Ain’t Necessarily So: Review and Critique of Recent Meta-Analyses of
Behavioral Medicine Interventions in Health Psychology
James C. Coyne
University of Pennsylvania School of Medicine
and University of Groningen
Brett D. Thombs
McGill University and Jewish General Hospital, Montreal,
University of Groningen
Objective: We examined four meta-analyses of behavioral interventions for adults (Dixon, Keefe, Scipio,
Perri, & Abernethy, 2007; Hoffman, Papas, Chatkoff, & Kerns, 2007; Irwin, Cole, & Nicassio, 2006; and
Jacobsen, Donovan, Vadaparampil, & Small, 2007) that have appeared in the Evidence Based Treatment
Reviews section of Health Psychology. Design: Narrative review. Main Outcome Measures: We applied
the following criteria to each meta-analysis: (1) whether each meta-analysis was described accurately,
adequately, and transparently in the article; (2) whether there was an adequate attempt to deal with
methodological quality of the original trials; (3) the extent to which the meta-analysis depended on small,
underpowered studies; and (4) the extent to which the meta-analysis provided valid and useful evidence-
based recommendations. Results: Across the four meta-analyses, we identified substantial problems with
the transparency and completeness with which these meta-analyses were reported, as well as a depen-
dence on small, underpowered trials of generally poor quality. Conclusion: Results of our exercise raise
questions about the clinical validity and utility of the conclusions of these meta-analyses. Results should
serve as a wake up call to prospective authors, reviewers, and end-users of meta-analyses now appearing
in the literature.
Keywords: cancer, pain, fatigue, insomnia, arthritis
Providers of behavioral medicine services face formidable chal-
lenges justifying empirically not just which interventions are to be
utilized, but whether the strength of evidence warrants that specific
interventions for particular medical conditions be made available
to patients and financed by third-party payments. They also need
to be able to supply patients and payees with reasonable estimates
of the balance of potential benefits that are likely to be obtained
versus the financial and opportunity costs of behavioral treatments.
Recognizing limitations of single studies and box score or narra-
tive summaries, meta-analyses are appearing with increasing fre-
quency in Health Psychology and elsewhere. These reports are
widely viewed as an authoritative means to answer questions about
treatment efficacy by characterizing and quantitatively synthesiz-
ing results from relevant studies, with the expectation that a
representative summary effect size will result. The hope is that
such meta-analyses will provide accessible, dependable, clinically
informed aids to decision making.
Application of meta-analysis is facilitated by the availability of
a number of user-friendly software packages. Yet, ease of use risks
that results can be obtained without authors necessarily having an
adequate understanding of basic principles of meta-analysis, in-
cluding standards for evaluating and reporting the quality of avail-
able randomized controlled trials (RCTs) or the degree to which
available RCTs are reasonably combined in a single meta-analysis.
Paralleling CONSORT (Consolidated Standards of Reporting Tri-
als; Moher, Schulz, & Altman, 2001) reporting guidelines for
clinical trials, QUOROM (Quality of Reporting of Meta-analysis;
Moher et al., 1999) guidelines were developed by expert consensus
to improve reporting of meta-analyses and provide a checklist and
flowchart for assessing the transparency with which meta-analyses
are reported. Transparency, that is, presentation of basic details of
how a meta-analysis was conducted, is essential so that readers can
form their own independent opinion of the adequacy of methods,
results, and conclusions. Over 1,100 citations of the original
QUOROM paper in less than a decade indicate wide dissemination
of these standards. However, not one citation of QUOROM can be
found in Health Psychology, and there have been only two passing
references in Annals of Behavioral Medicine, neither in the context
of a meta-analysis. None of the more than 30 post-QUOROM
James C. Coyne, Department of Psychiatry, University of Pennsylvania
School of Medicine, and Department of Health Sciences, Graduate School
for Health Research, University Medical Center Groningen, University of
Groningen; Brett D. Thombs, Department of Psychiatry, McGill University
and Jewish General Hospital, Montreal, Quebec, Canada; and Mariet
Hagedoorn, Department of Health Sciences, Graduate School for Health
Research, University Medical Center Groningen, University of Groningen.
Dr. Thombs is supported by a New Investigator Award from the Cana-
dian Institutes of Health Research and an E´tablissement de Jeunes Cher-
cheurs award from the Fonds de la Recherche en Sante ´ Que ´bec.
Correspondence concerning this article should be addressed to James C.
Coyne, Ph.D., Department of Psychiatry, University of Pennsylvania
School of Medicine, 3535 Market St., Room 676, Philadelphia, PA 19104.
2010, Vol. 29, No. 2, 107–116
© 2010 American Psychological Association
meta-analyses published in Health Psychology or Annals of Be-
havioral Medicine mentions QUOROM. This raises the question
of whether authors, reviewers, or intended consumers of meta-
analyses of behavioral medicine have adequate knowledge of
standards for conducting and reporting meta-analyses, recent con-
ceptual and statistical developments, or current controversies in
meta-analysis methodology. It also suggests that early warnings
about the perils of conducting meta-analysis as if it were a straight-
forward, even mechanical procedure with a minimal amount of
subjectivity or arbitrary judgment by authors (Wanous, Sullivan, &
Malinak, 1989) may not have been heeded.
Coyne, Thombs, and Hagedoorn (2008) recently provided a
extensive critique of a meta-analysis of interventions for distress
among breast cancer patients (Zimmermann, Heinrichs, & Bau-
com, 2007). The first research question addressed by Zimmermann
et al. (2007) was whether patients with breast cancer had better
outcomes when they received interventions as part of a study that
only included those with breast cancer as compared with studies
that included patients with mixed diagnoses. Zimmermann et al.
concluded from their meta-analysis that studies that mixed the type
of cancer had significantly larger effect sizes than studies limited
to breast cancer. The implication would seem to be that patients
with breast cancer should be provided with nonspecific psycho-
logical interventions designed for patients with any type of cancer,
rather than having interventions tailored to the breast cancer ex-
perience. However, going back to the original studies, we were
unable to identify a single RCT that provided data to compare
results between patients with breast cancer being treated with
treatment protocols designed specifically for breast cancer versus
being treated with protocols designed generally for patients with
cancer. In addition, no allowance was made for the poor method-
ological quality of studies entered into the meta-analysis. Previous
authors had either abandoned efforts to conduct meta-analyses
because of the poor quality of available trials (Newell, Sanson-
Fisher, & Savolainen, 2002), or had substantially lowered esti-
mates of efficacy when studies that were of poor quality or that
used overly small sample sizes were excluded (Sheard & Maguire,
1999). We were unable to find a number of basic details in the
article as to how the meta-analysis had been conducted. For
instance, studies with multiple outcomes were assigned single
effect sizes without indication of how this was done. We requested
more information from the authors. Comparing these materials to
the original studies, we found a substantial error in calculating an
effect size, several misclassifications of interventions, and the
same intervention trials being counted two and three times. Our
review was not comprehensive, but was sufficient to raise doubts
as to whether clinical and policy decisions should be based on the
article’s conclusions. We were also left wondering how pervasive
the problems we observed in Zimmermann et al. were in meta-
analyses of behavioral medicine interventions.
In the present paper, we undertook a similar exercise with four
meta-analyses of behavioral interventions for adults (Dixon,
Keefe, Scipio, Perri, & Abernethy, 2007; Hoffman, Papas, Chat-
koff, & Kerns, 2007; Irwin, Cole, & Nicassio, 2006; and Jacobsen,
Donovan, Vadaparampil, & Small, 2007) that appeared in a new
section of Health Psychology, Evidence Based Treatment Re-
views. Since our objective was to identify the degree to which
meta-analyses of behavioral interventions are based on flawed
methodology, and not to evaluate the pooled effect sizes reported
in each meta-analysis per se, we did not redo these meta-analyses,
but provide an evaluation of the adequacy of their conduct, report-
ing, and clinical recommendations. Presumably readers would face
a similar task in evaluating these articles, although they might not
be motivated to look beyond the meta-analyses themselves due to
confidence in the objective, straightforward nature of the tasks of
conducting a meta-analysis, reporting findings, and making rec-
ommendations. We started with the articles themselves and any
supplementary materials, asked questions of the authors, then went
to the original RCTs and related articles. We asked:
(1)Was the conduct of the meta-analysis accurately, ade-
quately, and transparently described in the article or
(2) Was there an adequate attempt to deal with the meth-
odological quality of the original intervention trials?
(3) To what extent did the results of the meta-analysis
depend on small, underpowered studies?
(4)To what extent did the meta-analysis provide valid and
useful evidence-based recommendations to clinicians
Items 2, 3 and 4 warrant brief elaboration. The Cochrane Col-
laboration has spelled out guidelines for conducting meta-analyses
that emphasize the necessity of taking methodological quality into
account (Higgins & Altman, 2008). Serious deficiencies in RCTs
of behavioral medicine interventions have been noted (Coyne,
Lepore, & Palmer, 2006; Newell et al., 2002; Sheard & Maguire,
1999). While dozens of scales show validity for evaluating meth-
odological quality, they nonetheless differ in their ratings in an
arbitrary fashion (Juni, Witschi, Bloch, & Egger, 1999). There is
increasing acceptance of the idea that rather than weighting trials
for their methodological quality as scored with these scales, some
threshold should be set as a basis for outright exclusion of trials
that either do not achieve this minimal quality or for which
analyses should be conducted both with and without their inclusion
(Higgins & Altman, 2008; Juni, Altman, & Egger, 2001).
Our third criterion is controversial, but we believe it is impor-
tant. Kraemer, Gardner, Brooks, and Yesavage (1998) propose
excluding small, underpowered studies from meta-analyses. The
risk of including studies with inadequate sample size is not limited
to clinical and pragmatic decisions being made on the basis of
trials that cannot demonstrate effectiveness when it is indeed
present. Rather, Kraemer et al. demonstrate that inclusion of small,
underpowered trials in meta-analyses produces gross overesti-
mates of effect size due to substantial, but unquantifiable confir-
matory publication bias from nonrepresentative small trials. With-
out being able to estimate the size or extent of such biases, it is
impossible to control for them. Other authorities voice support for
including small trials, but generally limit their argument to trials
that are otherwise methodologically adequate (Sackett & Cook,
1993; Schulz & Grimes, 2005). Small trials are particularly sus-
ceptible to common methodological problems, however, such as
lack of baseline equivalence of groups; undue influence of outliers
on results; selective attrition and lack of intent-to-treat analyses;
investigators being unblinded to patient allotment; and not having
COYNE, THOMBS, AND HAGEDOORN
a predetermined stopping point so investigators are able to stop a
trial when a significant effect is present.
Staines and Cleland (2007) recently analyzed the psychotherapy
literature and concluded that the failure to reduce the weight of
studies with small sample sizes resulted in only a “minor” upward
bias in effect size estimates of approximately 1.4 times unweighted
effect estimates. However, the inclusion of one or several studies
with small sample sizes is one thing. It is an altogether different
problem when most or all of the studies included in a given
meta-analysis have small sample sizes. Small trials that are not
statistically significant are not usually published because of the
criticism that significant effects could not have been expected,
whereas a trial that obtains statistically significant effects despite
being underpowered is considered noteworthy and results are
readily publishable. Small trials that are published generally need
to have sizable effect sizes just to meet the minimum threshold for
statistical significance (e.g., p ? .05). A trial with 20 participants
in the treatment and control groups, for instance, would require an
effect size of at least 0.66 for statistical significance. Even with
n ? 50 per cell a minimum effect size of 0.40 would be needed.
This does not accurately describe the extent of the problem,
however, since small studies that cross the p ? .05 threshold do so
by varying degrees, with some producing quite large effect sizes,
even when the null hypothesis of no treatment effect is true.
Kraemer et al. (1998) showed that when the true effect of a
treatment is zero and n ? 20 per subgroup, the estimated stan-
dardized mean difference effect size in a meta-analysis of statis-
tically significant RCTs will be between 0.90 and 1.00. With n ?
50 per subgroup and a true null finding, the expected effect size
would be approximately 0.60. If small studies are only published
when their results are significant, the effect sizes available in the
published literature will of necessity appear moderate to large,
because such effect sizes are the only ones that can reach statistical
significance with small sample size. Other authors have provided
similar critiques of the ramifications of combining sets of small
studies to produce a single effect estimate (e.g., Ioannidis, 2008a;
Howard et al., 2009).
How much power is sufficient for inclusion of a study in a
meta-analysis? Kraemer et al. (1998) suggest at least 50% power,
but note that proposals for individual studies usually require at
least 70% power. Kraemer (personal communication, December 8.
2008) proposes that trials have at least a .70 probability of detect-
ing a moderate size effect (e.g., ? ? .50 based on Cohen, 1992),
requiring at least 50 patients per group. Unfortunately, a large
proportion of studies of behavioral medicine interventions do not
meet this criterion. For instance, only 16 of 56 (29%) studies
reviewed by Zimmermann and colleagues (2007), included at least
50 patients per cell. Thus, we reluctantly will apply a more liberal
criterion of 35 patients per cell, with 55% power of detecting a
Our fourth criterion involves evaluating the pragmatic signifi-
cance of findings of a meta-analysis. This criterion takes into
account our other three criteria, but also the clinical heterogeneity
of the patients, outcomes, interventions, and study procedures that
contributed to the overall effect size. The degree to which a
summary effect size represents a set of trials with similar study
characteristics reflects how well one might expect the overall
effect size to generalize to any given intervention. Ioannidis
(2008b) argues cogently that a lack of statistical heterogeneity
often does not indicate a lack of clinical heterogeneity. In our
review of Zimmermann et al.’s meta-analysis (2007), for instance,
we found that composite effect sizes were constructed from,
among other things, scores on a measure of patient satisfaction
with a cancer center tour (McQuellon et al., 1998), the immediate
mood of patients with breast cancer following a cosmetics class
with free cosmetics (Manne, Girasek, & Ambrosino, 1994), and
Hamilton Depression Rating Scale scores for patients who re-
ceived a problem-solving intervention after having been pre-
screened for high distress with a threshold that excluded most
patients (Nezu, Nezu, Felgoise, McClure, & Houts, 2003). Thus,
we ask to what degree clinically meaningful generalizations can be
made from the summary effect estimate back to the patients, from
interventions and outcomes of each of the individual studies that
were synthesized to generate the summary measure.
In the following sections, we review each of the four meta-
analyses in question based on this set of criteria, beginning with
the meta-analysis by Irwin et al. (2006) and followed by the
meta-analyses by Hoffman et al. (2007); Dixon et al. (2007), and
Jacobsen et al. (2007). In each section, we provide an overview of
the meta-analysis, followed by a description of problems identified
in the conduct and interpretation of the meta-analysis, then a
critique of the authors’ conclusions and a message to consumers of
Irwin et al. (2006)
Irwin and colleagues conducted a meta-analysis of behavioral
interventions for insomnia with a stated objective of “comparing
responses in studies that exclusively enrolled persons who were 55
years of age or older versus outcomes in randomized controlled
trials that enrolled adults who were, on average, younger than 55
years of age” (p. 4). They retrieved 51 articles, of which 23 were
included in the meta-analysis. The findings revealed significant
overall effects of behavioral interventions for sleep quality, la-
tency, efficiency, and wakening after sleep onset (d ? 0.50 to
0.79), and a nonstatistically significant effect for total sleep time
(d ? 0.17). Some moderator effects were found for intervention
type and age.
Transparency of Reporting
Irwin et al.’s review of behavioral interventions for primary
insomnia was published before Health Psychology’s webpage was
available for providing supplementary material, and presentation
of basic details of the included RCTs was likely compromised by
limitations on article length. Nonetheless, details important for the
evaluation and interpretation of the results of the meta-analysis
were not available for readers. For instance, the authors indicated
that decisions whether to include studies were based on method-
ological quality, but no description of the evaluation and decision
process was provided.
Sample Sizes of Original Studies and Other Problems
Exclusion of small trials (n ? 35) would have eliminated all
eight studies of older adults; five of these studies included 15 or
fewer participants per condition. Of the studies including younger
adults, 14 of the 15 studies had fewer than 35 participants per
condition. Furthermore, most moderator analyses comparing older
versus younger patients and different intervention types were
based on only a few studies per subgroup (median ? 5). Even if
one accepts the small sample sizes of the original studies, the
significant moderator effects are disputable. For example, the
analysis purported to show an effect for intervention type on sleep
efficiency compared three cognitive–behavioral therapy (CBT)
studies (ES ? 1.47, 95% CI ? 1.00–1.94) to two relaxation
studies (ES ? ?0.35, 95% CI ? ?0.75–0.05) of older adults. The
effect size (d ? 2.64) for the Rybarczyk, Lopez, Benson, Alsten,
and Stepanski (2002) CBT study seems to be exceptionally high.
Also, Irwin et al. appear to have included the effect size of the
Sleep Compression group (d ? ?0.02) instead of the Relaxation
group (d ? 0.16) of the study by Lichstein Riedel, Wilson, Lester,
and Aguillard (2001).
Message to Consumers
Irwin et al. (2006) offered an optimistic assessment: “The re-
view supported the efficacy of behavioral interventions . . . The
magnitudes of the effect sizes were substantial” and “CBT proved
to be substantially more effective than relaxation training in im-
proving sleep efficiency” (p. 10). Further: “. . . the current meta-
analyses confirmed the general efficacy of behavioral interven-
tions across cohorts with two exceptions. Behavioral interventions
were more effective in the younger cohort in TST and efficiency in
the older cohort” (p. 11). These claims, however, are based on a
collection of studies that include only one study with 35 or more
participants per cell. Even in the case of a true null, such a
collection of published small studies would be expected to produce
a robust effect size estimate (Howard et al., 2009; Ioannidis,
2008a; Kraemer et al., 1998). Furthermore, appraisal of these
claims requires information unavailable in the article that only a
skeptical reader would likely seek.
Hoffman et al. (2007)
In a meta-analysis of psychological interventions for chronic
low back pain, Hoffman et al. (2007) reported that “a total of 205
effect sizes from 22 studies were pooled in 34 analyses” and that
“positive effects of interventions were found for pain intensity,
pain-related interference, health-related quality of life, and depres-
sion” (pp. 1). Hoffman and colleagues retrieved 96 articles, of
which 39 met inclusion criteria, and 34 (representing 31 studies)
had extractable data for the meta-analysis. Another nine studies
were eliminated, mostly because they featured contrasts between
interventions considered by Hoffman et al. for the purposes of their
meta-analysis to be identical.
Transparency of Reporting
Overall, data from 22 studies were entered into the meta-
analysis. However, tracking which studies were entered into par-
ticular comparisons across the various tables in the article became
a frustrating task because numbers did not match up. In some
cases, this could have occurred because data were not available for
particular outcomes, but in other instances, this could not have
been the explanation. To cite one of a number of examples, for
post-treatment pain interference, the number of comparisons be-
tween intervention and active control (k) and number of patients
(N) are the same in Table 2 and 3, but d ? ?.10 in Table 2 and .20
in Table 3.
Methodological Quality of Included Studies
Focusing on material presented in the article alone, we found a
lack of evidence that psychological interventions were superior to
other active treatments and no evidence of enduring effects of
psychological interventions beyond immediate posttreatment as-
sessments. Moreover, based on a table of methodological ratings
that the authors graciously provided, we found only five of 22
RCTs met more than half of the 12 applicable methodological
criteria that were applied by the authors. The largest RCT
(Alaranta et al., 1994) met 17%. Further examining the table
provided by the authors, we found that 60% of the studies involved
intervention and control groups that were not comparable on key
variables at baseline; less than half of the studies adequately
indicated the number of patients enrolled, treatment drop-out and
reasons for drop-outs; and only 15% of trials provided intent-to-
treat analyses. Less than a third had manualized treatment proce-
dures or detailed protocols; only three assessed patient adherence
to prescribed activities and only three restricted outside interven-
Sample Sizes of Original Studies and Other Problems
Turning to the original studies, we found that 17 of the 22
studies included by Hoffman fell below n ? 35 per group. Exclu-
sively psychological interventions were distinguished from multi-
modal interventions in which a psychological intervention was
embedded, but no study of a multicomponent intervention allowed
evaluation of the independent contribution of a psychological
component. This cointervention confound (Cochrane Collabora-
tion; O’Connor, Green, & Higgins, 2008) left no way of distin-
guishing if psychological components were superfluous, additive,
or crucially decisive. Moreover, there was often no indication that
the multicomponent treatments applied psychological principles or
required psychologically trained interventionists. The details pro-
vided were often sparse, but one trial described the psychological
component as “a lecture to give the patient an understanding that
ordinary physical activity would not harm the disk and a recom-
mendation to use the back and bend it” (Brox et al., 2003). Of the
studies providing effect sizes for a comparison between a psycho-
logical intervention and an active control treatment, three were
small, underpowered studies (Hernandez-Reif, Field, Krasnegor,
& Theakston, 2001, n ? 12 for each group; Kankaanpaa, Taimela,
Airaksinen, & Hanninen, 1999, n ? 30 and 24 for the experimental
and control group, respectively; Turner, Clancy, Mcquade, &
Cardenas, 1990, n ? 25 for each group), and two studies involved
complex interventions for which the independent contribution of
the psychological component could not be isolated. One study
involved massage as the treatment, while in another study massage
was the control condition.
COYNE, THOMBS, AND HAGEDOORN
Message to Consumers
Nonetheless, Hoffman et al. claimed positive effects for psy-
chological interventions contrasted with various control groups,
for pain intensity, pain related interference, health-related quality
of life, and depression, plus evidence of efficacy of CBT and
self-regulatory treatments. Claims were made for the efficacy of
multidisciplinary approaches including a psychological compo-
nent, at least in terms of short-term effects on pain interference and
long-term effects on return to work. “The robust nature of these
findings should encourage confidence among clinicians and re-
searchers alike.” (pp. 8). Given the methodological and conceptual
shortcomings in the meta-analysis, such confidence is unwar-
Dixon et al. (2007)
Dixon et al. reported reviewing 27 RCTs with 33 active inter-
vention groups testing the effects of psychosocial interventions on
pain in adult patients diagnosed with arthritis. They reported an
overall standardized effect size of 0.18 for pain reduction.
Transparency of Reporting
In general, a lack of transparency made it difficult to assess
independently the results presented by Dixon et al. First, only 15
studies (with 20 intervention groups) of the 27 studies were actu-
ally included in the meta-analysis. The authors did not explain the
loss of 12 studies with 13 active intervention groups that they
described as “represented in the final analysis” and for whom
demographic data were included in summary descriptive statistics,
but it appears from appendixes that 10 studies with 11 intervention
groups were excluded because they did not report basic data for
postintervention pain outcomes. It is noteworthy that only one of
the 11 discarded intervention groups obtained significant results
for pain. Many of the studies they excluded, apparently for the lack
of published means and standard deviations, had, in fact, been
included in a previous meta-analyses (e.g., Warsi, LaValley,
Wang, Avorn, & Solomon, 2003).
Second, they did not present design characteristics of each
study. Even in the Data Extraction tables of Appendix 2, only
minimal data are presented, often discrepant with what is included
in the published meta-analysis. Dixon et al. indicated that “Of the
studies extracted to evidence tables, most demonstrated high qual-
ity for both internal and external validity” (p. 244). Procedures for
rating study quality are described and the specific studies are rated
in an appendix. We did not systematically rerate the studies.
However, we did note that Barlow, Turner, and Wright (2000)
received a perfect quality rating despite losing more patients from
the intervention arm (77 of 311, 25%) by the 4-month follow-up
than the number of patients in the intervention groups from all
other studies except Lin et al. (2003). Previous systematic reviews
of psychological interventions for arthritis pain (Astin, Beckner,
Soeken, Hochberg, & Berman, 2002; Riemsma, Taal, Kirwan, &
Rasker, 2004) have found the RCTs included by Dixon et al. to be
of generally low quality and have provided specific reasons for
why they were downgraded.
Third, decisions with respect to the inclusion criteria for inter-
ventions were unclear. Most of the 15 studies included in Dixon et
al.’s review provided CBT or stress management led by psychol-
ogists or advanced psychology trainees. Three studies reviewed by
Dixon et al. (Barlow et al., 2000; Hammond & Freeman, 2001;
Riemsma, Taal, & Rasker, 2003) were described in the original
studies as self-management or educational interventions. They
included CBT components, but were delivered by nonpsycholo-
gists, including lay group leaders who typically had arthritis (Bar-
low et al., 2000) or a variety of medical staff, including nurses
occupational therapists, or physical therapists (Hammond & Free-
man, 2001; Riemsma et al., 2003). It is not clear why these three
self-management/educational interventions were included, and
others excluded. Barlow et al. (2000) and Riemsma et al. (2003)
tested Lorig’s Arthritis Self-Management Program. Other RCTs
that have tested the same program were not identified as eligible
studies by Dixon et al. (e.g., Lorig et al., 1986; Lorig et al., 1989),
but no explanation was provided for this. One may also wonder
how similar these three self management/educational interventions
were to the control group of Keefe et al. (1996), which was
described as a 10-session educational intervention on the nature
and management of arthritis.
Sample Sizes of Original Studies
The largest study included in the meta-analysis was a secondary
analysis of a 12-month collaborative care intervention for de-
pressed primary care patients (Lin et al., 2003), which Dixon et al.
misclassified as a psychodynamic intervention. In fact, the patients
received depression care from a nurse or psychologist working
with a physician. The psychotherapy intervention that was avail-
able to patients was a CBT problem-solving therapy. However,
most patients in the intervention arm were using an antidepressant
medication at 12 months, and less than half received specialty
mental health services or psychotherapy, making it impossible to
evaluate any independent contribution of the psychotherapy. It is
also noteworthy that the Lin et al. study had at least nine times
more patients in the intervention group than all but one of the other
studies (Barlow et al., 2000) reviewed by Dixon et al. and ac-
counted for almost half of all patients included in tabulating the
summary effect size. The study should have been excluded from
Eleven studies (15 interventions) were psychological interven-
tions delivered by trained psychologists or advanced psychology
students. None of the intervention groups met the threshold cell
size of ?35. We found substantial baseline differences in pain for
nine of 20 comparisons (e.g., Hedges’s g ? 0.10, including Hedg-
es’s g ? 0.75 in 4 cases), and posttreatment differences in pain
scores may have reflected the persistence of baseline differences in
For studies to be included in the review, patients did not have to
meet a threshold criterion for pain, the primary objective of the
intervention did not have to involve pain reduction, and pain did
not have to be a primary outcome. Dixon et al. did not conduct a
systematic review of the secondary outcomes. Rather, they re-
ported other outcomes if data happened to be available in the same
articles as the pain outcomes. This may be the rationale for
including the Lin et al. (2003) secondary analysis of collaborative
care for depression. However, because depression outcomes for
Lin et al. were reported in another paper, the effect was not
included in Dixon et al.’s meta-analysis of depression outcomes.
This suggests what could be a more pervasive problem in calcu-
lating effect sizes for outcomes other than pain due to different
outcomes being reported in separate papers.
We found numerous discrepancies in reporting details of studies
and erroneous calculations of effect sizes in the published meta-
analysis. Not all of the studies presented in Dixon et al.’s Figure 1
are even listed in Appendix 2, the Data Extraction Table. Sample
sizes for at least half a dozen of the studies listed in Figure 1 do not
match the sample sizes reported in the original studies. For in-
stance, Sharpe et al. (2001) explicitly indicate that they report data
in their tables for 23 intervention and 22 control completers. Dixon
et al. report sample sizes of 19 and 18. Dixon et al. do not indicate
how they selected pain measures for the meta-analysis when
studies provided more than one measure.
The authors do not state how effect sizes were calculated, but
reanalysis suggests that post-treatment means and standard devi-
ations were used when possible, with change scores used if post-
treatment data were not provided. When the latter was apparently
done for the Riemsma et al. (2003) study at 12-months, however,
the group education effect was zero, but listed as ?0.17 in Dixon
et al.’s Figure 1. The effect size listed by Dixon et al. for the group
education with spousal involvement from the Riemsma study was
correct, but in the wrong direction: the intervention group had
worse pain at the outcome. Overall, there were five intervention
groups erroneously listed in Figure 1 by Dixon et al. with negative
effect sizes (lower pain in intervention group) when the interven-
tion groups had higher pain levels (CBT2 from Keefe et al., 2004;
Kraaimaat, Brons, Geenen, & Bijlsma, 1995; CBT1 from
Radojevic, Nicassio, & Weisman, 1992; Shearn & Fireman, 1985;
CBT1 Riemsma et al., 2003).
Message to Consumers
Dixon et al. claimed, “These findings indicate that psychosocial
interventions may have significant effects on pain and other out-
comes in arthritis patients. Ample evidence for the additional
benefit of such interventions over and above that of standard
medical care was found” (p. 241). They also recommended, “. . . it
is important that arthritis patients be made aware that although
psychosocial interventions appear to have some effects on pain,
these treatments are most likely to enhance their quality of life by
producing improvements in other important areas such as coping,
anxiety, pain, self-efficacy, depression, joint swelling, and physi-
cal disability” (p. 248). A Clinician Commentary (Pisetsky, 2007)
accompanying the article echoed this assessment: “As described in
the article . . . well-designed and well-controlled trials have con-
clusively established the value of various psychosocial interven-
tions . . . in reducing arthritis pain. Although the literature on
cognitive—behavioral therapy is the most extensive, data are
available to support the utility of all modalities tested” (p. 657).
Confidence in these conclusions, however, is mitigated by the
methodological issues and problems noted above. Even if one
accepted the basic results of the meta-analysis, one would not
know what to do with them. Should psychological services be
provided by doctoral level providers? Or will self-management
programs run by nurses do about as well? The review by Dixon et
al. does not answer these questions nor clarify to which type of
intervention their results apply.
Jacobsen et al. (2007)
Jacobsen et al. (2007) conducted their meta-analysis to deter-
mine the efficacy of psychological and activity-based interventions
for cancer-related fatigue. They reported a statistically significant
overall effect size of d ? 0.09, as well as a statistically significant
effect for psychological interventions (d ? 0.10), and a nonsignif-
icant effect for activity-based interventions (d ? 0.05). Jacobsen
and colleagues reviewed 24 psychological and 17 activity-based
trials for their meta-analysis of interventions for cancer-related
fatigue. Nineteen studies provided sufficient information for in-
clusion in the meta-analysis and another 11 could be included after
additional information was obtained from the authors of the orig-
inal studies. In total, 18 psychological and 12 activity-based stud-
ies were included in the meta-analysis.
Kangas, Bovbjerg and Montgomery (2008) claimed that Jacob-
sen et al. failed to identify over 40 additional trials meeting their
criteria, which might have been due to a restricted search strategy
including the use of only PsycINFO, MEDLINE, and CINAHL.
While it is beyond the purposes of this article to resolve this
important discrepancy, we did find that 20 RCTs published before
Jacobsen et al. completed their search were left out by Jacobsen et
al., but included in Kangas et al. (2008).
Previous smaller meta-analyses (2 to 11 trials) of nonpharma-
cological interventions for cancer-related fatigue which included
non-RCTs, reported slightly higher effect sizes between 0.11 and
0.24 (Conn, Hafdahl, Porock, McDaniel, & Nielsen, 2006; Lueb-
bert, Dahme, & Hasenbring, 2001; Schmitz et al., 2005). The
recent meta-analysis by Kangas et al. (2008) reported a much
higher effect size of 0.34 based on 57 RCTs. No significant
difference was found by Kangas et al. for psychological versus
activity-based interventions. Besides the difference in number of
studies included, another reason for the difference in overall effect
size may be that Jacobsen et al. (2007) utilized the final follow-up
measurement while Kangas et al. (2008) utilized the first follow-up
measurement. However, discrepancies in effect size were also
present for activity-based interventions that mostly reported out-
comes immediately after the intervention (0.05 in the Jacobsen et
al. study vs. 0.42 for fatigue and 0.69 for vigor in the Kangas et al.
study). The conflicting results of these two meta-analyses highlight
the subjectivity of meta-analysis in terms of search strategy, in-
clusion criteria and integration; different decisions may lead to
very different conclusions.
Methodological Quality of Included Studies
A supplementary table of methodological ratings published on-
line revealed that the quality of 70%–80% of the studies included
in the Jacobsen et al. meta-analysis was rated as only fair. Only
COYNE, THOMBS, AND HAGEDOORN
40% of the studies included in the meta-analysis presented statis-
tics showing that the intervention and control groups were com-
parable at baseline; fewer than half indicated the number of pa-
tients enrolled, treatment drop-out and reasons for drop-out; and
only 4% of the psychological and 29% of the activity-based
intervention trials provided intent-to-treat analyses.
Sample Sizes of Original Studies
Appendixes with information on the original studies showed
that six of the 18 psychological and seven of the 12 activity-based
intervention studies included in Jacobsen et al.’s meta-analysis fell
below n ? 35. Of the activity-based intervention studies, four
studies had a cell size of 13 or less. Of the 12 psychological
interventions with at least 35 patients per cell, Bordeleau et al.
(2003) and Goodwin et al. (2001) reported on the same sample.
The interventions evaluated in the included RCTs were quite
diverse, including supportive expressive group therapy, mindful-
ness meditation in a group setting or group psychoeducation;
group or individual CBT; telephone education about energy con-
servation and activity management; individual pain education and
management; individual cancer health education; individual stress
management, or the provision of an audiotape of a consult with the
oncologist. Such clinical heterogeneity precludes a meaningful
answer as to the intervention type to which an effect can be
Of the five activity-based intervention studies with cell sizes of
at least 35, one study compared a group who received psychother-
apy to a group receiving psychotherapy plus exercise. Another
study reported a larger decrease in fatigue in the control than the
exercise condition. Two studies focused on supervised exercise,
while the other three studies focused on home-based exercise.
Thus, clinical heterogeneity noted in the intervention conditions
extended to the comparison-control conditions as well.
The most serious criticism of Jacobsen et al. is that few of the
RCTs included in the meta-analysis had the specific aim of reduc-
ing fatigue or even stated fatigue reduction as a relevant hypoth-
esis. At best, such interventions might be construed as active
comparison-control treatments and contrasted, rather than inte-
grated with treatments explicitly targeting fatigue. In only three of
the 18 (17%) psychological intervention studies was fatigue a
primary outcome and in only five of the 12 (42%) activity-based
intervention studies. In no studies was there a minimal threshold of
fatigue as an entry criterion. Kangas et al. (2008) is subject to the
same criticism, but distinguished between RCTs that had aims or
hypotheses concerning fatigue and those that did not. In their
larger sample of studies, only 28% had a specific fatigue-related
aim or hypothesis, and of these, half had positive effects, a sub-
stantially greater proportion than RCTs without such an aim or
Many of the RCTs that did not have aims or hypotheses related
to fatigue were selected because they included the Profile of Mood
States (POMS) among their outcomes, which has subscales assess-
ing fatigue and vigor-activity. Studies targeting distress commonly
include the POMS as part of a battery of distress measures. Fatigue
and vigor-activity are often included as an outcome for RCTs
without an explicit hypothesis simply because these subscales are
part of the instrument. Outcomes in these studies are reported
without a prioritizing (primary vs. secondary) of these multiple
measures and with a strong confirmatory bias (See Coyne et al.,
2006). Whether results for fatigue and vigor-activity subscales are
reported at all may depend on whether a case can otherwise be
made for the efficacy of the intervention for distress in terms of
depression-dejection or anxiety-tension subscales of the POMS.
Thus, results for fatigue and vigor-activity may only be selectively
available. Overall, however, we find that Jacobsen et al.’s deci-
sions to include RCTs simply on the basis of a relevant published
outcome measure, not on the basis of the aim or hypothesis of the
study and their failure to distinguish aims or hypotheses of studies
in conducting moderator analyses undercuts any claims of clinical
or pragmatic implications of the results.
Message to Consumers
Jacobsen and colleagues claimed: “results of this review provide
limited support for the clinical use of nonpharmacological inter-
ventions to prevent or relieve cancer-related fatigue” and “. . .
evidence of efficacy is stronger for psychological interventions
than for activity-based interventions.” (p. 665). We did not find
any evidence in the article, however, to suggest that there is a
difference in efficacy of psychological versus activity-based inter-
ventions. Specifically, the moderator analysis for type of interven-
tion was not significant. In fact, none of the moderator analyses
were significant, including comparisons of the efficacy based on
whether fatigue or vigor was measured as an outcome, whether
participants had been diagnosed with breast cancer or another type
of cancer, whether interventions were delivered to individuals or a
group, and whether interventions were home-based or supervised.
The overall effect size that Jacobsen et al. reported, 0.09 (95%
CI ? .02–.16) which translates to an r2of .002, indicates a
negligible effect. If accepted at face, this result should discourage
offering psychosocial services to patients with cancer for relief of
fatigue. It is not clear from the meta-analysis provided by Jacobsen
et al., however, if this would be the correct decision.
Integration and Commentary
Consistent with our experience with the meta-analysis by Zim-
mermann and colleagues (2007), evaluating these four meta-
analyses of interventions for adults (Dixon et al., 2007; Hoffman et
al., 2007; Irwin et al., 2006; and Jacobsen et al., 2007) that
appeared in a new section of Health Psychology, Evidence Based
Treatment Reviews, was an arduous, labor intensive and ultimately
frustrating process. We started with the published meta-analyses
and found numerous lapses in transparency and notable inconsis-
tencies, miscalculations, and contradictions. We reviewed addi-
tional sources, such as the original RCTs, but also related studies
and meta-analyses often covering the same literatures. Our sense
increased that there were fatal flaws in these meta-analyses related
to inaccuracies, failure to adequately address issues of quality and
arbitrariness of study selection and inclusion. We doubt whether a
casual reader or a consumer in need of quick clinically or policy
relevant summaries would be motivated or alert to the need to
undertake such a reappraisal. In all likelihood, they would defer to
the evaluations of the literature usually confidently offered by
meta-analyses and discouraged by the opaqueness with regard to
key methods and decisions from questioning further.
Many of the problems encountered in these meta-analyses
stemmed from the notable inadequacies in the conduct and reporting
of the original RCTs considered for inclusion. Quality was often only
poor to fair at best, and these studies also tended to be underpowered,
compounding the problems by inadequacies in the design, analyses,
and reporting of these studies. While these meta-analyses sometimes
acknowledged the problem with the original literature and quantified
the problem with formal ratings, no effort was made in any analysis
to exclude poor quality studies or to perform sensitivity analyses
evaluating effects of whether they were excluded. We found evidence
of studies identified in search procedures as eligible for inclusion not
being included in the meta-analysis, some of the excluded studies
nonetheless having been included in other published meta-analyses
(Dixon et al., 2007; Jacobsen et al., 2007), and of results being more
accessible in original studies when they were favorable to the evalu-
ation of an intervention (e.g., Dixon et al.). Thus, a confirmatory bias
in the original studies was compounded by a confirmatory bias in
whether they were included in these meta-analyses. We had to turn to
the original literature before identifying some problems. For instance,
none of the RCTs evaluating multi-component interventions for back
pain allowed isolation of the independent contribution of the psycho-
logical component. In another case, by far the largest RCT included in
whose data were meta-analyzed, similarly did not allow isolation of
the contribution of psychotherapy. All of these problems speak to the
subjectivity of meta-analysis and high likelihood that meta-analyses
of behavioral medicine interventions at this time would benefit from
more careful attention to methodological issues, including when it is
appropriate to conduct a meta-analysis, given the confirmatory bias
and limitations of the existing trials, most of which are not of high
We found support for our proposal that small studies with less
than 55% power to detect an effect even when it was present
should be excluded. First, some analyses heavily depended on
studies so small that there was substantially less than 55% prob-
ability of moderate effects being identified. Second, there was
evidence that the poor quality of the small RCTs influenced
whether effects were available for scrutiny. For instance, some
meta-analyses were influenced by pre-post differences that were
more accurately attributable to the intervention and control groups
not being equivalent at baseline, and in at least one instance, a
substantial number of small RCTs were not entered into the
meta-analysis because sufficient data for meta-analysis from these
nonsignificant trials were not made available in the original arti-
cles. While serious methodological problems should be of concern
for any sized study, they can become more decisive in their impact
on small studies and whether the results become available in
published articles. While we can readily detect that such biases
exist, our inability to specify the extent of bias precludes any
confidence in efforts to compensate for bias statistically (Kraemer
et al., 1998).
Do these meta-analyses supply a suitable foundation for clinical
and policy decisions? Do they indicate that psychosocial interven-
tions should be staffed and funded by third party payments? Or
which ones? For numerous reasons, we do not believe the meta-
analyses we reviewed provide a basis for evaluating the potential
efficacy of such interventions. At best, it would be premature to
make decisions on the basis of their results. The first set of issues
lies in a lack of transparency and other substantive and method-
ological problems with which the analyses were conducted and
reported, including their being conducted with unrepresentative
subsamples of the available literature. Second, the meta-analyses
depend on small numbers of underpowered, methodologically
inadequate trials, particularly for any moderator analyses compar-
ing alternative treatments. Third, the reviews do not establish
standards for clinically meaningful effects. Jacobsen et al. (2007);
Hoffman et al. (2007), and Dixon et al. (2006) claim what would
reasonably be considered clinically negligible effects without iden-
tifying them as such.
Our review of these meta-analyses has a number of notable
limitations. It was important that we did not undertake a systematic
re-review of the relevant literatures, nor recalculate every effect
size we encountered. Often, our probing of the literature was
initiated because of a suspicion about what was presented in the
published meta-analyses and available supplementary materials.
Also, it is likely that with extended dialogue with the authors, we
could have clarified additional points and even resolved some
ambiguities and apparent contradictions in the published papers.
However, our goal was not to characterize the literatures covered
by these meta-analyses, but to conduct an appraisal of the ade-
quacy and accuracy of these meta-analyses in summarizing these
literatures. In doing so, we were more concerned with uncovering
any evidence that the meta-analyses were inadequate, undepend-
able or likely biased as the foundations for practical decision-
making. Our view is that meta-analyses should be held to high
standards. As a secondary literature, there is the likelihood that
their conclusions will be accepted in lieu of a scrutiny of the
primary RCTs, particularly when these conclusions are presented
confidently and persuasively and without adequate transparency.
There is the potential that particular claims based on the meta-
analyses about the relative efficacy of interventions will be used to
override patient and clinician preferences and restrict the avail-
ability of interventions, regardless of their accuracy of these
claims. Such claims can also influence research priorities by indi-
cating that particular empirical questions have been settled and so
no further funding should be allocated to addressing them.
We think that results of our exercise should serve as a wake up
call: prospective authors of meta-analyses, reviewers, and antici-
pated consumers should be educated about how to conduct and
report a meta-analysis and the numerous threats to their validity.
We do not know how generalizable our criticisms are to other
meta-analyses of behavioral medicine interventions, but they do
provide a basis for heightened skepticism. Overall, we would like
to see more attention in the behavioral medicine literature to the
controversies and developing standards for doing and reporting
meta-analyses that are appearing in clinical epidemiological and
biomedical journals. However, the behavioral medicine commu-
nity should be active participants in the process of improving the
process of evaluating interventions, not just spectators, and its key
journals need to provide a forum for debate tailored to the specific
needs and interests of the field. Recently, elaborate new American
Psychological Association standards were announced for reporting
both clinical trials and systematic reviews and meta-analyses
COYNE, THOMBS, AND HAGEDOORN
(Cooper, Maxwell, Stone, & Sher, 2008). Even before these stan-
dards are adopted as requirements for publication in APA journals
and elsewhere, they provide invaluable guidance for avoiding
some of the problems we identified with these four meta-analyses.
Yet, it will be decades before these new standards are seen in the
quality of the bulk of the trials available for consideration for
inclusion in meta-analyses. Meanwhile, authors contemplating
conducting a meta-analysis must contend with a literature domi-
nated by methodologically flawed studies and decide whether and
how to proceed. One way to resolve this dilemma is not to conduct
a meta-analysis, as Moher, Jadad, and Klassen (1998) suggest:
There is often a perception that the statistical combination of data
across studies is the most important part of a systematic review. We
take such a view cautiously. We believe that a well-reported, system-
atic qualitative review is much better than an inappropriately con-
ducted and reported quantitative review or meta-analysis (pp. 916).
The risk of publishing meta-analyses that are premature because
of limitations in the number and quality of available studies is that
the accumulation of better, larger-scale studies and the integration
of their results in a future meta analysis will be discouraged
because of a false impression that the research question was
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