Efficacy of cognitive behavioral therapy targeting severe fatigue following COVID-19: results of a randomized controlled trial 2023, Kuut, Knoop et al

This same as published except the references have been reformatted in published edition.

Dear Editor,

Kuut et al (2023) published their trial of CBT for severe, prolonged fatigue in patients
following Covid-19 infection (ReCOVer). Unfortunately, their trial design and
methodology are at high risk of expectation bias due to the sole use of subjective
primary outcome measures in a highly variable condition coupled with an inability to
blind trial participants for inclusion or exclusion from the psychologist-delivered
intervention (CBT) or not (CAU) (Edwards, 2021). Such poor-quality trial designs
have been subjected to rigorous 3-year review and deemed to be of very low quality
(NICE (2021)). The wide-ranging assumptions underpinning the CBT model used in
the trial and the efficacy for its use in general has been much criticised for its
inconsistency and is highly contested due to underlying trial design weaknesses and
intervention content (Geraghty et al., 2019).

The inherent bias problems with the use of subjective outcome measures in
unblinded trial designs are well known. By using such a trial design, it can be
predicted that expectation bias will result in modest, positive changes when
assessed via subjective questionnaires. Furthermore, it is likely that modest
changes will be unrelated to real world benefits to patients, such as return to
work/resumption of occupation or studies, full re-engagement in family life and the
absence of on-going troubling symptoms, such as post exertional malaise, cognitive
dysfunction, which were not assessed in this trial (Bonilla et al, 2023). Therefore, the
ReCOVer trial is unable to develop a reliable evidence-base or provide an adequate
gauge of efficacy of the CBT intervention on which to base any patient treatment
recommendations. Objective measures of pre and post-intervention patient ability
are needed in unblinded trial designs to inform good quality clinical decision making.
An opportunity to assess such arose within this trial as actigraphy data was recorded
at T0 and T1, according to the trial protocol (Kuut et al., 2021). Unfortunately, this
data was not published missing an opportunity to provide valuable information about
efficacy, which the study claimed to assess. The authors need to publish this
information to allow independent examination.

Using the CIS as a primary outcome measure is problematic as this has a well￾known ceiling effect in severely fatigued patients. It is therefore, unable to record
patients who have worsened. Further, as harms have been reported in similar
conditions and adverse events were only explored at T1 in this study, not at 6-month
follow up, it is hard to ascertain if any patients have been harmed. Moreover,
defining a difference of 6 points as significant is questionable as this is likely to
overestimate the subjective positive gains, as outcomes were significantly higher for
CBT at T1 (M=30.6 (1.4)) than those found in healthy controls (17.3 (10.1)) (Schulte￾van Maaren, 2014).

Ethically, due to the limitations of the trial design to inform clinical practice and the
predictable modest results, along with the ongoing high level of debility, perhaps it
would be more helpful to invest in good quality psychological support for patients
while the underlying mechanisms can be determined.

References
Bonilla H, Quach TC, Tiwari A, Bonilla AE, Miglis M, Yang PC, Eggert LE, Sharifi H,
Horomanski A, Subramanian A, Smirnoff L, Simpson N, Halawi H, Sum-Ping O,
Kalinowski A, Patel ZM, Shafer RW, Geng LC. (2023). Myalgic
Encephalomyelitis/Chronic Fatigue Syndrome is common in post-acute sequelae of
SARS-CoV-2 infection (PASC): Results from a post-COVID-19 multidisciplinary
clinic. Frontier of Neurology, 24 (14):1090747.

Edwards, J. (2021). Myalgic encephalomyelitis (or encephalopathy) / chronic fatigue
syndrome: diagnosis and management. NICE guideline NG206. Appendix 3: Expert
testimonies The difficulties of conducting intervention trials for the treatment of
myalgic encephalomyelitis/chronic fatigue syndrome.
Downloaded October, 2021,
https://www.nice.org.uk/guidance/ng206/evidence/appendix-3-expert-testimonies￾pdf-333546588760

Geraghty, K., Jason, L.A., Sunnquist, M, Blease, C.R., Tuller, D.M., & Adeniji, C.,
(2019). The 'Cognitive Behavioural Model' of chronic fatigue syndrome: Critique of a
flawed model, Journal of Health Psychology 6(1).

Kuut, T.A., et al. (2021). A randomised controlled trial testing the efficacy of Fit after
COVID, a cognitive behavioural therapy targeting severe postinfectious fatigue
following COVID-19 (ReCOVer): study protocol. Trials, 22:867

Kuut, T.A., et al. (2023). Efficacy of cognitive behavioral therapy targeting severe
fatigue following COVID-19: results of a randomized controlled trial. Clinical
Infectious Diseases, ciad257.

NICE (2021). Myalgic encephalomyelitis (or encephalopathy)/chronic fatigue
syndrome: diagnosis and management. NICE guideline [NG206].

Schulte-van Maaren, Y.W.M. (2014). NormQuest: reference values for ROM
instruments and questionnaires. Retrieved May 12, 2023, from
https://scholarlypublications.universiteitleiden.nl/handle/1887/23044
 
The reply seems to fall under the "admit the limitations of the study so you can't be accused of ignoring them but then act like they don't matter" category.

Can anyone check if the results exceed the modest improvements that could be reasonably assumed to be merely a placebo effect? (yes I know that placebo effects are context dependent. The authors seem to argue that they have obtained better results than expected for placebo)
 
Last edited:
Hoopoe said:
The authors seem to argue that they have obtained better results than expected for placebo
Click to expand...
They used the flawed Wessely review to argue that placebo effects in ME/CFS are small.

The effect for the primary outcome fatigue is quite large (Cohen's d of 0.69) while the effect for physical fatigue was probably not clinically significant (Cohen's d of 0.3).
 
Unfortunate that nobody touched on the strange numbers in table 3.

They report for example a standard error of 0.5 in the CBT-group at baseline. Because the sample size was 57, the standard deviation would be: 0.5 * sqrt(57) = 3.77.

This is extremely small. The mean was 47! In other papers, for example on ME/CFS patients, the standard deviation is around 12-15 points.

EDIT: This was an error: the post-treatment the SD is often large, above 10 points, as it was in this paper. But at baseline the SD is often smaller, around 4-5 points, making the SD 3.77 small but not in an extreme way.
See this post by Mark Vink further up this thread: https://www.s4me.info/threads/effic...23-kuut-knoop-et-al.33229/page-11#post-482332
 
Last edited:
ME/CFS Skeptic said:
They used the flawed Wessely review to argue that placebo effects in ME/CFS are small.

The effect for the primary outcome fatigue is quite large (Cohen's d of 0.69) while the effect for physical fatigue was probably not clinically significant (Cohen's d of 0.3).
Click to expand...

Thanks. While the effect is larger than that reported by Wessely, this doesn't save the study because this is an unreliable and unorthodox method for attempting control for placebo effects.

I'm not getting the impression that care as usual is generally a positive and helpful experience for long covid patients.
 
Secondly, the outcomes were solely self-reported, with inherent limitations. Objective outcome measures, such as physical fitness (CPET), exercise behaviour and return to work that could have supported the authors conclusions have not been included. The results of the actometer that were planned in the study protocol are lacking for unreported reasons.
Click to expand...
Oh. No. Way. Total mild shock on my face. I'm sure the reasons are very mysterious.
 
rvallee said:
y. Total mild shock on my face. I'm sure the reasons are very mysterious.
Click to expand...

Interestingly, they now claim in their response that there was no difference in the actigraphy results. Has anyone ever seen a response in correspondence that cites data deliberately left out of the actual study? ADD: And isn't it research misconduct to fail to report results that do not support your conclusions. I mean, they're acknowledging they had null results for this outcome. It's a disgrace not to include them in the report of the trial.
 
Last edited:
Grigor said:
Response by Kuut et al. to Biere-Rafi et al. and Joan S Crawford.

Click to expand...

Thanks very much to those who wrote.
It was great to get this out of them:
In our study there was no significant difference between the conditions in the increase in physical activity assessed with actigraphy.
Click to expand...
It's a pity they didn't give the raw numbers but still useful.
 
Dolphin said:
Thanks very much to those who wrote.
It was great to get this out of them:
In our study there was no significant difference between the conditions in the increase in physical activity assessed with actigraphy.
Click to expand...
It's a pity they didn't give the raw numbers but still useful.
Click to expand...
I wonder whether the numbers could be obtained using a freedom of information request?
 
ME/CFS Skeptic said:
They used the flawed Wessely review to argue that placebo effects in ME/CFS are small.
Click to expand...
The vastly more methodologically robust Rituximab study completely refutes their claim. There is a sizable placebo effect in self-report for ME/CFS. Like most other conditions.
dave30th said:
And isn't it research misconduct to fail to report results that do not support your conclusions. I mean, they're acknowledging they had null results for this outcome. It's a disgrace not to include them in the report of the trial.
Click to expand...
Given the history of this pattern of behaviour from the psychosomatic ideologues since at least PACE (2011) it is now way past mere misconduct.

There are simply no excuses for them not knowing of this problem, and dealing with it. There never were, but there sure as hell isn't now.

To persistently not report, or to misreport, or to fail to adequately take into account results that clearly falsify your hypothesis is, IMHO, straight scientific fraud.
 
Last edited:
Dolphin said:
I wonder whether the numbers could be obtained using a freedom of information request?
Click to expand...

Hm. They might insist they are including them in another study or something. Maybe they'll do three CBT long covid trials, call them all a success, then publish all three sets of null actigraphy findings together a few years later while explaining how they're not a good measure because they contradict the subjective ones.

The phrasing implies that both groups improved on that measure. But it's hard to tell. Obviously those findings were disappointing to them. I wonder why they even included them? And why, if they decided to, only for the T1 results, not T2 and T3.

Definitely worth writing to the journal and indicating that hiding salient data that might undermine your conclusions is research misconduct. The actual numbers won't change that. But it would be interesting if the non-intervention group actually did better, even if it wasn't statistically significant.
 
You must log in or register to reply here.
Back
Top Bottom