Dear editor,

We are pleased to respond to Drs Lee and Hoge's1 commentary on our randomised controlled trial (RCT) published in JAMA (a summary of the original article can be found at https://www.ncbi.nlm.nih.gov/pubmed/26241597).2 While we readily acknowledge several limitations to the study, Drs Lee and Hoge have failed to consider or acknowledge several aspects of the study and its results.

The main concern with Lee and Hoge's critique is its focus on a single time-point of data that seems to invite readers to ignore all other data. Lee and Hoge argue that the lack of a statistically significant difference between groups at post-treatment equates, of necessity, to a lack of evidence of effectiveness. The authors neglect to consider that despite appropriate randomisation procedures, which they commend, there were significant differences between groups on baseline PTSD symptoms. Participants in the mindfulness-based stress reduction group had significantly greater severity of baseline PTSD symptoms than those in the present-centred therapy group as measured by both the patient-reported PTSD Checklist (PCL; mean score 63.6 vs 58.8) and Clinician-Administered PTSD Scale (CAPS; mean score 69.9 vs 62.5). As a result, similar levels of outcomes at post-treatment reflect greater amounts of change in the treatment group than the active-control group. Put another way, there was a 9.2-point drop in PCL scores over the course of the study for the mindfulness group compared to a 2.8-point drop for the present-centred group. This difference in change was indeed statistically significant. Lee and Hoge argue that the change over time is ‘a less clinically significant variable’. This is a startling assertion since change over time is precisely the desired outcome of any psychotherapy. The term ‘clinical significance’ is typically used to refer to changes in symptoms that are clinically meaningful or noticeable to the patient. Clinical significance is measured using what is called a ‘minimal clinically important difference’ (MCID) score, which is the smallest change in an outcome (eg, PTSD symptoms) that a patient would identify as important. A reduction of 10 or more points on the PCL is considered a minimally clinically important difference.3 Based on this widely used operational definition, we found that a greater proportion of participants in the treatment group showed clinically significant improvements in PTSD symptoms at follow-up than the control group (48.9% vs 28.1%). In contrast to Lee and Hoge, we do believe such a difference between groups is clinically meaningful.

In the present RCT, we used linear mixed-effects models to analyse the efficacy of mindfulness-based stress reduction compared with present-centred group therapy over 9 weeks of treatment and at 2-month follow-up. Linear-mixed models and growth curve analysis are the most widely used approach in intent-to-treat analyses of longitudinal data4 and have been used extensively for over two decades.5 ,6 The validity and merit of this approach cannot be accurately described as ‘uncertain’; rather, it is the standard approach.

Lee and Hoge appropriately pointed out that the PCL is a self-report measure that brings with it inherent limitations. It was chosen in this case as the primary outcome because it allows a more thorough assessment of change by facilitating more frequent observation of symptoms. Determination of the primary outcome is made prior to initiation of the clinical trial and is documented in our clinical trial registration on clinicaltrials.gov. Here also, there is a myopic focus in Lee and Hoge's argument in that it disregards the fact that the present study collected, analysed and reported results on the very ‘gold standard’ blinded clinical interviews that they advocate for, and with very similar results (a change of 20.1 points in the mindfulness group compared to a change of 11.9 points in the present-centred group on the CAPS). This statistically significant difference makes it hard to credit their claim “…CAPS scores started and ended at almost identical points.”

Our assertion is not that this study is without flaws, or that it has definitively established that mindfulness-based stress reduction should be used as a first-line treatment for PTSD. Lee and Hoge do make some excellent points about differences between the two conditions in terms of length of sessions and total clinical time spent with patients. Issues of differential time and attention remain empirical questions that can and should be addressed in future studies. While we have previously acknowledged the design weaknesses highlighted by Drs Lee and Hoge, and indeed several other limitations, we find no merit in their assertion that our data reporting and analysis were questionable, and we are concerned by what appears to be their misleading interpretation of our findings. It seems questionable to ignore the preponderance of data collected and focus exclusively on a single time point, and a single measure, in a clinical trial. In our view, doing so can introduce serious bias in the reporting and interpretation of these results.