Implications for clinical practice, training and treatment

The present review has several strengths, in particular the close attention to RCT control arm type and study quality, the inclusion of post-treatment as well as follow-up findings and the use of two ways of exploring the effect of trauma frequency on treatment efficacy. Moreover, the present work was conducted in accordance with gold standard guidelines on meta-analysis (i.e. PRISMA guidelines), all steps were carried out by at least two researchers working independently and discrepancies were solved through through discussions until consensus was reached. Last, we adjusted for the fact that dichotomising a continuous variable is always associated with a certain degree of arbitrariness and might blur results. That is, we assessed the potential influence of trauma frequency on efficacy outcomes both dichotomously as well as continuously and results were in line.

Identification and selection of studies

Some limitations also need to be noted. First, some studies had to be excluded from the quantitative analyses as they did not report trauma frequency. Therefore, we strongly encourage authors to report on this important clinical variable. Second, our definition of multiple trauma can be criticised. Our cut-off for being considered a multiple-exposure trial was that at least 50% of participants had suffered multiple trauma exposures. However, we carried out a sensitivity analysis with a more conservative definition of multiple-exposure trial (i.e. at least 90% of participants reporting multiple lifetime trauma exposures) and results and conclusions were very similar (i.e. no differential treatment efficacy between single- versus multiple-exposure trials). Third, it would have been desirable also to focus on other metrics of treatment success beyond standardised mean differences. However, in the field of paediatric PTSD there is no gold standard definition of treatment response or clinically meaningful change. Applied definitions of treatment success varied substantially between included trials (e.g. a decrease in symptom severity of at least 50% pre- to post-treatment, participant not scoring within the clinical range on a self-report measure at post-treatment, participant not meeting diagnostic criteria in a clinical interview at post-treatment) and most trials (and particularly older trials) reported only group means. Fourth, some of the included trials were of low methodological quality. Although trial quality across all trials was moderate (mean 5.37 Nisa in Portugal marriage agency out of 8), some trials had a low quality sum score (e.g. owing to n ? 50 or application of completer analyses). However, all included trials fulfilled our rather strict inclusion criteria and thus were of sufficient methodological rigour to warrant valid analyses. For instance, we only included trials with n ? 20, in an effort to exclude chance findings. Last, the generalisability of results from RCTs to clinical practice might be impeded by the (required) standardisation (e.g. inclusion and exclusion criteria for participants, highly standardised treatments).

Categorisation of treatment and control groups

We performed various checks for detecting and addressing (potential) biases. We performed outlier-adjusted analyses whenever we detected one or more outliers. As recommended, Reference Tabachnick and Fidell 23 we defined outliers as g-values that were extraordinarily high or low (i.e. scoring at least 3.3 standard deviations below or above the pooled g for the given comparison). We conducted additional moderator analyses to identify whether trial quality (see Risk of bias assessment’ above) may bias results and potentially confound hypothesised effects. More specifically, we analysed in meta-regressions within the single- versus multiple-trauma categories whether or not trial quality was associated with outcomes when the evidence base was sufficiently large (k ? 10). As recommended, Reference Sterne, Sutton, Ioannidis, Terrin, Jones and Lau 19 we only checked for potential publication bias when the evidence base was sufficiently large (k ? 10). We checked for potential publication bias using Egger’s test of asymmetry. Reference Egger, Smith, Schneider and Minder 24 As recommended, Reference Duval and Tweedie 25 we only performed the trim-and-fill method when the Egger’s test was statistically significant. The trim-and-fill method supplies asymmetry-adjusted estimates by introducing hypothetical effects.

Fig. 2 Forest plots depicting the efficacy of psychological interventions versus passive control conditions at treatment end-point in samples exposed to (a) a single trauma or (b) (mainly) multiple traumas.