The implications of Leuchter et al’s research ^{Reference Leuchter, Hunter, Tartter and Cook1} not only have potential for our further understanding of placebo responses in clinical trials, but also bring into question the pharmacological advantage of antidepressant medication over placebo in clinical outcomes for depression. Their findings warrant full evaluation so that they can be considered within the context of the wider research base. However, an accurate appraisal is currently limited by a lack of clarity in the methodology presented. We suggest several areas in which further clarification could assist critical appraisal.

First, the use of the Hamilton Rating Scale for Depression (HRSD) as a measure of depression severity warrants discussion. A 2014 literature review failed to find evidence to support its use, describing it as irretrievably flawed. Interestingly, many scale items were not found to sufficiently contribute to the measure of depression severity. ^{Reference Bagby, Ryder, Schuller and Marshall2} Without a valid measure of severity, can we be assured that participants met criteria for at least moderate depressive symptoms at baseline? Any failure to exclude those with milder symptoms could also account for the similar outcomes demonstrated in pill-taking groups. The National Institute for Health and Care Excellence advocate the avoidance of antidepressant prescription in those with less than moderate depressive symptoms, because of the poor risk-benefit ratio. ³

In terms of the study design, the sample size appears to be smaller than one would anticipate. This is not helped by the significant, 24% loss to follow-up. Given that the report does not reference a power calculation, are the authors able to provide clarity regarding their choice of sample size?

The process of recruitment also requires clarification. Recruitment via advertisement can be prone to selection bias and can account for loss of external validity within studies. ^{Reference Fransen, van Marrewijk, Mujakovic, Muris, Laheij and Numans4} We suggest that advertisement recruitment may have attracted participants particularly keen to seek active treatment, possibly in order to avoid healthcare expenditure. It is understood that random allocation of recruited participants took place. Further clarification regarding this process would be helpful.

It is also understood that research coordinators were blinded during supportive-care interactions. Double-blinding is clearly essential in a study that involves a subjective outcome measure. Given that the research coordinators were often trained nurses, we raise the concern that they may have recognised relevant side-effects and unintentionally deduced a participant’s group assignment. With any loss of their impartiality, clinicians form expectations and these have the power to significantly influence outcomes. ^{Reference Even, Siobud-Dorocant and Dardennes5} As trained nurses, it is also likely that their interactions might have provided therapeutic input aside from that considered to be consistent with supportive care. Were certain professionals more likely to report improvements in the placebo group?

Of further interest, we cannot find evidence to rule out suicidal behaviour as another potential confounder in this study. Participants’ response to antidepressant medication may have been influenced by differences in serotonergic functioning, which has been linked to having a history of suicidal acts. ^{Reference Sullivan, Oquendo, Milak, Miller, Burke and Ogden6}

With the above concerns in mind, we suggest that further consideration of the risk of type II error may be of value. We would be interested in the extent to which the authors have explored the potential for type II error and welcome their response.