Types of studies

We included randomised controlled trials, as well as cluster‐randomised trialsand cross‐over trials.

Types of participants

We included trials of male and female participants over the age of 18, irrespective ofcultures and settings. Investigators currrently have used several sets of criteria todiagnose CFS (Carruthers 2011;Fukuda 1994;NICE2007;Reeves 2003;Sharpe 1991); therefore we decided to includetrials in which participants fulfilled the following diagnostic criteria for CFS orME.

• Fatigue, or a symptom synonymous with fatigue, was a prominent symptom.

• Fatigue was medically unexplained (i.e. other diagnoses known to cause fatiguesuch as anorexia nervosa or sleep apnoea could be excluded).

• Fatigue was sufficiently severe to significantly disable or distress theparticipant.

• Fatigue persisted for at least six months.

We included trials that included participants with disorders other than CFS providedthat > 90% of participants had been given a primary diagnosis of CFS based on thecriteria discussed above. We included in the analysis of this review trials in whichless than 90% of participants had a primary diagnosis of CFS only if data on CFS werereported separately.

Types of interventions

Types of outcome measures

Electronic searches

The Cochrane Collaboration's Depression, Anxiety and Neurosis (CCDAN) ReviewGroup's Trials Search Coordinator (TSC) searched their Group's SpecializedRegister (CCDANCTR‐Studies and CCDANCTR‐References) (all years to 9 May2014). This register is created from routine generic searches of MEDLINE (1950‐), EMBASE (1974‐ ) and PsycINFO (1967‐ ). Details of CCDAN's generic search strategies, used to inform he CCDANCTR can be foundon the Group‘s web site.

The CCDANCTR‐Studies Register was searched using the followingterms: Diagnosis = ("Chronic Fatigue Syndrome" or fatigue) andFree Text = (exercise or sport* or relaxation or "multi convergent" or"tai chi")

The CCDANCTR‐References Register was searched using a more sensitive list offree‐text search terms to identify additional untagged/uncoded references, e.g.fatigue*, myalgic encephalomyelitis*, exercise, physical active* and taiji.Full search strategy listed in Appendix 1.

A complementary search of the following bibliographic databases and international trialregisters were also conducted to 9 May 2014 (see Appendix 2):

• SPORTSDiscus (1985 ‐ );

• The Cochrane Central Register of Controlled Trials (CENTRAL, all years ‐);and

• WHO International Clinical Trials Portal.

Searching other resources

We contacted the authors of included studies and screened reference lists to identifyadditional published or unpublished data. We conducted citation searches using theInstitute for Scientific Information (ISI) Science Citation Index on the Web ofScience.

Selection of studies

Two of three review authors (LL, JO‐J, KGB) inspected identified studies, usingeligibility criteria to select relevant studies. In cases of disagreement, theyconsulted a third review author (JRP).

Data extraction and management

Melissa Edmonds and Jonatahan R Price independently extracted data from includedstudies for the 2004 version of this review, and LL and JO‐J did so for thisreview update, using a standardised extraction sheet. They extracted mean scores atendpoint, the standard deviation (SD) or standard error (SE) of these values and thenumber of participants included in these analyses. When only the SE was reported, reviewauthors converted it to the SD. For dichotomous outcomes, such as drop‐outs, weextracted the number of events. We sought clarification from trial authors whennecessary from investigators involved in the following trials:Fulcher 1997,Moss‐Morris 2005,Wallman2004,Wearden 2009,Wearden 2010 andWhite 2011. We resolved disagreement between review authors by discussion.

Assessment of risk of bias in included studies

Working independently, LL and JO‐J, KGB or Jane Dennis (JD) assessed risk ofbias using The Cochrane Collaboration risk of bias tool which was published in the mostrecent version of theCochrane Handbook for Systematic Reviews of Interventions(Higgins 2011). This tool encouragesconsideration of how the sequence was generated, how allocation was concealed, theintegrity of blinding at outcome, the completeness of outcome data, selective reportingand other potential sources of bias. We classified all items in the risk of biasassessment as low risk, high risk or unclear risk by the extent to which bias wasprevented.

Measures of treatment effect

Unit of analysis issues

Dealing with missing data

When possible, we calculated missing standard deviations from reported standard errors,P values or confidence limits using the methods described in Chapter 7 (Sections 7.7.3.2and 7.7.3.3) of theCochrane Handbook for Systematic Reviews of Interventions(Higgins 2011). We approached trialinvestigators to obtain other types of missing data.

Assessment of heterogeneity

For this update, we assessed heterogeneity in keeping with the recommendations of theCochrane Handbook for Systematic Reviews of Interventions (I² valuesof 0 to 40%: might not be important; 30% to 60%: may represent moderate heterogeneity;50% to 90%: may represent substantial heterogeneity; 75% to 100%: show considerableheterogeneity;Higgins 2011). In addition tothe I² value (Higgins 2003),we present the P value of the Chi² test, and we considered the direction andmagnitude of treatment effects when making judgements about statistical heterogeneity.We deemed that no analyses were inappropriate as a result of the presence of statisticalheterogeneity, as the measures and statistics used have low power and are unstable whenbased on few and small studies. A P value < 0.1 from the Chi² test wasused as an indicator of statistically significant heterogeneity because of the low powerof provided measures.

Assessment of reporting biases

We planned at the protocol stage to construct funnel plots when sufficient numbers oftrials allowed a meaningful presentation, to establish whether other potential biasescould be present. Asymmetry of these plots may indicate publication bias, although italso may represent a true relationship between trial size and effect size. We identifiedan insufficient number of studies to use this approach in the present version of thereview (Egger 1997). We considered clinicaldiversity of the studies as a possible explanation for some of the heterogeneityapparent between studies.

Data synthesis

As the result of expected clinical heterogeneity (slightly different interventions,populations and comparators) among studies, we chose the random‐effects model asthe default method of analysis because the alternative fixed‐effect model assumesthat the true treatment effect in each trial is the same, and that observed differencesare due to chance.

We performed analyses using Review Manager 5.0.

Subgroup analysis and investigation of heterogeneity

We planned no subgroup analyses a priori. To explore possible differences betweenstudies that used different strategies (e.g. exercise therapy), control conditions anddiagnostic criteria, we performed post hoc subgroup analyses. We describe results ofthese subgroup analyses in the text of the review.

Sensitivity analysis

We planned no sensitivity analyses a priori. To explore the possible impact of ourpooling strategy (e.g. the impact of using SMD vs MD), we performed post hoc sensitivityanalyses. In addition, we performed sensitivity analyses when studies with outlyingresults where excluded. We describe results of these sensitivity analyses in the text ofthe review.

Results of the search

Our searches identified 908 unique records. Of these, we retrieved 50 records and readthe full text. Along with the five included studies from the 2004 version of this review(Fulcher 1997;Moss‐Morris 2005;Powell 2001;Wallman 2004;Wearden 1998), we haveincluded three additional studies in this update (Jason 2007;Wearden 2010;White 2011; seeFigure 1).

Included studies

A total of eight studies (Fulcher 1997;Jason 2007;Moss‐Morris 2005;Powell 2001;Wallman 2004;Wearden 1998;Wearden 2010;White 2011) met our inclusion criteria for thisreview (23 reports in all). All included studies were written in English and werepublished in peer‐reviewed journals.

Excluded studies

Two studies were excluded in 2004, as the diagnoses used were Gulf War veterans'illness (Guarino 2001) and subclinical chronicfatigue (Ridsdale 2004). The study awaitingassessment from 2004 was also excluded (Stevens1999), as exercise therapy was a minor part of a combination treatment.

The current version excluded 14 studies (Evering2008;Gordon 2010;Guarino 2001;Nunez 2011;Ridsdale 2004;Ridsdale 2012;Russel 2001;Stevens 1999;Taylor 2004;Taylor 2006;Thomas 2008;Tummers 2012;Viner 2004;Wright 2005). In additionto the two studies excluded from the 2004 version because of the population included(Guarino 2001;Ridsdale 2004), another with the diagnosis ofchronic fatigue was excluded (Ridsdale 2012),as were two in which participants were younger than 18 years (Viner 2004;Wright 2005). Along with the one study excluded in 2004 (Stevens 1999), another five studies (Evering 2008;Nunez 2011;Russel 2001;Taylor 2004;Tummers 2012) were excluded in this review update because exercise therapy wasa minor part of the intervention. One study was excluded because investigators comparedtwo exercise interventions (Gordon 2010). Twostudies were excluded because they were not RCTs (Taylor 2006;Thomas 2008).

Allocation

All but one of the studies had adequate sequence generation (Wallman 2004). We judged five reported methods ofallocation concealment as 'adequate' and found that methods described by theremaining three were unclear (Jason 2007;Powell 2001;Wallman 2004).

Blinding

As the intervention did not allow for blinding of participants or personnel deliveringthe exercise‐based interventions, and as all measures were performed byself‐report, blinding was impossible. This inevitably puts the review at somerisk of bias, and all of the included studies were rated as having high risk ofbias.

Incomplete outcome data

Risk of bias due to incomplete outcomes was low in five of the eight included studies,reflecting the fact that loss to follow‐up was low, and that participants whowere lost to follow‐up were evenly distributed between intervention and controlgroups (Fulcher 1997;Moss‐Morris 2005;Powell 2001;Wallman 2004;White 2011). One trialwas associated with unclear risk of attrition bias (Wearden 2010). The drop‐out rate in the intervention groups in thistrial was relatively high, but most of the participants who dropped out from treatmentwere still available for follow‐up assessments and were analysed within thegroups to which they were randomly assigned (Wearden2010). Two trials were associated with high risk of attrition bias (Jason 2007;Wearden 1998).Wearden 1998 reportedlarge drop‐out rates in all intervention groups as compared with control groups,and many participants were lost to follow‐up. InJason 2007, the conservatively defineddrop‐out rate (i.e. "attending four or fewer sessions or stopping therapyprior to satisfactory completion of therapy") on average was 25%. Study authorsused the best linear unbiased predictor to avoid taking missing data into account, butas loss to follow‐up for various intervention groups was not reported, weassessed the risk of attrition bias as high for this trial.

Selective reporting

Two studies (Wearden 2010;White 2011) referenced published protocols, andwhen we checked these against the published results, we found that reporting wasadequate. In one study (Wearden 1998), trialinvestigators reported numerical data for only one subscale (health perception) of theMedical Outcomes Survey (MOS) scale (Ware1992), for which data favour the intervention group; no numerical data were givenfor the five other subscales, nor for another scale (anxiety), as data were"similar in trial completers." It was not possible to check the other studiesfor selective reporting bias; therefore their risk of bias is considered unclear.

Other potential sources of bias

Seven of the eight studies seem to be free of other sources of bias, and one showed abaseline difference across groups for several variables (Jason 2007). These were not discussed when resultswere presented in the paper. In addition this study had 25 outcome measures; because ofthis large number, one significant measure would be expected to occur by chance (Jason 2007).Wallman 2004 showed differences between groups for anxiety and mental fatigueat baseline, and this might have influenced the results.

Exercise therapy versus control

Exercise therapy versus other treatments

Exercise therapy adjunctive to other treatment versus the other treatmentalone

Encouraging evidence suggests that exercise therapy can contribute to alleviation ofsome symptoms of CFS, especially fatigue. Exercise therapy seems to perform betterthan no intervention or pacing and seems to lead to results similar to those seen withcognitive behavioural therapy. Reported results were obtained from patients who wereable to participate (not from those too disabled to attend clinics); these resultswere inconclusive as to type of exercise therapy and showed heterogeneity. Few seriousadverse reactions were reported. We think the evidence suggests that exercise therapymight be an effective and safe intervention for patients able to attend clinics asoutpatients.

Further randomised controlled studies are needed to clarify the most effective type,intensity and duration of exercise therapy. These studies should report contextualcharacteristics of the exercise therapy provided, such as deliverer of theintervention, schedule, explanation and materials, supervision and monitoring. It isimportant that these trials measure health service use alongside the primary outcomesof fatigue and adverse effects, as well as alongside relevant secondary outcomes.Researchers should take care to describe which set of diagnostic criteria they haveused and how they operationalised the diagnostic process.

Summary

The two reviews about chronic fatigue syndrome (CFS) (on exercise and CBT) areimportant documents in a controversial field. However, they seem to be listed on thewebsite as mental health topics, alongside depression, etc. CFS is not a form of mentalillness, although of course individual cases may have a psychological component that canbe addressed during treatment. May I suggest that you place them elsewhere, as it ismisleading and confusing to include them under the mental health umbrella?

Reply

Many thanks for your comment on the two Cochrane CFS reviews. Apologies for the delayin responding, I have been on annual leave. We appreciate your observations about theplacement of these reviews inThe Cochrane Library. Feedback on reviews isnormally dealt with by the relevant review author, but in this case I am responding, asyour query relates more to an organisational issue. These reviews are listed as topicsunder a mental health heading because, as a result of the psychological component towhich you refer, both reviews are supported by a mental health Cochrane group. Similararrangements are in place for reviews of treatments for other disorders involving avariety of component problems and that as a result do not easily fit within the scope ofone Cochrane group. These reviews however can be accessed in a number of different ways,for example, by searching for the specific topic (CFS and associated terminology,exercise and associated terminology, CBT and associated terminology); by searching forthe study authors; by looking under subject headings, etc. The subject headings are notreally intended as a comment on/guide to the aetiology of an illness, but they sometimesreflect the services involved in management of the condition. I have copied thisresponse to the review authors in case they wish to comment further. Many thanks foryour feedback.

Contributors

Cathy Stillman‐Lowe (occupation freelance editor/sciencewriter) cathy.stillman‐lowe@care4free.net Submitteragrees with default conflict of interest statement: I certify that I have noaffiliations with or involvement in any organisation or entity with a financial interestin the subject matter of my feedback.

Summary

Unfortunately, this review ignores the large body of patient testimony suggesting thatmany persons with severe myalgic encephalomyelitis have been harmed by graded exercisetherapy.

Since it was prepared, the International Consensus Primer and Guidelines for MedicalPractitioners have been published.

Current thinking is to stay within your energy envelope. People with ME tend tooverdo not underdo what they are capable of....

Care must be taken to NOT encourage them to do too much.

Further many definitions are used for CFS, and this muddies the waters.

I agree with the conflict of interest statement below:

I certify that I have no affiliations with or involvement in any organisation or entitywith a financial interest in the subject matter of my feedback.

Reply

Thank you for your comments on this Cochrane Review.

In conducting this review, our aim was to gather and synthesise a specific type ofevidence—that reported by randomised controlled trials. We fully accept thatpatient testimony, particularly that gathered and synthesised by high‐qualityqualitative research, is invaluable in any clinical area, particularly in an area aschallenging for patients and healthcare professionals as CFS‐ME. However, thisproject was not designed to incorporate such evidence.

We do consider the possibility of harm arising from graded exercise therapy byconsidering reported adverse events. Clearly this is an important issue to considerwith any therapeutic intervention. Moreover, in the usual course of any illness,the condition of some patients improves (with or without treatment) and the condition ofothers worsens (with or without treatment). It is only through the use of randomisedcontrolled trials that the effects (whether beneficial or adverse) of putativetreatments can be disentangled reliably from the natural history of illness.

You raise the important point that (some) 'people with ME tend to overdo notunderdo what they are capable of.' The critical point is the extent to whichpatients should be 'encouraged to do more' and the way in which they should beencouraged to do so. These are important research questions. As you know, new randomisedevidence is available from the PACE trial, published in 2011 inLancet. Whilstthis is a controversial trial, it is an important randomised comparison of gradedexercise therapy and 'adaptive pacing.' We look forward to further randomisedevidence in due course.

We also look forward to continuing to work in this clinical area, in the hope that wecan advance our understanding of the impact of this treatment approach.

Contributors

Submitter: Adrienne.

Response prepared by Jonathan Price.

Summary

I would first like to thank those involved for their work in preparing this document.Even for those of us who have read the individual Chronic Fatigue Syndrome (CFS) papersit is useful to have the results collated, as well as details regarding theinterventions. Also it is interesting to see the results of sensitivity analyses,subgroup analyses, standardised mean differences, etc.

I would like to make a few comments. I’m splitting them into twosubmissions as the piece had become very long. I’ve added some looseheadings to hopefully make it more readable.

Objective measures

The review assessed the studies as having a high risk of bias regarding blinding, sinceneither participants nor assessors were blinded. Evidence suggests that subjectiveoutcomes are more prone to bias than objective outcomes when there is no blinding (1).It is thus unfortunate that the review concentrated almost exclusively on subjectivemeasures, failing to include results from nearly all the objective outcome measures thathave been published with trials. (The exception was health resource use for which youpresented follow‐up data from one trial).

I hope objective outcome data can be included in a future revision or edition of thisreview.

Examples of objective outcomes include: exercise testing (work capacity by oxygenconsumption); fitness test/step test; the six minute walking test; employment status;and disability payments.

Adding in these results would allow a more rigorous assessment of the effectiveness andrelevance of the therapies, their causal mechanisms, therapeutic compliance, andsafety.

On exercise testing, for example, in the PACE Trial (the largest trial in the review)there was no improvement in fitness levels as measured by a step test (2). The fitnessdata contrasts sharply with the many positive results from subjective self‐reportmeasures in the trial, so one is left wondering how much the subjective measures reflectreality.

On another exercise test used in the PACE Trial, the 6 minute walk test, there was asmall (mean) increase from 312 metres at baseline to 379 metres at 12 months: this was35.3 metres more than the "passive" control group when adjustments were made.However, the final result of 379 metres remains very poor compared to the more than 600metres one would expect from healthy people of a similar age and gender make‐up(3,4). By comparison, a group with Class III heart failure walked an average of 402metres (5). A score of less than 400 metres has been suggested as the level at whichsomebody should be put on a lung transplant list (6). Such information from objectivemeasures helps to add important context to the subjective measures and restraint to theconclusions that can be drawn from them.

Objective data is also needed to check compliance with a therapy. If patientsdiligently exercised for 12 months one would expect much better results on fitness andexercise testing than the aforementioned results in the PACE Trial. This is importantwhen considering adverse events and safety: such trials may not give us good informationon the safety of complying with such interventions if patients haven't actuallycomplied.

Employment and receipt of disability payments are practical objective measures ofgeneral functional capacity so data on them would help establish whether patients canactually do more overall or whether they may just be doing, for example, a little moreexercise but have substituted that for doing less in other areas (7,8). Also, CFSpatients are sometimes pressured by insurance companies into doing graded exercisetherapy (GET) programs so it would be useful to have data collated on employmentoutcomes to see whether pressure can in any way be justified (9,10). In the PACE Trial,there was no significant improvement in employment measures and receipt of disabilitypayments in the GET group (11). Outside the realm of clinical trials, the quantitativeand qualitative data in a major (UK) ME Association survey also found that GETdidn't lead to higher levels of employment and lower levels of receipt ofdisability payments on average (9). Also, extensive external audits were performed ofBelgian CFS rehabilitation clinics that treated using cognitive behavioural therapy(CBT) and GET. The main reports are in French and Dutch (12,13), with an English summaryavailable (14) that says, "Employment status decreased at the end of the therapy,from an average of 18.3% of a 38h working week, to 14.9% [...] The percentage ofpatients living from a sickness allowance increased slightly from 54 to 57%." Thiscontrasts with the average improvements reported in the audit for some symptoms likefatigue.

While data on (self‐reported) symptoms like fatigue (one of your two primaryoutcomes) is interesting, arguably more important to patients is improving their overalllevel of functioning (and again, objective measures are needed here). Being able towork, for example, despite experiencing a certain level of fatigue would likely be moreimportant for many than being unable to work but having slightly lower levels offatigue.

An example of how reductions in the reported levels of fatigue may not lead toimprovements in functioning can be seen in an analysis of three gradedactivity‐oriented CBT therapy interventions for CFS (15). The analysis showed,compared to controls, there were no improvements in overall activity levels as measuredby actometers despite improvements in self‐reported fatigue (15). Activity inthese trials was assessed using actometers. Another study that exemplifies the problemof focusing too much on fatigue scores after behavioural interventions is a study of CBTin multiple sclerosis (MS) patients with “MSfatigue”(16). The study found that following the intervention,patients with MS reported significantly lower (i.e. better) scores on the ChalderFatigue Scale (0‐33 scoring) than those in a healthy, nonfatigued comparisongroup! This significant difference was maintained at 3 and 6 months’follow‐up. It is difficult to believe that patients with MS fatigue (at baseline)truly subsequently had less fatigue than healthy nonfatigued controls: a much morelikely scenario is that undertaking the intervention had led to response biases.

You mention that "many patient charities are opposed to exercise therapy forchronic fatigue syndrome (CFS)". One reason for concern about the way in whichexercise programmes are promoted to patients is that they are often based upon modelswhich assume that there is no abnormal physiological response to exercise in thecondition, and make unsupported claims to patients. For example, in the FINE trial(Wearden et al., 2010) patient booklet (17), it is boldly asserted that: "Activityor exercise cannot harm you" (p. 49). However, a large number of studies have foundabnormal responses to exercise, and the possibility of harm being done simply cannot beexcluded on the basis of current evidence (discussed in 4, 18‐20)."

Compliance

The review doesn't include any information on compliance. I'm not sure thatthere is much published information on this but I know there was a measure based onattendance at therapy sessions (which could be conducted over the phone) given for thePACE Trial (3). Ideally, it would be interesting if you could obtain some unpublisheddata from activity logs, records from heart‐rate monitors, and other records tohelp build up a picture of what exercise was actually performed and the level ofcompliance. Information on adherence and what exercise was actually done is important interms of helping clinicians, and indeed patients, to interpret and use the data. Imention patients because patients' own decisions about their behaviour is likely tobe affected by the medical information available to them, both within and outside of asupervised programme of graded exercise; unlike with an intervention like a drug,patients can undertake exercise without professional supervision.

"Selective reporting (outcome bias)" and White et al. (2011)

I don't believe that White et al. (2011) (the PACE Trial) (3) should be classed ashaving a low risk of bias under "Selective reporting (outcome bias)" (Figure2, page 15). According to the Cochrane Collaboration's tool for assessing risk ofbias (21), the category of low risk of bias is for: "The study protocol isavailable and all of the study’s pre‐specified (primary andsecondary) outcomes that are of interest in the review have been reported in thepre‐specified way". This is not the case in the PACE Trial. The threeprimary efficacy outcomes can be seen in the published protocol (22). None have beenreported in the pre‐specified way. The Cochrane Collaboration's tool forassessing risk of bias states that a “highrisk” of bias applies if any one of several criteria are met,including that “not all of the study’spre‐specified primary outcomes have been reported” or“one or more primary outcomes is reported using measurements,analysis methods or subsets of the data (e.g. subscales) that were notpre‐specified”. In the PACE Trial, the third primaryoutcome measure (the number of "overall improvers") was never published. Also,the other two primary outcome measures were reported using analysis methods that werenot pre‐specified (including switching from the bimodal to the Likert scoringmethod for The Chalder Fatigue Scale, one of the primary outcomes in your review). Thesefacts mean that the “high risk of bias”category should apply.

Thank you for taking the time to read my comments.

Tom Kindlon

Conflict of Interest statement: I am a committee member of the Irish ME/CFS Associationand do a variety of unpaid work for the Association.

References:

1. Turner L, Boutron I, Hróbjartsson A, Altman DG, Moher D: The evolution ofassessing bias in Cochrane systematic reviews of interventions: celebratingmethodological contributions of the Cochrane Collaboration. Syst Rev 2013, 2:79.

2. Chalder T, Goldsmith KA, White PD, Sharpe M, Pickles AR. Rehabilitative therapiesfor chronic fatigue syndrome: a secondary mediation analysis of the PACE trial. LancetPsychiatry. 2015;2:141‐152.

3. White PD, Goldsmith KA, Johnson AL, Potts L, Walwyn R, DeCesare JC, et al.Comparison of adaptive pacing therapy, cognitive behaviour therapy, graded exercisetherapy, and specialist medical care for chronic fatigue syndrome (PACE): a randomisedtrial. The Lancet 2011;377:823‐36.

4. Kindlon T. Reporting of Harms Associated with Graded Exercise Therapy and CognitiveBehavioural Therapy in Myalgic Encephalomyelitis/Chronic Fatigue Syndrome. Bull IACFSME. 2011;19:59‐111.http://iacfsme.org/ME‐CFS‐Primer‐Education/Bulletins/BulletinRelatedPages5/Reporting‐of‐Harms‐Associated‐with‐Graded‐Exercise.aspx

5. Lipkin DP, Scriven AJ, Crake T, Poole‐Wilson PA (1986). Six minute walkingtest for assessing exercise capacity in chronic heart failure. British Medical Journal292, 653‐5.

6. Kadikar A, Maurer J, Kesten S. The six‐minute walk test: a guide toassessment for lung transplantation. J Heart Lung Transplant. 1997Mar;16(3):313‐9.

7. Friedberg F, Sohl S. Cognitive‐behavior therapy in chronic fatigue syndrome:is improvement related to increased physical activity? J Clin Psychol. 2009 Feb 11.

8. Friedberg F. Does graded activity increase activity? A case study of chronic fatiguesyndrome. Journal of Behavior Therapy and Experimental Psychiatry, 2002, 33, 3‐4,203‐21

9. Results and In‐depth Analysis of the 2012 ME Association Patient SurveyExamining the Acceptability, Efficacy and Safety of Cognitive Behavioural Therapy,Graded Exercise Therapy and Pacing, as Interventions used as Management Strategies forME/CFS. Gawcott, England.http://www.meassociation.org.uk/2015/05/23959/ Accessed: September 3, 2015

10. Critical Illness ‐ A Dreadful Experience with Scottish Provident.http://forums.moneysavingexpert.com/showthread.php?t=2356683 Accessed:September 4, 2015

11. McCrone P, Sharpe M, Chalder T, Knapp M, Johnson AL, Goldsmith KA, White PD.Adaptive pacing, cognitive behaviour therapy, graded exercise, and specialist medicalcare for chronic fatigue syndrome: a cost‐effectiveness analysis. PLoS One.2012;7(8):e40808.

12. Rapport d’évaluation (2002‐2004) portant surl’exécution des conventions de rééducation entre leComité de l’assurance soins de santé (INAMI) et lesCentres de référence pour le Syndrome de fatigue chronique (SFC). 2006.http://health.belgium.be/internet2Prd/groups/public/@public/@shc/documents/ie2divers/14926531_fr.pdf(Starts on page 223.) Accessed September 4, 2015 (French language edition)

13. Evaluatierapport (2002‐2004) met betrekking tot de uitvoering van derevalidatieovereenkomsten tussen het Comité van de verzekering voor geneeskundigeverzorging (ingesteld bij het Rijksinstituut voor Ziekte‐ eninvaliditeitsverzekering) en de Referentiecentra voor het Chronischvermoeidheidssyndroom (CVS). 2006.http://health.belgium.be/internet2Prd/groups/public/@public/@shc/documents/ie2divers/14926531.pdf(Starts on page 227.) Accessed September 4, 2015 (Dutch language version)

14. Stordeur S, Thiry N, Eyssen M. Chronisch Vermoeidheidssyndroom: diagnose,behandeling en zorgorganisatie. Health Services Research (HSR). Brussel: FederaalKenniscentrum voor de Gezondheidszorg (KCE); 2008. KCE reports 88A (D/2008/10.273/58)https://kce.fgov.be/sites/default/files/page_documents/d20081027358.pdfAccessed September 4, 2015

15. Wiborg JF, Knoop H, Stulemeijer M, Prins JB, Bleijenberg G. How does cognitivebehaviour therapy reduce fatigue in patients with chronic fatigue syndrome? The role ofphysical activity. Psychol Med. 2010; 40:1281‐1287.

16. Van Kessel K, Moss‐Morris R, Willoughby, Chalder T, Johnson MH, Robinson E,A randomized controlled trial of cognitive behavior therapy for multiple sclerosisfatigue, Psychosom. Med. 2008; 70:205–213.

17. Powell P. FINE Trial Patient Booklethttp://www.fine‐trial.net/downloads/Patient%20PR%20Manual%20ver9%20Apr05.pdfAccessed September 7, 2015

18. Twisk FNM, Maes M. A review on Cognitive Behavorial Therapy (CBT) and GradedExercise Therapy (GET) in Myalgic Encephalomyelitis (ME)/Chronic Fatigue Syndrome (CFS):CBT/GET is not only ineffective and not evidence‐based, but also potentiallyharmful for many patients with ME/CFS. Neuro Endocrinol Lett.2009;30:284‐299.

19. Carruthers BM et al. Myalgic Encephalomyelitis – Adult & Paediatric:International Consensus Primer for Medical Practitioners. ISBN978‐0‐9739335‐3‐6http://www.investinme.org/Documents/Guidelines/Myalgic%20Encephalomyelitis%20International%20Consensus%20Primer%20‐2012‐11‐26.pdfAccessed September 5, 2015

20. Twisk FN. Objective Evidence of Post‐exertional“Malaise” in Myalgic Encephalomyelitis andChronic Fatigue Syndrome. J Sports Med Doping Stud 2015. 5:159. doi:10.4172/2161‐0673.100015

21. Higgins JPT, Green S: Cochrane Handbook for Systematic Reviews of InterventionsVersion 5.1.0 [updated March 2011]. Table 8.5.d. The Cochrane Collaboration; 2011.http://handbook.cochrane.org/chapte...a_for_judging_risk_of_bias_in_the_risk_of.htmAccessed: September 5, 2015

22. White PD, Sharpe MC, Chalder T, DeCesare JC, Walwyn R; on behalf of the PACE trialgroup. Protocol for the PACE trial: A randomised controlled trial of adaptive pacing,cognitive behaviour therapy, and graded exercise as supplements to standardisedspecialist medical care versus standardised specialist medical care alone for patientswith the chronic fatigue syndrome/myalgic encephalomyelitis or encephalopathy. BMCNeurology 2007, 7:6http://www.biomedcentral.com/1471‐2377/7/6 Accessed: September 5,2015

Reply

Thank you for reading the review so carefully and for your comments. I have split theanswers according to the headings you have used.

Objective measures and compliance

The protocol for this review did not include objective measurements or compliance asoutcomes, hence are not included. You make a strong case and including objectivemeasures and compliance should be carefully considered in an update.

Selective reporting (outcome bias)

The Cochrane Risk of Bias tool enables the review authors to be transparent about theirjudgments, but due to the subjective nature of the process it does not guarantee anindisputable consensus. You particularly mention the risk of bias in the PACE trialregarding not providing pre‐specified outcomes however the trial didpre‐specify the analysis of outcomes. The primary outcomes were the same as inthe original protocol, although the scoring method of one was changed and the analysisof assessing efficacy also changed from the original protocol. These changes were madeas part of the detailed statistical analysis plan (itself published in full), which hadbeen promised in the original protocol. These changes were drawn up before the analysiscommenced and before examining any outcome data. In other words they werepre‐specified, so it is hard to understand how the changes contributed to anypotential bias. The relevant paper also alerted readers to all these changes and gavethe reasons for them. Overall, we don’t think that the issues you raisewith regard to the risk of selective outcome bias are such as to suspect high risk ofbias, but recognize that you may reach different conclusions than us.

Kind Regards,

Lillebeth Larun

Contributors

Feedback submitted by: Tom Kindlon

Response submitted by: Lillebeth Larun

Summary

Variation in interventions

It would have been useful to have some more information on the“exercise with pacing” intervention tested inthe Wallman et al. (2004) trial and how it was distinct from some other exerciseinterventions tested. The authors say (1): “On days when symptomsare worse, patients should either shorten the session to a time they consider manageableor, if feeling particularly unwell, abandon the sessionaltogether” (p. 143). I don't believe the description givenin the review conveys this. In the review, this approach is described as "Exercisewith pacing: exercise in which the incremental increase in exercise was personallyset." But Wallman et al.’s approach allows patients to decrease aswell as increase how much exercise they do on the day. This approach also contrasts withhow White (an investigator in two of the trials) has described graded exercise therapy:"if [after increasing the intensity or duration of exercise] there has been anincrease in symptoms, or any other adverse effects, they should stay at their currentlevel of exercise for a further week or two, until the symptoms are back to theirprevious levels" (2). In the PACE Trial manual White co‐wrote (3), the GETintervention was guided by the principle that “planned physicalactivity and not symptoms are used to determine what the participantdoes” (p. 21); similarly, “it is theirplanned physical activity, and not their symptoms, that determine what they are asked todo” (p. 20). Compliance data would help us examine which approachpatients are actually using: I suspect many patients are in fact doing exercise withpacing even in trials such as the PACE Trial (i.e. when they have increased symptoms,often reducing levels of exercise and sometimes doing no exercise activities at all onthat day).

Bimodal versus Likert scoring in Wearden et al. (2010)

I find it odd that the fatigue scores for the Wearden et al. (2010) trial (4) are givenin the 0‐33 format rather than the 0‐11 scoring method. The 0‐11scoring system is what is mentioned as a primary outcome measure in the protocol and iswhat is reported in the main paper reporting the results (4, 5). It is even what yourown report says on p. 44 is the scoring method (“Fatigue Scale, FS;11 items; each item was scored dichotomously on a 4‐point scale [0, 0, 1 or1]”). This is important because using the scoring method for whichyou don't report data (0‐11), there is no statistically significantdifference at the primary outcome point of 70 weeks (5).

Diagnostic criteria

One problem with using these trials as an evidence base, which I don't believe wasmentioned, is that all the trials used the Oxford and Fukuda diagnostic criteria (6, 7).Neither of these criteria require patients to have post‐exertional malaise (orsomething similar). Many consider this to be a core symptom of ME/CFS and it ismandatory in most of the other major criteria (8‐11). [Aside: The London criteriawere assessed in the PACE Trial (12) but they seem to have been operationalised in anunusual way. Ninety seven per cent of the participants who satisfied the (broad) Oxfordcriteria who didn't have a psychiatric disorder satisfied the definition of M.E.used (13). Ellen Goudsmit, one of the authors of the London criteria, has rejected theway they were used in the PACE Trial (14)]. So this lack of requirement for patients tohave post‐exertional malaise (or a similar description) means we cannot be surethat the evidence can be generalised to such patients. An independent NationalInstitutes of Health committee this year concluded "continuing to use the Oxforddefinition may impair progress and cause harm. Therefore, for progress to occur, werecommend that this definition be retired" (15). An Agency for Healthcare Researchand Quality review of diagnostic methods this year reached a similar conclusion:"Consensus groups and researchers should consider retiring the Oxford casedefinition because it differs from the other case definitions and is the leastrestrictive, probably including individuals with other overlappingconditions” (16). An Agency for Healthcare Research and Qualityreview of ME/CFS treatments said: "The Oxford CFS case definition is the leastrestrictive, and its use as entry criteria could have resulted in selection ofparticipants with other fatiguing illnesses or illnesses that resolve spontaneously withtime" (17).

Exclusion of some data from analyses due to baseline differences

It seems unfortunate that some data cannot be used due to baseline differences e.g."Four trials (669 participants) contributed data for evaluation of physicalfunctioning at follow‐up (Jason 2007; Powell 2001; Wearden 2010; White 2011).Jason 2007 observed better results among participants in the relaxation group (MD 21.48,95% CI 5.81 to 37.15). However, results were distorted by large baseline differences inphysical functioning between the exercise and relaxation groups (39/100 vs 54/100);therefore we decided not to include these results in the meta‐analysis". Itwould be good if other methods could be investigated (e.g. using baseline levels ascovariates) to analyse such data.

Thank you for taking the time to read my comments.

Tom Kindlon

I am a committee member of the Irish ME/CFS Association and do a variety of unpaid workfor the Association.

1. Wallman KE, Morton AR, Goodman C, Grove R. Exercise prescription for individualswith chronic fatigue syndrome. Med J Aust. 2005;183:142‐3.

2. White P. How exercise can help chronic fatigue syndrome. Pulse: 1998. June20:86‐87.

3. Bavinton J, Darbishire L, White PD ‐on behalf of the PACE trial managementgroup. Graded Exercise Therapy for CFS/ME (Therapist Manual)http://www.pacetrial.org/docs/get‐therapist‐manual.pdf

4. Wearden AJ, Riste L, Dowrick C, Chew‐Graham C, Bentall RP, Morriss RK, PetersS, Dunn G, Richardson G, Lovell K, Powell P. Fatigue Intervention by NursesEvaluation‐‐the FINE Trial. A randomised controlled trial of nurse ledself‐help treatment for patients in primary care with chronic fatigue syndrome:study protocol. [ISRCTN74156610]. BMC Med. 2006 Apr 7;4:9.

5. Wearden AJ, Dowrick C, Chew‐Graham C, Bentall RP, Morriss RK, Peters S, RisteL, Richardson G, Lovell K, Dunn G; Fatigue Intervention by Nurses Evaluation (FINE)trial writing group and the FINE trial group. Nurse led, home based self help treatmentfor patients in primary care with chronic fatigue syndrome: randomised controlled trial.BMJ. 2010 Apr 23;340:c1777. doi: 10.1136/bmj.c1777.

6. Sharpe M, Archard L, Banatvala J, Borysiewicz LK, Clare AW, David A, et al. Chronicfatigue syndrome: guidelines for research. Journal of the Royal Society of Medicine1991;84 (2):118–21.

7. Fukuda K, Straus SE, Hickie I, et al. The chronic fatigue syndrome: A comprehensiveapproach to its definition and study. Ann Intern Med. 1994; 121: 953‑959.

8. Carruthers BM, Jain AK, De Meirleir KL, et al. Myalgic Encephalomyelitis/chronicfatigue syndrome: Clinical working case definition, diagnostic and treatments protocols.Journal of Chronic Fatigue Syndrome. 2003; 11: 7‐115.

9. Carruthers BM, van de Sande MI, De Meirleir KL, et al. Myalgic encephalomyelitis:International Consensus Criteria. J Intern Med. 2011; 270: 327‐338.

10. IOM (Institute of Medicine). Beyond myalgic encephalomyelitis/chronic fatiguesyndrome: Redefining an illness. Washington, DC: The National Academies; 2015.

11. National Institute for Health and Clinical Excellence. Chronic fatiguesyndrome/myalgic encephalomyelitis (or encephalopathy): diagnosis and management ofCFS/ME in adults and children, 2007.http://www.nice.org.uk/guidance/CG53 Accessed September 6, 2015. London:National Institute for Health and Clinical Excellence.

12. White PD, Goldsmith KA, Johnson AL, Potts L, Walwyn R, DeCesare JC, et al.Comparison of adaptive pacing therapy, cognitive behaviour therapy, graded exercisetherapy, and specialist medical care for chronic fatigue syndrome (PACE): a randomisedtrial. The Lancet 2011;377:823‐36.

13. Kindlon T. PACE Trial ‐ 97% of the participants who didn't have apsychiatric disorder satisfied the definition of M.E. used.https://listserv.nodak.edu/cgi‐bin/wa.exe?A2=ind1106A&L=CO‐CURE&P=R2764Accessed: September 6, 2015

14. Ellen Goudsmit on PubMed Commons:http://www.ncbi.nlm.nih.gov/myncbi/ellen m.goudsmit.1/comments/

15. Green CR, Cowan P, Elk R, O'Neil KM, Rasmussen AL. National Institutes ofHealth Pathways to Prevention Workshop: advancing the research on myalgicencephalomyelitis/chronic fatigue syndrome. Ann Intern Med. 2015; 162:860‐5.

16. Haney E, Smith MEB, McDonagh M, Pappas M, Daeges M, Wasson N, et al. Diagnosticmethods for myalgic encephalomyelitis/chronic fatigue syndrome: a systematic review fora National Institutes of Health Pathways to Prevention Workshop. Ann Intern Med. 2015;162:834‐40.

17. Smith MEB, Haney E, McDonagh M, Pappas M, Daeges M, Wasson N, et al. Treatment ofmyalgic encephalomyelitis/chronic fatigue syndrome: a systematic review for a NationalInstitutes of Health Pathways to Prevention Workshop. Ann Intern Med. 2015;162:841‐50.

Reply

Variation in interventions

There is ongoing work to improve descriptions of interventions both in primary studiesand in systematic reviews (Scroter 2012, Glasziou 2008). We tried to describe theexercise programs, and differences between them in great detail. We did this both in thetables of study characteristics, and in the Characteristics of exercise interventiontable (table 2). We also contacted trial authors to check that the information wascorrect. We recognize the need for more research to explore which parts of an exercisetreatment program that are most essential or most closely correlated to an successfuloutcome, i.e. the active ingredient.

Bimodal versus Likert scoring in Wearden et al. 2010

To enable pooling of as many studies as possible in a mean differencemeta‐analyses, we used the 33‐scale results reported by Wearden. Yousuggest that the decision to use the 33‐point fatigue scores in our analysis maybias the results because there is no statistically significant difference at the11‐point data at 70 weeks. This statement suggests that there is a statisticallysignificant difference when using the 33‐point data, but if you look intoanalysis 1.2 that is not the case. At 70 week we report MD ‐2.12 (95% CI‐4.49 to 0.25) for the FINE trial, i.e. not statistically significant.

Review authors response: Diagnostic criteria As the use of variousdiagnostic criteria is often emphasised as particularly important with regard totreatment response, we performed subgroup analyses based on diagnostic criteria. Theavailability of relevant trials limits which subgroup analyses are possible to carry outin a systematic review, and hence, we were only able to contrast CDC versus Oxfordcriteria and found no evidence for a difference. We realize that the role of diagnosticcriteria as a possible moderator for the efficacy of exercise receives a lot ofattention, and would welcome trials to investigate these matters more thoroughly.

Exclusion of some data from analyses due to baseline differences

In meta‐analysis based on aggregated data the authors have to act based on theinformation that is available from original publications or additional informationobtained from the original investigators. As you state, these restrictions may besuboptimal. It is possible to adjust for baseline differences in meta‐regressiontype analyses, but this requires adjustment for dependency between the intervention andcontrol group results from the same trial. As a consequence, three variables(intervention vs control, baseline level, and trial) would have to be accounted for inthe analyses. This implies that at least 30 data points will be needed to gain somewhatstable and trustworthy estimates adjusted for baseline levels. Systematic reviews basedon individual patient data (IPD) allows for more appropriate processing andstandardization of data. We are happy to inform you that we have now received individualpatient data from most of the studies included in this review, and that the preparationof an IPD review is in progress.

Scroter S, Glasziou P, Heneghan C. Quality of descriptions of treatments: a review ofpublished randomized trials. BMJ Open 2012:2e001978doi:10.1136/bmjopen‐2012‐001978

Glasziou P, Meats M, Heneghan C, Sheppers S. What is missing in descriptions oftreatment in trials and reviews? BMJ 2008;336:1472 doi: /10.1136/bmj.39590.732037.47

Contributors

Feedback submitted by: Tom Kindlon

Response submitted by: Lillebeth Larun

Summary

Query regarding use of post‐hoc unpublished outcome data: Scoring system forthe Chalder fatigue scale, Wearden, 2010

I would like to highlight what appears to be a discrepancy within the Cochrane review[1] with respect to the analysis of data from Wearden 2010 [2,3]. Throughoutthe Cochrane review (please see details below), the impression is given that onlyprotocol defined and published data or outcomes were used for the Cochrane analysis ofthe Wearden 2010 study.

However, this does not appear to be the case and, to the best of my knowledge, insteadof using protocol defined or published data, the Cochrane analyses of fatigue for theWearden 2010 study, appears to have used an alternative unpublished set of data.

The relevant analyses of fatigue in the Cochrane review are: Analyses: 1.1, 1.2, 2.1and 2.3. Each of these analyses states that the“0,1,2,3” scoring system was used for theChalder fatigue questionnaire. This scoring system is known as the Likert scoring systemand uses a fatigue scale of 033 points.

However, to the best of my knowledge, data or analyses using this scoring system werenot proposed in the Wearden 2010 trial protocol [3], and were not included in Wearden2010 [2], and have not previously been formally (i.e. via peer review) published byWearden et al. A posthoc informal analysis using this data has been informally releasedby Wearden et al. as a BMJ Rapid Response comment [4].

In the Cochrane review, the analyses using the 0, 1, 2, 3 scoring system contradicttext within the section “Characteristics OfStudies”, in relation to Wearden 2010: Under“Outcomes”, it is stated that Chalder fatiguewas measured using the 0,0,1,1 scoring system using a scale from 011 points:“Fatigue (Fatigue Scale, FS; 11 items; each item wasscored dichotomously on a 4 point scale (0, 0, 1 or 1)”.

Wearden 2010 prespecified Chalder fatigue questionnaire scores as a primary outcome at70 weeks, and as a secondary outcome immediately after treatment at 20 weeks. Thescoring, in both cases, used the 0,0,1,1 system, with a scale of 011. This scoringsystem was described both in the trial protocol [3] and the main results paper publishedin 2010 [2].

The Likert (0, 1, 2, 3) scoring system was neither proposed in the trial protocol, norformally published, and so the Likert scores should be considered posthoc. Even if it isargued that the Chalder fatigue questionnaire (irrespective of the scoring system) waspredefined as a primary outcome measure, data using the Likert scoring system wasneither proposed nor published and so the data itself must surely be considered to beposthoc. The outcome analyses using the Likert data must be considered posthoc.

Simply changing a scoring system may, at first glance, appear not to be a significantor major adjustment, however, we do not know what difference it made because asensitivity analysis has not been published.

I cannot find any explanation within the Cochrane review that explains why the Cochranereview has replaced predefined published data with an unpublished and posthoc set ofdata.

Is it normal practice for a Cochrane metaanalysis to selectively ignore the predefinedprimary outcome data for a trial, and to selectively include and analyse posthoc data? Iwonder if some clarity could be shed on this situation?

I suggest that the posthoc data are replaced with the original published data.Otherwise, the posthoc data should be clearly labelled as such and the risk of biasanalysis amended accordingly; and an explanation should be included in the reviewexplaining why an apparently adequate predefined set of data has been replaced with anapparent novel set of posthoc data.

Also, I suggest that any discrepancies that I will outline below, should be correctedwhere necessary; Either the analyses (1.1, 1.2, 2.1 and 2.3) should be amended orthe description of the data should be amended so it is not incorrectly labelled asprotocol defined and published data with a “lowrisk” of bias.

Discrepancies within the text of the Cochrane Analysis

Please note that all page numbers used below are pertinent to the current version(version 4) of the Cochrane review in PDF format.

1. On page 28 of the Cochrane review [1], in section “Potentialbiases in the review process”, under the heading“Potential bias in the review process”, inrelation to the review in general, it is stated that: "For this updated review, wehave not collected unpublished data for our outcomes ..." However, as explainedabove, this is not the case for the Wearden 2010 fatigue data for which unpublished datahas been used in the Cochrane analysis.

2. On page 45 of the review, in section “Characteristics OfStudies”, specifically in relation to Wearden 2010 [2,3], it isstated that only protocol defined outcomes were used: "all relevantoutcomes are reported in accordance with the protocol". "Selective reporting(reporting bias)" is rated as "low risk". However, as explained above,this is not the case, because the Wearden 2010 fatigue data (used in the Cochraneanalysis) was not proposed in the protocol. If the data is posthoc, then the“low risk” category will need to berevised.

3. On page 44 of the review, in section “Characteristics OfStudies”, in relation to Wearden 2010 [2,3], under“Outcomes”, it is stated that Chalder fatiguewas measured using the 0,0,1,1 scoring system using a scale from 011 points:“Fatigue (Fatigue Scale, FS; 11 items; each item wasscored dichotomously on a 4 point scale (0, 0, 1 or 1)”. Wearden2010 did indeed use the 0,0,1,1 scoring system for the Chalder fatigue scale: Thisscoring system was proposed in the trial protocol and published with the main outcomedata in Wearden 2010. However, as explained above, this scoring system has not been usedin the Cochrane analysis.

4. If figures 2 and 3 also contain discrepancies, after any amendments to the review,then they should be amended accordingly.

There may be other related discrepancies and inaccuracies in the text that Ihaven’t noticed. I thank the Cochrane team in advance for giving thissubmission careful consideration, and for making amendments to the analysis, andproviding explanations, where appropriate. I hope you will agree that clarity,transparency and accuracy in relation to the analysis is paramount.

References: 1. Larun L, Brurberg KG, Odgaard Jensen J, Price JR.Exercise therapy for chronic fatigue syndrome. Cochrane Database Syst Rev. 2016;CD003200.

2. Wearden AJ, Dowrick C, ChewGraham C, et al. Nurse led, home based self helptreatment for patients in primary care with chronic fatigue syndrome: randomisedcontrolled trial. BMJ. 2010; 340:c1777.

3. Wearden AJ, Riste L, Dowrick C, et al. Fatigue Intervention by Nurses Evaluation– The FINE Trial. A randomised controlled trial of nurse ledselfhelp treatment for patients in primary care with chronic fatiguesyndrome: study protocol. BMC Med. 2006; 4:9.

4. Wearden AJ, Dowrick C, ChewGraham C, et al. Fatigue scale. BMJ Rapid Response. 2010.http://www.bmj.com/rapidresponse/2011/11/02/fatiguescale0 (accessed April16, 2016).

Reply

Dear Robert Courtney

Thank you for your detailed comments on the Cochrane review 'Exercise Therapy forChronic Fatigue Syndrome'. We have the greatest respect for your right to commenton and disagree with our work. We take our work as researchers extremely seriously andpublish reports that have been subject to rigorous internal and external peer review. Inthe spirit of openness, transparency and mutual respect we must politely agree todisagree.

The Chalder Fatigue Scale was used to measure fatigue. The results from the Wearden2010 trial show a statistically significant difference in favour of pragmaticrehabilitation at 20 weeks, regardless whether the results were scored bi‐modallyor on a scale from 0‐3. The effect estimate for the 70 week comparison with thescale scored bi‐modally was ‐1.00 (CI‐2.10 to +0.11; p =.076) and‐2.55 (‐4.99 to ‐0.11; p=.040) for 0123 scoring. The FINE datameasured on the 33‐point scale was published in an online rapid response after areader requested it. We therefore knew that the data existed, and requested clarifyingdetails from the authors to be able to use the estimates in our meta‐analysis. Inour unadjusted analysis the results were similar for the scale scored bi‐modallyand the scale scored from 0 to 3, i.e. a statistically significant difference in favourof rehabilitation at 20 weeks and a trend that does not reach statistical significancein favour of pragmatic rehabilitation at 70 weeks. The decision to use the 0123 scoringdid does not affect the conclusion of the review.

Regards,

Lillebeth Larun

Contributors

Feedback submitted by: Robert Courtney

Response submitted by: Lillebeth Larun

Summary

Comment: Assessment of Selective Reporting Bias in White 2011

With reference to the current Cochrane review of exercise therapy for chronic fatiguesyndrome [1], I would like to follow‐up the discussion between Tom Kindlon andLillebeth Larun that has been published in the latest version of the full reviewpublished in 2016. Kindlon submitted two comments, dated 9 September 2016, and Larunissued a response to each.

Kindlon raised the issue of the study referred to as "White 2011" in theCochrane review, commonly known as the PACE trial [2]; specifically whether or not therisk of bias for selective reporting of outcomes for the trial has been assessed andcategorised appropriately, in terms of Cochrane's guidelines and policies.

In this submission I will make reference to the current "Cochrane Handbook forSystematic Reviews of Interventions" [3], including Table 8.5.d ("Criteria forjudging risk of bias in the ‘Risk of bias’ assessmenttool"), which I will refer to as the "Cochrane guidelines".

In his submission, Kindlon said: "I don't believe that White et al. (2011)(the PACE Trial) [...] should be classed as having a low risk of bias under"Selective reporting (outcome bias)"."

In a considered response, Larun concluded: "Overall, we don’tthink that the issues you raise with regard to the risk of selective outcome bias aresuch as to suspect high risk of bias, but recognize that you may reach differentconclusions than us."

Larun's response to the concerns raised by Kindlon has left me unsure aboutwhether Cochrane's guidelines have been applied appropriately in this case, so Iwould like to discuss some of the finer details.

Pre‐Planned Analysis

I note that the PACE trial's protocol was submitted for publication in 2006 andpublished in 2007 [4], which was after the trial had commenced in 2005 [2]. This raisesthe question of whether the protocol itself can be defined as a pre‐trial report.Cochrane's glossary of terms defines a "pre‐specified" analysis asa "Statistical analyses specified in the trial protocol; that is, planned inadvance of data collection." [5] So the Cochrane glossary states that apre‐specified analysis plan, or protocol, must be completed before datacollection has commenced.

Other sources, such as the Wiley Encyclopedia of Clinical Trials, also define apre‐planned analysis as that which has been defined before data collection hascommenced: "A primary efficacy endpoint needs to be specified before the start ofthe clinical trial." [6]

To be certain that the PACE trial's analyses were defined before data collectionhad commenced then we would need an earlier publication such as a trial register [7] ortrial identifier, both of which were created and which included definitions of primaryendpoints which were different to the trial protocol (see appendix, below, for detaileddescriptions). To my knowledge, the Cochrane review, does not discuss these issues.

Nevertheless, the Cochrane guidelines (section 8.14.2) advise using a trial protocol asa guide to determine which trial outcomes were pre‐determined: "If theprotocol is available, then outcomes in the protocol and published report can becompared".

As the protocol was published after the trial had commenced, it seems certain that anysubsequent (i.e. after the protocol had been published) changes to methodology were madeafter data collection had commenced and were therefore not pre‐specified.

Statistical Analysis Plan

Larun states that various changes from the protocol were "made as part of thedetailed statistical analysis plan (itself published in full), which had been promisedin the original protocol." The protocol did indeed refer to a statistical analysisplan, but the protocol wording suggests to me that no changes from the protocol wereplanned, but that the statistical analysis plan would simply flesh out the protocol:"A full Analysis Strategy will be developed, independently of looking at the trialdatabase, and before undertaking any analysis. This paper [i.e. the protocol] summarisesthe analysis plan." There was no suggestion that there would be wholesale changesto primary, secondary or recovery outcomes. But, in any case, even if theinvestigators' initial intentions had been to make changes after data collectionhad started, the result would still not be a pre‐specified analysis according tothe Cochrane glossary of terms [5].

The statistical analysis plan was submitted for publication in 2012 and published in2013 [8] after the main trial results had been published in 2011 [2], and long after thetrial had commenced in 2005, so the statistical analysis plan cannot reasonably beconsidered to be a priori. Indeed the statistical analysis report itself confirms thatthe analysis was finalised or approved towards the end of data collection in 2010:"These planned analyses were written with a view to publication and are reproducedalmost as they were approved by the Trial Steering Committee (Version 1.2 dated 2 May2010) prior to database lock."

Larun states that the "changes [to the trial] were drawn up before the analysiscommenced and before examining any outcome data. In other words they werepre‐specified [...]" However, the latter assertion is not consistent withCochrane's glossary, which states that pre‐specified changes are thosedefined before data collection has commenced [5].

Investigators of an open‐label trial can potentially gain insights into a trialbefore formal analysis has been carried out. If changes to a planned methodology aremade after a trial has started and/or after data collection has commenced (whether ornot the data has been formally analysed) then it is generally accepted that this failsthe definition of a "pre‐specified" study, which is confirmed by theCochrane glossary and other sources. Otherwise trial registries and protocols could bedrawn up after all data had been collected but before the formal analysis has commenced,and still be described as pre‐planned. This would be particularly problematic inopen‐label trials such as the PACE trial.

Pre‐Planned and Unplanned Primary Endpoints

The PACE trial's protocol had proposed three primary efficacy analyses which allhad binary outcomes (i.e. a positive or negative outcome for each patient), whereas thefinal primary analyses were entirely different; they were continuous measures focused onthe differences in mean improvements between intervention groups at 52 weeks. So thechanges to the protocol were substantial. (See appendix, below, for detaileddescriptions.) The PACE trial's three a priori primary efficacy analyses were notincluded in the final published results, and have never been published and, to myknowledge, no sensitivity analysis has been published for the final published primaryanalyses.

The PACE trial's published results paper [2] confirmed the unplanned outcomeswitching, as follows: "We used continuous scores for primary outcomes to allow amore straightforward interpretation of the individual outcomes, instead of theoriginally planned composite measures (50% change or meeting a thresholdscore)."

This entirely contradicts Larun's claims that: "the trial didpre‐specify the analysis of outcomes" and: "The primary outcomes werethe same as in the original protocol".

The Cochrane guidelines give guidance that is specific to the issue of changing apre‐planned analysis for the same set of data and they describe such an action as"selective reporting of analyses using the same data". The guidelinescouldn't be more specific that changing a method for analysing the same set of datashould be considered selective reporting.

The Cochrane guidelines (8.14.1) state: "Selective reporting of analyses using thesame data: There are often several different ways in which an outcome can be analysed.For example, continuous outcomes such as blood pressure reduction might be analysed as acontinuous or dichotomous variable, with the further possibility of selecting frommultiple cut‐points."

Scoring System for Chalder Fatigue

A change from the protocol, that will have had a direct impact on the Cochraneanalysis, was the scoring system used for the Chalder fatigue scale. The PACE trialprotocol proposed two self‐report questionnaires as tools to use for the primaryendpoint analyses: one was the Chalder fatigue questionnaire, and the other was theShort Form 36 (SF‐36) physical function subscale. The scoring system for theChalder fatigue questionnaire was pre‐defined as a bimodal scoring system (i.e. ascore of 0 or 1 for each response to the 11 questions, giving a fatigue scale of0‐11). However, after data collection had commenced, the decision was to made tochange to a continuous scoring system, known as the Likert system (i.e. a score of 0 ,1,2, or 3 for each response to the 11 questions, giving a fatigue scale of 0‐33).This change was made after the PACE trial's nominal 'sister trial', knownas the FINE trial, had completed its analysis of very similar type of data using boththe bimodal and Likert scoring systems. The FINE trial investigators had found nosignificant effect for their primary endpoint when using the bimodal scoring system forChalder fatigue [9] but determined a significant effect using the Likert system in aninformal post‐hoc analysis [10]. The FINE trial has published its raw data, aspart of the PLoS One data sharing commitment, and an informal analysis has shown thatthere may potentially be other significant differences in some outcomes, when changingfrom bimodal to Likert scoring [11].

With regards to risk of selective reporting bias specifically in relation to the PACEtrial, the Cochrane review states: “Our primary interest is theprimary outcome reported in accordance with the protocol, so we do not believe thatselective reporting is a problem."

However, the Likert scoring system for the Chalder fatigue questionnaire is clearlylabelled as a secondary outcome in the PACE trial protocol, and not a primary outcome.The protocol specifically lists "Chalder Fatigue Questionnaire Likert scoring(0,1,2,3)" as a "secondary outcome" only. This contradicts the abovestatement in the review (i.e. "our primary interest is the primary outcome reportedin accordance with the protocol"), and it contradicts Larun's impliedassertion that the Likert scoring system was "pre‐specified" for use asa primary outcome measure.

So, to reiterate, the Likert scoring system, that the Cochrane review has described asa primary outcome measure, is specifically described as only a secondary measure in thePACE trial's protocol. It could not be more specific.

The change in questionnaire scoring methods is more than just a technicality, and mayhave made a significant difference to the trial's outcomes [11]. The rationale forthe change (i.e. "to more sensitively test our hypotheses of effectiveness")may or may not be justified, and the change may or may not be beneficial in terms ofbetter understanding treatment effects, but the fact remains that it was not part of apre‐specified trial plan.

Considering the issues discussed above, the analysis of the Chalder fatigue scores inthe Cochrane review should undoubtedly, in my opinion, be considered an unplannedanalysis and labelled as such.

Sensitivity Analysis

The Cochrane review focused on the mean differences between intervention groups, andwhether there was a statistically significant effect, which is the same analysis as thePACE trial's final published outcomes.

Analyses of the PACE trial data using the pre‐planned methods have not beenpublished and, to my knowledge, a sensitivity analysis for the (unplanned) finaloutcomes has neither been published in the PACE trial literature nor the Cochranereview, so it is impossible for the reader to have insight into the impact of thechanges.

In terms of what should be done when only post‐hoc data is available theCochrane guidelines (section 8.14.2) advise that a sensitivity analysis should bepublished: "It is not generally recommended to try to ‘adjustfor’ reporting bias in the main meta‐analysis. Sensitivityanalysis is a better approach to investigate the possible impact of selective outcomereporting (Hutton 2000, Williamson 2005a)."

It would be helpful if this guideline was adhered to.

Assessment of Risk of Reporting Bias

As well as those outlined above, various other important outcomes in the trial werechanged dramatically, such as the recovery analysis, which was reported in a separatepublication [12]. Also, the pre‐defined 'clinically importantdifference' was dropped, and was replaced with a 'clinically usefuldifference' which had an entirely different definition. There were too manydeviations from the protocol in the final analyses to list them all in detail here.

The Cochrane guidelines (8.14.2) state: "The assessment of risk of bias due toselective reporting of outcomes should be made for the study as a whole, rather than foreach outcome. Although it may be clear for a particular study that some specificoutcomes are subject to selective reporting while others are not, we recommend thestudy‐level approach because it is not practical to list all fully reportedoutcomes in the ‘Risk of bias’ table."

The Cochrane review currently designates the risk of reporting bias for the PACE trialas "low risk": Under the subheading "Characteristics of includedstudies" and under: "Selective reporting (reporting bias)", White 2011 isdesignated as "Low risk". This designation is repeated elsewhere in thereview, such as the "Risk of bias summary" in Figure 2.

Kindlon pointed out that the Cochrane guidelines (Table 8.5.d) set out the criteria forthe judgement of high risk of reporting bias as follows:

"Any one of the following:

• Not all of the study’s pre‐specified primary outcomes havebeen reported;

• One or more primary outcomes is reported using measurements, analysis methods orsubsets of the data (e.g. subscales) that were not pre‐specified;

• One or more reported primary outcomes were not pre‐specified (unless clearjustification for their reporting is provided, such as an unexpected adverseeffect);

• One or more outcomes of interest in the review are reported incompletely so thatthey cannot be entered in a meta‐analysis;

• The study report fails to include results for a key outcome that would beexpected to have been reported for such a study."

I consider the trial to meet at least the first three of these requirements for a highrisk of bias. However, in the response to Kindlon, Larun says: "Overall, wedon’t think that the issues you raise with regard to the risk ofselective outcome bias are such as to suspect high risk of bias, but recognize that youmay reach different conclusions than us."

I find this claim impossible to square with the Cochrane risk of bias tool, for which,in my opinion, the PACE trial unambiguously meets at least three high risk criteria whenonly one is required to label the study as high risk.

The Cochrane guidelines advise that the bias risk of a study should be assessed bytaking into account the study as a whole; and as all of the PACE trial's mainpublished analyses, including the primary analyses and the recovery analysis, were notpre‐planned, this suggests that the Cochrane report should have labelled thetrial as having a high risk of reporting bias, according to my interpretation of theCochrane guidelines.

I request that a revaluation is carried out, with reference to the Cochraneguidelines.

Definition of a Primary Endpoint

In his submission to Cochrane, Kindlon explained that the three pre‐plannedprimary endpoint analyses were abandoned in favour of novel analyses in the final trialanalysis: "The three primary efficacy outcomes can be seen in the publishedprotocol" and "None have been reported in the pre‐specified way.

I find Larun's response to Kindlon to be confusing and unsatisfactory. As far asmy understanding goes, the response does not seem to take account of the Cochraneguidelines. Larun acknowledges that the scoring system for one of the primary outcomeassessment tools, was changed: "the scoring method of one was changed", andshe acknowledges that the trial's primary endpoint analyses were changed: "theanalysis of assessing efficacy also changed from the original protocol."

However, Larun seems to contradict this by saying: "The [final] primary outcomeswere the same as in the original protocol [...]"

Larun's latter statement contradicts the published results which state that the"originally planned" "primary outcomes" were switched: "We usedcontinuous scores for primary outcomes [...] instead of the originally planned compositemeasures (50% change or meeting a threshold score)." [2]

The primary endpoints (i.e. criteria to judge a successful outcome) were defined inprecise detail rather than simply being described as 'fatigue' and'physical function'. Instead, a specific primary endpoint efficacy analysiswas defined which included a required threshold for a positive outcome in fatigue andfunction at 52 weeks. Also, the questionnaire and scoring method was defined for eachprimary endpoint.

As the primary endpoint analyses were changed then I would argue that the primaryoutcomes were substantially changed.

A "primary efficacy endpoint" has been described as "a clinical orlaboratory outcome measured in an individual after randomization that allows one to testthe primary hypothesis and provides the means of assessing whether a therapy iseffective compared with its control." [6]

An example of "Completely defined pre‐specified primary and secondaryoutcome measures, including how and when they were assessed" is given in theConsort guidelines: "Example—“The primary endpoint withrespect to efficacy in psoriasis was the proportion of patients achieving a 75%improvement in psoriasis activity from baseline to 12 weeks as measured by the PASI[psoriasis area and severity index] Additional analyses were done on the percentagechange in PASI scores and improvement in target psoriasis lesions" [13]

In the PACE trial the primary objectives were to compare CBT and GET against SMC. Toeffectively achieve this comparison, a specific primary analysis was provided, as theprimary endpoint, to determine a successful outcome. The results for thepre‐planned primary endpoints have not been released.

Conclusion

Larun says: "The Cochrane Risk of Bias tool enables the review authors to betransparent about their judgments, but due to the subjective nature of the process itdoes not guarantee an indisputable consensus."

I accept that assessment of bias can be subjective but, as I have outlined above, theissues relating to the PACE trial seem clear‐cut, according to the Cochraneguidelines, which give very specific advice in relation to the type of the changes thatwe see here. I do not accept Larun's suggestion that this is a nuanced orsubjective evaluation. PACE seems to fail at least the first three criteria in the'high risk' category of the Cochrane risk tool for reporting bias.

The changes to the PACE trial's primary outcomes had the effect of lowering thethreshold for a positive outcome and therefore portraying the interventions in a morepositive light. A major purpose of a trial protocol is to avoid bias that canpotentially arise through selective reporting. Avoidable bias does a disservice for themedical and patient communities and I would expect Cochrane to be rigorous in pointingout potential bias, and discussing the implications of bias, labelling bias correctlyand including unbiased data where possible or including a sensitively analysis wherepossible. Indeed, this is what the Cochrane guidelines advise, and it is what the publicexpect of Cochrane. I feel that these issues have been neglected in this specificinstance, and a reader of the Cochrane review in isolation would be unaware of any ofthe issues discussed above, relating to the PACE trial.

I ask for a reassessment and revaluation of this review in relation to the PACE trialand risk of bias.

Many thanks, in advance, for your careful consideration of these issues.

‐‐‐

Appendix

PACE trial: protocol‐defined primary endpoints ‐ trial protocol [4].

Three Primary Endpoints.

"Primary outcome measures – Primary efficacy measures"

1. “The 11 item Chalder Fatigue Questionnaire measures theseverity of symptomatic fatigue, [27] and has been the most frequently used measure offatigue in most previous trials of these interventions. We will use the 0,0,1,1 itemscores to allow a possible score of between 0 and 11. A positive outcome will be a 50%reduction in fatigue score, or a score of 3 or less, this threshold having beenpreviously shown to indicate normal fatigue. [27]"

2. “The SF‐36 physical function sub‐scale [29]measures physical function, and has often been used as a primary outcome measure intrials of CBT and GET. We will count a score of 75 (out of a maximum of 100) or more, ora 50 % increase from baseline in SF‐36 sub‐scale score as a positiveoutcome. A score of 70 is about one standard deviation below the mean score (about 85,depending on the study) for the UK adult population. [51, 52]”

3. "Those participants who improve in both primary outcome measures will beregarded as overall improvers."

PACE trial: post‐hoc primary endpoints ‐ main results paper [2].

The difference between mean changes in fatigue and physical function acrossintervention groups at 52 weeks, using an effect size to assess the efficacy ofinterventions.

PACE trial: pre‐specified primary endpoints ‐Trial Registry [7]

"Endpoints/primary outcome(s)

1. The 11 item Chalder fatigue questionnaire, using categorical item scores to allow acategorical threshold measure of “abnormal”fatigue with a score of 4 having been previously shown to indicate abnormal fatigue.

2. The SF‐36 physical function sub‐scale, counting a score of 75 (out ofa maximum of 100) or more as indicating normal function."

‐‐‐

References:

1. Larun L, Brurberg KG, Odgaard‐Jensen J, Price JR. Exercise therapy forchronic fatigue syndrome. Cochrane Database Syst Rev. 2016; CD003200.

2. White PD, Goldsmith KA, Johnson AL, et al. Comparison of adaptive pacing therapy,cognitive behaviour therapy, graded exercise therapy, and specialist medical care forchronic fatigue syndrome (PACE): a randomised trial. Lancet 2011; 377:823‐36.

3. Higgins JPT, Green S (editors). Cochrane Handbook for Systematic Reviews ofInterventions. Version 5.1.0 [updated March 2011]. The Cochrane Collaboration, 2011.http://handbook.cochrane.org/front_page.htm (accessed 19 April 2016).

4. White PD, Sharpe MC, Chalder T, et al. Protocol for the PACE trial: a randomisedcontrolled trial of adaptive pacing, cognitive behaviour therapy, and graded exercise,as supplements to standardised specialist medical care versus standardised specialistmedical care alone for patients with the chronic fatigue syndrome/myalgicencephalomyelitis or encephalopathy. BMC Neurol. 2007; 7:6.

5. Glossary. Cochrane Community Archive.https://community‐archive.cochrane.org/glossary/5#term82 (accessed 20April 2016)

6. Follmann DA. Primary Efficacy Endpoint. Wiley Encyclopedia of Clinical Trials.2007.

7. Trial Registry. BioMed Central. Internet Archive.http://web.archive.org/web/20050524130106/http://www.controlled‐trials.com/mrct/trial/CHRONICFATIGUE SYNDROME/1042/40645.html (accessed 29 April 2016)

8. Walwyn R, Potts L, McCrone P, et al. A randomised trial of adaptive pacing therapy,cognitive behaviour therapy, graded exercise, and specialist medical care for chronicfatigue syndrome (PACE): statistical analysis plan. Trials 2013; 14:386.

9. Wearden AJ, Dowrick C, Chew‐Graham C, et al. Nurse led, home based self helptreatment for patients in primary care with chronic fatigue syndrome: randomisedcontrolled trial. BMJ. 2010; 340:c1777.

10. Wearden AJ, Dowrick C, Chew‐Graham C, et al. Fatigue scale. BMJ RapidResponse. 2010.http://www.bmj.com/rapid‐response/2011/11/02/fatigue‐scale‐0(accessed 21 Feb 2016).

11. Carter S. Exploring changes to PACE trial outcome measures using anonymised datafrom the FINE trial. PubMed Commons 2016.http://www.ncbi.nlm.nih.gov/pubmed/23363640#cm23363640_14248 (accessed 20 Feb2016).

12. White PD, Goldsmith K, Johnson AL, Chalder T, Sharpe M. Recovery from chronicfatigue syndrome after treatments given in the PACE trial. Psychol Med. 2013;43:2227‐35.

13. Moher D, Hopewell S, Schulz KF, et al. CONSORT 2010 explanation and elaboration:updated guidelines for reporting parallel group randomised trials. BMJ. 2010;340:c869.

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I do not have any affiliation with or involvement in any organisation with a financialinterest in the subject matter of my comment

Reply

Dear Robert Courtney

Thank you for your detailed comments on the Cochrane review 'Exercise Therapy forChronic Fatigue Syndrome'. We have the greatest respect for your right to commenton and disagree with our work. We take our work as researchers extremely seriously andpublish reports that have been subject to rigorous internal and external peer review. Inthe spirit of openness, transparency and mutual respect we must politely agree todisagree.

Cochrane reviews aim to report the review process in a transparent way, for example,are reasons for the risk of bias stated. We do not agree that Risk of Bias for the Pacetrial (White 2011) should be changed, but have presented it in a way so it is possibleto see our reasoning. We find that we have been quite careful in stating the effectestimates and the certainty of the documentation. We note that you read thisdifferently.

Regards,

Lillebeth

Contributors

Feedback submitted by: Robert Courtney

Response submitted by: Lillebeth Larun

Summary

Comment: concerns regarding the use of unplanned primary outcomes in the Cochranereview

Summary

In this submission, I will discuss the details and implications of unplanned revisionsto the Cochrane review's protocol, specifically changes to the primary outcomes. Iwill raise concerns about the clarity with which the changes to the protocol have beenexplained in the review and I will question the justification given for switching theprimary outcomes. I will compare the details of the pre‐specified primaryoutcomes with the unplanned (revised) primary outcomes. I will explore how the protocolrevisions have impacted the overall conclusions of the review, and how some reviewoutcomes have been misrepresented in the main discussions. I will also briefly discusspotential biases involved in reviewing open‐label studies that useself‐report outcomes, and how such biases may potentially have affected thereview's outcomes. Finally, I will discuss what I believe is: a lack of clarity inhow the review has discussed and portrayed outcomes, and; a lack of depth in howpotential biases have been considered and explored.

I will conclude by asking the reviewers to reassess the review, including the decisionto switch the primary outcomes, with a view to improving clarity, rigour and accuracy. Ispecifically ask the reviewers to:

1. Amend the review as per the Cochrane guidelines (i.e. "every effort should bemade to adhere to a predetermined protocol"), and revert to the pre‐plannedprimary analyses; and

2. Clearly and unambiguously explain that all but one health indicator (i.e. fatigue,physical function, overall health, pain, quality of life, depression, and anxiety, butnot sleep) demonstrated a non‐significant outcome for pooled treatment effects atfollow‐up for exercise therapy versus passive control; and

3. Include a rigorous assessment of how the potential for bias may have affectedoutcomes.

Introduction

After detailed scrutiny of the current version of the Cochrane review of exercisetherapy for chronic fatigue syndrome (version 4, dated 7 February 2016) [1], I havenoticed that the primary outcomes of the review have not been reported as per thepre‐specified review plan, but that unplanned (revised) primary analyses havebeen published in the place of the pre‐specified analyses. (By'unplanned', I refer to revisions to the methodology that were notpre‐specified in the review's protocol.) The switching of primary outcomes(from pre‐specified to unplanned analyses) is not mentioned in the maindiscussions, conclusion, or abstract, and is not explicitly explained anywhere in thereview. I had to carry out a detailed inspection of the review to understand exactlywhat had been changed.

At the very end of the full version of the review, a section titled "[d]ifferencesbetween protocol and review" explains the deviations from the protocol:

"[...] in the protocol it is stated, "where results for continuous outcomeswere presented using different scales or different versions of the same scale, we usedstandardised mean differences (SMDs)." We realise that the standardised meandifference (SMD) is much more difficult to conceptualise and interpret than the normalmean difference (MD); therefore we decided to report both MDs and SMDs in the Resultssection. In general, MDs are reported in the main Results section, whereas SMDs aresupplied under the "Sensitivity and subgroup analysis" subheading."

Although the above quote isn't explicit in referring to the primary outcomes, itexplains the nature of, and rationale for, the unplanned changes to the review'sprimary outcomes. The only reason given for changing the pre‐specified outcomeswas that "the standardised mean difference (SMD) is much more difficult toconceptualise and interpret than the normal mean difference". No evidence isprovided to support this assertion, and it appears to be an assumption about thereaders' ability to interpret outcomes.

The outcomes of the review's pre‐specified primary analyses are outlined inthe analysis section, but are only mentioned briefly (i.e. only one or two sentences areused to explain each outcome), and the pre‐specified outcomes are not discussedin the review's main discussions, abstract or conclusions. The pre‐specifiedanalyses have been relegated to the status of "sensitivity analyses", and itis not explicitly explained that these sensitivity analyses are the pre‐specifiedprimary analyses. It is easy for a reader to overlook these important outcomes and tomisunderstand their significance. I am concerned that most readers will be unaware ofthese changes to the primary outcomes and of the significance of the changes to theprotocol.

I consider the changes to have significantly altered the fundamental design, the mainoutcomes, and overall interpretation of the review.

Primary Outcomes

I would like to take this opportunity to explain the details of the changes to theprimary outcomes to the reader, to the best of my understanding. The review comparesexercise therapy with a passive control (e.g. treatment as usual), which is the focus ofthis submission. Outcomes for exercise therapy compared with other interventions (e.g.cognitive‐behavioural therapy, supportive therapy, and pacing) are also includedin the review, but are not central to the concerns of this submission and will not bediscussed further. The review uses two primary outcome measures (fatigue and adverseoutcomes) but adverse outcomes are not relevant to this submission. A primary analysisat both end of treatment (12 to 26 weeks) and at follow‐up (52 to 70 weeks) iscarried out. This submission focuses on primary analyses in relation to fatigue only,for exercise therapy versus passive control only.

The protocol defined two pre‐specified primary analyses (one at end of treatmentand one at follow‐up) that were to determine the pooled treatment effects of alleligible studies on fatigue. The two analyses were to determine a standardised meandifference (SMD) for the pooled studies.

An unplanned decision was later made to relegate these pre‐specified primaryanalyses to the status of sensitivity analyses and to replace them with two unplannedanalyses which assessed the same studies but by a different statistical method. Theunplanned analyses (1.1 and 1.2) do not provide an overall (pooled) treatment effect butprovide mean differences in a number of sub‐analyses of studies grouped togetherbased on the specific tool or scoring method used to measure fatigue.

The two pre‐specified primary analyses are published as sensitivity analysis1.19 (fatigue at end of treatment) and another analysis (fatigue at follow‐up)which has not been designated a numerical identifier. To reiterate; these two analysesprovide the pooled standardised mean difference for fatigue for all eligible studies.Analysis 1.19 was included within the comprehensive set of tables published in thereview, however, the follow‐up analysis (which demonstrated anon‐significant outcome) was (uniquely for primary outcomes) omitted from the setof tables (i.e. it was not published as a table) but was only briefly outlined under thesubheadings: "Sensitivity analysis" > "Investigatingheterogeneity" (see appendix, below, for quote). As this analysis is not mentionedelsewhere in the review, and is only mentioned in one sentence, it is easy to miss.

To clarify; the unplanned analyses assess the same studies as the pre‐specifiedanalyses, but only the pre‐specified analyses indicate the overall treatmenteffect for all eligible studies pooled together.

The outcomes of the two pre‐specified analyses, using a pooled standardised meandifference (SMD) for all eligible studies, were that exercise therapy (versus passivecontrol) at end of treatment (i.e. analysis 1.19) had a significant positive treatmenteffect (SMD: ‐0.68; 95% CI ‐1.02 to ‐0.35), whereas atfollow‐up the treatment effect was not significant (SMD: ‐0.63; 95% CI‐1.32 to 0.06).

The unplanned primary analysis 1.1 (fatigue at end of treatment) includes threeseparate sub‐analyses which all demonstrate a positive treatment effect, whereasunplanned analysis 1.2 (fatigue at follow‐up) had mixed outcomes with two out ofthree sub‐analyses demonstrating a significant treatment effect.

So, to reiterate, the pre‐specified primary analyses demonstrate that exercisetherapy (versus passive control) had a significant pooled treatment effect on fatigue atend of treatment, but no significant effect at follow‐up. Whereas the unplanned(revised) analyses demonstrate significant treatment effects at end of treatment butmixed outcomes at follow‐up.

The fact that unplanned analysis 1.2 (fatigue at follow‐up) did not consistentlydemonstrate significant treatment effects is not explained with clarity in the maindiscussions of the review. For example, the outcomes are described as follows:"Moderate‐quality evidence showed exercise therapy was more effective atreducing fatigue compared to ‘passive’ treatment or notreatment." (See the appendix, below, for more quoted examples.)

The main discussions in the review also fail to inform the reader that the pooledtreatment effect on fatigue (compared to a passive control), for all eligible studies atfollow‐up, demonstrated a lack of significance, as per the pre‐specifiedprimary analysis.

All Outcomes at Follow‐Up

Despite the limitations associated with self‐report measures [2], physicalfunction (a secondary outcome in the review) is widely considered a useful measure fordemonstrating severity of illness and functional changes in outcomes for chronic fatiguesyndrome [3,4,5]. It may be an especially helpful measure when assessing exercisetherapy because exercise therapy is designed specifically to address physical functionor tolerance to exercise, or both [6]. It seems reasonable to expect physical functionto improve after a course of exercise therapy in chronic fatigue syndrome patients, ifthe therapy is clinically beneficial. The review reports that exercise therapy (whencompared to passive control) has a positive effect on self‐report physicalfunction at end of treatment (analysis 1.5), but this effect is not sustained and therewas no significant treatment effect at follow‐up (see analysis 1.6).

There was also no significant effect on self‐perceived overall health atfollow‐up (see analysis 1.15). Indeed, if we consider all of thehealth‐related pre‐specified (primary and secondary) outcomes for thereview, for exercise therapy versus passive control, then with the exception only ofsleep, all the indicators of health (i.e. fatigue, physical function, overall health,pain, quality of life, depression, and anxiety), showed no significant treatment effectsat follow‐up. (The remaining measures were: serious adverse reactions totreatment; drop‐outs; and 'health resource use' for which a pooledeffect size was not provided but which demonstrated non‐significant differencesbetween intervention arms in all but one of the sub‐analyses.) This means thatonly sleep had a significant positive treatment outcome, at follow‐up, as per thepre‐specified health indicators, for exercise therapy versus passive control.

Put simply, apart from sleep, all the pooled analyses demonstrate that there were nosignificant health benefits from exercise therapy at follow‐up.

These outcomes present a significantly different picture to the impression given by thereview authors in their main discussions, abstract, conclusions and summaries wherein,for example, outcomes in general, including fatigue, physical function and overallhealth, are described as being broadly positive (e.g. it is stated that "patientswith CFS may generally benefit and feel less fatigued following exercise therapy"and: "Exercise therapy had a positive effect on people’s dailyphysical functioning, sleep and self‐ratings of overall health.")Furthermore, some specific erroneous information has been included in the main text tosupport the review authors' interpretation; i.e. the main discussion erroneouslydescribes both physical function and self‐rated overall health as indicating apositive treatment effect at follow‐up, when in fact the outcomes (i.e. analyses1.6 and 1.15) were not significant. The reviewers erroneously assert that: "Apositive effect of exercise therapy was observed both at end of treatment and atfollow‐up with respect to [...] physical functioning (Analysis 1.5; Analysis 1.6)and self‐perceived changes in overall health (Analysis 1.14; Analysis1.15)." (See appendix, below, for full quote.)

The non‐significant outcomes seen in all but one of the pre‐specifiedhealth indicators at follow‐up (exercise vs passive control) were not discussedor explored in the discussions of the Cochrane review. I find this omissiondisappointing because the information would help to inform patients and clinicians ofthe ongoing treatment effects that they might realistically expect from behaviouraltherapies such as exercise therapy. I believe that the review would be more robust andhelpful if it accurately highlighted and adequately explored these issues in the maindiscussions.

The health outcomes at follow‐up would currently be completely lost on a readerwho did not scrutinise the individual analyses of the review but relied upon theabstract or main discussions.

Bias Inherent in Open‐Label Studies

Another issue that I believe is not explored with careful consideration is the possibleimplications relating to a review of purely open‐label studies; i.e. thepossibility that any initial positive treatment effects broadly seen in this review atend of treatment, may entirely, or to some degree, reflect biases inherent in trialmethodologies that are unable to blind patients, therapists or trial investigators tothe treatment arm. The review itself explains that formal blinding "is notinherently possible in trials of exercise therapy" and that this "increasesrisk of bias, as instructors' and participants' knowledge of group assignationmight have influenced the true effect." The trend in this review towardsnon‐significant effects, after treatment has ended, may lend strength to aconcern that the initial self‐report treatment effects are transient and may bethe result of various inherent methodological biases in open‐label trials thatuse self‐report outcome measures [2,7,8]. Potential methodological biases inopen‐label trials using self‐report outcomes may be, for example:inadequate control conditions; self‐reporting bias; therapist allegiance; and/orunplanned changes to trial methodology [7,9].

Readers might be interested to note that, for White 2011, which was the largest trialincluded in the review, the follow‐up data used in the review was at 52 weeks[10] but further follow‐up data has also been published, at a median of 2.5 yearsafter randomisation, which demonstrated no significant differences between interventionarms for the primary outcomes [11].

Summary of Outcomes

In summary, the pre‐specified primary analyses for fatigue were to assess thepooled standardised mean differences. However, the reviewers then made a post‐hocdecision to replace these analyses for which the only rationale provided was anassumption that a standardised mean difference is supposedly "more difficult toconceptualise and interpret". When all of the eligible studies are pooled, as perthe pre‐specified plan, the pooled treatment effect at follow‐up is notsignificant. However, the promotion of the unplanned analyses has allowed the lack of asignificant pooled treatment effect at follow‐up to be overlooked and dismissedin the main analyses and discussions, to the point where the main discussions could beinterpreted to indicate that the treatment effects for fatigue were entirely positive(see appendix, below, for quotes).

I question whether this is an appropriate level of clarity compared to what is expectedfrom a Cochrane review. Cochrane reviews have a reputation of providing transparent,uncomplicated, straightforward and reliable explanations of complex and rigorousanalyses, whereas this review has: used unplanned primary outcomes without a robust orevidence‐based reason for switching outcomes; provided just one sentence toexplain the changes to the pre‐specified primary outcomes; omitted a crucialsensitivity analysis from the tables section; has not reflected the entire range ofoutcomes in the abstract, conclusions or main discussions; and has inaccuratelydescribed outcomes at follow‐up for physical function and overall health.

Justification for Switching Primary Outcomes

The reason given for switching the primary outcomes in the review is: "We realisethat the standardised mean difference (SMD) is much more difficult to conceptualise andinterpret than the normal mean difference (MD) [...]".

However, it is questionable whether the reason given for switching the primary outcomesjustifies such an unplanned fundamental change in the methodology of the review; nojustification is given as to why the reviewers believe that readers would find it easierto interpret the mean scores of a range of disparate fatigue questionnaires, in a seriesof sub‐analyses, rather than a single standardised mean difference for a pooledanalysis of eligible studies. It is not clear to me why it is assumed that a variety ofseparate fatigue scales should be easier to understand and interpret than a singlestandardised mean difference. As the changes to the protocol have had the effect ofchanging the primary outcomes at follow‐up, this means it would be desirable toprovide a well‐reasoned case to deviate from the protocol and switch the primaryoutcomes.

The claim with regards to interpretability raises the question of why standardised meandifferences are adequate for other Cochrane studies, but not this particular study.Cochrane has not adopted a policy of avoiding using standardised mean differences;instead the Cochrane guidelines (section 12.6) encourage their use [12]. So thisdecision appears to be a novel post‐hoc decision specific for this study.

The Cochrane guidelines (section 12.6.1) actually suggest that ordinary meandifferences can be difficult to interpret: "The units of such outcomes [i.e. meandifferences] may be difficult to interpret, particularly when they relate to ratingscales." [12] The guidelines (section 12.6.1) acknowledge that there may bedifficulties in interpreting standardised mean differences: "Without guidance,clinicians and patients may have little idea how to interpret results presented asSMDs." The guidelines do not favour one method over another in general, butdescribe how each may be used for specific purposes; if one wishes to provide an overalltreatment effect for studies that use different measures to measure the same construct,then the standardised mean difference is a standard tool which is used widely inCochrane reviews and other research. The guidelines suggest that "[t]here areseveral possibilities for re‐expressing [standardised means differences] in morehelpful ways".

Implications Related to Changing Trial Protocols and Outcome Switching

The unplanned changes to the review make it vulnerable to potential bias or accusationsof bias; conscious or unconscious personal or professional preferences have thepotential to affect post‐hoc decisions with respect to methodology. Even ifinvestigators are scrupulous in the rigour of their decision making, unexpected biaseshave the potential to creep into unplanned decisions, which is an issue that factorsinto the reasons why pre‐trial plans (e.g. trial registers and protocols) havebecome widespread [7], and are used for Cochrane reviews [12].

The Cochrane Guidebook for reviewers (Section: 2.1; "Rationale forprotocols") [12] explains: "Post hoc decisions made when the impact on theresults of the research is known, such as excluding selected studies from a systematicreview, are highly susceptible to bias and should be avoided."

In the same paragraph, the guidelines also state: "While every effort should bemade to adhere to a predetermined protocol, this is not always possible orappropriate."

However, it seems that, in this case, every effort was not made to adhere to theprotocol because the unplanned changes seem to be based on preference rather thennecessity, and the pre‐planned analyses have not been shown to be inferior,inadequate or inappropriate.

Conclusion

I find the changes to the protocol to be of particular concern for the followingreasons:

1. The final primary analyses are unplanned and have replaced adequate, and arguablymore helpful, pre‐specified analyses;

2. The rationale provided for the changes was neither robust nor evidence‐basedbut was based upon an assumption;

3. The changes have significantly altered the main outcomes and affected theinterpretation of the review (i.e. changed one of the two main outcomes from aninsignificant treatment effect to an inconsistent but broadly positive effect); and

4. The pre‐planned analysis for fatigue at follow‐up, has been omittedfrom the tables section of the review which, as far as I understand, is a uniqueomission for the primary outcomes.

For the sake of simplicity, rigour, and transparency, I ask the review team to reassessthe review, including the decision to switch the primary outcomes, and to:

1. Amend the review as per the guidelines in the Cochrane Guidebook quoted above (i.e."every effort should be made to adhere to a predetermined protocol"), and torevert to the pre‐planned primary analyses; and

2. Clearly and unambiguously explain that all but one health indicator (i.e. fatigue,physical function, overall health, pain, quality of life, depression, and anxiety, butnot sleep) demonstrated a non‐significant outcome for pooled treatment effects atfollow‐up for exercise therapy versus passive control; and

3. Include a rigorous assessment of how the potential for bias may have affectedoutcomes of the open‐label studies in this review, with consideration of the useof self‐report measures in open‐label studies.

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Appendix

Relevant Quotes from the Review

Differences between protocol and review

"[...] in the protocol it is stated, "where results for continuous outcomeswere presented using different scales or different versions of the same scale, we usedstandardised mean differences (SMDs)." We realise that the standardised meandifference (SMD) is much more difficult to conceptualise and interpret than the normalmean difference (MD); therefore we decided to report both MDs and SMDs in the Resultssection. In general, MDs are reported in the main Results section, whereas SMDs aresupplied under the "Sensitivity and subgroup analysis" subheading."

Quotes detailing the outcomes of the pre‐specified analyses:

Effects of interventions > Exercise therapy versus treatment as usual, relaxation orflexibility > Sensitivity analysis

Fatigue, End of Treatment

"At end of treatment, fatigue was measured and reported on different scales, andwe performed a sensitivity analysis in which all available studies were pooled using anSMD method. This strategy led to a pooled random‐effects estimate of ‐0.68(95% CI ‐1.02 to ‐0.35), but the analysis suffered from considerableheterogeneity (I² = 78%, P value < 0.0001; Analysis 1.19). The observedheterogeneity was caused mainly by the deviating results presented in Powell 2001.Exclusion of Powell 2001 gave rise to a pooled SMD of ‐0.46 (95% CI ‐0.63to ‐0.29) – an estimate that was not associated with heterogeneity (I²= 13%, P value 0.33)."

Fatigue, Follow‐up

"At follow‐up, the four available studies (Jason 2007; Powell 2001; Wearden2010; White 2011) measured and reported fatigue on different scales, and we performed asensitivity analysis in which all available studies were pooled using an SMD method. Thepooled SMD estimate is ‐0.63 (95% CI ‐1.32 to 0.06), but heterogeneity wasextensive (I² = 93%, P value < 0.00001)."

Quotes from main discussion sections of review re effectiveness of graded exercise(compared with passive control) on fatigue

Abstract > Authors' conclusions

"Patients with CFS may generally benefit and feel less fatigued following exercisetherapy, and no evidence suggests that exercise therapy may worsen outcomes."

Plain language summary > What does evidence from the review tell us?

"Moderate‐quality evidence showed exercise therapy was more effective atreducing fatigue compared to ‘passive’ treatment or notreatment."

 Discussion > Summary of main results

"When exercise therapy was compared with 'passive control,' fatigue wassignificantly reduced at end of treatment (Analysis 1.1)."

Quotes selectively reporting secondary outcomes

 Abstract > Authors' conclusions

"A positive effect with respect to sleep, physical function andself‐perceived general health has been observed, but no conclusions for theoutcomes of pain, quality of life, anxiety, depression, drop‐out rate and healthservice resources were possible."

Plain language summary > What does evidence from the review tell us?

"Exercise therapy had a positive effect on people’s daily physicalfunctioning, sleep and self‐ratings of overall health."

Erroneous reporting of outcomes for physical function and overall health atfollow‐up

Discussion > Summary of main results

"A positive effect of exercise therapy was observed both at end of treatment andat follow‐up with respect to sleep (Analysis 1.12; Analysis 1.13), physicalfunctioning (Analysis 1.5; Analysis 1.6) and self‐perceived changes in overallhealth (Analysis 1.14; Analysis 1.15)."

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References

1. Larun L, Brurberg KG, Odgaard‐Jensen J, Price JR. Exercise therapy forchronic fatigue syndrome. Cochrane Database Syst Rev. 2016; CD003200.

2. Kindlon TP. Objective measures found a lack of improvement for CBT & GET in thePACE Trial: subjective improvements may simply represent response biases or placeboeffects in this non‐blinded trial. BMJ Rapid Response 2015.http://www.bmj.com/content/350/bmj.h227/rr‐10 (accessed May 18,2016).

3. Buchwald D, Pearlman T, Umali J, Schmaling K, Katon W. Functional status in patientswith chronic fatigue syndrome, other fatiguing illnesses, and healthy individuals. Am JMed. 1996;101:364‐70.

4. Cook DB, Lange G, DeLuca J, Natelson BH. Relationship of brain MRI abnormalities andphysical functional status in chronic fatigue syndrome. Int J Neurosci.2001;107:1‐6.

5. Crawley E, Sterne JA. Association between school absence and physical function inpaediatric chronic fatigue syndrome/myalgic encephalopathy. Arch Dis Child.2009;94:752‐6.

6. Bavinton J, Darbishire L, White PD. PACE manual for therapists; graded exercisetherapy for CFS/ME. 2004. Internet.http://www.wolfson.qmul.ac.uk/images/pdfs/5.get‐therapist‐manual.pdf(accessed May 18, 2016).

7. Moher D, Hopewell S, Schulz KF, et al. CONSORT 2010 explanation and elaboration:updated guidelines for reporting parallel group randomised trials. BMJ. 2010;340:c869.

8. Wilshire CE. Re: Tackling fears about exercise is important for ME treatment,analysis indicates. BMJ Rapid Response 2015.http://www.bmj.com/content/350/bmj.h227/rr‐7 (accessed May 18,2016).

9. Van de Mortel TF. Faking it: social desirability response bias in self‐reportresearch. Australian Journal of Advanced Nursing, The. 2008;25:40.

10. White PD, Goldsmith KA, Johnson AL, et al. Comparison of adaptive pacing therapy,cognitive behaviour therapy, graded exercise therapy, and specialist medical care forchronic fatigue syndrome (PACE): a randomised trial. Lancet 2011; 377:823‐36.

11. Sharpe M, Goldsmith KA, Johnson AL, et al. Rehabilitative treatments for chronicfatigue syndrome: long‐term follow‐up from the PACE trial. LancetPsychiatry 2015; 2:1067–74.

12. Higgins JPT, Green S (editors). Cochrane Handbook for Systematic Reviews ofInterventions. Version 5.1.0 [updated March 2011]. The Cochrane Collaboration, 2011.Internet.http://handbook.cochrane.org (accessed May 12, 2016).

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I do not have any affiliation with or involvement in any organisation with a financialinterest in the subject matter of my comment.

Reply

Dear Robert Courtney

Thank you for your ongoing and detailed scrutiny of our review. We have the greatestrespect for your right to comment on and disagree with our work, but in the spirit ofopenness, transparency and mutual respect we must politely agree to disagree.

Presenting health statistics in a way that makes sense to the reader is a challenge.Statistical illiteracy is – according to Girgerenzer and co‐workers –common in patients, journalists, and physicians (1). With this in mind we have presentedthe results as mean difference (MD) related to the relevant measurement scales, forexample Chalder Fatigue Scale, as well as standardised mean difference (SMD). The use ofMD enables the reader to transfer the results to the relevant measurement scale directlyand judge the effect in relation to the scale. We disagree that presenting MD and SMDrather than SMD and MD is an important change, and we disagree with the claim that theanalysis based on MD and SMD are inconsistent. This has been discussed as part of thepeer‐review process. Confidence intervals are probably a better way to interpretdata that P values when borderline results are found (2). Interpreting the confidenceintervals, we find it likely that exercise with its SMD on ‐0.63 (95% CI‐1.32 to 0.06) is associated with a positive effect. Moreover, one should alsokeep in mind that the confidence interval of the SMD analysis are inflated by theinclusion of two studies that we recognize as outliers throughout our review. Absence ofstatistical significance does not directly imply that no difference exists.

All the included studies reported results after the intervention period and this is themain results. The results at different follow‐up times are presented in the text,but we have only included data available at the last search date, 9 may 2014. When thereview is updated, a new search will be conducted to find new, relevant follow up dataand new studies. As a general comment, it is often challenging to analysefollow‐up data gathered after the formal end of a trial period. There is always achance that participants may receive other treatments following the end of the trialperiod, a behaviour that will lead to contamination of the original treatment arms andchallenge the analysis.

Cochrane reviews aim to report the review process in a transparent way, which enablesthe reader to agree or disagree with the choices made. We do not agree that thepresentation of the results should be changed. We note that you read thisdifferently.

Regards,

Lillebeth Larun

1. Girgerenzer G, Gaissmaier W, Kurtz‐Milcke E, Schwartz LM, Woloshin S. HelpingDoctors and Patients Make Sense of Health Statistics. Pyschological Science in thePublic Interest, 2008;8:(2):53‐96.http://www.psychologicalscience.org/journals/pspi/pspi_8_2_article.pdf.

2. Hackshaw A and Kirkwood A. Interpreting and reporting clinical trials with resultsof borderline significance.BMJ 2011;343:d3340 doi: 10.1136/bmj.d3340

Contributors

Feedback submitted by: Robert Courtney

Response submitted by: Lillebeth Larun

Summary

Comment: A query regarding the way outcomes for physical function and overall healthhave been described in the abstract, conclusion and discussions of the review.

I would like to query the way that the outcomes for both physical function and overallhealth have been reported in the abstract, conclusion and in the main discussion sectionof the current version (version 4) of the Cochrane review by Larun et al., dated 7February 2016 [1].

The abstract, conclusion and main discussion section unambiguously indicate that therewas a positive treatment effect on both physical function and overall health, inrelation to exercise therapy compared to a passive control.

For example, with respect to exercise therapy versus passive control, the"authors' conclusions" in the abstract state without qualification that:"A positive effect with respect to sleep, physical function andself‐perceived general health has been observed[...]". Another section ofthe review ("What does evidence from the review tell us?") asserts that:"Exercise therapy had a positive effect on people’s daily physicalfunctioning, sleep and self‐ratings of overall health." The "summary ofmain results" unequivocally states that: "A positive effect of exercisetherapy was observed both at end of treatment and at follow‐up with respect tosleep (Analysis 1.12; Analysis 1.13), physical functioning (Analysis 1.5; Analysis 1.6)and self‐perceived changes in overall health (Analysis 1.14; Analysis1.15)." (Please see the appendix, below, to read these quotes in full.)

However, upon careful consideration of the relevant analyses, it seems that there werenot consistent positive treatment effects for either physical function or overall healthin relation to exercise therapy versus passive control. Instead, for both of thesevariables, there was a significant treatment effect only at end of treatment, but not atfollow‐up.

The relevant analyses are 1.5 (end of treatment) and 1.6 (follow‐up) forself‐report physical function, and 1.14 (end of treatment) and 1.15(follow‐up) for self‐report overall health.

Analysis 1.5 assessed the pooled treatment effect on physical function at end oftreatment for all eligible studies, and demonstrates a significant effect. Analysis 1.6used the same criteria but at follow‐up, and demonstrates that there was not asignificant effect for physical function at follow‐up.

Analysis 1.14 assessed the pooled treatment effect on overall health at end oftreatment for all eligible studies, and demonstrates a significant effect. Analysis 1.15used the same criteria but at follow‐up, and demonstrates that there was not asignificant effect for overall health at follow‐up.

The lack of a significant treatment effect at follow‐up is clearly illustratedby analyses 1.6 and 1.15.

These outcomes are also confirmed in the analysis section of the review where, inrelation to the difference between exercise therapy versus passive control, for physicalfunction at follow‐up, it is confirmed that: "[...] little or no differencecannot be ruled out." And for overall health at follow‐up, it is confirmedthat "the confidence interval implies inconclusive results".

I believe that these outcome are not reflected accurately in the abstract, the maindiscussions or the conclusions of the review; specifically the extracts that are quotedabove and in the appendix below. For example, the "summary of main results"specifically claims that positive treatment effects are demonstrated by analyses 1.6 and1.15, but these analyses actually demonstrate an absence of significant treatmenteffects. The discussion claims: "A positive effect of exercise therapy was observed[...] at follow‐up with respect to [...] physical functioning ([...]Analysis 1.6)and self‐perceived changes in overall health ([...]Analysis 1.15)."

It is generally understood that a "positive" treatment effect equates to asignificant effect, and I believe that the Cochrane text should reflect this, or atleast clarify that the term "positive effect" is being used to indicate a lackof significance.

It is likely that many readers will not read the full report or scrutinise eachindividual analysis but will read only the abstract, main discussions or conclusions, soI believe it is important for the discussions to carefully and accurately reflect theoutcomes of the analyses.

Cochrane has a reputation for upholding the highest standards including with respect toexplaining outcomes in accurate and straightforward language. With this in mind, Irequest that the Cochrane review team kindly review the apparent disparities describedabove and amend the text of the discussions and conclusions where appropriate, in orderto reflect the lack of a significant treatment effect for physical function and overallhealth at follow‐up with respect to exercise therapy versus passive control.

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Appendix

Quotes from the review:

Abstract > Authors' conclusions

"Patients with CFS may generally benefit and feel less fatigued following exercisetherapy, and no evidence suggests that exercise therapy may worsen outcomes. A positiveeffect with respect to sleep, physical function and self‐perceived general healthhas been observed, but no conclusions for the outcomes of pain, quality of life,anxiety, depression, drop‐out rate and health service resources werepossible."

What does evidence from the review tell us?

"Moderate‐quality evidence showed exercise therapy was more effective atreducing fatigue compared to ‘passive’ treatment or notreatment. Exercise therapy had a positive effect on people’s dailyphysical functioning, sleep and self‐ratings of overall health."

Summary of main results

"[...] A positive effect of exercise therapy was observed both at end of treatmentand at follow‐up with respect to sleep (Analysis 1.12; Analysis 1.13), physicalfunctioning (Analysis 1.5; Analysis 1.6) and self‐perceived changes in overallhealth (Analysis 1.14; Analysis 1.15)."

‐‐‐

Reference

1. Larun L, Brurberg KG, Odgaard‐Jensen J, Price JR. Exercise therapy forchronic fatigue syndrome. Cochrane Database Syst Rev. 2016; CD003200.

‐‐‐

I do not have any affiliation with or involvement in any organisation with a financialinterest in the subject matter of my comment.

Reply

Thank you for your ongoing and detailed scrutiny of our review. We have the greatestrespect for your right to comment on and disagree with our work, but in the spirit ofopenness, transparency and mutual respect we must (again) politely agree todisagree.

All the included studies reported results after the intervention period and this is themain result. The results at different follow‐up times are presented in the text.It can be noted that the quality of the evidence is higher for theend‐of‐treatment time point because more trials are included, and hence,we do not agree that it is wrong to give higher weight to these results in the abstract.Additionally, it is often challenging to analyse follow‐up data gathered afterthe formal end of a trial period. There is always a chance that participants may receiveother treatments following the end of the trial period, a behaviour that will lead tocontamination of the original treatment arms and challenge the analysis.

Cochrane reviews aim to report the review process in a transparent way, which enablesthe reader to agree or disagree with the choices made. We do not agree that thepresentation of the results should be changed. We note that you read thisdifferently.

Contributors

Feedback submitted by: Robert Courtney

Response submitted by: Lillebeth Larun

Summary

Comment: I'm concerned regarding your conclusion that no evidence suggests thatexercise therapy may worsen outcome, as you have stated that no conclusions werepossible for the drop‐out rate.

Whilst I appreciate that you are unable to draw conclusions about drop‐out ratesdue to insufficient data, is it perhaps potentially misleading or ambiguous to summarisethat in general patients may benefit from GET with there being no evidence for symptomsworsening, when there are a researchers that support the claim that CBT/GET isdetrimental to the long term prognosis of patients with ME/CFS. Without assessment ofdata concerning those whom have dropped out (those most likely to experience worseningsymptoms) the conclusions you have stated could prove harmful if taken as encouragementfor GPs to place their patients on GET regimes.

I do not question your analysis of the data, but rather I am concerned with the way inwhich you have expressed your findings.

Reply

Thank you for your interest in the review and your comment.

In our systematic review, we aim to summarise the effect estimates associated with theuse of exercise therapy for patients diagnosed with chronic fatigue syndrome CFS/ME. Wedecided to rely on data from randomised controlled trials (RCT), as RCTs provide muchmore robust data than for example anecdotal evidence. We held serious adverse reactions(SAR) and serious adverse events (SAE) as our primary outcome, whereas thedrop‐out rate was added as a secondary outcome.

Systematic reviews based on aggregated data dependent on the data reported in theincluded trials. One trial reported that SARs and SAEs were rare in both groups,suggesting that the difference between the groups is small when measured in absoluteterms. Analysis of drop‐out rates did not reveal statistical differences betweenthe groups, and we cannot conclude that exercise is associated with higherdrop‐out rates. Even if we had seen differences between the groups, however,drop‐out rates must be interpreted with caution. It is important to be aware thatdrop‐out is not a direct measure of harm. There might be several reasons patientsdrop out, and some of these reasons are not expected to distribute equally between thegroups. Harm is one possible reason for drop‐out, but patients may also withdrawbecause they are unhappy with the randomisation (preconceptions), because they feelbetter or because they don’t experience the expected level ofimprovement etc.

Systematic reviews aim to bring the best evidence to the clinical encounter, but shareddecision making includes patient preferences and clinical expertise when a treatmentplan is decided upon.

Contributors

Feedback submitted by: Richard Gardner

Response submitted by: Lillebeth Larun

Summary

It has been raised by others that the Cochrane review erroneously places ME/CFS in itsmental health category. The response provided by Cochrane when this issue was raiseddoes not inspire confidence in their knowledge/advice on the disease. ME/CFS was thesubject of a comprehensive literature review carried out by the USA National Academy,published in 2015 this report categorically determined that the disease ME/CFS is not amental health disorder. The large volume of biomedical research findings of a wide rangeof organic abnormalities is also at odds with a mental health disorder. Further more theWorld Health Organisation has categorised ME/CFS as a neurological disease. The NationalCentre for Neuroimmune and Emerging Diseases has patented a blood test for the diseaseand is in the early stages of validating it. It would be much appreciated if Cochranewould categorise ME/CFS in the appropriate group i.e. along with other neurologicaldiseases such as Parkinson's, Huntington's, multiple sclerosis etc. Delightedto see that the latest review has been suspended and look forward to its replacementwith a review that bases its findings on OBJECTIVE outcome data.

Reply

Many thanks for your comment and for noting recent categorisations of Chronic fatiguesyndrome (CFS)/myalgic encephalomyelitis (or encephalopathy) (ME). Feedback on reviewsis normally dealt with by the relevant review author, but in this case as your queryrelates more to an organisational management issue, we are responding on behalf of theCochrane Common Mental Disorders (CMD) Review Group and the Cochrane Editor inChief.

We value your observations about the placement of CFS/ME reviews in The CochraneLibrary. We want our evidence to properly support those with lived experience of CFS/MEand to ensure that the CFS/ME community have confidence in our portfolio of reviews. Weare also aware that the hosting of this topic by the Cochrane CMD Review Group has beenantagonistic to some in the CFS/ME community.

Cochrane has recently created eight new Networks of Cochrane Review Groups (CRGs). Theformation of these networks provides a timely opportunity to review the scope of allCRGs and to consider changes where appropriate. In response to concerns raised bymembers of the CFS/ME community, Cochrane has been considering repositioning theeditorial oversight of CFS/ME reviews. The Cochrane CMD Review Group currently sitswithin the Brain, Nerves and Mind (BNM) Network. In the future, reviews on this topicmight sit with another Cochrane Review Group within the BNM Network, or they mighttransfer to another Network altogether, such as the Long Term Conditions and Ageing 2Network. Please be reassured that this is currently under consideration and a decisionis anticipated before the end of 2018.

We would also like to refer you to the recent published note for the latest informationabout the status of this particular review ‘This review is subject to anongoing process of review and revision following the submission of a formal complaint tothe Editor in Chief. Cochrane considers all feedback and complaints carefully, andrevises or updates reviews when it is appropriate. The review author team have advisedus that a resubmission of this review is imminent. A decision on the status of thisreview will be made once this resubmission has been through editorial process, which weanticipate will be towards the end of November 2018’.

Contributors

Feedback submitted by: Adrienne Wooding

Response: Peter Coventry and Jessica Hendon

Peter Coventry is the Feedback Editor of the CMD Review Group and Jessica Hendon is theManaging Editor of the CMD Review Group. No other conflicts of interest declared.

Summary

A few questions about where the disease ME/CFS will be placed by Cochrane in thefuture. If Cochrane moves myalgic encephalomyelitis/chronic fatigue syndrome (ME/CFS)into the Long term conditions and Aging Network, will it be moved into the Metabolic andEndocrine Disorders review group within this network? I'm making this assumption,based on the metabolic abnormalities, found in people with ME/CFS, when objectivemetabolic exercise tests, are carried out, as per "Cardiopulmonary Exercise TestMethodology for Assessing Exertion Intolerance in Myalgic Encephalomyelitis/ChronicFatigue Syndrome" ‐https://www.ncbi.nlm.nih.gov/pubmed/30234078? If, in the alternative, Cochranedecides that ME/CFS is to remain in the Brain, Nerves and Mind (BNM) Network, will it bemoved into a separate group of its own? As whilst the disease fits within the BNMNetwork, it doesn't fit into any of the listed Cochrane Review Groups. The closestfit is probably the Multiple Sclerosis and rare diseases of the CNS? However, given thatME/CFS is thought to be more prevalent that multiple sclerosis and is not rare, itdoesn't really fit into this group. Will a new Cochrane Review Group, be made forME/CFS, that is in line with the published biomedical and physiological findings?

Reply

Many thanks for your follow‐on comments related to Cochrane’sdecision to consider repositioning its chronic fatigue syndrome (CFS)/myalgicencephalomyelitis (or encephalopathy) (ME) reviews. The repositioning of the editorialoversight of CFS/ME reviews is ongoing. Your feedback has been forwarded to the CochraneEditor in Chief so that it can be considered as part of this process.

Contributors

Feedback submitted by: Adrienne Wooding

Response: Jessica Hendon (Managing Editor of the Cochrane Common Mental DisordersReview Group)

Summary

Recently I have published a reanalysis of this Cochrane review. Unfortunately there aremany problems with the review and the trials in it. For example, P‐Hacking,extensive endpoint changes, overlap in entry/recovery criteria, selecting patients whodon't have the disease, ignoring null effects, relying on subjective outcomes inunblinded trials and ignoring the absence of objective improvement. The reanalyses whichlooked at the objective outcomes showed that graded exercise therapy is not an effectivetreatment for ME/CFS. The studies in the review do not provide any evidence that gradedexercise therapy is safe, on the other hand, patient evidence and the literature showthat it is not safe.

The open access reanalysis can be read here:https://journals.sagepub.com/doi/full/10.1177/2055102918805187

Reply

Many thanks for your feedback on this review. Cochrane recognises the importance of thereview and is committed to providing a high quality review that reflects the bestcurrent evidence to inform decisions. The Editor in Chief is currently holdingdiscussions with colleagues and the author team to determine a series of steps that willlead to a full update of this review. Your feedback will be considered as part of thisprocess so that it can inform future versions of the review. These discussions will beconcluded as soon as possible.

Contributors

Feedback submitted by: Mark Vink

Response: Jessica Hendon (Managing Editor of the Cochrane Common Mental DisordersReview Group)

Cluster trials

Studies often employ 'cluster randomisation' (such as randomisation byclinician or practice), but analysis and pooling of clustered data pose problems. First,study authors often fail to account for intraclass correlation in clustered studies,leading to a 'unit of analysis' error (Bland1997) whereby P values are spuriously low, confidence intervals unduly narrowand statistical significance overestimated. This causes type I errors (Bland 1997;Gulliford 1999).

No cluster RCTs were identified in this version of the review. Should such studies beidentified in future updates, we will use the following methodological approach. Whenclustering has not been accounted for in primary studies, we will present data in atable, with a (*) symbol to indicate the presence of a probable unit of analysiserror. We will seek to contact first authors of studies to obtain intraclass correlationco‐efficients for their clustered data and to adjust for this by using acceptedmethods (Gulliford 1999). When clustering isincorporated, we will present the data as if from a parallel‐group randomisedstudy, but adjusted for the clustering effect. We will additionally exclude such studiesin a sensitivity analysis.

If cluster studies are appropriately analysed by taking into account intraclasscorrelation co‐efficients and relevant data documented in the report, synthesiswith other studies will be possible using the generic inverse variance technique.

Cross‐over trials

A major concern of cross‐over trials is the potential for carry‐overeffect. This occurs when an effect (e.g. pharmacological, physiological, psychological)of treatment in the first phase is carried over to the second phase. As a consequence ofentry to the second phase, participants can differ systematically from their initialstate despite a wash‐out phase. For the same reason, cross‐over trials arenot appropriate when the condition of interest is unstable (Elbourne 2002). As both effects are very likely inCFS/ME, randomised cross‐over studies were eligible but only when data up to thepoint of first cross‐over were used. Data from the subsequent (second) period ofthe cross‐over trial were not considered for analysis.

Studies with multiple treatment groups

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