By David Tuller, DrPH
The Journal of Psychosomatic Research has often served as a house organ of sorts for the “biopsychosocial” ideological brigades. That’s to be expected, given that folks like Per Fink, Michael Sharpe, and Jon Stone are all members of the journal’s editorial board. It should therefore not be surprising that the journal would publish crap like “Cognitive-behavioral therapy for post COVID-19 condition: A pilot randomized controlled trial.”
This paper, published in late June, is the latest in a gusher of reports in which the researchers strive mightily to present underwhelming results in a positive light. On X, the account @mecfsskeptic has already explained the main issues with this trial, conducted by investigators from the psychology department at Johannes Gutenberg University in Mainz, Germany. I can’t really improve on @mecfsskeptic’s points, but they bear repeating nonetheless. So let’s go through why this study offers nothing new and actually documents that cognitive behavior therapy (CBT) does not work for this population.
Like similar trials, this one was unblinded—which is understandable when it comes to non-pharmacological interventions. However, unblinded trials that rely solely on subjective outcomes are a recipe for an unknown amount of bias, making their results hard to interpret. It should not be surprising when trials with this design produce marginally or modestly positive results in favor of the intervention, especially in the short term. In fact, that is what has generally occurred in these studies.
And that result is even more likely when participants in the comparison group are offered a “waiting list” condition—in essence, nothing. In many trials, investigators try to match the time and attention involved with the intervention in order to “control” for factors other than the therapeutic components that might impact participant responses. That didn’t happen in this case. In other words, it wasn’t really a “randomized controlled trial.” It was just randomized.
The trial included 53 participants who were “severely impaired” with “post-Covid condition” (PCC), per the World Health Organization’s definition. One problem here is that the WHO definition, like the umbrella term Long Covid itself, is very broad. Given the heterogeneous patient population, lumping everyone together as if they all have the same thing, rather than separating them into similar sub-groups, is not necessarily a smart approach.
In the trial, the participants were randomized to either CBT or the waiting list condition. The CBT consisted of eight group sessions and five individual sessions over the course of a few months. Assessments were taken right after the course of treatment and at three-month follow-up. The intervention was “based on a bio-psycho-social model and comprised cognitive and behavioral elements, including attention flexibility, cognitive restructuring, and modification of maladaptive activity patterns through behavioral experiments.” Typical stuff—the CBT targeted the factors believed by these to be causing the prolonged symptoms.
**********
A marginal reported benefit for the intervention
The main finding was a marginal benefit for the intervention arm in the primary outcome of self-reported fatigue right after treatment. The benefit was well within the range that might be expected from the bias inherent in the study design alone. As X commenter @HumanManifold pointed out, the benefit did not reach the threshold for what would be considered a minimal clinically important difference on the fatigue scale. In any event, that benefit disappeared by the three-month follow-up.
Beyond that issue, the investigators made an unusual choice—besides fatigue, they selected four other primary outcomes. (Most trials have one, or maybe two.) Right after treatment, besides the marginal benefit for the intervention arm on fatigue, there was a benefit on a breathing measure right that also disappeared at follow-up. The other three primary outcomes had null results both right after treatment and at follow-up. The intervention also showed no benefits for a range of secondary results, including depression and anxiety.
Despite all the outcomes, the investigators did not correct their results for having conducted multiple statistical tests—a standard step in such circumstances. Had they done so, the apparent benefits right after treatment for two of the five primary outcomes would no longer have been found to be statistically significant.
The investigators did acknowledge the obvious—their intervention didn’t work too well. But they make the unwarranted presumption that the reported finding of a marginal benefit right after treatment is an actual “treatment effect” rather than an artifact of the bias inherent in the study design.
Here’s what they wrote: “Overall, these findings point to potential challenges regarding the stability of treatment effects. From a clinical perspective, a short-term CBT intervention might be insufficient to ensure sustained improvements.” Seeking to address this concern, they proposed that solutions like “extending treatment duration and implementing booster sessions…could help to consolidate gains.” Of course, they provided no evidence to support the argument that extending treatment or adding booster sessions would do anything at all.
And here’s their conclusion: “This pilot trial suggests the feasibility and preliminary efficacy of CBT for PCC. Larger RCTs with active control groups should confirm these findings.”
No, the trial doesn’t suggest the preliminary efficacy of CBT for PCC, or any efficacy of CBT for PCC. And these meager findings do not suggest the need for larger trials. On the contrary, they suggest that further funding would be an indefensible waste of valuable resources. However, because this study reported a marginal benefit in fatigue right after treatment, CBT proponents will likely tout it as a “positive” trial that supports their position.