these factors
are endemic to the effects of placebo, raising the
issue of whether psychotherapy is a placebo, a
disturbing conjecture to some, as noted by
Kirsch (2005):
116 WAMPOLD, FROST, AND YULISH
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There is a problem with identifying psychotherapy
with the placebo effect. A placebo is something that is
sham, fake, false, inert, and empty. Psychotherapy is
none of these. In this sense, it is different from medical
placebos, and it does not deserve the pejorative con-
notations associated with the term. (p. 797)
Kirsch goes on to address this issue:
But what does it mean to say that a particular psycho-
therapy is a placebo? It cannot mean that the treatment
is ineffective, because placebos can be effective. If this
were not the case, there would be no need for placebo
controls in any kind of outcome research, whether for
pills, surgery, or psychotherapy. The general assump-
tion seems to be that psychotherapy is a placebo if its
effects are nonspecific. This is generally stated as if the
meaning of the term nonspecific were clear. But it is
not clear at all. Specifically, it is not clear how the
effects of placebos are any less specific than any other
psychologically produced effects. (p. 797)
Despite Kirsch’s compelling argument, few
have been willing to explicitly discuss psycho-
therapy as a placebo. Indeed, a perusal of the
major sources that discuss the common factors
in psychotherapy will reveal that they either
avoid mentioning the placebo concept or dis-
cuss, as Kirsch did, that the application of the
term to psychotherapy is fraught with concep-
tual difficulties. However, decades ago Jeffer-
son Fish in a volume titled Placebo Therapy
argued that psychotherapy could be guided by
what is known about placebos and understand-
ing the mechanisms of placebos could guide the
delivery of psychotherapy (Fish, 1973).
Conclusions
The adoption of the RCTs in psychotherapy
outcome research, while providing a means to
test the efficacy of various psychotherapies, has
been plagued by logical problems. These prob-
lems were identified at the origins of the RCT in
psychotherapy, but have been often ignored,
leading to flawed conclusions about specificity.
A perusal of the psychotherapy outcome lit-
erature reveals that when placebo psychothera-
pies are compared with evidence-based psycho-
therapies (treatments with active/specific
ingredients) the evidence-based psychothera-
pies tend to demonstrate superiority. However,
as we have identified, when the placebo thera-
pies are engineered to be more structurally
equivalent these differences in outcome dissi-
pate (Frost et al., 2014). That is, when the
integrity of the placebo is not a factor, a placebo
psychotherapy that is allegedly “inert” can be
equally effective at remediating symptoms and
alleviating psychological distress. This may
seem perplexing to some, but it clearly implies
that there are shared mechanisms by which
these treatments are achieving their outcome. It
has been outlined in detail elsewhere (Wampold
& Imel, 2015) that elements common to all
psychotherapies may be the mechanisms by
which the placebo and psychotherapies achieve
their therapeutic effects. In this regard, a pla-
cebo psychotherapy is not “inert.”
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Received October 20, 2014
Revision received January 6, 2015
Accepted January 22, 2015
120 WAMPOLD, FROST, AND YULISH
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... Treatment expectations as the main mechanism driving placebo effects could explain the lack of differences between placebo and treatment groups [5,[9][10][11][12]. ...
... Furthermore, research on placebo interventions has shown that a convincing treatment rationale which considers patients' expectations, hopes, and learning history that is delivered by a trustworthy and credible clinician who believes in the remedial qualities of the intervention is able to produce similar treatment effects as other evidence-based interventions [12,79,[82][83][84][85]. We believe a treatment rationale that is in line with the illness model will produce more fruitful grounds for a patient to expect and experience a positive treatment response, irrespective of what the treatment might be (pharmacological or psychological). ...
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Background Placebo effects are a well-established phenomenon in the treatment of depression. However, the mechanism underlying these effects are not fully understood. Treatment expectations are considered one explanation for why placebos work. Treatment expectations are likely to be affected by clinician-patient interactions. This study aims to investigate the role of the communicated treatment rationale in modulating treatment expectations and its effects on the treatment outcomes of a pharmacological and a psychological active placebo intervention for depression. In this study, treatment expectations are modulated by presenting illness models that are either congruent or incongruent with the treatment intervention that follows. Methods This 2 × 2 randomized controlled trial will involve patients with major depression. Participants will either receive a biological or a psychological illness model from a clinician. Following this, they are randomly assigned to receive either a pharmacological or a psychological active placebo intervention. The illness model and the treatment are either congruent or incongruent with each other, resulting in four groups. In addition, a natural course control group will be included. Discussion This study will provide insights into the mechanism of expectation modulation in active placebo treatments for major depression. The results may provide insights for clinicians to improve their communication with patients by focusing on treatment expectations. By identifying the factors that contribute to placebo effects, this study has the potential to improve the effectiveness of existing depression treatments and reduce the burden of this highly prevalent mental health condition. Trial registration This trial has been registered prospectively at ClinicalTrials.gov under the identifier: NCT04719663. Registered on January 22, 2021.
... Treatment expectations as the main mechanism driving placebo effects could explain the lack of differences between placebo and treatment groups (5,(9)(10)(11)(12). Particularly active placebo groups are effective in inducing positive treatment expectations and thus placebo effects. ...
... Furthermore, research on placebo interventions has shown that a convincing treatment rationale which considers patients' expectations, hopes, and learning history, that is delivered by a trustworthy and credible clinician who believes in the remedial qualities of the intervention, is able to produce similar treatment effects as other evidence-based interventions (12,79,(82)(83)(84)(85). We believe a treatment rationale that is in line with the illness model will produce more fruitful grounds for a patient to expect and experience a positive treatment response, irrespective of what the treatment might be (pharmacological or psychological). ...
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Full-text available
Background Placebo effects are a well-established phenomenon in the treatment of depression. However, the mechanism underlying these effects are not fully understood. Treatment expectations are considered one explanation for why placebos work. Treatment expectations are likely to be affected by clinician-patient interactions. This study aims to investigate the role of the communicated treatment rationale in modulating treatment expectations and its effects on the treatment outcomes of a pharmacological and a psychological active placebo intervention for depression. In this study, treatment expectations are modulated by presenting illness models that are either congruent or incongruent with the treatment intervention that follows. Methods This 2x2 randomized controlled trial will involve patients with major depression. Participants will either receive a biological or a psychological illness model from a clinician. Following this they are randomly assigned to receive either a pharmacological or a psychological active placebo intervention. The illness model and the treatment are either congruent or incongruent with each other, resulting in four groups. In addition, a natural course control group will be included. Discussion This study will provide insights into the mechanism of expectation modulation in active placebo treatments for major depression. The results may provide insights for clinicians to improve their communication with patients by focusing on treatment expectations. By identifying the factors that contribute to placebo effects, this study has the potential to improve the effectiveness of existing depression treatments and reduce the burden of this highly prevalent mental health condition. Trial registration This trial has been registered prospectively at clinicaltrials.gov under the identifier: NCT04719663.
... However, designing sham or placebo interventions for psychosocial interventions is conceptually challenging as it necessitates the establishment of intervention credibility without including any active therapeutic elements. [64][65][66] A fourth limitation is that this was not a developerindependent trial; that is, several authors and research personnel are employed by the company that developed and owns the digital intervention examined in this study. Industry-sponsored research generally tends to favor the product being investigated, 67,68 and investigator allegiance can introduce biases even in psychotherapy research, regardless of whether the study is funded by industry or the intervention developers. ...
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Objective Despite the availability of pharmacological treatment for seizures, people with epilepsy (PwE) commonly experience impairments in quality of life (QoL). Given the limited access to psychosocial treatments for PwE, digital interventions could bridge treatment gaps and help improve QoL. The objective of this study was to examine the effectiveness of emyna, a fully automated digital intervention based on cognitive behavioral therapy (CBT) techniques, in improving health‐related QoL among PwE who reported impairments in QoL. A previous trial showed that emyna was effective in improving depressive symptoms among PwE with a comorbid depressive disorder, but its effects on QoL among PwE without comorbid depression remain unknown. Methods A pragmatic randomized controlled trial was conducted with N = 438 PwE (mean age = 37.5, 70.3% women, physician‐verified diagnoses) who were assigned to the intervention group (n = 216), which used emyna alongside treatment as usual (TAU), or the control group (n = 222), which received TAU only. QoL and secondary outcomes such as general self‐efficacy, medication adherence, general distress, and epilepsy‐related work and social adjustment were assessed at baseline, 3 months, and 6 months. The primary outcome was QoL assessed with the Quality of Life in Epilepsy [QOLIE‐31] total score at 3 months post‐randomization. Results Findings from the intent‐to‐treat analyses showed that after 3 months, participants in the intervention group experienced significant and clinically relevant improvements in health‐related QoL compared to the control group (baseline‐adjusted group difference = 4.5; 95% CI = [2.0, 6.9], p < 0.001; Cohen's d = 0.32). Effects on secondary outcomes did not reach statistical significance. Significance This study extends previous research by demonstrating that emyna facilitates improvements in QoL in a diverse group of PwE treated in routine care settings. This CBT‐based digital intervention therefore presents a convenient and cost‐effective addition to healthcare providers' treatment repertoire. Plain Language Summary In our study, we tested a digital program called emyna, which conveys cognitive behavioral therapy (CBT) techniques to help improve the quality of life for people living with epilepsy. We found that those who used emyna alongside their usual treatments felt better about their quality of life compared to those who did not use the program. Emyna offers a new, convenient way for people with epilepsy to manage their condition, which can be used alongside currently available treatments.
... These studies should also aim to clarify the intervention's overall clinical significance, initial uptake, adherence and attrition rates. The therapeutic alliance is often cited as a key predictor of change in face-to-face therapy (Cuijpers, Reijnders, and Huibers 2019;Horvath et al. 2011;Wampold, Frost, and Yulish 2016;Wampold et al. 2017). Thus, it is particularly crucial for future research to explore SH ICBT, which challenges traditional beliefs regarding the role of the therapeutic relationship in the symptomatic improvement of individuals with mental health disorders. ...
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Obsessive–compulsive disorder (OCD) is a common mental health condition characterized by distressing, intrusive thoughts (obsessions) and repetitive behaviours (compulsions) aimed at reducing anxiety. Internet-based cognitive behavioural therapy (ICBT) has emerged as an effective treatment modality for various mental health disorders. This meta-analysis evaluates the efficacy of guided self-help ICBT (GSH ICBT) and unguided self-help ICBT (SH ICBT) against active and passive control conditions in adults with OCD. A comprehensive systematic literature search yielded 12 randomized controlled trials (RCTs) comprising 15 comparison arms (N = 1416) that met the inclusion criteria. Results indicate that GSH ICBT significantly reduced OCD symptomatology posttreatment compared to active controls (g = 0.378, k = 9), with no significant effects maintained at follow-up (g = 0.153, k = 4). GSH ICBT was also found to be as effective as active CBT interventions in reducing comorbid anxiety and depression symptoms posttreatment (g = 0.278, k = 6) and at follow-up (g = 0.124, k = 4). However, improvements in quality of life were not significant posttreatment (g = 0.115, k = 4) nor at follow-up (g = 0.179, k = 3). Combined GSH and SH ICBT demonstrated large effects on reducing OCD symptoms (g = 0.754, k = 6), medium effects on comorbid symptoms (g = 0.547, k = 6) and small effects on quality of life (g = 0.227, k = 2) when compared to inactive controls. No significant differences were found between GSH and SH ICBT in all measured outcomes posttreatment (OCD: g = 0.098, k = 3; AD: g = 0.070, k = 3; QoL: g = −0.030, k = 1) and at follow-up (OCD: g = 0.265, k = 2; AD: g = 0.084, k = 2; QoL: g = 0.00, k = 1). Sample size was identified as a significant moderator of treatment effects. This paper further explores clinical significance, treatment adherence, therapist time investment and moderator influences of the ICBT. The limitations of the study and recommendations for future research are thoroughly discussed.
... Including a third study arm (next to an active placebo), consisting of an additional control condition that receives no treatment at all, allows a formal quantification of the size of the placebo effect and a control for treatment nonspecific factors. 119 All studies should assess patients' and therapists' expectations prior to and during trials, which provides information necessary to control for expectation and placebo effects. 26 Another solution is to induce more realistic expectations for clinicians and patients by providing explicit information about the current uncertainty regarding the efficacy of psychedelic therapy in the informed consent of studies. ...
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Research in the last decade has expressed considerable optimism about the clinical potential of psychedelics for the treatment of mental disorders. This optimism is reflected in an increase in research papers, investments by pharmaceutical companies, patents, media coverage, as well as political and legislative changes. However, psychedelic science is facing serious challenges that threaten the validity of core findings and raise doubt regarding clinical efficacy and safety. In this paper, we introduce the 10 most pressing challenges, grouped into easy, moderate, and hard problems. We show how these problems threaten internal validity (treatment effects are due to factors unrelated to the treatment), external validity (lack of generalizability), construct validity (unclear working mechanism), or statistical conclusion validity (conclusions do not follow from the data and methods). These problems tend to co-occur in psychedelic studies, limiting conclusions that can be drawn about the safety and efficacy of psychedelic therapy. We provide a roadmap for tackling these challenges and share a checklist that researchers, journalists, funders, policymakers, and other stakeholders can use to assess the quality of psychedelic science. Addressing today’s problems is necessary to find out whether the optimism regarding the therapeutic potential of psychedelics has been warranted and to avoid history repeating itself.
... For medical devices (e.g., digital mental health interventions), the U.S. FDA recommends using "sham" interventions to control for placebo effects (i.e., interventions that appear like the tested treatment, but deliver no actual therapy); but also acknowledges that constructing such control groups can be difficult [133]. Some authors have argued that the idea of a blinded placebo control does not apply to psychological interventions altogether, since both can be regarded as treatments that work solely through psychological means [134][135][136][137][138]; and that placebo controls should therefore be abandoned in psychotherapy research [136]. This conclusion is not uncontroversial, and others contend that some types of placebo controls can be helpful to test the "true" effect of psychological interventions [139]. ...
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Background Considered one of the highest levels of evidence, results of randomized controlled trials (RCTs) remain an essential building block in mental health research. They are frequently used to confirm that an intervention “works” and to guide treatment decisions. Given their importance in the field, it is concerning that the quality of many RCT evaluations in mental health research remains poor. Common errors range from inadequate missing data handling and inappropriate analyses (e.g., baseline randomization tests or analyses of within-group changes) to unduly interpretations of trial results and insufficient reporting. These deficiencies pose a threat to the robustness of mental health research and its impact on patient care. Many of these issues may be avoided in the future if mental health researchers are provided with a better understanding of what constitutes a high-quality RCT evaluation. Methods In this primer article, we give an introduction to core concepts and caveats of clinical trial evaluations in mental health research. We also show how to implement current best practices using open-source statistical software. Results Drawing on Rubin’s potential outcome framework, we describe that RCTs put us in a privileged position to study causality by ensuring that the potential outcomes of the randomized groups become exchangeable. We discuss how missing data can threaten the validity of our results if dropouts systematically differ from non-dropouts, introduce trial estimands as a way to co-align analyses with the goals of the evaluation, and explain how to set up an appropriate analysis model to test the treatment effect at one or several assessment points. A novice-friendly tutorial is provided alongside this primer. It lays out concepts in greater detail and showcases how to implement techniques using the statistical software R, based on a real-world RCT dataset. Discussion Many problems of RCTs already arise at the design stage, and we examine some avoidable and unavoidable “weak spots” of this design in mental health research. For instance, we discuss how lack of prospective registration can give way to issues like outcome switching and selective reporting, how allegiance biases can inflate effect estimates, review recommendations and challenges in blinding patients in mental health RCTs, and describe problems arising from underpowered trials. Lastly, we discuss why not all randomized trials necessarily have a limited external validity and examine how RCTs relate to ongoing efforts to personalize mental health care.
... Different types of placebo control groups are often used in mental health research, not only placebo pills but also other kinds of placebo interventions such as psychological placebo and physical placebo . Psychological placebo is often constructed to target the non-specific components in psychotherapies (Hróbjartsson & Miller, 2012;Wampold et al., 2016;Wampold & Imel, 2015). Physical placebos are constructed to target the built-in components of a given physical treatment such as acupuncture or exercise . ...
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Borderline personality disorder (BPD) is a highly studied condition. During the last 3 decades, the understanding of the disorder has substantially changed, based on thorough, accumulating research. At the same time, the interest in BPD is still not decreasing but continues to grow. This article aims to critically discuss research trends in clinical trials of personality disorders in general and BPD in particular, to highlight topics that deserve closer attention, and to give recommendations for the design and conduct of future psychotherapy or pharmacotherapy studies in the field. (PsycInfo Database Record (c) 2023 APA, all rights reserved).
... In psychotherapy research, a vigorous debate has been going on for decades, and some authors hold that the effect of psychotherapy is mostly due to nonspecific effects of therapeutic support, positive relationships, and activation of patients [23,24]. Therefore, it is questionable whether the term "placebo effect" is a meaningful concept at all, as it implicates a derogatory meaning of a therapeutic effect less valuable [25,26], and it is likely more useful to reframe the placebo effect as a self-healing or meaning response which is always present [27,28]. Moreover, the concept of the "efficacy paradox" makes the search for "specific" effects over and above any "placebo" component ques-tionable [29][30][31]. ...
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This meta-analysis tested the Dodo bird conjecture, which states that when psychotherapies intended to be therapeutic are compared, the true differences among all such treatments are 0. Based on comparisons between treatments culled from 6 journals, it was found that the effect sizes were homogeneously distributed about 0, as was expected under the Dodo bird conjecture, and that under the most liberal assumptions, the upper bound of the true effect was about .20. Moreover, the effect sizes (a) were not related positively to publication date, indicating that improving research methods were not detecting effects, and (b) were not related to the similarity of the treatments, indicating that more dissimilar treatments did not produce larger effects, as would be expected if the Dodo bird conjecture was false. The evidence from these analyses supports the conjecture that the efficacy of bona fide treatments are roughly equivalent.
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Despite the advances in psychotherapy outcome research, findings are limited because they do not fully generalize to the way therapy is conducted in the real world. Research's clinical validity has been compromised by the medicalization of outcome research, use of random assignment of clients without regard to appropriateness of treatment, fixed number of therapy sessions, nature of the therapy manuals, and use of theoretically pure therapies. The field needs to foster a more productive collaboration between clinician and researcher; study theoretically integrated interventions; use process research findings to improve therapy manuals; make greater use of replicated clinical case studies; focus on less heterogeneous, dimensionalized clinical problems; and find a better way of disseminating research findings to the practicing clinician.
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Suggests that the placebo in psychotherapy has retained the negative connotation of an inert "nuisance variable," a label that it originally incurred in the field of medicine. In addition, the transition toward more cognitive models of psychotherapy, particularly A. Bandura's theory of self-efficacy, has led to problems in defining the placebo within psychology. This transition has resulted in an awkward interface between certain preferred cognitive metaphors and the negative connotations of a presumably cognitive placebo construct. Suggestions have been made to dismiss the placebo construct from psychology and to do away with the use of true placebo controls in outcome research. The present analysis maintains that (a) the placebo can be adequately defined within psychology, (b) the negative connotation of the placebo label is largely undeserved, (c) the placebo retains a continuing conceptual and empirical utility for evaluating psychotherapy, and (d) the therapeutic efficacy of current therapies is well established even though they have not generally been shown to be more effective than nonspecific treatment. (29 ref)
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Presents an integrative theoretical framework to explain and to predict psychological changes achieved by different modes of treatment. This theory states that psychological procedures, whatever their form, alter the level and strength of self-efficacy. It is hypothesized that expectations of personal efficacy determine whether coping behavior will be initiated, how much effort will be expended, and how long it will be sustained in the face of obstacles and aversive experiences. Persistence in activities that are subjectively threatening but in fact relatively safe produces, through experiences of mastery, further enhancement of self-efficacy and corresponding reductions in defensive behavior. In the proposed model, expectations of personal efficacy are derived from 4 principal sources of information: performance accomplishments, vicarious experience, verbal persuasion, and physiological states. Factors influencing the cognitive processing of efficacy information arise from enactive, vicarious, exhortative, and emotive sources. The differential power of diverse therapeutic procedures is analyzed in terms of the postulated cognitive mechanism of operation. Findings are reported from microanalyses of enactive, vicarious, and emotive modes of treatment that support the hypothesized relationship between perceived self-efficacy and behavioral changes. (21/2 p ref)
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The Patient’s Brain describes and explains recent advances within neuroscience that enable us to describe and discuss the biological mechanisms that underlie the doctor-patient relationship, how this new scientific knowledge can be put to great practical use, and the doctor-patient relationship can be subdivided into at least four steps: feeling sick, seeking relief, meeting the therapist, and receiving therapy.
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Posted July 15, 2002. Introduces the meta-analysis reported by I. Kirsch et al (see record 2002-14079-003), which studied antidepressant drug and placebo effects. The following topics are covered: (1) definitions of placebo and the placebo effect, (2) evaluations of the placebo effect, (3) evidence of placebo effects, and (4) whether there is a powerful antidepressant drug effect. Their concern was not to assess the placebo effect but rather to examine the magnitude of the drug effect. The authors expected a substantial placebo effect, but were surprised by the small medication effect that they found. It is suggested that their analysis of FDA data is likely to prove controversial, and although the difference in response between antidepressant medication and inert placebo was statistically significant, in clinical terms it was very small, leading Kirsch et al to ask whether these medications are "the emperor's new drugs."