My comments to the Cochrane review

I plan to submit these comments to the current version of the Cochrane review next week (sorry I took me so long to write these down - long story). I thought it might be useful to post it here on S4ME first in case someone notices any mistakes so that I can still correct these before formally submitting it.

Comments to the Cochrane review on exercise therapy for CFS
I appreciate the efforts made by Cochrane and the authors to correct some of the errors in the previous version of this review. There are however some major problems that remain and significantly impact the results and conclusion. I hope to clarify these in my comments below. All my comments concern the main comparison of graded exercise therapy (GET) versus a passive control condition (treatment as usual or relaxation/flexibility therapy).

‘Long-term’ follow-up results downplayed
The review highlights assessments made directly after treatment ended and downplays assessments made several months later even though the latter formed the primary outcome for the trials that provide most of the data.

The authors’ conclusions in the abstract for example states: “Exercise therapy probably has a positive effect on fatigue in adults with CFS compared to usual care or passive therapies.” At follow-up, however, the difference in fatigue scores between the exercise- and passive control groups were no longer statistically significant (Analysis 1.2). The three largest trials which provide most of the data in this Cochrane review (PACE, FINE, and Powell et al., 2001) defined their primary outcome at this follow-up assessment 52 to 70 weeks post-randomization. Their intent was likely to reduce bias as one of these trials, the FINE trial, noted that “assessment at week 70 is required because short-term assessments of outcome in a chronic health condition such as CFS/ME can be misleading.” Using interim assessments made directly after treatment ended, to claim that “exercise therapy probably has a positive effect on fatigue” seems unwarranted as the majority (75%) of the data for this comparison comes from trials that defined their primary outcome several months later. At that time point, the pooled between-group differences were no longer statistically significant. This is true for other outcomes as well, such as physical functioning.

The review frequently uses the term ‘long-term follow up’ for assessments made 52 to 70 weeks post-randomization. This might be confusing to readers. The long-term follow-up results of the largest trial, the PACE trial, for example, refer to assessments made 2 years or longer after randomization as this is the terminology used by the trial authors in their protocol and publications. (1) The term ‘long-term follow up’ doesn’t normally refer to the assessments made a half year after treatment ended as these were reported as the main results of the trial. In the PACE-trial, patients in the GET group also received booster-sessions 36 weeks post-randomization. This indicates that the assessments 52 weeks post-randomization are not adequately described as a ‘long-term’ follow-up.

Fatigue post-treatment should be rated as low instead of moderate quality evidence
The certainty of evidence for all outcomes in comparison 1 (exercise therapy versus treatment as usual, relaxation or flexibility) was assessed as low to very low according to the GRADE system. (2) The sole exception is fatigue measured at the end of treatment which was assessed as providing moderate certainty evidence. It is unclear why the certainty of evidence for this outcome wasn’t downgraded for inconsistency and/or imprecision as was the case for physical function measured at the end of treatment.

The meta-analysis of post-treatment fatigue was associated with considerable heterogeneity (I2 = 80%, P< 0.0001). This heterogeneity was mainly caused by one outlier, the trial by Powell et al. If this trial is excluded, heterogeneity is reduced to acceptable levels (I2 = 26%, P = 0.24) but the standardized mean difference (SMD) drops by one third, from -0.66 to -0.44. This corresponds to a 2.3 point instead of 3.4 point reduction when re-expressed on the 33-point Chalder Fatigue Scale, a difference that may no longer be clinically meaningful. A minimal important difference (MID) of 3 points on the Chalder Fatigue Scale has previously been used in an exercise trial for CFS. (3)

Fatigue post-treatment could also be downgraded for imprecision as the confidence interval crosses the line of no clinically significant effect. The 95% confidence interval of the SMD for fatigue (.31-1.10) corresponds to a 1.6 to 5.3 point interval when re-expressed on the 33-point Chalder Fatigue Scale. For continuous outcomes, the GRADE handbook recommends: “Whether you will rate down for imprecision is dependent on the choice of the difference (Δ) you wish to detect and the resulting sample size required.” Given that the authors of this Cochrane review specified a MID of 2.3 for the Chalder Fatigue Scale and that a MID of 3 points or higher has been used for CFS (3) and other chronic conditions (4,5), it seems warranted to downgrade this outcome for imprecision.

I recognize that for both inconsistency and imprecision the case isn’t clear-cut. The GRADE handbook, however, writes that if there is a borderline case to downgrade the certainty of evidence for two factors, it is recommended to downgrade for at least one of them. The handbook writes: “If, for instance, reviewers find themselves in a close-call situation with respect to two quality issues (risk of bias and, say, precision), we suggest rating down for at least one of the two.” (2) Therefore the outcome fatigue measured at the end of treatment should preferably be downgraded to low certainty evidence.

Problems with the Chalder Fatigue Scale
Fatigue is the primary outcome measure of this review and it has the largest effect size. All exercise trials in the review used a version of the Chalder Fatigue Scale to measure fatigue. The sole exception is the trial by Jason et al., 2007 which only provided assessments at follow-up and didn’t report a statistically significant difference between the exercise and control group. Consequently, a large part of the conclusion of this review is based on how trial participants filled in different versions of the Chalder Fatigue Scale after receiving exercise therapy.

Unfortunately, several problems have been noted with the Chalder Fatigue Scale and its scoring systems. (6,7) The questionnaire was not included in the Common Data Elements (CDEs) formulated for Myalgic Encephalomyelitis/Chronic Fatigue Syndrome (ME/CFS) in 2017. Instead, the CDE listed 9 other questionnaires for the assessment of fatigue in patients with ME/CFS. (8) In my comments below I hope to clarify that some of the issues with the Chalder Fatigue Scale could have significantly impacted the results and conclusion of the Cochrane review.

Ceiling effects
Ceiling effects have been noted for the Chalder Fatigue Scale especially if bimodal scoring (0-11) is used. (9,10) In the trial by Powell et al., for example, patients had a fatigue score of 10.28 out of 11 points at baseline. In the FINE Trial, the second-largest trial in the review, patients had a score of 10.45 out of 11 points at baseline. An increase in fatigue might not be recorded in these trials as most participants already had a score close to the maximum on the scale.

If a worsening of fatigue is equally likely in the exercise- and passive control group, ceiling effects might not have favored one over the other. But this assumption is rather unlikely as a worsening of symptoms following (physical) exertion is one of the characteristics of CFS (11) and in multiple surveys CFS patients report to have worsened following GET. (12,13) More generally, participating in an exercise intervention has been shown to increase the relative risk of non-serious adverse events. (14) Therefore, it seems reasonable to assume that more CFS patients in the exercise than in the control group could have experienced an increase in fatigue after scoring (close to) the maximum on the Chalder Fatigue Scale. This would have distorted the results and caused a false impression of improvement.

I would like to spell out this argument more clearly as it could easily be overlooked or misinterpreted. To clarify we could use an imaginary exercise trial where all participants have a fatigue score of 9 out of 11 at the start of the trial. In the passive control group, half of the participants’ fatigues scores increase with 2 points while in the other half it decreases with 2 points. The average of the control group at the end of the trial would still be 9 out of 11. In the exercise group, half of the participants’ fatigues scores increase with 6 points while for the other half it decreases with 6 points. Their average is not 9 but 7 out of 11 because an increase of 6 points could not be fully recorded on the scale. Something similar might have happened in exercise trials for CFS where patients scored close to the maximum on the Chalder Fatigue Scale at the start of the trial.

Interpretation problems
The Chalder Fatigue Scale also has problems of interpretability as it asks trial participants if they experience fatigue symptoms less than usual compared to when they were last well. (6,7) When questionnaires are completed after the treatment ends, patients might be confused and compare themselves to how they were before the trial started, rather than when they were last well. This misinterpretation occurred in a Japanese trial exploring the effects of yoga in CFS. (15) One of the participants recorded very low scores on the Chalder Fatigue Scale post-treatment because she was confused by the baseline comparison. The authors note: “whereas the intent was to compare her current condition to when she last felt well, she had been sick and almost bed-bound for some years so she misunderstood ‘than usual’ as ‘than the days sick in bed’ because it had become a regular part of life for her.” In a trial on cognitive behavioral therapy in multiple sclerosis, patients in both the intervention and control group reported having less fatigue on the Chalder Fatigue Scale than healthy controls at the end of the trial. (16) A plausible explanation is that patients wanted to indicate that they had less fatigue since the start of the trial rather than compared to when they were last well. These interpretation problems question the validity of the Chalder Fatigue Scale in measuring improvements over time.

In this Cochrane review, none of the problems with the Chalder Fatigue Scale are mentioned or taken into consideration when interpreting effect sizes.

Bias due to lack of blinding
The review focuses on patient-reported outcome measures (PROMs) in trials where blinding of patients and healthcare providers was not practically feasible. This creates a high risk of response- and expectancy bias. (17,18) The authors have downgraded the certainty of evidence of almost all outcomes with one level according to the GRADE system. As I hope to explain in this section, there are reasons to think this does not adequately address the risk of bias involved.

A 2014 review by Hrobjartsson et al. on trials that compared blinded and non-blinded groups, reported an average difference in effect size for patient-reported outcomes of -0.56. (19) This is very similar to the effect sizes reported in this review and suggests that bias due to a lack of blinding questions not only the certainty of evidence but the evidence itself. Response- and expectancy bias were likely quite high in the exercise trials included in the review as the intervention included close collaboration with therapists and strong statements designed to raise patients’ expectations of treatment. A therapist manual of the PACE trial, for example, said about patients: “[…] it is important that you encourage optimism about the progress that they may make with this approach. You can explain the previous positive research findings of GET and show in the way you discuss goals and use language that you believe they can get better.” (20)

Unfortunately, the review does not consider the possibility that the small to moderate effect sizes found could be the result of bias associated with a lack of blinding patients and therapists. Downgrading the certainty of evidence with only one level seems to underestimate the risk of bias involved.

Objective outcomes not reported
One of the major problems with the review is that except for various data on health service resources from the PACE trial, it doesn’t report on objective outcome measures that were included in the eight exercise trials. Objective outcomes are thought to be more robust than PROMs towards bias associated with a lack of blinding. One of the largest studies on bias in randomized trials, for example, concluded: “Our results suggest that, as far as possible, clinical and policy decisions should not be based on trials in which blinding is not feasible and outcome measures are subjectively assessed. Therefore, trials in which blinding is not feasible should focus as far as possible on objectively measured outcomes…” (21)

The authors of the Cochrane review did the opposite by focusing on subjective outcomes and largely ignoring objective outcomes. The eight exercise trials in this review have data on employment, activity levels, and various kinds of fitness tests. These did not show the improvements seen on the subjective outcomes measures (such as fatigue questionnaires) that were summarized and highlighted in this review. In 2018, Vink & Vink-Niese provided an overview of objective outcomes in the eight exercise trials for CFS in the Cochrane review. They concluded:

“The analysis of the objective outcomes in the trials provides sufficient evidence to conclude that graded exercise therapy is an ineffective treatment for myalgic encephalomyelitis/ chronic fatigue syndrome.” (7)​

The lack of reporting on objective outcomes was already noted by Kindlon T and Courtney R after a major update of the Cochrane review in 2015. The authors of the review responded that it was not possible to report on objective measurements as the protocol did not include them. The protocol published by Edmonds et al. in 2001, however, does mention “employment status”, and “timed walking tests and tests of strength or aerobic capacity” as outcomes. (22) It is unclear why these weren’t reported.

The review as it currently stands gives the impression that outcomes were cherry-picked. The outcomes that showed improvements in the GET-group (PROMs that are sensitive to bias) were highlighted while outcomes that didn’t or rarely show improvements in the GET group (objective outcomes that are more robust to bias) were largely ignored.

The fact that patients in the GET group weren’t able to increase their fitness on objective tests might help interpret scores on the SF-36 physical functioning subscale. Normally there is a significant correlation between this questionnaire and objective measures of fitness. (23) In the exercise trials, however, there seems to be a discrepancy between improvements reported with the SF-36 physical functioning questionnaire and the lack of significant improvements seen on more objective measures of fitness. This suggests that bias due to lack of blinding might have affected the validity of PROMs summarized in this review. Because objective outcomes were not reported in the Cochrane review, its readers will not be aware of this. After reading the reported improvements on the SF-36 subscale, they may be under the impression that CFS patients get fitter following GET, an assumption that is not supported by objective measurements.

No information on compliance
A lack of improvement on objective measures of fitness following a months-long exercise program could indicate a problem with compliance. Unfortunately, the review doesn’t discuss the level of compliance in the eight exercise trials even though this was mentioned as an outcome measure in the protocol. Kindlon T highlighted the need for compliance measures in his comments to the review in 2015, explaining that “Information on adherence and what exercise was actually done is important in terms of helping clinicians, and indeed patients, to interpret and use the data.” Unfortunately, none of the updates of the review acted upon this.

Information on compliance is relevant as several reports have suggested that CFS patients experience an “activity ceiling.” (24,25) These small, in-depth studies have used objective measurements of activity such as accelerometers and reported that ME/CFS patients struggle to significantly increase their physical activity level for a long time. (25–27) Black & McCully, for example, report that “the inability to sustain target activity levels, associated with pronounced worsening of symptomology, suggests the subjects with CFS had reached their activity limit.” (25) Friedberg & Sohl suggest that patients may be reducing other activities to keep up with exercise prescriptions. (27) Something similar might have occurred in the eight exercise trials included in the Cochrane review. This would have implications for the data on safety and acceptability of GET reported in this review. Therefore I would recommend including a section on compliance measures (or lack thereof) in future updates of the review.

....... End of part I .......

 

Indirectness of evidence: outdated diagnostic criteria
The Oxford criteria, the diagnostic criteria used to select patients in most of the exercise trials in this review, are now considered outdated. An NIH working group, for example, stated in 2015 that “continuing to use the Oxford definition may impair progress and cause harm. Therefore, for progress to occur, we recommend that this definition be retired.” (28) In the latest update of the review, a statement was added that tried to account for this shortcoming. It says: “All studies were conducted with outpatients diagnosed with 1994 criteria of the Centers for Disease Control and Prevention or the Oxford criteria, or both. Patients diagnosed using other criteria may experience different effects.” Unfortunately, this statement is rather vague as it doesn’t explain why patients selected with other criteria might experience different effects. More recent diagnostic criteria such as the Canadian Consensus Criteria (29), the International Consensus Criteria (30) and the criteria proposed by the National Academy of Medicine (11), all require that patients experience marked symptom exacerbations following (physical) exertion. This is usually referred to as post-exertional malaise (PEM) and considered to be a characteristic symptom of the illness. The diagnostic criteria used to select patients in the exercise trials of the Cochrane review, however, did not require patients to experience PEM. Consequently, they might have selected a cohort that differs from how ME/CFS is currently defined.

Reports of harm not mentioned
It is notable that the Cochrane review, which assesses the safety and efficacy of GET in patients with ME/CFS, does not inform its readers that PEM is a characteristic symptom of the illness. PEM implies that patients commonly experience symptom exacerbations or relapses following exertion. With GET, however, patients are encouraged “to increase the duration, frequency and intensity of exercise beyond their perceived limits.” (31) This indicates that graded exercise programs risk worsening ME/CFS patients’ health, at least temporarily. As noted by Cheshire et al. “It is an apparent paradox that graded exercise programmes are prescribed for patients with CFS/ME, when post-exertional malaise is a feature, which requires explanation.” (32) Readers of the Cochrane review will be largely unaware of this paradox.

The Cochrane review also does not mention the multiple surveys in which ME/CFS patients report to have been harmed by GET. (12,13) These surveys have consistently raised the same concern for almost three decades and have been conducted in multiple countries including the United Kingdom, The Netherlands, and Australia. (12) Suggestions that reports of harm are due to improper delivery of GET are unfounded. (33–35) In a 2010 survey by the ME Association GET was reported to be more harmful than pharmacological treatments with known side effects such as hydrocortisone, thyroxine or modafinil. (36) Similarly, in a 2014 Survey by Action for ME, GET was rated as more harmful than pain- and sleep medication. (37) This suggests that reports of harm following GET cannot be fully explained by selection bias. It is unclear why patient organizations would attract that many members claiming to have worsened following GET compared to other treatments.

Although these surveys have their limitations and methodological weaknesses, it seems advisable to mention them in a review assessing the safety and efficacy of GET in ME/CFS. Currently, the review only casually notes that “many groups representing the interests of those with CFS are opposed to exercise therapy.” The reader is left to wonder why this could be the case if GET is indeed effective in reducing fatigue and other CFS symptoms as the review claims. Instead of explaining the reports of harm following GET, the Cochrane review only refers to papers and guidelines that support its conclusion. Guidelines and documents that reached a different conclusion (38,39) were not mentioned.

Selective reporting in the PACE trial
Finally, one further issue with the review is that the PACE trial is rated as low risk of bias for selective reporting. As carefully explained by Kindlon T in 2015, this is not in accordance with the Cochrane handbook (version 5.1.0) used to assess bias in this review. The handbook recommended a study to be rated as high risk of bias for selective reporting if “not all of the study’s pre-specified primary outcomes have been reported.” For the PACE trial the primary outcome of overall improvers as defined in the protocol was never reported. I refer to Wilshere et al. (40) and Issue 9, Volume 22 of the Journal of Journal of Health Psychology for further discussion of selective reporting in the PACE trial, as my comments are already quite long. The PACE trial was the largest trial included in this review, so I hope its risk of bias for selective reporting will be thoroughly assessed in future updates.

Thank you for reading my comments.

References
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7. Vink M, Vink-Niese A. Graded exercise therapy for myalgic encephalomyelitis/chronic fatigue syndrome is not effective and unsafe. Re-analysis of a Cochrane review. Health Psychol Open. 2018 Dec;5(2):2055102918805187.

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11. Committee on the Diagnostic Criteria for Myalgic Encephalomyelitis/Chronic Fatigue Syndrome, Board on the Health of Select Populations, Institute of Medicine. Beyond Myalgic Encephalomyelitis/Chronic Fatigue Syndrome: Redefining an Illness [Internet]. Washington (DC): National Academies Press (US); 2015 [cited 2019 Nov 26]. (The National Academies Collection: Reports funded by National Institutes of Health). Available from: http://www.ncbi.nlm.nih.gov/books/NBK274235/

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14. Niemeijer A, Lund H, Stafne SN, Ipsen T, Goldschmidt CL, Jørgensen CT, et al. Adverse events of exercise therapy in randomised controlled trials: a systematic review and meta-analysis. Br J Sports Med. 2019 Sep 28;pii: bjsports-2018-100461.

15. Takakura S, Oka T, Sudo N. Changes in circulating microRNA after recumbent isometric yoga practice by patients with myalgic encephalomyelitis/chronic fatigue syndrome: an explorative pilot study. Biopsychosoc Med. 2019 Dec 2;13(1):29.

16. van Kessel K, Moss-Morris R, Willoughby E, Chalder T, Johnson MH, Robinson E. A randomized controlled trial of cognitive behavior therapy for multiple sclerosis fatigue. Psychosom Med. 2008 Feb;70(2):205–13.

17. Edwards J. PACE team response shows a disregard for the principles of science. J Health Psychol. 2017 Aug 1;22(9):1155–8.

18. Hróbjartsson A, Boutron I. Blinding in randomized clinical trials: imposed impartiality. Clin Pharmacol Ther. 2011 Nov;90(5):732–6.

19. Hróbjartsson A, Emanuelsson F, Skou Thomsen AS, Hilden J, Brorson S. Bias due to lack of patient blinding in clinical trials. A systematic review of trials randomizing patients to blind and nonblind sub-studies. Int J Epidemiol. 2014 Aug;43(4):1272–83.

20. Bavinton J, Darbishire L, White PD. PACE manual for therapists. Graded Exercise Therapy (GET) for CFS/ME. Final trial version: version 7 (MREC Version 2). [Internet]. PACE Trial Management Group; 2004 [cited 2019 Nov 26]. Available from: https://me-pedia.org/images/8/89/PACE-get-therapist-manual.pdf

21. Savović J, Jones H, Altman D, Harris R, Jűni P, Pildal J, et al. Influence of reported study design characteristics on intervention effect estimates from randomised controlled trials: combined analysis of meta-epidemiological studies. Health Technol Assess Winch Engl. 2012 Sep;16(35):1–82.

22. Edmonds M, McGuire HF, Price JJ. Exercise therapy for chronic fatigue syndrome. Cochrane Database Syst Rev [Internet]. 2001 [cited 2020 Apr 20];(3). Available from: https://www.cochranelibrary.com/cdsr/doi/10.1002/14651858.CD003200/full

23. van Campen C, Rowe PC, Verheugt FW, Visser FC. Physical activity measures in patients with myalgic encephalomyelitis/chronic fatigue syndrome: correlations between peak oxygen consumption, the physical functioning scale of the SF-36 questionnaire, and the number of steps from an activity meter. 2020 Apr 8 [cited 2020 Apr 18]; Available from: https://www.researchsquare.com/article/rs-21479/v1

24. Friedberg F, Krupp LB. A comparison of cognitive behavioral treatment for chronic fatigue syndrome and primary depression. Clin Infect Dis Off Publ Infect Dis Soc Am. 1994 Jan;18 Suppl 1:S105-110.

25. Black CD, McCully KK. Time course of exercise induced alterations in daily activity in chronic fatigue syndrome. Dyn Med DM. 2005 Oct 28;4:10.

26. Friedberg F. Does graded activity increase activity? A case study of chronic fatigue syndrome. J Behav Ther Exp Psychiatry. 2002 Dec;33(3–4):203–15.

27. Friedberg F, Sohl S. Cognitive-behavior therapy in chronic fatigue syndrome: is improvement related to increased physical activity? J Clin Psychol. 2009 Apr;65(4):423–42.

28. Green CR, Cowan P, Elk R, O’Neil KM, Rasmussen AL. National Institutes of Health Pathways to Prevention Workshop: Advancing the Research on Myalgic Encephalomyelitis/Chronic Fatigue Syndrome. Ann Intern Med. 2015 Jun 16;162(12):860–5.

29. Carruthers BM, Jain AK, Meirleir KLD, Peterson DL, Klimas NG, Lerner AM, et al. Myalgic Encephalomyelitis/Chronic Fatigue Syndrome. J Chronic Fatigue Syndr. 2003 Jan 1;11(1):7–115.

30. Carruthers BM, Sande MI van de, Meirleir KLD, Klimas NG, Broderick G, Mitchell T, et al. Myalgic encephalomyelitis: International Consensus Criteria. J Intern Med. 2011;270(4):327–38.

31. Clark LV, White PD. The role of deconditioning and therapeutic exercise in chronic fatigue syndrome (CFS). J Ment Health. 2005 Jun 1;14(3):237–52.

32. Cheshire A, Ridge D, Clark L, White P. Guided graded Exercise Self-help for chronic fatigue syndrome: patient experiences and perceptions. Disabil Rehabil. 2018 Oct 16;1–10.

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34. ME Association. ME/CFS Illness Management Survey Results “No decisions about me without me [Internet]. 2015. Available from: https://www.meassociation.org.uk/wp...No-decisions-about-me-without-me-30.05.15.pdf

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36. ME Association. Managing my M.E. What people with ME/CFS and their carers want from the UK’s health and social services [Internet]. 2010. Available from: https://www.meassociation.org.uk/wp-content/uploads/2010/09/2010-survey-report-lo-res10.pdf

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40. Wilshire CE, Kindlon T, Courtney R, Matthees A, Tuller D, Geraghty K, et al. Rethinking the treatment of chronic fatigue syndrome-a reanalysis and evaluation of findings from a recent major trial of graded exercise and CBT. BMC Psychol. 2018 Mar 22;6(1):6.

 

Well done. This is good.

This should be A NIH working group.

Could this expanded a little bit? I think it would be justified to say that this is reveals a dismissive attitude towards patients reporting harm and gives the impression that there is no justification for such reports.

PS: you could mention that post-marketing pharmacovigilance is considered important because some side effects are only discovered outside of clinical trials, and that there appears to be no formal way (in UK? generally?) to report harms from psychotherapy. These patient surveys could be the only way some harms could be discovered.

 

Exercise or exertion caused indefinite worsening in 55% of patients and also some cases of long-term worsening according to this poll: https://www.s4me.info/threads/has-exercise-or-exertion-lowered-your-pem-threshold.15055/.

 

Very good @Michiel Tack!

Would be better English as "The GRADE handbook, however, states that if ...". Also similar a bit later on. I'm not familiar with using the word 'writes' in this context, but I could be wrong. In any case, it may not really matter.

Extra space needed before the '/'?

Should be Wilshire.

Also, I don't know if it's relevant for the comment you are submitting, but I'll mention it anyway ...

The 2011 PACE paper states that GET is based on the deconditioning theory of CFS. Quite apart from that theory no longer being widely accepted, surely the trial results would have been hugely more positive if the deconditioning assumption had been correct. But the results were pitiful, supporting the idea that PACE was based on a flawed premise.

So if GET was trialled under flawed assumptions about the physiology of the condition it was aiming to treat, then surely it follows that assumptions made about identifying, monitoring and recording potential physiological harms due to GET during the trial could also be flawed. e.g. If participants genuinely had been suffering from deconditioning, the trial protocol might have deemed it unnecessary and irrelevant to consider progressive deterioration in physical function as being due to the harmful effects of GET, because that is not something they would expect to see if treating deconditioning the way they did. The scope of harms you need to monitor and record will be different, according to the physiology of the condition being treated. If you are treating on the assumption of a different condition, then certain harms may end up outside the scope of what you are looking for, and instead misattributed to some other, non-harmful reason, such as participant non-adherence to treatment regime. Effectively blinded to certain modes of harm, and therefore not recorded as harms.

 

Further to my previous post here.

This clearly states that GET was applied based on assumptions about the underlying physiology. It's not just 'activists' who assert this, it is the PACE authors themselves. The PACE authors are clearly stating here that they did not know the underlying physiology of ME/CFS.

So when the PACE authors had to decide what sort of harms to watch out for, did they base those decisions on their uncertainty of the underlying physiology of ME/CFS? No, they based their decisions regarding the scope of what harms to be alert to, on their 'knowing' the underlying physiology to be deconditioning! How else could they have missed the possibility that participants' worsening symptoms might be due to the treatment itself, and not participants' incorrect application of their treatment! The possibility that the treatment itself might be the cause of this mode of harm was completely off the radar to the PACE authors.

Whenever a trial is run that acknowledges the underlying physiology to be unknown, then the potential scope for harms during the trial should also be acknowledged in as open-minded a way as possible. Crucial for ensuring harms get correctly recorded and reported, and also of course to stop harming the participants at the earliest opportunity. It should be the solemn duty of all medical research scientists.

I think PACE clearly shows what happens when a group of closed-minded psychiatrists seek to trial behavioural treatments of a physical condition. There should be a law against it; maybe one day there will be.

Some might say this is is 20/20 vision hindsight, but good science is about guarding best as possible against biased closed minded assumptions.

 

My paragraphs here:

An important point.

In this view, the PACE study was rather a trial to show indirectly that the deconditioning theory is true: A successful treatment, made upon this assumption, would indicate that the assumption could be true. "Could be" rather, similar to a wet street that only "could be" wet due to rain; referring to a common knowledge in formal logic (which should be known by scientists).

So I would expect that the PACE study from out it´s claimed success tries to describe how far the assumption ("patients are only deconditioned") could be true, and in which respects this might be concluded too much.

For testing the hypothesis indirectly it would rather have been necessary to look out for effects that would not fit the hypothesis. Obviously they havn´t done it sufficiently. - I will finally read the paper, thank you for making it possible.


"To look out for effects" then reads furthermore in terms of moral to monitor any thinkable side effects thoroughly (because people could get harmed). As this didn´t happen (and even was rejected later) this shows that the authors havn´t conducted the study in agreement to ethical standarts although the possibility was already logically indicated in all clarity.

 

Yes, this no hindsight knowledge, but intrinsically a matter of debate, which they completely failed to spot.

 

I think "An NIH" is correct:
https://www.dailywritingtips.com/indefinite-article-with-initialisms/

 

Very impressive work again, Michiel.

It seems almost a pity so many of these points are not in something that is published but maybe you will get a chance to use them again.

 

One generally wouldn’t see “pain-medication” in English I think so I’d leave out the hyphen

 

Yes good point. Would be interesting to look into how harms are usually found and reported. Haven't the energy to look into this, but I suspect that the reporting of harms of drugs is taken quite seriously even if it occurs outside randomized trials as a sort of cautionary principle.

Yes that's better, thanks Barry, for your other corrections as well. Appreciate it.

Thanks

 

In the UK there is only the Yellow Card scheme, but it doesn't cover psychotherapy - this was confirmed after, I think, it was suggested in Parliament by the Government that the scheme should be used to report harms from CBT and/or GET and subsequently the Medicines & Healthcare products Regulatory Agency confirmed that it is out of their scope.

 

That makes some kind of very weak sense with CBT, even though psychological abuse from bad therapists is very much a serious issue that requires a flagging system, but GET is clearly a sort of physiotherapy intervention so it seems weird that it would be in the same category considering the (debunked but whatever) hypothesis is literally deconditioning, which is firmly in physiotherapy's remit, not psychology.

Somehow I expect that the reasons for that do not make sense and conflict with actual guidance but exemptions were made because nothing matters when it concerns a patient population exist in a weird superposition where medical interventions essentially have force of law (e.g. do this or your disability claim will not be evaluated) but are not considered to have a medical condition.

Not that I expect any of it to make sense but this especially does not make any. Either GET is based on the assumption of deconditioning, which is explicitly stated, or it's not. But that both are somehow true is just all sorts of corrupt and FUBAR.

 

I have formally submitted my comments to Cochrane. Like Tom Kindlon back in 2015, I have divided my comments into two submissions because the text was rather long. Unfortunately, the Cochrane submission text box did not allow for any formatting.

I have also sent my text to the independent advisory group led by Hilda Bastian and published the text of my submissions on my personal blog: https://mecfsskeptic.wordpress.com/...-cochrane-review-on-exercise-therapy-for-cfs/

 

Excellent. Thanks, Michiel. Sorry I've not been able to help.

 

Amazing work! Very impressed by your writing and analytical skills. Stunned I'd say!!!