Written Exposure Therapy vs Cognitive Processing Therapy-Reply

COMMENT & RESPONSE

In Reply

Two letters published in this issue of JAMA Psychiatry raise several questions about our study,¹ and we are pleased to have an opportunity to respond. Owing to space limitations, we have responded to those comments that have the greatest implications for our study findings and implications for methods used in randomized clinical trials about posttraumatic stress disorder (PTSD) more generally.

Perhaps the most significant issue raised pertains to the timing of assessments. Posttraumatic stress disorder treatment studies typically include an immediate posttreatment and at least 1 follow-up assessment.However, we could not use this approach because we compared 1 treatment that included 5 sessions and another that included 12 sessions; therefore, the timing of posttreatment assessments differed substantially. This difference in timing would have confounded any observed differences in treatment outcomes. To avoid any confounding, we scheduled the assessments for both treatments at equal intervals from baseline. Importantly, we scheduled assessments to approximate the end of treatment for participants in the 2 treatment groups. Of the treatment completers, everyone in written exposure therapy completed treatment by the 6-week assessment and 56% in cognitive processing therapy completed by the 12-week assessment.

Concern about assessment timing when comparing treatments is broadly applicable to PTSD treatment outcome research. Although investigators generally assume that posttreatment assessment occurs at the same time for all participants, this assumption can be incorrect. Some cognitive processing therapy participants in our study took significantly longer than 12 weeks to complete the protocol, and our study is not an outlier in that respect.² Any systematic group difference in the time to complete treatment could confound study results. Yet, investigators do not typically report the mean number (and range) of days their participants take to complete treatment protocols and do not control for any group differences in their analyses. We suggest that treatment outcome researchers begin collecting and reporting such information in their publications.

Another concern raised in both letters pertains to statistical power, although from opposing perspectives. Monson and colleagues suggested that we were sufficiently powered to conduct a completer analysis and wondered if there are treatment differences in the percentage of participants with a PTSD diagnosis at the last assessment. Analysis revealed no significant treatment difference (P = .18). In contrast, Leichsenring and Steinert argued that our entire study is underpowered. Notably, our sample size either meets or exceeds that of every other PTSD noninferiority trial, to our knowledge,^3–6 and we planned appropriately for our proposed analyses.

Other important stated concerns were the noninferiority margin used and the lack of reporting on secondary study outcomes. Regarding the noninferiority margin, we relied on what has been previously established for the prior version of the Clinician-Administered PTSD Scale (CAPS) because there is no established margin for the CAPS-5 (ie, CAPS for DSM-5) yet. This highlights the importance of identifying a noninferiority margin for the CAPS-5. Regarding outcomes, our study was designed specifically to examine changes in PTSD symptoms and diagnostic status, both of which were measured by the CAPS-5, an instrument widely considered to be the criterion standard. Examining additional outcomes not specified in a priori hypotheses runs the risk of capitalizing on chance.