Cognitive Behavioral Therapy Improves Physical Function & Fatigue in Mild & Moderate CFS: A Consecutive RCT, 2021, Gotaas et al

Cognitive Behavioral Therapy Improves Physical Function and Fatigue in Mild and Moderate Chronic Fatigue Syndrome: A Consecutive Randomized Controlled Trial of Standard and Short Interventions

Merethe Eide Gotaas, Tore C. Stiles, Johan Håkon Bjørngaard Petter C. Borchgrevink and Egil A. Fors

Open access; from Norway

Abstract:


Objective: To study whether standard cognitive behavioral therapy (CBT) and a shorter, interpersonal oriented cognitive behavioral therapy (I-CBT) can improve physical function and fatigue in patients diagnosed with mild to moderate chronic fatigue syndrome (CFS) in a multidisciplinary fatigue clinic.

Design: Consecutively 236 participants 18–62 years old meeting the Centre of Decease Control, CDC 1994 criteria, with a subsample also fulfilling the Canadian criteria for CFS, were randomly allocated to one of three groups. Two intervention groups received either 16 weeks of standard CBT or 8 weeks of I-CBT vs. a waiting-list control group (WLC). Primary outcome was the subscale Physical Function (PF) from SF-36 (0–100). Secondary outcome was amongst others fatigue measured by Chalder Fatigue Questionnaire (CFQ) (0–33). Outcomes were repeatedly measured up to 52 weeks from baseline.

Results: The additional effect relative to baseline at post-intervention for SF-36 physical function was 14.2 (95% CI 7.9–20.4 p < 0.001) points higher for standard CBT and 6.8 (0.5–13.2 p = 0.036) points higher for I-CBT compared with the control group. The additional effect relative to baseline at post-intervention for fatigue was 5.9 (95% CI 0.5–10.5 p = 0.03) points lower for standard CBT compared with the control group but did not differ substantially for I-CBT 4.8 (95% CI −0.4 to 9.9 p = 0.07). The positive change in physical function persisted at 1-year follow-up for both treatment groups, and for standard CBT also in fatigue. The two intervention groups did not differ significantly in self-reported physical function and fatigue at the 1-year follow-up. No serious adverse reactions were recorded in any of the groups during the trial period.

Interpretation: A 16-week standard, individual CBT intervention improves physical function and fatigue in CFS outpatients with mild to moderate disease. A shorter 8-week I-CBT program improves physical function. Both treatments are safe, and the effect persist 1 year after baseline.

Clinical Trial registration: ClinicalTrials.gov, Identifier: NCT00920777, registered June 15, 2009.


https://www.frontiersin.org/articles/10.3389/fpsyt.2021.580924/full

 

Outcome data collection was completed on September 26, 2013.

why has it taken this long to publish?

eta: 44% dropout

 

Oh my, that's hilarious! If they could get something like that so howlingly wrong, no wonder the rest of the paper is such nonsense.

I mean, really?

 

Oh no, they used the revised recovery criterion from the PACE trial, i.e. a SF-36 physical function score greater than 60... (bolding mine):

A clinically or minimal important difference (MID) was defined as an improvement of >10 points for the “mean difference, additional effect relative to baseline at post-intervention” or a mean score in SF-36 physical function of >75 post-intervention (56, 57). Norwegian reference values for physical function in SF-36 exists (58), but are calculated with a different edition of SF-36 (version 1) than the one used in our study (i.e. version 2). As an example of a similar population to compare with, the SF-36 physical function version 2 score for the UK working age population is 84, with a SD of 24. Thus, a SF-36 score equal to or above the mean minus 1 SD will be considered in the normal range (score of 60 or more) (56). That would make a SF-36 physical function score of 75 or more within normal range (56).
​

As @Carolyn Wilshire, @Tom Kindlon, @Simon M and Alem explained in their preliminary re-analysis of the PACE trial, the mean score of 84, is not that of the working age population (spacing and bolding mine):

In the original study protocol, recovery on this measure was defined as a score of 85 or above [12], a similar figure to that used in previous studies of behavioural interventions for CFS (e.g. [15,16]). This was a reasonable, albeit arguably low threshold: according to reference data from a large British community sample, the vast majority (90%) of people aged 18–59 without a long-term illness or disability actually score 90 or higher ([17]: for summary report, see Bowling et al. [18]).

However, in the Recovery paper, the minimum score for a recovery outcome was lowered to 60. This late post-protocol change increased the proportion of participants who met this criterion from 14% to 45%, a more than three-fold increase. The justification given for this change was that the original threshold of 85 was so high that ‘approximately half the general working age population would not meet it’ [3, p. 2229].

This claim is clearly incorrect: it seems to have been based on summary statistics from a large British reference sample reported in Bowling et al. [18], in which almost a third of participants were aged 60 or over, and one-fifth reported a long-term illness or disability that limited their daily activities or the work they could do. Since the PACE trial participants were screened and excluded for the presence of fatiguing illnesses other than CFS, any normative dataset used to define recovery should have also excluded such illnesses.
​

They also justify why subtracting 1 standard deviation (24) from the mean score of 84 is incorrect, and how a score of 60 represents serious disability:

In addition, the authors seem to have derived their ‘approximately half’ figure from calculations based on the sample mean and standard deviation, a method which was inappropriate, given the highly skewed distribution of scores (see Figure 1 for illustration).

Indeed, as Figure 1 shows, if we look just at those participants from the British reference sample who were aged 18–59 and did not have a long-term illness or disability, the median (and modal) score for this highly skewed normative sample was 100 and 93% scored at or above the original recovery threshold of 85 [17]. Their arguments do not therefore justify the lowering of the SF-36 physical function threshold score from the originally specified minimum level.

The revised recovery threshold score is so low that it is close to the mean score of patients with osteoarthritis of the hip, rheumatoid arthritis, and Class II congestive heart failure [19,20], as shown in Figure 1. This is a serious concern.​

 

The abstract is rather misleading: the clinically minimally important difference for the SF-36-PF score (10 points) is attained by the 16-week standard CBT group (graded activity) but not the 8-week I-CBT group, with respectively 14.2 vs 6.8 points at baseline compared to post-intervention (both p < .05), yet the authors report in the abstract that the latter also had "improved physical function".

Regarding norm scores, the authors also report that:

At post-intervention, 50% of the standard CBT group and 40% of the I-CBT group reached a predefined SF-36 physical function score of 75 points or more at post-intervention, compared to only 20% in the WLC group (57). Furthermore, 31% of the patients in the standard CBT group, 19% of the patients in the I-CBT group and 10% of the patients in the WLC- group reported normal fatigue scores related to the Norwegian population at the end of the waiting period (a fatigue score of 16.1 or less) (60).
​

However, according to tables 2 and 3, the mean SF-36-PF and fatigue scores (95% CIs) post-intervention were:

- standard CBT: 71.2 (66.3 - 76.1), 18.7 (17.1 - 20.4)
- I-CBT: 62.9 (58.0 - 67.9), 20.7 (19.1 - 22.4)
- waiting list: 57.9 (53.2 - 62.5), 24.1 (22.6 - 25.7)

The 95% CIs barely or do not overlap the norm scores (SF-36-PF > 75, fatigue <= 16.1). This suggests that when participants in the treatment groups reported scores better than the norms, they would in fact have been very close to the norms rather than the scores of the healthy working age population (SF-36-PF close to 100, fatigue <= 11.2). Not very convincing -- and misleading again.

It is also unfortunate that the authors did not report participants and results by length of disease duration, nor the differences between patients enrolled in the last year based on diagnostic criteria (Fukuda vs. Fukuda and Canadian).

 

And there is a glaring omission in this paragraph:

Clinical Global Impression Scale and Adverse Events

More patients rated themselves as “much better” or “very much better” in overall health measured by the Clinical Global Impression Scale (CGI) after both the standard CBT and I-CBT interventions compared to the control group. At post-intervention, 33 and 26% in the standard CBT vs. I-CBT group, respectively, rated themselves as “much better” or “very much better” in overall health compared to 8% in the WLC group. The registered adverse events were increased fatigue and worsening of other existing CFS such as nausea, headache and pain in muscles and joints.
​

A glance at Table 5 shows that 71% of participants in the standard CBT group and 65% in the I-CBT group reported "minimal change" post-intervention (87% in the waiting list group). Counting those who reported negative change, this climbs to 74% and 67% (92%) respectively. The numbers are similar at the 1-year follow-up: 65% and 67%.

No quantitative data on adverse events is reported. This may owe to therapeutic allegiance bias from the authors:

The 8 weeks of individual, interpersonal and personality-oriented CBT [I-CBT] was given by four trained cognitive therapists at the private health centre Coperio, Trondheim, Norway. The treatment manual was developed by co-author (TCS).
​

and:

However, due to few randomized studies with varying quality and the use of different sets of criteria for diagnosing CFS, there is no consensus whether CBT is an effective and safe treatment for all patients with CFS (20, 26–28). On the other hand, few adverse effects are found in CBT treatment. In a reanalysis of three RCTs on CBT for CFS, it was concluded that patients receiving CBT did not experience more frequent or more severe symptom deterioration than untreated patients and that the reported deterioration during CBT seemed to reflect the natural variation in symptoms (27). In spite of that, a small review by Twisk et al. have suggested worsening in patients with CFS after CBT and GET (29). Thus, the reporting of non-serious adverse events may reflect the nature of the illness rather than the effect of treatments (30).
​

This paper was submitted on August 19, 2020, i.e. before the release of the NICE draft guidance, but the paragraph above omits published reports of negative effects of CBT and GET such as @Tom Kindlon's 2017 paper and Keith Geraghty's.

 

The authors added the study protocol and deviations from the protocol as supplementary material.

The protocol states that the project was to run from January 1, 2012 to January 1, 2015, with 3 publications planned between fall 2012 and fall 2014. But the authors only briefly say:

Change in schedule and plan for dissemination of research results

3. Publication of results have been delayed due to non-academic reasons.
​

Interestingly:

Professor Trudie Chalder has not participated in the work with this article but has been a part of the project group as described in the study protocol.
​

ETA: @dave30th, you might want to look at this paper?

 

Same old outcome-seeking that argues meaningless "benefits" to be somehow useful through methodology that is infinitely manipulable.

Looks like ideas suffer the same malady as genetics after too many generations of inbreeding. Especially as this is basically the same idea giving birth to the same idea, in a kind of "I am my own grandfather" way. More like a cloning factory, or perhaps clowning is more apt.

 

It's also interesting to note that Egil A. Fors, one of the authors, is a close personal friend of Live Landmark (the Norwegian PhD in psychology/Lightning Process coach that's behind Paul Garner's "miraculous recovery"). Considering the fact that it was completed in 2013 and only published just now, I'm wondering if this publication is a strategic move to try to influence the NICE committee. I know that this paper is submitted before the NICE-draft was published, but they knew a new draft was coming and probably could have guessed that CBT/GET might be on block. So that's maybe why they've gotten the whole BPS brigade to publish their findings with any data they have lying around - considering the many strange studies on these interventions that have been published lately?

 

What a poorly designed trial. How can a waiting list control group account for the placebo effect? They could have used a sugar pill at least. We already know how strong the placebo effect can be, especially in ME/CFS (see Rituximab trials). They should have done more to control for it.

If this study was designed well, with proper placebo controls, I bet there would be almost no difference between the treatment and control groups.

 

If they were only friends, that would be interesting but hard to criticize.

According to ME-pedia however, Fors is a member of Wyller's, Landmark's et al LP research project.

Didn't fact-check -- here's the me-pedia link:

https://me-pedia.org/wiki/Live_Landmark

Edit: Forum thread here. Sorry, can't find the link to the study now.

 

Yes, I forgot to include the fact that he's a part of her study, but you're absolutely correct. Regarding the nature of their relationship, I've also seen her refer to him as her "mentor" somewhere, but I can't remember where. Whatever "mentor" may mean in this context. But I'm pretty sure they have a close personal relationship that also includes a shared, unshakeable belief in the infallibility of the BPS-ideology.

 

Found some info about the nature of Egil Fors involvement in the Lightning Process study from the project documents. Translated to English through Google from Norwegian it says:

"Co-supervisors at NTNU are Associate Professor Mons Bendixen at the Department of Psychology at
Faculty of Social Sciences and Education and Professor Egil Fors at the Department of
community medicine and nursing at the Faculty of Medicine and Health Sciences, where Fors is one of
Norway's foremost pain researchers. Professor Fors has recently conducted a study on cognitive
therapy on patients with chronic fatigue and has been the candidate's mentor since 2010."

The candidate here is of course Live Landmark.

This is the source, if anybody wants to look more closely into it: https://lillemeglede.files.wordpress.com/2020/05/prosjektbeskrivelse.pdf

 

I think the key word here is "waiting list control group".

Patients who received treatment I-CBT were compared to patients who also wanted I-CBT but were put on a waitlist for several weeks before they could try it.

Suppose a manufacturer wants to test the satisfaction with a new laptop model they have made. They recruit people who really want a laptop, randomize them into two groups and then test whether people who got the laptop are more satisfied than people who are put on a waiting list to get the laptop.

People who got the laptop will probably tell they are more satisfied than those who still forced to wait for the laptop. Does this mean that the computer is any good? Unfortunately, no. You'll have to compare the new laptop against another laptop to know if it is a good model.

 

Yes throughout the paper, the authors seem to favour I-CBT because that's the version they made and it's shorter and cheaper and at follow-up it didn't perform much worse than traditional CBT.

The problem, however, is that the I-CBT intervention didn't significantly outperform the waiting list control group for the primary outcome. Physical functioning in this group was 6.8 points higher than in the waiting list control group, while the authors themselves have defined the minimal important difference at 10 points. So as @cassava7 pointed out the statement in the abstract:

Seems to be an error.

Also confusing to write that the treatment effect was maintained at follow-up when there wasn't even a waiting list control group at that point.

 

Landmark tweetet the study today.
She says that the study finds that CBT is safe, is that so?

 

In the same sense as homeopathy and spoon-bending are safe. Same with rocks. Rocks are safe. That obviously includes tiger-repelling rocks. I think by that logic that means tiger-repelling rocks have the official support of the Norwegian health authorities but I'm not sure if that's the whole logic or just an arbitrarily convenient one*.


(* it's definitely that one)