R E S E A R C H A R T I C L E Open Access
Rethinking the treatment of chronic fatigue
syndrome—a reanalysis and evaluation of
findings from a recent major trial of graded
exercise and CBT
Carolyn E. Wilshire
, Tom Kindlon
, Robert Courtney
, Alem Matthees
, David Tuller
, Keith Geraghty
and Bruce Levin
Background: The PACE trial was a well-powered randomised trial designed to examine the efficacy of graded
exercise therapy (GET) and cognitive behavioural therapy (CBT) for chronic fatigue syndrome. Reports concluded
that both treatments were moderately effective, each leading to recovery in over a fifth of patients. However, the
reported analyses did not consistently follow the procedures set out in the published protocol, and it is unclear
whether the conclusions are fully justified by the evidence.
Methods: Here, we present results based on the original protocol-specified procedures. Data from a recent Freedom
of Information request enabled us to closely approximate these procedures. We also evaluate the conclusions from the
trial as a whole.
Results: On the original protocol-specified primary outcome measure - overall improvement rates - there was a
significant effect of treatment group. However, the groups receiving CBT or GET did not significantly outperform the
Control group after correcting for the number of comparisons specified in the trial protocol. Also, rates of recovery were
consistently low and not significantly different across treatment groups. Finally, on secondary measures, significant effects
were almost entirely confined to self-report measures. These effects did not endure beyond two years.
Conclusions: These findings raise serious concerns about the robustness of the claims made about the efficacy of CBT
and GET. The modest treatment effects obtained on self-report measures in the PACE trial do not exceed what could be
reasonably accounted for by participant reporting biases.
Keywords: Chronic fatigue syndrome, Myalgic encephalomyelitis, Graded exercise therapy, Cognitive behavioral therapy
For some time now, the officially recommended treatments
for chronic fatigue syndrome (CFS) in many countries have
been graded exercise therapy (GET) and cognitive behav-
ioural therapy (CBT). In an effort to provide high quality
evidence of the efficacy of these treatments, White and
colleagues undertook a large randomised trial, informally
referred to as the PACE trial . Reports from the PACE
trial concluded that GET and CBT were moderately
effective treatments for CFS, both leading to recovery in
over a fifth of patients [2–7]. The trial’ssizeanditspromo-
tion as a success have made it enormously influential in the
attempt to treat CFS .
However, there are some significant concerns with the
published reports of the trial. First, the outcomes and
analyses presented in these reports did not always follow
the procedures set out in the original published protocol
. Since the purpose of a trial protocol is to prevent ad
hoc modifications that may unduly favour the study
hypotheses, it is important to carefully scrutinise the
justification for these changes and how they may have
influenced outcomes. Also, it is unclear whether some of
* Correspondence: Carolyn.Wilshire@vuw.ac.nz
School of Psychology, Victoria University of Wellington, New Zealand, P.O.
Box 600, Wellington, New Zealand
Full list of author information is available at the end of the article
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reproduction in any medium, provided you give appropriate credit to the original author(s) and the source, provide a link to
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(http://creativecommons.org/publicdomain/zero/1.0/) applies to the data made available in this article, unless otherwise stated.
Wilshire et al. BMC Psychology (2018) 6:6
the trial’s conclusions about treatment efficacy were fully
justified by the evidence. Here, we present several new
analyses of the trial data, using methods that align with
those specified in the original trial protocol, and drawing
on data recently made available as part of a Freedom of
information application (). This dataset, henceforth
referred to as the FOIA dataset, is available to the public
(see Declarations section for instructions on how to
download the dataset). We also explore several other
aspects of the findings not considered in the published
reports, and evaluate the conclusions from the trial as a
Summary of the PACE trial
PACE was a large randomised trial whose primary aim
was to assess the effectiveness of GET and CBT as treat-
ments for CFS (early publications refer to it as a “rando-
mised controlled trial”, but “randomised trial”is more
appropriate, given that several nuisance variables were
not fully controlled across trial arms, e.g., contact hours).
Participants were 641 adults with mild-to-moderate CFS
defined by the Oxford criteria : the principal symp-
tom must be fatigue, which must have had a definite
onset, resulted in significant disability, and have
persisted for at least six months. Participants also had to
score 65 or less on the Short-Form Health Survey
Physical Function subscale . Also, they had to report
experiencing at least six of the 11 fatigue items on the
Chalder Fatigue Questionnaire (CFQ ), as “more
than”or “much more than”than prior to illness.
Participants were randomised into four groups. All were
offered at least three medical consultations. The first
group, which we will call Control, received no further
treatment (the trial publications use the term Specialised
Medical Care). The other groups received up to 15 ther-
apy sessions over 36 weeks. One group received CBT, one
GET, and the fourth group received a novel treatment,
Adaptive Pacing Therapy. Both the CBT and the GET
interventions were built upon a behavioural/decondition-
ing model of CFS. This model proposes that there is no
major ongoing disease process underlying CFS - only
deconditioning due to recent inactivity, and its various
consequences. When patients attempt to increase their
activity, they experience normal fatigue, stiffness and other
symptoms, which they misinterpret as signs of continuing
disease. The patients then become more focused on their
symptoms, and fearful of further activity, creating a self-
perpetuating cycle . The GET programme was designed
to help CFS patients overcome this purported fear of exer-
cise and intense symptom-focusing through graded expos-
ure to exercise, and thereby also reverse any
deconditioning that had occurred. Participants were asked
to choose an aerobic activity they enjoyed, and to grad-
ually increase the duration and intensity of that activity
under the supervision of a therapist. The CBT programme
had similar aims, but addressed the fear of activity, mal-
adaptive illness beliefs and symptom focusing using a
combination of CBT and practical activities (, p. 825).
Participants were encouraged to view their symptoms as
arising from anxiety, intense symptom focusing and/or
deconditioning. The sessions addressed fears about exer-
cise and other “unhelpful cognitions”that may perpetuate
symptoms, and encouraged participants to try gradually
increasing their activity (, p. 825).
Adaptive Pacing Therapy, in which patients were
advised not to exceed a certain level of activity, was cre-
ated specifically for the trial. Results for this trial arm
did not differ significantly from those for the Control
arm for any of the outcomes considered in this article.
Consequently, we will not discuss them further here.
The primary outcome for the trial, as specified in the
trial protocol published in 2007, was the percentage of
patients who fulfilled the specified criteria for overall
improvement 52 weeks after randomisation . Two
measures contributed to the definition of improvement:
self-rated fatigue, measured using the Chalder Fatigue
Questionnaire , and self-rated disability, measured
using the SF-36 Physical Function subscale . The
minimum levels of improvement required on each of
these two measures are given in Table 1(Definition A).
However, in May 2010, several months after data collec-
tion was complete, this primary outcome measure was
replaced with two continuous measures: fatigue and
physical function ratings on the two scales described
above (see [13,14] for details). According to the
researchers, the changes were made “before any examin-
ation of outcome data was started...”(, p. 25).
In 2011, the first major publication from the trial
reported results based on this new primary outcome
. It was found that, following treatment, scores on
both these continuous measures improved in all
groups, but significantly more so in the CBT and
GET groups than in the other groups. In the 2011
publication, rates of overall improvement were also
reported; however, these were not based on the
protocol-specified definition, but rather on a very dif-
ferent, and much more generous, one: Definition B in
pants and 61% of GET participants were classed as
having improved overall . However, 45% of Con-
trol participants did so too. Results for the original
protocol-specified definition of improvement - Defin-
ition A in Table 1–do not appear in any peer
reviewed publications from the trial (which number
in the double digits ).
Wilshire et al. BMC Psychology (2018) 6:6 Page 2 of 12
Rates of recovery
An important secondary outcome specified in the trial
protocol was the proportion of patients who met the
specified definition of recovery at the end of the trial .
The definition of recovery presented there considered
each participant’s scores on two key self-rated measures
(fatigue, physical function), one further measure of overall
self-rated improvement and finally, whether the partici-
pant still met various CFS case definitions. The complete
definition of recovery is given in Table 1(Definition A).
However, results for this outcome never appeared in
published reports. Instead, a 2013 paper reported recovery
rates based on a much more generous definition of recov-
ery (Definition B in Table 1). According to these new
criteria, 22% of patients in each of the CBT and GET
groups qualified as recovered, but only 7% in the Control
group. The difference in recovery rates between the CBT/
GET groups and the Control group was statistically signifi-
cant. The PACE investigators have not specified when the
decision to change the definition of recovery was made,
except to say it was “before the analysis occurred”;
the change does not appear in any documentation prior to
the final publication, and there is no published evidence
that it was approved by the trial steering committee.
Other outcome measures
A number of other secondary outcome measures were
collected at 52 weeks, including several additional
subjective outcomes, and also four objectively scored
measures, which are described further below. During
the course of the trial, data for a range of adverse
events and outcomes were also collected; these are
also described briefly below.
The four objectively scored measures examined at
52 weeks were: 1) distance walked in six minutes; 2)
max, estimated using the step-test method);
3) days lost from work during the six-month period
following the primary endpoint; and 4) the percentage of
participants receiving illness/disability benefit during
that same period. In the 2011 primary trial report, only
one of these outcomes was reported: walking speed .
Here, 69% of the GET group completed the test, and
walked approximately 10–12% farther in six minutes
than the 74% of Controls who completed the test. This
small difference was statistically significant (based on an
available case analysis), but given the high and uneven
drop-out rate for these outcome measures, this result
should be treated with caution. The CBT group did not
walk significantly farther than Controls. Results for the
other objective outcomes were not reported until some
years later, and then only in summary form [3,6].
H.owever, none appear to be associated with significant
treatment effects. For the fitness measure, a simple one-
way analysis of variance performed on the summary data
extracted from (, Figure 2) failed to reveal a significant
effect of treatment group, F(3,425) = 0.368, ns. For the
employment loss measure, a similar analysis of the sum-
mary data in (, Table 2) also failed to reveal a significant
treatment effect, F(3, 636) = 0.23, ns.Finally,forillness/
disability benefit data, a binary logistic regression
performed using the summary data in (, Table 3) did
not reveal any significant treatment effect, χ
(3) = 0.00, ns.
The adverse events measures collected during the trial
included: serious adverse events (death, hospitalisation,
etc.); serious deterioration (a broader category that
included a serious adverse event, sustained decrease in
Table 1 Definitions of improvement and recovery specified in the trial protocol , and those used in the final trial reports [2,4].
Improvement was the primary outcome measure specified in the protocol. Recovery was a secondary measure
Definition A: Specified in trial protocol Definition B: Used in published reports
Minimum score of 75 on the 100-point SF-36 physical
function scale or a score increase of 50% or more.
At least an 8 point increase in the 100-point SF-36 physical
Of the 11 fatigue items on the Chalder Fatigue Questionnaire
(CFQ), three or fewer rated as worse/much worse than prior to
illness OR the total items rated worse/much worse dropped by
at least a 50%.
At least a 2 point decrease on the 33-point CFQ (Likert scoring
Recovery Minimum score of 85 on the 100-point SF-36 physical function
Minimum score of 60 on the 100-point SF-36 physical function
Of the 11 items on the CFQ, three or fewer rated as worse/much
worse than prior to illness.
Maximum score of 18 on the 33-point CFQ.
Overall health self-rated as “very much better”on the Clinical Global
Impression scale .
Overall health self-rated as “much better”or “very much better”
on the Clinical Global Impression scale.
The final “caseness”criterion was met if the patient no longer
fulfilled: The Oxford case definition of CFS; the CDC criteria ;
AND the London ME criteria . (As determined by a non-blinded
The revised “caseness”criterion was met if ANY of the following
applied: a) the patient did not meet the standard Oxford case
definition; OR b) on the CFQ, they rated less than six of the 11
fatigue items as being worse than prior to illness; OR c) their
SF-36 Physical Function score was greater than 65.
CFQ Chalder Fatigue Questionnaire
Wilshire et al. BMC Psychology (2018) 6:6 Page 3 of 12
self-reported physical function or overall health, or with-
drawal due to worsening); and non-serious adverse
events. Serious adverse events were significantly more
prevalent in the GET group (8%) than in the Control
group (4%); there were no other statistically significant
A mail survey was conducted at least two years after
randomisation (median 31 months :). Survey response
rates were 72%, 74% and 79% for the Control, CBT and
GET groups respectively. Participants were again asked
to complete the trial’s primary fatigue and physical
rating scales, and several other questionnaires. A 2015
paper reported the results for the fatigue and physical
function measures, again treating them as separate, con-
tinuous variables . Analyses of these measures, based
on an available case approach, failed to yield any signifi-
cant effects of treatment group. However, the investiga-
tors did not view this negative result as a cause for
concern at all. They argued that many patients in the
Control and Adaptive therapy trial arms had received
some CBT or GET after the conclusion of the main trial,
and this could explain why they had since improved to
the level of the other patients.
The primary objective of our reanalyses was to exam-
ine how the trial outcomes would have looked if the
investigators had adhered to their published protocol.
Specifically, we were interested in analysing results
for the primary outcome set out in that document:
overall improvement rates. We also calculated recov-
ery rates based on the definition outlined in the
protocol. Results from this latter analysis have been
published elsewhere [17,18],butherewepresent
more complete details of our method and findings.
Finally, we explored the published data on long-term
outcomes to examine whether they had been contam-
inated by patients’post-trial therapy experiences, as
the PACE researchers hypothesised.
Using the FOIA dataset, we first calculated rates of
improvement at the primary 52-week endpoint according
to the definition specified in the trial protocol (Definition A
in Table 1). We used an intent-to-treat approach, again as
specified in the protocol: if the 52-week score was missing,
that case was counted as a non-improver (there were no
missing scores at baseline; missing scores had been replaced
with scores at screening as described in ). However, for
comparison, we also repeated the analysis based on an
available case sample: participants with missing scores at
52 weeks were simply excluded from the dataset.
Based on the methods stipulated in the published
protocol, we performed a logistic regression analysis on
the binary outcome data from all four treatment arms.
Where appropriate, we also performed pairwise compar-
isons between each of the two key treatment groups
(CBT and GET), and the Control group, correcting for
the total number of planned comparisons. The trial
protocol lists six planned comparisons . The statistical
analysis plan, published some years later, lists only five
. Here, we report outcomes based on both scenarios.
No method of correction was specified in the trial proto-
col, but in the statistical analysis plan, the Bonferroni
method was stipulated , so this was the method we
applied. All omnibus analyses (that is, all analyses exam-
ining the overall effect of treatment group on outcomes)
included the adaptive pacing therapy group, because it
forms part of the trial design. However, specific results
for this group are not detailed here.
The protocol specified that various stratification
variables would also be included in the primary out-
come analysis (e.g., treatment centre, therapist, pres-
ence/absence of co-morbid depression). These
variables were not available in the FOIA dataset, so
we were unable to include them. Nonetheless, they
were approximately evenly distributed across groups,
and therefore their inclusion would be unlikely to
change outcomes substantially . Also, our team has
previously shown that for one of the published logis-
tic regression analyses (that for recovery rates based
on Definition B in Table 1), replicating the analysis
Table 2 Outcomes at 52 weeks and long-term follow-up, excluding patients who completed any additional sessions of GET or CBT.
Confidence intervals were only available for the follow-up phase
Measure Group N 52 weeks (mean scores for subgroup) Long-term follow-up (means, 95%CIs)
SF-36 Physical Function Scale Control 49 56.8 62.6 (54.6, 70.6)
CBT 88 61.5 64.2 (58.6, 69.8)
GET 95 62.8 62.5 (57.1, 67.9)
Chalder Fatigue Scale
Control 49 22.6 18.7 (16.2, 21.2)
CBT 88 20 17.9 (16.1, 19.7)
GET 95 19.7 18.7 (17.1, 20.3)
CIs confidence intervals
Wilshire et al. BMC Psychology (2018) 6:6 Page 4 of 12
without the stratification variables had a negligible
effect on the outcome of the analysis .
We also calculated recovery rates based on the defin-
ition specified in the trial protocol (Definition A in Table
1). Results from this analysis have been published else-
where , but here we present more complete details
of our method and findings. In the published protocol, it
was not explicitly specified that an intent-to-treat ap-
proach would be applied, so we present results based on
both an intent-to-treat approach (according to the defin-
ition above) and an available case approach (again, ac-
cording to the definition above). Our definition of
recovery closely approximated Definition A from the
trial protocol, but may have been marginally more gen-
erous: in determining whether the final CFS “caseness”
criterion was met, we considered only the Oxford case
definition (the other case definitions were not available
in the FOIA dataset). However, it is unlikely that this
change impacted substantially on recovery rates, and if it
had, its likely effect would have been to further reduce
recovery rates for the CBT and GET groups relative to
the other two groups (the maximum effect it could pos-
sibly have had was to exclude a further three individuals
each from the CBT and GET “recovered”groups, and
none from the Control group. This is the number of in-
dividuals that were excluded from the “recovered”group
when these two alternative caseness criteria were
added to the recovery definition used in ). We
then performed a logistic regression analysis incorpor-
ating the binary recovery data from all four treatment
arms. Where appropriate, we performed planned pair-
wise comparisons according to the procedures set out
above for the primary outcome analysis.
Finally, to explore the PACE investigators’hypothesis
that long-term treatment effects may have been
obscured by patients’post-trial treatment choices, we
isolated the long-term self-rated fatigue and physical
function scores for those patients who did not receive
any post-trial CBT or GET. The relevant individual
patient data are not available in the FOIA dataset, so a
systematic reanalysis could not be performed. However,
since the relevant summary data are reported in , see
Supplementary materials, Table C], we were able to per-
form a simple one-way analysis of variance examining
the effect of original treatment allocation on long-term
outcomes in this subgroup.
Figure 1shows intent-to-treat means and confidence
intervals for the two self-rated measures that contrib-
uted to the definition of improvement, alongside esti-
mates of performance in healthy controls. A number of
the Chalder Fatigue Questionnaire scores needed to cal-
culate these rates of improvement were missing from
the FOIA dataset; however, in every such case, the out-
come could be inferred from other data available in the
FOIA set. Based on the protocol-specified definition of
improvement, 20% of CBT patients and 21% of GET
patients improved, and 10% of the Control patients.
These percentages accord with those calculated by the
investigators and posted to the Primary Investigator’s
institutional website shortly after the researchers were
directed to release the data under FOI legislation (;
these results were never formally published and the stat-
istical analyses specified in the original trial protocol
were never performed).
There was a statistically significant effect of treatment
on improvement rates, χ
(3) = 14.24, p= .003. The p-
value associated with the contrast between CBT and
Control was p= .015 and that for the contrast between
Fig. 1 Intent-to-treat means for fatigue and physical function ratings, the two measures that contributed to the criterion for improvement specified in
the published protocol (Definition A in Table 1). Estimates of healthy performance for the fatigue and physical function measures are based on
previously published samples that further excluded the elderly (over 60), and those with a significant medical condition (95% CI bands = upper and
lower bounds of 95% confidence interval). The relevant normative data for the Chalder Fatigue Questionnaire were obtained from , and those for
the SF-36 physical function scale were obtained from . In the case of the SF-36 scale, the healthy sample was highly negatively skewed, so medians
are reported. The median score for this sample was 100 (95% confidence intervals: 100,100)
Wilshire et al. BMC Psychology (2018) 6:6 Page 5 of 12
GET and Control was p= .010. If we take into account
all six planned comparisons listed in the protocol, the
Bonferroni-adjusted pthreshold for both pairwise com-
parisons is 0.008. Neither comparison reaches this
threshold. The situation is not much improved if we
consider only the five planned comparisons listed in the
subsequent statistical analysis plan (); the pthresh-
old is 0.010. The comparison between GET and Control
just reaches this threshold, but the comparison between
CBT and Control does not.
The percentage of participants with missing outcomes
at 52 weeks was small (5.2% across all trial arms). Never-
theless, to explore the impact of counting drop-outs as
non-improvers, we repeated our calculations based on an
available case sample. Using this definition, 11% of Con-
trol participants improved, compared to 22% and 21% of
CBT and GET participants respectively. There was again a
statistically significant overall effect of treatment group on
improvement rates, χ
(3) = 15.02, p=.002.Thep-value as-
sociated with the contrast between CBT and Control was
p= .010 and that for the contrast between GET and Con-
trol was p= .011. However, once more, neither of these
outcomes survives Bonferroni correction based on the
number of planned comparisons specified in the trial
protocol (corrected threshold pvalue = .008). Even using
the looser criterion based on the statistical analysis plan
(p= .010), the comparison between CBT and Control only
just reaches the threshold of 0.01 and the comparison
between GETand Control does not.
In addition to overall improvement rates, the trial
protocol identifies rates of improvement on each of the
two major contributing criteria –self-rated fatigue and
physical function - as primary outcomes in their own
right. So we analysed these outcomes in the same man-
ner as above, using an intent-to-treat approach as speci-
fied in the protocol. Rates of protocol-specified
improvement on the SF36 physical function criterion
were 44% for the Control group, 48% for the CBT group,
and 61% for the GET group. The overall effect of treat-
ment arm was significant, χ
(3) = 16.31, p= .001. The p-
value associated with the contrast between CBT and
Control was p= .34 and that for the contrast between
GET and Control was p= .002. The comparison between
GET and Control survives correction for multiple com-
parisons (irrespective of whether one assumes five or six
planned comparisons) but that between CBT and Con-
trol does not.
Rates of protocol-specified improvement on the CFQ cri-
terion were 13% for the Control group, 26% for the CBT
group, and 24% for the GET group. There was also a statis-
tically significant effect of treatment on rates of improve-
ment on the fatigue criterion, χ
(3) = 13.19, p= .004. The p-
value associated with the contrast between CBT and Con-
trol was p= .004 and that for the contrast between GET
and Control was p= .015. The former remains after correct-
ing for multiple comparisons, but the latter does not.
Using the protocol-specified definition of recovery, and ap-
plying an intention-to-treat approach, the rates of recovery
were 7%, 4% and 3% for the CBT, GET and Control groups
respectively. Applying an available-case approach, these
rates were 8%, 5%, and 3% respectively. In neither instance
was there a statistically significant effect of treatment on re-
covery rates (pvalues were 0.14 and 0.10, respectively, for
the intent-to-treat and available case approaches).
Out of those who responded to the long-term follow-up,
43% of the Control participants had received no further
CBT or GET after the completion of the trial. This was
also the case for 74% and 75% of the respondents from
the CBT and GET arms respectively. Considered together,
this subset of participants was perhaps slightly less
severely affected than the remaining patients: they scored
slightly better on the primary physical function and fatigue
scales at 52 weeks than those who opted for further treat-
ment (physical function: 61.3 vs. 48.1; fatigue: 23.9 vs.
25.9). However, at 52 weeks, the pattern of scores across
treatment arms was the same as for the sample as a whole:
the CBT and GET participants in our subset rated their fa-
tigue as slightly lower and their physical function slightly
higher at 52 weeks than the Control participants. In this
respect, our subsample may be considered reasonably rep-
resentative of the sample as a whole.
Table 2provides arithmetic means for the two major
self-report outcome measures for this subset of patients
(i.e., those who received no further treatment). The pat-
tern of results presented here mirrors that obtained for
the entire cohort: the small group differences apparent
on these measures at 52 weeks are no longer evident at
long-term follow-up. A one-way analysis of variance
revealed that there were no statistically reliable effects of
treatment group on either outcome measure (Physical
function: F(3,291) = 0.70, ns; Fatigue F(3,291) = 0.17, ns).
If we repeat the analyses, adding in those cases who
received some additional therapy sessions, but less than
the minimum 10 considered by the investigators to be
an “adequate”dose (, p.1071), the outcome does not
change (Physical function: F(3,384) = 1.85, ns; Fatigue
F(3,384) = 0.86, ns). Consequently, the disappearance of
group differences at long-term follow-up cannot be
attributed to the effects of additional post-trial therapy.
Discussion of new results
Our reanalyses of the trial data based on the published
protocol generated some troubling findings. First, scores
Wilshire et al. BMC Psychology (2018) 6:6 Page 6 of 12
on the protocol-specified primary outcome measure
—improvement in self-reported fatigue and physical
function –were numerically higher for the CBT and the
GET groups than for the Control group. However, these
differences did not pass the threshold for statistical sig-
nificance after correcting for the number of planned
comparisons specified in the trial protocol. Using a more
lenient correction (assuming only five planned compari-
sons), outcomes are only marginally more positive: the
comparison between GET and Control just reaches this
threshold, but the comparison between CBT and Control
does not. Of course, our analyses did not incorporate a
number of important stratification variables that were
unavailable in the FOIA dataset. However, it appears
unlikely that their inclusion would substantially alter the
result, and our analyses remain the closest approxima-
tion to the originally specified one that has ever been
published. Our findings suggest that, had the investigators
stuck to their original primary outcome measure, the out-
comes would have appeared much less impressive.
Improvement rates for self-rated fatigue and physical
function considered individually did yield some statisti-
cally significant findings, which suggests that the inter-
ventions were somewhat specific in the way they altered
patients’illness perceptions. Self-rated physical function
scores showed greater improvement in the GET group
than in the Control group —but not self-rated fatigue
scores –which suggests GET had a modest effect on
patients’perceptions of their physical function, but did
not do much to alter symptom perceptions. Conversely,
self-rated fatigue showed greater improvement in the
CBT group than in Controls –but not physical function
–which suggests CBT elicits modest reductions in
symptom-focusing, but does not do much to improve
patients’confidence in their physical capacities.
Second, when recovery rates were calculated using the
definition specified in the published protocol, these were
extremely low across the board, and not significantly
greater in the CBT or GET groups than in the Control
group. Neither an intent-to-treat nor an available case
analysis yielded a significant benefit for these therapies
over conventional medical care. Again, we were unable
to incorporate a number of stratification variables into
this analysis, but it is unlikely that the result would be
different had we done so.
With respect to long-term outcomes, the investigators’
original analysis did not reveal any significant effects of
treatment allocation on self-reported fatigue and physical
function at long-term follow-up . They suggested this
null effect may have been due to the confounding effects
of post-trial therapy. Our informal re-examination of the
long-term follow-up results provide no support for this
suggestion. We found that even when patients who
received post-trial CBT or GET are excluded, there is still
no evidence of any long-term treatment-related benefits –
not even a trend in the hypothesised direction. Of course,
our analyses were informal. Ideally, we would have repli-
cated the analysis reported in  for this patient subset,
which included all the covariates listed in that analysis
(, p. 1068), such as fatigue and physical function scores
at 52 weeks, time of follow-up, trial centre and disease
caseness. This was not possible on the data available.
However, until better evidence becomes available, there is
no reason to believe that post-trial therapy can offer a
viable explanation for the absence of treatment effects at
One major problem for the PACE trial is that it was
originally designed around a highly optimistic view of
the therapeutic benefits of CBT and GET. Drawing on
results from previous, smaller trials, the PACE investiga-
tors estimated that CBT would be likely to yield an
improvement rate some six times greater than medical
care alone, and GET would yield a rate five times greater
. These expectations formed the basis of the power
calculations for the trial. But unfortunately, the improve-
ment rates for CBT and GET participants - when com-
pared with Control participants - fell markedly short of
those expectations. So it is perhaps not surprising that
an analysis of the binary improvement data alone was in-
sufficient to detect any statistically reliable effects. In this
context, it would have been perfectly acceptable first to
report the protocol-specified primary outcome analysis,
and then to explore the data using methods that are
more sensitive to smaller effects –for example, analysis
of the individual, continuous outcome measures. How-
ever, instead, the researchers chose to omit the former
analysis altogether, and report only the latter. They then
reported improvement rates based on an entirely new,
and much more generous, definition of improvement. In
sum, the analyses that were the least complimentary to
CBT and GET never appeared in the published reports;
the analyses that showed these interventions in a more
favourable light were the only ones to be published.
As we have already pointed out, the timing of the
change to the primary outcome –several months after
trial completion - was highly problematic. There was also
insufficient independent justification for making the
change. For reasons that are never made clear, investiga-
tors had suddenly taken the view that “…a composite
measure would be hard to interpret, and would not allow
us to answer properly our primary questions of efficacy
(i.e. comparing treatment effectiveness at reducing fatigue
and disability).”(, p. 25). Certainly, the separate ana-
lysis of the two continuous measures provides useful add-
itional information, but this does not justify abandoning
the originally planned outcome. Further, the protocol
already included measures of specific improvement rates
in self-rated fatigue and physical function, and it is not
Wilshire et al. BMC Psychology (2018) 6:6 Page 7 of 12
clear why these were abandoned in favour of the new
Turning now to the recovery rates, the late changes to
the definition of recovery made it much easier for a
patient to qualify as recovered. These changes were quite
substantial. For example, the minimum physical function
score required to qualify as recovered was reduced from
85 to 60, which is close to the mean score for patients
with Class II congestive heart failure (57/100 ), and
lower than the score required for trial entry (65/100).
Also, on the fatigue criterion, a patient could now count
as “recovered”despite reporting continuing fatigue on as
many as seven out of the 11 fatigue questionnaire items,
a level that substantially overlaps with that required for
trial entry. Again, these changes operated to favour the
study hypotheses. They enabled the researchers to make
the claim that CBT and GET were significantly more
likely to lead to recovery than conventional medical care
(the original recovery definition would have yielded a
null result), and to declare that at least “a fifth”of partic-
ipants recover with CBT and GET [4,22]. Neither claim
could have been made if the original definition of recov-
ery had been used.
Again, the timing of the change to the recovery defin-
ition –over a year after the trial was completed - is
highly problematic. Also, an adequate justification for
the change is yet to be provided. In their 2013 publica-
tion on recovery rates, the researchers argued that the
normal ranges for some key scores were wider than pre-
viously thought, which would justify classing more par-
ticipants as “recovered”on these measures . However,
we have recently shown that when the chronically ill and
the very old were excluded from the relevant reference
samples, and where correct statistics were applied to de-
termine appropriate cut-off values, the normal ranges
are, if anything, narrower than previously believed .
Consequently, this argument does not stand up to scru-
tiny (see  for further details).
Several other arguments have been presented in de-
fence of these changes [23,24]. One was that since there
is no agreed definition of recovery, the new modified
one is just as good as the original (the original definition
“simply makes different assumptions”, p. 289). This
argument fails to explain why the definition was changed
in the first place. If both definitions are indeed equally
good, then the one to be preferred is surely the one that
was specified in advance, before any of the results were
known. Another argument was that the recovery rates
obtained with the modified definition were numerically
similar to those found in some previous trials of CBT for
CFS . However, these other trials used entirely differ-
ent definitions of recovery, so are not relevant here. One
final argument was that the original definition of recov-
ery was simply “too stringent to capture clinically
meaningful recovery”. However, the only supporting
evidence for this statement comes from the disappoint-
ing recovery rates in the PACE trial itself; no independ-
ent justification is offered. Clearly, a strong concept like
recovery must be operationalised carefully. Physicians
and lay people understand this term to mean a return to
good health , and any definition must preserve this
core meaning. If anything, the original protocol-specified
definition was rather generous, and may have identified
some individuals that had not recovered in the plain
English sense of the word. For example, on the primary
physical function measure (the SF36), it was possible to
score in the bottom decile for working age individuals
with no long-term illness or disability, and still count as
recovered on that criterion . The definition also did
not require evidence of an ability to return to work or
other premorbid activities, even though these are very
important components of what recovery means to
patients. There was certainly no justification for further
loosening that definition. In sum, none of the trial inves-
tigators’arguments adequately justified the late changes
to the recovery definition. More detailed discussion of
these issues can be found elsewhere .
Turning now to long-term follow-up, the original pub-
lication of the long-term follow-up data reported no sig-
nificant differences amongst treatment groups at this
time point . However, the authors dismissed their
own finding, arguing that many participants received
additional post-trial therapy which might have operated
to obscure group differences. Instead, they based their
main conclusion on comparisons between time points.
For example, the first line of the Discussion reads: “The
main finding of this long-term follow-up study of the
PACE trial participants is that the beneficial effects of
the rehabilitative CBT and GET therapies on fatigue and
physical functioning observed at the final 1 year out-
come of the trial were maintained at long-term follow-
up 2·5 years from randomisation.”( p. 1072, Italics
added). This conclusion is repeated in the Abstract. The
decision to lead with this conclusion again operated to
show the findings in a more positive light than would have
been possible based on their own primary between-groups
analysis. The informal analyses we presented here provide
no support for the investigators’claim that post-trial ther-
apy contaminated the long-term outcome data. Of course,
our analyses did not include important potentially con-
founding variables that might differ amongst trial arms,
and such a comprehensive analysis might possibly produce
a different result. However, until there is positive evidence
to suggest that this is the case, the conclusion we must
draw is that PACE’s treatment effects are not sustained
over the long term, not even on self-report measures. CBT
and GET have no long-term benefits at all. Patients do just
as well with some good basic medical care.
Wilshire et al. BMC Psychology (2018) 6:6 Page 8 of 12
Overall evaluation of the trial
Some notable strengths of the PACE study included the
large sample size (determined a priori using power ana-
lysis ), the random allocation of patients to treatment
arms, the use of a well-formulated protocol to minimise
drop-outs, and the reporting of the full CONSORT trial
profile (including detailed information about missing
data). The incorporation of an active comparison group -
Adaptive Pacing Therapy - also provided a useful second-
ary control for factors such as overall therapy time and
patient-therapist alliance. It is worth pointing out that re-
sults for this group were not significantly different from
those for the Control group on any of the measures con-
sidered in this paper. Other strengths were that each ther-
apy group received a substantial dose of therapy, and
standardised manuals ensured comparability of treatments
across centres and therapists. Finally, a wide range of out-
comes was measured, including several objective mea-
sures, as well as various adverse events measures.
However, despite these strengths, the design, analysis
and reporting of the results introduced some significant
biases. We have already discussed some of the biases
that were introduced at the analysis and reporting stage.
Several key results that showed CBT and GET in less
than favourable light were omitted and replaced with
new ones that appeared more favourable to the treat-
ments. These changes were made at a late stage in the
trial, and we have argued here that none had sufficient
independent justification. In reality, the effects of CBT
and GET were very modest - and not statistically reliable
overall if we apply procedures very close to those speci-
fied in the original published protocol.
Another source of bias arose from the trial’s heavy reli-
ance on self-reports from participants who were aware of
their treatment allocation. Clearly, in a behavioural inter-
vention trial, full blinding is not possible. Nevertheless, it
is the researchers’responsibility to consider the possible
effects of lack of blinding on outcomes, and to ensure
such factors are insufficient to account for any apparent
benefits. A trial that is not blinded, self-reported outcomes
in particular can produce highly inflated estimates of
treatment-related benefits [27,28]. A recent meta-analysis
of clinical trials for a range of disorders found that when
patients were not blinded to their treatment allocation,
their self-reported improvement on the treatment of inter-
est was inflated by 0.56 standard deviations, on average,
when compared to a corresponding blinded phase of the
same trial . In contrast, observer-rated measures of
improvement were not significantly affected by blinding.
Given this discrepancy in the effects of blinding on sub-
jective and objective measures, it appears unlikely that
these effects reflect genuine health benefits. Amore plaus-
ible explanation is that they are expectation-related arte-
facts –for example, they reflect the operation of
attentional biases that favour the reporting of events con-
sistent with one’s expectations , or recall/confirmation
biases that enhance recollection for expectation-
consistent events .
The PACE investigators have argued that expectancy
effects alone cannot account for the positive self-reported
improvements, because at the start of treatment, patients’
expectations of improvement were not greater in the CBT
and GET groups than in the other groups [2,23]. How-
ever, they fail to point out that CBT and GET participants
were primed during treatment to expect improvement.
The manual given to CBT participants at the start of treat-
ment proclaimed CBT to be “a powerful and safe treat-
ment which has been shown to be effective in... CFS/ME”
(, p. 123). The GET participants’manual described
GET as “one of the most effective therapy strategies cur-
rently known”(, p. 28). Both interventions emphasised
that faithful adherence to the programme could lead to a
full recovery. Such messages —from an authoritative
source —are likely to have substantially raised patients’
expectations of improvement. Importantly, no such state-
ments were given to the other treatment groups. When we
add to this the fact that the CBT programme, and to a
lesser extent GET, was designed to reduce “symptom
focusing”, which may have further influenced self-report
behaviour in the absence of genuine improvement [27,34],
these findings start to look very worrying indeed.
A further cause for concern in the PACE trial was that
the two primary self-report measures appear to behave
in different ways depending upon the intervention. Our
analysis based of the protocol-specified outcomes indi-
cated that GET produces modest enhancements in
patients’perceived physical function, but has little effect
on symptom perception. Conversely, CBT improved
symptom perception –specifically, self-rated fatigue
scores –but had little effect on perceived physical func-
tion. If these interventions were operating to create a
genuine underlying change in illness status, we would
expect change on one measure to be accompanied by
change on the other.
Given the high risk of participant response bias in this
study, it was therefore crucial to demonstrate
accompanying improvement on more objective measures.
However, only one such measure showed a treatment ef-
fect. On the six-minute walking test, the originally-
reported available case analysis found that GET partici-
pants walked reliably farther than Control participants at
the primary, 52-week endpoint. However, after an entire
year, this group walked an average of just 67 m farther
than baseline, and around 30 m farther than Controls. To
put this in context, a sample of Class II chronic heart fail-
ure patients with similar baseline walking distances
increased their distance by an average of 141 m after only
three weeks of a gentle graded exercise programme .
Wilshire et al. BMC Psychology (2018) 6:6 Page 9 of 12
No other objective measures yielded significant
treatment effects. Most notably, treatment did not
affect aerobic fitness, measured using a step test. If
GET had genuinely improved participants’physical
function and levels of activity, these improvements
should have been clearly evident on fitness measures
taken a full year after trial commencement. Treatment
also did not affect time lost from work . There
was ample opportunity for improvement here: during
the six months preceding the trial, 83% of partici-
able (based on the number reporting lost work days).
This suggests they could have immediately increased
their hours if their health had permitted. Finally, the
percentage of participants receiving government bene-
fits or income protection actually increased over the
treatment period for all groups . It is concerning that
these negative findings were not even published until
years after the primary results had been reported, so these
inconsistencies are not immediately apparent to the
reader. For example, the crucial fitness results were not
published until four years after the primary outcomes.
The investigators dismissed most of these measures as un-
important or unreliable; they did not consider them valu-
able as a means of estimating the degree of bias inherent
in their self-report outcomes.
The absence of evidence for treatment-related
recovery is an additional, serious concern for the trial.
CBT and GET were not seen as adjunct treatments that
might relieve a little distress. Rather, they were seen as
capable of reversing the very behaviours and cognitions
responsible for CFS. The behavioural-deconditioning
model, on which the treatments were based, assumes
that there is no underlying disease process in CFS,
and that patients’concerns about exercise are merely
“fearful cognitions”that need addressing (, p.
47–8). Participants in some trial arms were even told
that “there is nothing to stop your body from gain-
ing strength and fitness”(, p. 31). If this model
of CFS were correct, and if the treatments were
operating as hypothesised, then some participants that
duly followed the programme should have returned to
the levels of health and physical function, that they
enjoyed prior to illness onset. Therefore, the rates of
recovery in the CBT and GET groups should have
been significantly and reliably higher than in the Con-
trol group, irrespective of the method used to define
recovery. This was not the case.
The failure of CBT and GET to “reverse”CFS is per-
haps not so surprising when we consider recent exercise
physiology studies. CFS patients have shown various
physical abnormalities when tested 24 h after exertion
max and/or anaerobic thresholds; for a
review, see ). These abnormalities are not seen in
sedentary, healthy adults or even in patients with cardio-
vascular disease, and therefore cannot be attributed to
deconditioning alone. Such findings call into question
the core assumption of the behavioural/deconditioning
model that there is no ongoing disease process. If there
is a rational basis for patients’concerns over exercise,
encouraging them to push through symptoms may be
harmful, and recasting patients’concerns as dysfunc-
tional may cause additional, psychological harm.
Turning now to safety issues, there were few group dif-
ferences in the incidence of adverse events, and the
researchers concluded that both CBT and GET were safe
for people with CFS. This finding –particularly that
relating to GET - contrasts markedly with findings from in-
formal surveys conducted by patient organisations [38,39].
In these surveys, between 33% and 79% of respondents re-
port worsened health as a result of having participated in
some form of graded exercise programme (weighted aver-
age across 11 different surveys: 54% ). Of course, in
such surveys, participant self-selection may operate to en-
hance the reporting rates for adverse outcomes. However,
this finding is so consistent, and the number of participants
surveyed is so large (upwards of 10,000 cases), that it can-
ancy between PACE’s findings and those of patient surveys
is the conservative approach used in PACE’sGET
programme. Patients were encouraged to increase activity
only if it provoked no more than mild symptoms . Un-
fortunately, compliance with the activity recommendations
was not directly assessed: actigraphy data were collected
only at trial commencement  and never reported. This
is a significant omission, since there is evidence that graded
exercise therapies are not always successful in actually in-
creasing CFS patients’activity levels . Even those
who comply with exercise goals may reduce other ac-
tivities to compensate . The lack of improvement
in fitness levels in PACE’s GET group does suggest
that participants may not have substantially increased
their activity levels, even over the course of an entire
year. Also, even though the majority of GET partici-
pants chose walking as their primary activity , this
group demonstrated an average increase in walking
speed of only 10% after an entire year (increases of
50% or more have been observed in other patient
populations ). Given these features, it is inappro-
priate to generalise the safety findings from PACE to
graded activity programmes more widely, especially as
they are currently implemented in clinical settings.
In conclusion, the various treatment effects reported
in the PACE trial were modest, almost entirely con-
fined to self-report measures, and did not endure be-
yond two years. If one were to ask, “Given the
Wilshire et al. BMC Psychology (2018) 6:6 Page 10 of 12
procedures used here, what pattern of results would
we expect if these therapies did not produce genuine
change?”the answer would be, “Modest, short-lived
changes in self-report behaviour unaccompanied by
objectively measurable changes”—apatternmuch
like the one obtained. Given the size and power of the
PACE trial, it seems unlikely that further research based on
these treatments will yield more favourable results. Indeed,
another large parallel trial that involved home-based ther-
apy, described as PACE’s“sister trial”(), also yielded null
outcomes at its primary endpoint [44,45]. The time has
come to look elsewhere for effective treatments. Current
major NIH research initiatives include a large intramural
study of post-infectious CFS, which aims to examine the
pathophysiology of this phenotype specifically , and a
systematic investigation of inflammatory markers (both per-
ipheral and CNS) in CFS, and how they are influenced by
exertion . Such initiatives have the potential to play a
key role in generating new treatment paradigms.
CBT: Cognitive behavioural therapy; CDC: US Centers for Disease Control;
CFQ: Chalder Fatigue Questionnaire; CFS: Chronic fatigue syndrome;
CI(s): Confidence interval(s); CNS: Central nervous system;
CONSORT: Consolidated Standards of Reporting Trials; FOI(A): United
Kingdom Freedom of Information (Act); GET: Graded exercise therapy;
ME: Myalgic encephalomyelitis; NIH: US National Institutes of Health; SF-
36: Short-form; VO2max: Maximal oxygen uptake
We would like to thank the UK ME Association for their contribution towards
the article processing fee for the pulication of this open access article. DT’s
position at UC Berkeley is part funded by a public crowdfunding campaign
in support of his work on chronic fatigue syndrome. KG receives part
funding from the UK ME Association.
Availability of data and materials
The datasets analysed during the current study are available in the PACE-
FOIR Google Sites repository, at https://sites.google.com/site/pacefoir/pace-
ipd_foia-qmul-2014-f73.xlsx. A readme file is available at https://sites.google.-
CW wrote the manuscript, and contributed to the statistical analyses, the
review of background literature and the development of key arguments. AM
contributed to statistical analyses, and BL advised on statistical procedures.
TK, AM, RC, and DT contributed to the review of background literature and
to the development of key arguments. TK, BC, AM, DT, KG and BL all
commented on previous versions of the manuscript. All authors read and
approved the final manuscript.
Ethics approval and consent to participate
Not applicable. The research reported in this article utilises data already
available in the public domain.
Consent for publication
All authors have read the competing interests statement, and declare no
competing interests. TK is a (volunteer) committee member of the Irish ME/
Springer Nature remains neutral with regard to jurisdictional claims in
published maps and institutional affiliations.
School of Psychology, Victoria University of Wellington, New Zealand, P.O.
Box 600, Wellington, New Zealand.
Irish ME/CFS Association, Dublin, Ireland.
School of Public Health, University of
California, Berkeley, California, USA.
School of Health Sciences, University of
Manchester, Manchester, UK.
Department of Biostatistics, Columbia
University, New York, USA.
Received: 29 May 2017 Accepted: 22 February 2018
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