---
title: "Comparison of adaptive pacing therapy, cognitive behaviour therapy, graded exercise therapy, and specialist medical care for chronic fatigue syndrome (PACE): a randomised trial"
authors: "White PD, Goldsmith KA, Johnson AL, Potts L, Walwyn R, DeCesare JC, Baber HL, Burgess M, Clark LV, Cox DL, Bavinton J, Angus BJ, Murphy G, Murphy M, O'Dowd H, Wilks D, McCrone P, Chalder T, Sharpe M, on behalf of the PACE trial management group"
journal: "The Lancet"
year: 2011
doi: "10.1016/S0140-6736(11)60096-2"
url: "https://europepmc.org/article/PMC/PMC3065633"
conditions: ["ME/CFS"]
studyType: "Randomised trial, four arms, n=641, 52 weeks, unblinded"
kind: paper
humanInput: none
reviewedOn: 2026-10-16
guideVersion: "0.8.1"
model: "claude-opus-5-5"
score: 4
verdict: "A large, well-run trial whose gains rest on questionnaires filled in by patients who knew their treatment, while fitness, work and benefits did not improve; it cannot show that talking therapy or graded exercise changed the illness rather than how it was reported."
confidence: "high"
importance: "high"
strengths:
  - "Large, properly randomised, very few dropouts"
  - "Pacing arm matched for therapist time"
  - "Manualised treatments with fidelity checks"
  - "Outcome changes disclosed in the paper"
weaknesses:
  - "Main outcomes self-rated by unblinded patients"
  - "Fitness, work and benefits did not improve"
  - "Main outcome changed after data collection ended"
  - "Safety claim overstated; severe patients excluded"
context:
  - note: "A 2018 reanalysis using data released under a Freedom of Information request approximated the protocol's original main outcome: 20% (talking therapy) and 21% (graded exercise) improved, against 10% with medical care alone. The trial authors disputed the reanalysis in 2019."
    source: "https://doi.org/10.1186/s40359-018-0218-3"
  - note: "In 2017 the journal that published the trial's cost-effectiveness paper issued an expression of concern about it, because the individual patient data were not released under the journal's data policy. The authors disagreed with it."
    source: "https://doi.org/10.1371/journal.pone.0177037"
  - note: "In October 2021 the guideline on ME/CFS from the UK National Institute for Health and Care Excellence (NG206) said not to offer graded exercise therapy, defined as fixed incremental increases in activity based on deconditioning and exercise avoidance theories."
    source: "https://www.nice.org.uk/guidance/ng206/chapter/Recommendations"
guideNotes:
  - "Unblinded trials where the therapy aims to change symptom interpretation make self-report bias worse than usual"
  - "Check whether 'normal range' or recovery thresholds overlap with entry criteria"
  - "Check whether a post-hoc responder threshold is met by a large share of the control arm"
design: randomised-trial
topics: ["treatment", "rehabilitation", "exercise-pem"]
---

## Study design

PACE (Pacing, graded Activity, and Cognitive behaviour therapy: a randomised Evaluation) was a four-arm, parallel-group, multicentre randomised trial. It recruited 641 patients from six specialist chronic fatigue syndrome clinics in the UK National Health Service between 2005 and 2008. All arms received specialist medical care (SMC). Three arms also received a therapy: adaptive pacing therapy (APT), cognitive behaviour therapy (CBT) or graded exercise therapy (GET). Therapy was up to 14 sessions over 23 weeks plus a booster at 36 weeks. The primary endpoint was 52 weeks after randomisation.

Much of the design is good. Allocation was done by an independent clinical trials unit, by minimisation with a random component, stratified by centre, depressive disorder and two alternative case definitions. Treatments were manualised. Sessions were audio-recorded and a sample was rated for fidelity. Loss to follow-up was low: 33 of 640 (5%), and only 10 had no outcome data at all. The statistician running the primary analysis was masked to allocation. The trial was registered (ISRCTN54285094) and its protocol was published in 2007.

APT is the most useful design feature. It was matched to CBT and GET for therapist contact (median 13 to 14 sessions in each therapy arm), and participants rated it as logical and promising before treatment at least as often as CBT. This means the trial is not just "therapy versus no therapy". It goes some way to controlling for attention and contact time. As discussed under **Bias**, it does not control for what each therapy tells patients about their symptoms, and that matters for self-rated outcomes.

There was no blinding of participants, therapists, doctors or research assessors. For a behavioural trial, blinding participants is not possible, and the authors say so. The consequence is that the outcome measures carry the whole burden of protecting against bias. Here they do not (see **Outcome measures**).

## Sample selection

**Case definition.** Participants met the Oxford criteria for chronic fatigue syndrome. These require fatigue as the main symptom, with significant disability, for at least six months, and no exclusionary medical or psychiatric diagnosis. They do not require post-exertional malaise (PEM), or any other symptom. The international criteria, by contrast, require four or more accompanying symptoms, and only 67% of PACE participants met them. Entry also required a score of 6 or more out of 11 on the Chalder fatigue questionnaire (bimodal scoring) and a score of 65 or less out of 100 on the short form-36 (SF-36) physical function subscale. The SF-36 threshold was raised from 60 to 65 eleven months into recruitment "to increase recruitment".

**PEM ascertainment.** PEM was not an inclusion criterion and was not measured with a validated instrument. The only PEM data are a yes/no item from the symptom list of the international (Reeves/Centers for Disease Control) criteria. At baseline, 82% to 87% per arm reported it. Patients were also classified by the international criteria (67%, which need four of eight accompanying symptoms, of which PEM is one option) and by the London criteria for myalgic encephalomyelitis (51%), which do require post-exertional fatigue. The trial applied the London criteria's exclusion of a primary depressive or anxiety disorder as an "absence of any such disorder". That is a stricter reading than the wording, and it ties the London subgroup to the absence of psychiatric comorbidity as much as to the presence of post-exertional symptoms.

**How many participants had ME/CFS?** This cannot be estimated well from the paper. The guide's f (the share of included cases who truly have myalgic encephalomyelitis/chronic fatigue syndrome, ME/CFS) is lowest for broad definitions, and a definition requiring no accompanying symptoms is broad. Against that, diagnosis was made by specialist clinic doctors after medical work-up, and a structured psychiatric interview (the Structured Clinical Interview for the Diagnostic and Statistical Manual of Mental Disorders IV) was used to exclude psychosis, bipolar disorder, substance misuse and eating disorders. Mood and anxiety disorders were not exclusionary: 47% had one, and 34% had a depressive disorder at randomisation. A plausible range for f is wide, perhaps 0.4 to 0.7, and the paper gives no way to narrow it. This matters in two directions. It dilutes any effect specific to ME/CFS. It also allows effects in people who do not have ME/CFS, such as those with depression or simple deconditioning, to show up as effects "in chronic fatigue syndrome".

**Subgroups.** The paper says the subgroups "yielded equivalent results" because treatment-by-criteria interaction tests were not significant. A non-significant interaction test in a trial not powered for it does not show equivalence. The subgroup results are reassuring that the pattern is not reversed in London-criteria patients. They do not show the same size of effect.

**Severity and representativeness.** Patients unable to attend hospital were excluded, so the trial says nothing about housebound or bedbound patients. Mean baseline SF-36 physical function was 37 to 39, which is moderate disability. Median illness duration was 32 months. Of 3158 patients screened, 641 were recruited. The commonest reason for exclusion at clinician screening was not meeting Oxford criteria (1011 patients), most of whom did not have chronic fatigue syndrome.

**Comorbidities.** There is no information on postural orthostatic tachycardia syndrome or orthostatic intolerance (POTS/OI) or mast cell activation syndrome (MCAS). There is no standardised severity scale beyond the SF-36.

## Outcome measures

**Primary outcomes.** Both were self-rated questionnaires: the Chalder fatigue questionnaire (Likert scoring, 0 to 33, lower is better) and the SF-36 physical function subscale (0 to 100, higher is better). On the guide's scale these sit at the most bias-prone end. They are completed by participants who know their allocation, and whose therapy may have changed how they interpret and report symptoms.

This is the central weakness of the trial, and it is sharper than in most unblinded trials. CBT in PACE was based on the "fear avoidance theory": its stated aim was to change "the behavioural and cognitive factors assumed to be responsible for perpetuation of the participant's symptoms and disability", and therapists guided participants "to address unhelpful cognitions, including fears about symptoms or activity". GET was based on "deconditioning and exercise intolerance theories" that include "an increased perception of effort". APT, by contrast, was based on the "envelope theory", which "regards chronic fatigue syndrome as an organic disease process that is not reversible by changes in behaviour", and taught participants to monitor and stay within their perceived energy limits. So the treatments differ not only in what patients did but in what patients were taught their symptoms meant. Questions about feeling weak, or about being limited in climbing stairs, can then get different answers because the interpretation changed, not the illness. The trial cannot separate these.

The Chalder fatigue questionnaire also asks about change relative to "usual", which is hard to interpret in a chronic illness. Neither scale has test-retest data reported in this population, and the paper gives no smallest detectable change.

**Change of scoring and of the primary outcome.** The 2007 protocol defined the primary outcome as the proportion of participants with a "positive outcome" on each measure: for fatigue, a 50% reduction or a bimodal score of 3 or less; for physical function, a score of 75 or more or a 50% increase. "Overall improvers" were those who improved on both. The published paper instead analysed mean differences on continuous scores, and changed Chalder scoring from bimodal (0 to 11) to Likert (0 to 33). The paper discloses both changes and says they were made "before outcome data were examined". The statistical analysis plan, published in 2013, says the plan was approved by the Trial Steering Committee in May 2010. Its own text gives the end of 52-week data collection as 31 January 2010. So the change was approved after all outcome data had been collected, in an unblinded trial, though not, on the authors' account, after the data were analysed.

Analysing continuous scores is, in itself, a defensible and usually more powerful choice. The problem is what happened to the protocol analysis. It is not reported in this paper. A reanalysis by Wilshire and colleagues (2018), using data released under a Freedom of Information request, approximated the protocol definition: 20% of CBT, 21% of GET and 10% of SMC participants improved overall (CBT versus SMC p=0.015; GET versus SMC p=0.010). The trial was powered on the assumption of 60% response to CBT, 50% to GET and 10% to SMC. On the trial's own original outcome, the observed effect was about a fifth to a quarter of the hypothesised one. Whether it was "significant" depends on the correction for multiple comparisons; the trial authors argue that Wilshire and colleagues applied an excessive Bonferroni correction. Both readings agree on the substance: a doubling of a small improver rate on self-report.

**Post-hoc "improvement" and "normal range".** The paper adds two post-hoc analyses. The first counts as "improved" anyone who gained 2 points on fatigue and 8 on physical function. By this definition 45% of the SMC-alone group improved, against 59% for CBT and 61% for GET. The threshold is low enough that nearly half the control arm passes it.

The second reports the share "within normal ranges" for both outcomes: 30% for CBT, 28% for GET, 15% for SMC. The "normal" physical function threshold was a score of 60 or more, defined as the mean minus 1 standard deviation (SD) of the UK working-age population (84 minus 24). Entry required a score of 65 or less. A participant could therefore enter the trial at 65, decline to 60, and be counted as within the normal range. The same overlap exists for fatigue: by my arithmetic, a participant scoring 2 on six items and 1 on five meets the entry threshold (bimodal score 6) and the "normal" threshold (Likert score 17, at or below 18) at once. The SF-36 physical function scale is also strongly skewed towards the ceiling in healthy people, so the mean minus 1 SD is not a valid lower bound of normal. Mean physical function at 52 weeks in the best arms was 58, below even this lowered threshold.

The paper is restrained about the normal-range result in its discussion ("No more than 30% of participants were within normal ranges"). But "normal range" is a phrase that will be read as "recovered", and the threshold does not support that reading. A later paper from the trial (White et al., 2013) used the same physical function threshold of 60 in its definition of "recovery".

**Clinically useful difference.** This was defined as 0.5 of the baseline SD: 2 points on fatigue and 8 on physical function. Entry criteria truncate the baseline distribution, so the baseline SD is narrow (3.6 to 4.0 on fatigue), and a fraction of it is a small change in absolute terms. One of the eight main comparisons fell below its own threshold: CBT versus SMC on physical function, 7.1 points (95% confidence interval 2.0 to 12.1). The paper describes the differences as having "almost always exceeded" the threshold, which is literally true.

**Objective and performance measures.** The protocol listed several more objective measures: the 6-minute walk test, a self-paced step test of fitness, employment and benefits data, and baseline actigraphy (a wrist-worn activity monitor).

- **6-minute walk test.** This is reported. GET participants walked 35 m further than SMC at 52 weeks (p=0.0002); CBT and APT did not differ from SMC. Only 69% to 76% per arm completed the test at 52 weeks, so this is not an intention-to-treat result. The guide rates the walk test as at high risk of performance bias: an unblinded participant encouraged to walk more will try harder. Mean distance in the GET arm rose from 312 m to 379 m.
- **Step test of fitness.** Not reported in this paper. Wilshire and colleagues report that summary data from a 2015 trial paper show no difference between arms. I did not check that 2015 paper directly.
- **Work and benefits.** Not reported in this paper. The trial's cost-effectiveness paper (McCrone et al., 2012) found "with the exception of a difference between CBT and APT, there were no significant differences in either lost work time or benefits between the treatments during follow up. In fact, benefits increased across all four treatments."
- **Actigraphy.** In the published protocol, actigraphy is collected at baseline only, as a predictor. It was never used as an outcome. So there is no measure of whether GET or CBT participants actually became more active over the day.

The pattern across these is important. The only objective measure that moved was the one most open to effort, and only for GET. The measures least open to effort did not move.

**Secondary self-report outcomes.** The work and social adjustment scale, sleep, anxiety, depression, symptom count, and the clinical global impression of change mostly favoured CBT and GET. These are all self-rated by unblinded participants, so they share the primary outcomes' weakness. They add consistency, not independence.

**PEM.** The paper says "The comparatively greater reduction in postexertional malaise with both CBT and GET compared with the other two treatments is notable." This rests on a single yes/no symptom item, self-rated by unblinded participants after therapy that targeted symptom interpretation. It cannot carry the weight the discussion puts on it, given that fear of PEM is the main concern patients raise about GET. Whether a participant was in a PEM episode at the time of each assessment was not recorded, so assessments may have been made in different states.

## Bias

**Expectation and reporting bias.** The authors' main defence is the expectation data. Before treatment, 72% of APT and 70% of GET participants were confident it would help, against 57% for CBT and 41% for SMC. CBT did as well as GET despite lower expectations, and APT did no better than SMC despite high ones (it was the worst arm on physical function). This is a real point and it should be weighed. But expectations were measured once, after allocation and before the first session. They say nothing about what participants believed after months of therapy designed to change beliefs about symptoms. Wilshire and colleagues quote the CBT participant manual describing CBT as "a powerful and safe treatment which has been shown to be effective" and the GET manual describing GET as "one of the most effective therapy strategies currently known". I have not checked the manuals myself. APT may also bias self-report in the opposite direction, because it trained participants to watch for and act on symptoms. So the CBT/GET versus APT contrast, which gives the largest differences on physical function, is the one most exposed to differential reporting.

**Investigator allegiance.** The three principal investigators (White, Chalder and Sharpe) developed and tested CBT and GET for this condition before PACE, The CBT and GET manuals were based on manuals from earlier trials, including CBT trials led by Sharpe (1996) and by Deale, Chalder and colleagues (1997), and a GET trial by Fulcher and White (1997). The introduction states the hypothesis that "CBT and GET would be more effective than would APT and SMC". APT was created for the trial; the manual was piloted and endorsed by the charities Westcare and Action for ME. APT therapists were the most experienced, and APT fidelity and alliance were rated as high as the other therapies, which partly answers the concern that APT was set up to fail. Allegiance is still a recognised source of bias in psychotherapy trials, and here it ran in the direction of the result.

**Assessor and therapy-rater masking.** Research assessors were not masked, and recorded the primary outcomes themselves (for example dictated by telephone) on 74 of 1920 occasions. The independent raters of therapy sessions were unmasked in 25 of 62 sessions (40%).

**Funding and interests.** The trial was publicly funded: Medical Research Council, Department of Health for England, Scottish Chief Scientist Office and the Department for Work and Pensions. Declared interests include consultancy work for insurance companies (White for Swiss Re, Chalder and Sharpe for insurance companies) and for the Departments of Health and Work and Pensions, and book royalties. These were declared. They do not show the analysis is wrong. They are relevant because the trial's conclusions bear on disability benefits and insurance claims.

**Co-interventions.** More SMC-alone participants received a non-allocated treatment (14% against 3% to 5%), and SMC participants had more medical sessions. The SMC arm had a shorter median illness duration (25 against 33 to 36 months). None of these obviously favours CBT or GET.

## Statistical and methodological issues

- The main analysis is sound in itself: mixed models with baseline adjustment, allowance for clustering by practitioner, Kenward-Roger standard errors, and Bonferroni-corrected p values for five comparisons per outcome. The main CBT and GET effects survive correction.
- Missing data were few. The analysis excluded only the 10 participants with no outcome data. A per-protocol analysis (556 of 640) gave very similar, slightly larger effects.
- The effect sizes are modest. At 52 weeks, fatigue was 20.3 (CBT) and 20.6 (GET) against 23.8 (SMC), on a 0 to 33 scale, from baselines near 28. Physical function was 58.2 (CBT) and 57.7 (GET) against 50.8 (SMC). In absolute terms all arms remained substantially impaired.
- The protocol set a significance level of 0.01 for secondary outcomes "unless profiles of response can be specified in advance". Several secondary results in the paper fall between 0.01 and 0.05 (for example CBT versus SMC on symptom count, p=0.0329, and on sleep, p=0.0216). The paper treats these at 0.05.
- The secondary outcomes reported were "a subset of those specified in the protocol, selected in the statistical analysis plan as most relevant to this report". The protocol's objective outcomes other than the walk test were left to later papers.
- The noise questions from the guide cannot be answered: the paper reports no test-retest reliability, no smallest detectable change for either scale in this population, and the post-hoc responder thresholds (2 and 8 points) are not shown to exceed measurement error.

## Safety

The abstract says CBT and GET "can safely be added", Panel 2 says "all four treatments tested are safe", and the discussion says "patients need not be concerned about safety".

What the data show: serious adverse reactions were rare and similar across arms (1% to 2%). Serious deterioration, a composite, was similar (6% to 9%). Serious adverse events were more frequent with GET than SMC (13 against 7 participants; 10.6 against 4.4 per 100 person-years; p=0.0433), which the authors set aside because the scrutinisers did not judge them related to treatment. The scrutinisers were masked when deciding whether an event was serious, but were unmasked when deciding whether it was related to treatment.

This is reasonable evidence that the PACE versions of CBT and GET, delivered by trained therapists to ambulatory patients under supervision, did not cause frequent severe harm in the first year. It is weaker evidence than the wording suggests, for four reasons.

1. Two of the four components of serious deterioration are self-ratings (SF-36 decline, global impression "much worse"), open to the same reporting effects as the efficacy outcomes.
2. There was no objective activity measure, so it is unknown how far GET participants actually increased their activity. GET in PACE also set heart rate targets "when necessary to avoid overexertion".
3. Housebound and more severely ill patients were excluded, and they are the ones for whom harm is most often reported.
4. With about 160 per arm, the trial can rule out common severe harm but not uncommon harm.

"Safe in PACE, for these patients, as delivered here" is supported. "Patients need not be concerned about safety" is not.

## Biological plausibility

CBT and GET in PACE were explicitly based on models in which the illness is perpetuated by reversible deconditioning, fear avoidance and unhelpful beliefs. The trial offers a test of those models, and the test mostly fails where it is most direct. If GET reversed deconditioning, a fitness measure should move; by the account of Wilshire and colleagues, the step test did not. If the treatments restored function, work and benefit receipt should change; they did not. If the effects were real but specific to self-report, they would be expected to fade once therapy ended. At long-term follow-up (median 31 months) the arms no longer differed, though the authors attribute this to post-trial treatment, received by 63% of SMC and 50% of APT respondents against 31% to 32% of CBT and GET respondents.

The guide's PEM questions are not addressed: neither model explains the delayed onset, multimodal triggers or duration of PEM. The trial was not designed to test those, but its conclusions are applied to a population in which PEM is the defining feature.

The paper notes that "The effectiveness of behavioural treatments does not imply that the condition is psychological in nature." That is correct, and fair to quote.

## Interpretation and spin

| Claim in the paper | What the data show |
|---|---|
| "CBT and GET can safely be added to SMC to moderately improve outcomes for chronic fatigue syndrome" | Modest improvement on self-rated fatigue and function in an unblinded trial. No improvement in work, benefits or (per later reports) fitness. A 35 m gain in walk distance for GET only, with 24% to 31% missing. |
| "APT is not an effective addition" | Fair for this manualised APT on these outcomes. Self-rated outcomes may be biased against a therapy that trains symptom monitoring. |
| Subgroups by other criteria "yielded equivalent results" | Interaction tests were non-significant, in a trial not powered for them. Absence of evidence of a difference, not evidence of equivalence. |
| "The comparatively greater reduction in postexertional malaise … is notable" | A single yes/no self-rated item. |
| "all four treatments tested are safe"; "patients need not be concerned about safety" | No large excess of severe harm in ambulatory patients over one year. Serious adverse events were higher with GET. Deterioration measures partly self-rated. Severe patients excluded. |
| 28% to 30% "within normal ranges" | The physical function threshold (60) is below the entry threshold (65). |
| Primary outcomes changed "before outcome data were examined" | Approved May 2010, after 52-week data collection ended in January 2010. The protocol-specified analysis is not reported. |

The abstract's "Interpretation" line and the final recommendation that patients "should be offered individual CBT or GET" are stronger than the evidence. The limitations paragraph does state the key problem: "Primary outcomes were subjective and rated by participants. While this avoided investigator bias, it could be subject to other biases." It then answers this only with the expectation data, which do not fully answer it.

## What the study actually demonstrates, and what it does not

It demonstrates:

- In ambulatory UK secondary-care patients meeting Oxford criteria, adding PACE-style CBT or GET to specialist medical care produced modestly better self-rated fatigue and physical function at one year than SMC alone or APT.
- These differences are not explained by contact time alone.
- PACE-style GET produced a small gain in 6-minute walk distance.
- Within this population and this year of follow-up, no large excess of serious harm from the PACE versions of CBT or GET was detected.
- The manualised APT used here did not improve self-rated outcomes over SMC.

It does not demonstrate:

- That CBT or GET change the course of the illness, as opposed to how it is reported. The objective outcomes least open to effort did not move.
- That the effects last; between-arm differences were gone at long-term follow-up.
- That the results apply to ME/CFS defined with PEM required, or to housebound or severely ill patients.
- That GET is safe for patients in general, or in less supervised settings.
- That "pacing" in general is ineffective. Only one manualised version was tested, on outcomes that may penalise it.
- Recovery or return to normal function.

## Critical missing elements

- The protocol-specified primary analysis (proportion of improvers on the original definitions).
- Objective activity measurement at follow-up.
- The step test and employment outcomes, reported alongside the primary results.
- Any measure of whether participants' symptom reporting style changed, as distinct from symptoms.
- A validated PEM measure, and PEM required for at least one analysed subgroup.
- POTS/OI and MCAS status.
- Test-retest and smallest-detectable-change data for the primary outcomes in this population.

## Recommendations

**For readers and clinicians.** Read PACE as evidence that these therapies change self-rated fatigue and function by a modest amount, in mildly to moderately affected, ambulatory patients defined without requiring PEM. Do not read it as evidence of recovery, of objective functional gain, or of safety in severe ME/CFS.

**For guideline developers.** The objective and long-term results should be weighed alongside the primary outcomes, not after them. In 2021 the UK National Institute for Health and Care Excellence (NICE) guideline NG206 told clinicians not to offer graded exercise therapy, defining it in terms very close to PACE's GET.

**For researchers.** Unblinded behavioural trials in ME/CFS need primary outcomes that are hard to bias: continuous actigraphy, work hours, and more sophisticated exercise physiology. They should require PEM at entry, measure it with a validated instrument, and report the protocol-specified analysis first.

## Final assessment

The question for the grade is how far the evidence carries the paper's main claim: that CBT and GET "moderately improve outcomes" for chronic fatigue syndrome and can be added "safely".

What prevents a higher score:

- The primary outcomes are self-rated by unblinded participants. Two of the treatments were explicitly designed to change how patients interpret their symptoms. This is the single most important flaw, and it cannot be designed away after the fact. It means the trial cannot separate a change in illness from a change in reporting.
- The objective outcomes least open to effort (fitness, work, benefits, as reported later) showed no benefit. The one that moved (walk distance, GET only) is open to effort and was missing for about a quarter of participants.
- The primary outcome was changed after data collection ended. The protocol analysis was not reported, and when others approximated it, the effect was much smaller than the trial was designed to detect.
- The post-hoc "normal range" threshold for physical function lies below the entry threshold.
- The safety conclusion is worded beyond what the data and the population allow.
- Broad Oxford case definition, PEM not required or properly measured, severe patients excluded.
- The between-arm differences did not persist at long-term follow-up.

What prevents a lower score:

- The trial is large, properly randomised with concealed allocation, and had very little missing primary data.
- APT is a genuine active comparator for contact time and early credibility, and CBT did as well as GET despite lower expectations. That makes "pure placebo from attention" an incomplete explanation.
- Treatments were manualised and fidelity was checked.
- The changes to the primary outcome and scoring are disclosed in the paper, the post-hoc analyses are labelled post hoc, and the limitations paragraph names the subjective-outcome problem.
- Safety was monitored systematically, with masked scrutiny of adverse events, and the data rule out frequent severe harm from the trial's versions of CBT and GET in ambulatory patients.
- The GET walk-test gain is small but in the predicted direction, and is not nothing.

Taken together: the trial is well run, but its design cannot separate the claimed effect from reporting bias, and its own objective measures point towards bias rather than away from it. The framing then claims more than even the self-reported results support. This puts it in the band where the design cannot separate the claimed effect from bias. It sits towards the upper part of that band because of its size, its active comparator and its disclosure, not because the main claim holds.

Confidence is high. The full paper, the web appendix, the published protocol and the statistical analysis plan were all available. Two points rest on secondary sources I did not check directly: the step test result (from Wilshire and colleagues' reading of a 2015 trial paper) and the quotes from the participant manuals. Neither changes the grade.

## Executive summary

PACE was a large UK trial of 641 people with chronic fatigue syndrome. Everyone had specialist medical care. Some also had pacing, cognitive behaviour therapy (talking therapy aimed at changing beliefs about symptoms and activity) or graded exercise therapy (a step-by-step increase in activity). It was well run in many ways: properly randomised, with few dropouts, and with a pacing arm that matched the therapy time.

Its main weakness is how it measured success. The main outcomes were questionnaires that patients filled in about their own fatigue and physical function. Patients knew which treatment they had. Two of the treatments were designed to change how patients think about their symptoms. So a better questionnaire score may reflect a change in how symptoms were reported, not in the illness. The measures that are hardest to influence this way did not improve: fitness, days lost from work, and receipt of benefits. Walking distance improved slightly with graded exercise, but a quarter of participants were not tested, and effort affects that test. The differences between groups were gone at long-term follow-up.

The main outcome was changed after data collection ended. The original analysis was not reported. When others approximated it, the effect was much smaller than the trial was designed to detect. One "normal range" threshold was set below the level that qualified people to enter the trial. The safety claim, that "patients need not be concerned", goes further than the data. Severely ill and housebound patients were excluded, and the definition used did not require post-exertional malaise, the worsening of symptoms after effort that defines ME/CFS.

Grade: 4 / 10.