Comments on “The Efficacy and Durability of Mindfulness-based Cognitive Therapy in the Treatment of Anxiety and Depressive Disorders: A Systematic Review and Meta-analysis”

Dear Editor,

Nandarathana and Ranjan, ¹ described a systematic review and meta-analysis of the short- and long-term efficacy of mindfulness-based cognitive therapy (MBCT) in anxiety and depressive disorders. This study is essential. However, we present specific observations to guide the authors and other researchers in their future work, as this is an essential objective of constructive academic dialogue.

First, the article did not clarify which anxiety and depressive disorders were studied in the included trials. We therefore cannot determine to which diagnostic categories the findings of the meta-analysis apply. When pooled effect sizes are derived from diagnostically heterogeneous samples, the clinical generalizability of the findings is unclear, making the findings challenging to interpret and potentially misleading.

Second, the article did not state which outcome measures were prioritized, and why, when studies included multiple instruments; this may have resulted in the selective extraction of data that favored the authors’ hypotheses. Furthermore, the article did not present the data extracted in either forest plots or tables. Given that the Morris method ² was used to compute pooled effect sizes, data on means and standard deviations at both baseline and post-treatment would have been required for the MBCT and control groups separately, for each study. It is not evident whether these data were consistently available in the primary studies. It is also unclear whether the authors used endpoint scores or change scores in their calculations. This distinction is important because many studies report only change scores post-treatment, and such scores are inappropriate for the Morris method computations required in a follow-up analysis. Without access to the extracted data and without clarity on how they were handled, the reader cannot understand the baseline severity of illness in each study, the absolute improvements, and the correctness of the statistical processing.

Third, all analyses were characterized by very high statistical heterogeneity, with I² values ranging from 91% to 99%. The article did not present subgroup analyses by diagnostic category, by region of origin of the studies, or by type of control group (e.g., waitlist, active treatment, treatment as usual [TAU]), nor did it explore heterogeneity using meta-regression. Sensitivity analyses did not lead to a meaningful reduction in heterogeneity. In the absence of successful efforts to explain heterogeneity, the pooled results cannot be assumed to represent beneficial summary effects.

Fourth, the article presented a questionable definition of durability. It examined whether changes in pooled symptom scores from post-treatment to follow-up differed between the MBCT and control groups. However, this approach fails to consider the absolute symptom levels at follow-up. If both groups deteriorated equally over time, the analysis conducted would still indicate durability of response despite a loss of treatment benefit. True durability should also be demonstrated by the stability of the absolute scores.

Other concerns also deserve mention. First, the search strategy was simplistic and may have failed to identify all eligible studies. Second, the statistical plan of analysis was not clearly outlined. Third, in the article, Table 1 included four columns that presented identical information across studies but omitted important details such as diagnoses, sample sizes, and outcome data for each study. Fourth, the components of TAU were not described, and so it remains unclear whether patients received pharmacotherapy, psychotherapy, or minimal intervention. Medication use was permitted in both the MBCT and control groups, but was not quantified. These factors introduce uncontrolled confounds that limit interpretability. Fifth, most studies used self-rated measures and waitlist controls. Given the absence of placebo effects in waitlisted patients and the impossibility of patient blinding in waitlist control designs, the risk of bias is likely to be high; however, the article reported a low risk of bias in most studies.

In summary, we applaud the authors for their hard work and especially for their use of the Morris method to estimate effect size. However, for reasons that we have explained, the conclusions drawn about the long-term efficacy of MBCT remain open to question.