Post-traumatic stress disorder (PTSD) is a highly disabling condition, with recent estimates reporting a lifetime prevalence (Box 1) of 5.6% among trauma-exposed people worldwide (ranging from 0.5% to 14.5% between countries) (Koenen Reference Koenen, Ratanatharathorn and Ng2017a). The World Health Organization (WHO) further reported an age-standardised point prevalence of 15.3% specific to conflict settings (Charlson Reference Charlson, van Ommeren and Flaxman2019).
BOX 1 What is prevalence?
Prevalence refers to the number/percentage of people with a disorder/risk factor/characteristic within a specific time period. It is calculated using the formula:
It is often reported using a percentage or number per 10 000/per 100 000.
Lifetime prevalence refers to the proportion of people who have ever had the disorder in their lifetime.
The point prevalence is the proportion of people who have the disorder at a specific time point.
The age-standardised prevalence allows a comparison of prevalence rates between populations, where the age ranges in the populations are different. For example, in a sample with an ageing population, the prevalence of a disease more common in older age would be higher than in a younger population group.
Prevalence is often confused with incidence, which is the rate of new cases/an event (e.g. death) in a specific time period.
PTSD can be associated with increased psychiatric comorbidities, including depression, anxiety, suicidality and substance misuse (Brady Reference Brady, Killeen and Brewerton2000; Debell Reference Debell, Fear and Head2014; Head Reference Head, Goodwin and Debell2016; Facer-Irwin Reference Facer-Irwin, Blackwood and Bird2019), and with higher risk of cardiovascular disease, type 2 diabetes, stroke, respiratory problems, pain and cancer (Buckley Reference Buckley, Mozley and Bedard2004; Kubzansky Reference Kubzansky, Koenen and Spiro2007; Possemato Reference Possemato, Wade and Andersen2010; Asnaani Reference Asnaani, Reddy and Shea2014; Koenen Reference Koenen, Sumner and Gilsanz2017b). People with PTSD therefore have a high demand for specialised healthcare services. Furthermore, there is a significant economic burden. For example, Kessler (Reference Kessler2000) showed a loss of 3.6 workdays/month (missing part or all of a workday or working less efficiently), with an annual productivity loss of $3 billion in the USA. More recent data have shown excess direct and indirect costs to be over $232 billion in 2018 in the USA (Davis Reference Davis, Schein and Cloutier2022).
Given the impact, identifying effective pharmacotherapy for PTSD is vital, and this month's Cochrane Corner review (Williams Reference Williams, Phillips and Stein2022) offers beneficial guidance for clinicians. However, it is important that evidence from the literature is carefully analysed, as recommendations based on poor-quality evidence could have negative implications. This commentary intends to give a balanced view of the review, to further inform professionals on its usefulness in clinical practice.
What has been found before this?
National Institute for Health and Care Excellence (NICE) guidelines for PTSD recommend primarily psychological approaches, advising that drug therapy should not be used first line (NICE 2018a). When appropriate, selective serotonin reuptake inhibitors (SSRIs: sertraline and paroxetine) and venlafaxine are recommended. Antipsychotics can be considered in case of non-response or if arousal or psychotic symptoms are present. Some other studies reviewed for possible inclusion in the NICE guidelines also showed significant results for amitriptyline, imipramine, phenelzine, prazosin, hydroxyzine and eszopiclone (Davidson Reference Davidson, Kudler and Smith1990; Kosten Reference Kosten, Frank and Dan1991; Raskind Reference Raskind, Peskind and Hoff2007; Pollack Reference Pollack, Hoge and Wothington2011; Ahmadpanah Reference Ahmadpanah, Sabzeiee and Hosseini2014). However, in these studies, the evidence base was found to be too small to be confident that the benefits were the true effects (NICE 2018b). Given the large impact of PTSD and the potential for effective pharmacological treatments, it is key to follow an evidenced-based treatment strategy to optimise recovery.
Previous reviews reported that SSRIs showed a small but significant effect size compared with placebo, especially fluoxetine, paroxetine, and venlafaxine (Hoskins Reference Hoskins, Pearce and Bethell2015). Interestingly, no statistically significant evidence for sertraline, currently licensed for PTSD, was found. Others (Albucher Reference Albucher and Liberzon2002; Asnis Reference Asnis, Kohn and Henderson2004; Ipser Reference Ipser and Stein2012; Coventry Reference Coventry, Meader and Melton2020) also highlighted the promising therapeutic potential of venlafaxine, mirtazapine, nefazodone, trazodone, prazosin and antipsychotics.
This month's Cochrane Review (Williams Reference Williams, Phillips and Stein2022) is an update of previous versions (Stein Reference Stein, Zungu-Dirwayi and van der Linden2000, Reference Stein, Ipser and Seedat2006). The review authors acknowledge that several recent reviews have provided a helpful summary of pharmacotherapy for PTSD but they note that these had various methodological weaknesses. In the present review they therefore aimed to assess the literature using improved methods and a systematic search strategy.
Is there a clear research question?
This Cochrane Review clearly specified its research question using the PICO model (patient, population or problem; intervention; comparison; outcome). Only randomised controlled trials (RCTs) were included. Participants included were diagnosed with PTSD (population). A PTSD diagnosis was ‘as determined by the study author’, with no mention of the specific diagnostic criteria used, symptom duration or severity, although these were then tabulated to look at their impact on the medication effect. No restrictions were made to exclude patients with comorbid disorders.
A wide range of medication was listed as the intervention. Polypharmacotherapy was allowed, but studies with participants undergoing psychotherapy were excluded. Interventions were compared with either placebo or another medication (comparison). There were no restrictions placed on timing, dosage or duration of treatment.
Primary outcomes focused on treatment efficacy, determined using the Clinical Global Impressions Scale – Improvement (CGI-I), and treatment tolerability (outcome). The review authors note that they chose the CGI-I because it is a widely used outcome measure in RCTs looking at PTSD and they therefore concluded that it was robust. There is little information given beyond this, and the reference (Davidson Reference Davidson1997) links to an article seemingly unrelated to the statement, so it is unclear what the evidence is for this.
It seems that the primary outcome measure (the CGI-I) is quite a simple, broad and generalised scale, whereas it might have been more helpful to have used a PTSD symptom-specific scale (such as the Clinically Administered PTSD Scale (CAPS), which they did use to assess the secondary outcome of PTSD symptom reduction). This would have perhaps fit better with the review's main objective, assessing the effects of medication in reducing PTSD symptoms. The review found that 36 of the 66 RCTs used the CGI-I (primary outcome) as their primary or secondary outcome whereas 47 of the 66 RCTs used the CAPS, indicating that perhaps the CAPS would have been better as a primary outcome measure as there were more data to examine. As the CGI-I is a subjective scale, there is likely to be an effect on the reliability and validity of this outcome measure.
This Round the Corner commentary will focus on the primary outcome of treatment efficacy, determined using the CGI-I; results for treatment tolerability and secondary outcomes will not be discussed in detail.
I used the PRISMA checklist (Box 2) to critically appraise this Cochrane Review.
BOX 2 The PRISMA checklist
The Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) checklist is an evidence-based list advising those writing systematic reviews and meta-analyses of the minimum information they need to include, to encourage transparency in reporting (Page Reference Page, McKenzie and Bossuyt2021). The checklist can also be used to critically appraise reviews, as it goes through what it is necessary to report. Fig. 1 shows an example of the first page of the checklist (Page Reference Page, McKenzie and Bossuyt2021). Most people are aware of PRISMA guidelines, but more for their use in PRISMA flowcharts (Fig. 2). A PRISMA flowchart is recommended for use in systematic reviews, documenting how many records were retrieved and each stage of the inclusion/exclusion process.
FIG 1 Example of a section of the PRISMA checklist (adapted from Page et al, Reference Page, McKenzie and Bossuyt2021, licensed under CC BY 4.0).
FIG 2 A mock PRISMA flowchart (created using the template in Page et al, Reference Page, McKenzie and Bossuyt2021).
How were the searches performed?
The review authors searched eight databases: the Cochrane Central Register of Controlled Trials, Cochrane Common Mental Disorders Controlled Trials Register, Embase, MEDLINE, PsycInfo, PTSDPubs Proquest, Clinicaltrials.gov and the WHO International Clinical Trials Registry Platform. As some lesser-known medications were also investigated, searches were performed for ‘population only’ (i.e. no search terms for interventions were included). These trials would probably have been missed otherwise – the search strategy was therefore evidence of good practice for trying to capture all the relevant literature. The review's appendix contains the search terms but does not mention whether searches were made in languages other than English, although this seems to be the case, as there was no language filter. The Cochrane Handbook (Higgins Reference Higgins and Thomas2022: Box 1.5.a) states that removing language restrictions, which is what the authors seem to have done in this case, is not a good substitute for searching non-English databases. Relevant RCTs from across the world might have been overlooked as a result.
Assessment of publication/reporting bias was demonstrated through funnel plots, although this could only be calculated for SSRIs, as the calculation was dependent on having >10 trials. Risk of bias was assessed using the Cochrane risk of bias tool (Higgins Reference Higgins, Altman, Sterne, Higgins and Green2011). Quality of the evidence was assessed using the Grading of Recommendations Assessment, Development and Evaluation (GRADE) framework (Schünemann Reference Schünemann, Brozėk and Guyatt2013).
What did the results show?
In total, 66 RCTs were eligible for inclusion, with 54 included in the meta-analysis, involving 7442 individuals aged 18–82 years with PTSD. The review explained that six RCTs not included were small and of poor quality, with not enough information for the meta-analysis. The omission of these RCTs was documented to be unlikely to have had an impact on the results, although there does not seem to be any evidence that this was tested. It is not clear why a further six trials were excluded.
All articles were in English, perhaps suggesting that studies in other languages could not be found.
SSRIs had a statistically significant beneficial effect compared with placebo (RR = 0.66, 95% CI 0.59–0.74), from 8 studies with moderate-certainty evidence. The review found that 58% of the SSRI group responded, compared with 35% on placebo. Sertraline (RR = 0.68, 95% CI 0.56–0.81) and paroxetine (RR = 0.64, 95% CI 0.55–0.74) showed benefit, but not fluoxetine (RR = 0.73, 95% CI 0.19–2.82), possibly owing to the small sample size (65 participants).
Positive results were also found for mirtazapine (RR = 0.45, 95% CI 0.22–0.94, 1 study), with 65% response versus 22% for placebo (low-certainty evidence), and for amitriptyline (RR = 0.60, 95% CI 0.38–0.96, 1 study), with 50% response versus 17% for placebo (low-certainty evidence).
No benefit was found for antipsychotics (RR = 0.51, 95% CI 0.16–1.67, 2 studies), anticonvulsants, GR205171, GSK561679 and brofaromine. No studies could be found that used the CGI-I as an outcome measure for venlafaxine or other included medications. The review also looked at the total effect of medications compared with placebo across all medication classes, showing a benefit (RR = 0.74, 95% CI 0.64–0.85).
In total, 17 comparisons with placebo were performed between medication classes, ranging from those currently recommended, such as SSRIs (NICE 2018a), to lesser-known drugs, such as NK-1 receptor antagonists. Results suggested there was no evidence that most of the listed medications improved treatment efficacy. The strength of these conclusions was limited by the low quality of available evidence.
Sixteen studies were measured as being at high risk for at least one type of bias (Box 3); most studies had an unclear risk of bias. High/unclear risk of bias was related to studies that did not describe satisfactory randomisation (44 trials), allocation concealment (53 trials), participant masking (57 studies) and assessor masking (53 trials) – the most crucial domains in RCTs. Other sources of bias included industry involvement, which left a significant number of studies ranked as unclear.
BOX 3 Risk of bias
Risk of bias can be assessed using the Cochrane risk of bias tool. This has guidelines that support the author in the assessment of each study, looking at different areas where bias could be introduced (Sterne Reference Sterne, Savović and Page2019). In the current version (RoB 2) the areas evaluated are:
• randomisation (selection bias)
• allocation concealment (selection bias)
• masking (‘blinding’) of participants and staff (performance bias)
• masking (‘blinding’) of outcome assessment (detection bias)
• missing data (attrition bias)
• selective reporting (reporting bias)
• other bias.
Each area is given a ranking – low, unclear or high risk of bias – and the reasoning for the ranking is given.
Risk of bias assessments can be displayed in a chart for easier reading, as shown in Fig. 3.
A high level of heterogeneity was also seen between RCTs (Box 4).
BOX 4 Heterogeneity
It is impossible to complete clinical studies that are the same in their methods, population demographics and statistics. There will always be some level of variability between studies. The measure of heterogeneity is the difference between studies not thought to be due to chance.
Heterogeneity is also demonstrated within the methods and statistical tests used. It is more difficult to compare two randomised controlled trials if one is double-blind and the other is not. In this review it seems that there was a lack of information on the level of masking (‘blinding’) and randomisation in the studies (Williams Reference Williams, Phillips and Stein2022).
Heterogeneity can be measured as a statistic. Confidence intervals are calculated for each study, and generally, if these do not cross, then there is evidence of heterogeneity. This can be seen visually on a forest plot and can be commented on using a χ2-test and I 2-statistic. If the P-value of the χ2-test is <0.1, then there is statistically significant heterogeneity between the studies. A high P-value is related to the low power of the χ2-test when there are few studies or small sample size; heterogeneity can be missed when P < 0.05. When the number of studies is low, it is better to look at the I 2, a percentage giving an estimate of the level of variability due to heterogeneity rather than chance.
For example, a statistically significant χ2-test P-value of 0.007 and an I 2 of 54% indicate that there may be substantial heterogeneity present.
GRADE ratings suggested that most of the certainty of evidence was very low or low (Schünemann Reference Schünemann, Brozėk and Guyatt2013).
FIG 3 A mock risk of bias chart created using the Risk-of-bias VISualization (robvis) tool (robvis is described in McGuinness & Higgins, Reference McGuinness and Higgins2020).
Subgroup analysis showed evidence of better treatment response in trials including participants with major depressive disorder (22 trials clearly included such participants, seven did not and the rest were unclear). The review authors queried whether this response was related to treating PTSD or depressive symptoms. There was also a non-significant between-group benefit on the CGI-I for trials that did not include war veterans compared with trials that did, perhaps because there was more treatment-resistance in the latter subgroup.
Thoughts on the results and review
This Cochrane Review showed a beneficial effect of SSRIs, mirtazapine and amitriptyline in treating PTSD. The review attempted to find high-quality evidence from RCTs, but it was difficult to assess the clinical significance of the results found, given the mostly unclear risk of bias for the included studies (due to lack of information within trials) and the certainty of evidence being ‘very low’ to ‘moderate’.
Bias
Of the 66 trials, 16 were assessed as being at high risk of bias. However, one trial (Li Reference Li, Ma and Yang2017) showed that it was feasible to conduct a trial with a relatively low level of bias, with only one domain scoring as unclear (publication bias). Although SSRIs had the most studies, the majority were assessed as being at unclear risk of bias for randomisation, which has an impact on their internal validity.
It is unclear why the review authors used an archived version of the Cochrane Handbook and risk of bias tool (Higgins Reference Higgins, Altman, Sterne, Higgins and Green2011), as the most recent version of the handbook is from February 2022 (Higgins Reference Higgins and Thomas2022) and the RoB 2 was published in 2019 (Sterne Reference Sterne, Savović and Page2019).
Heterogeneity
There was significant methodological and clinical heterogeneity between studies. No clear definition was provided for a PTSD diagnosis, only that it was ‘as determined by the study author’. The review authors may have done this to capture the widest number of studies. In individual studies, the diagnostic criteria used included the CAPS, MINI, DSM-III, DSM-III-R, DSM-IV and DSM-IV-TR. It would have been helpful to have a definitive guideline regarding a diagnosis of PTSD in this review, even if it was that participants met the relevant DSM diagnostic criteria at the time of the study. The phrase ‘as determined by the study author’ leaves a lot of questions. The non-specific definition gives rise to possible problems with the review's findings: participants in the various studies might have varied significantly in symptom severity, dose and treatment resistance, thus affecting treatment efficacy. The review authors mentioned they did ‘tabulate’ the differences in clinical features between participants, but they did not include an analysis looking into whether these clinical characteristics had any effect on response.
To highlight some of the variety in clinical factors: treatment length varied between 13 days and 28 weeks; the mean age ranged from 27.9 to 59.8 years; sample sizes ranged from 12 to 551 participants; and follow-up ranged from 2 weeks to 6 months. There were no comparisons made for duration of illness, and no subgroup analysis looking at the possible heterogeneity between these clinical factors. It is unclear whether this would have made a difference to the findings.
Subgroup analysis was conducted to examine the effect of heterogeneity between single versus multicentre trials – results indicating low or no heterogeneity. The analysis also assessed the differences between trials including and excluding participants with depression, showing an I 2 of 61.1%. This indicates possible substantial heterogeneity, although this statistic needs to be interpreted with caution because only one small trial was available in this subgroup, responsible for all of the heterogeneity.
Eligibility criteria
Many of the RCTs excluded participants with substance misuse or physical health problems, common comorbidities in PTSD, thus reducing the generalisability of the results. The review authors could have explored this in a subgroup analysis – the impact of comorbid physical health conditions on response.
There was further variability among study inclusion and exclusion criteria, some including participants with sleep disorders, some excluding women of childbearing potential if they did not use contraception, and whether participants could be on other medication. Some studies included participants having ongoing psychotherapy, which was in contradiction to the exclusion criteria for the review, which specified that those receiving psychological therapy should be excluded.
Lack of studies
The review authors intended to investigate a large range of medications, but most medications had only one or no trials to draw data from, leaving the results for these non-significant, biased or absent.
Surprisingly, no studies were found on the efficacy of venlafaxine as determined by the CGI-I (primary outcome), despite it being recommended by NICE (NICE 2018a). Two venlafaxine studies were found that used the CAPS to measure the secondary outcome of PTSD symptom reduction. This shows that perhaps the secondary outcome of change in symptom severity may have been more suitable as the primary outcome, as there seemed to be more data.
The SSRI group had the most studies, but for the primary outcome, this only included eight studies. Despite SSRIs being reported to be superior, some studies showed no difference in reduction of PTSD symptoms.
Mirtazapine and amitriptyline each had only one study, but the review authors were transparent about the paucity of evidence, making it clear in the abstract.
Funding of the trials
A relevant aspect is that 35 of the 66 identified RCTS (53%) were industry-funded, potentially increasing the risk of sponsorship bias – a common problem with pharmacotherapy trials. A larger reduction in PTSD symptom scores in industry-funded studies was observed, with potential implications for the reliability of these results. However, when you look at the CGI-I, although there was an improvement in symptoms in both groups, the differences between the groups were not statistically significant, perhaps indicating that again symptom severity scores would have been more valid.
What conclusions can we make?
This review concluded that SSRIs have the most evidence of benefit in the treatment of PTSD, in line with previous reviews and guidelines (Albucher Reference Albucher and Liberzon2002; Asnis Reference Asnis, Kohn and Henderson2004; Ipser Reference Ipser and Stein2012; Hoskins Reference Hoskins, Pearce and Bethell2015, Reference Hoskins, Bridges and Sinnerton2021; American Psychological Association 2017; NICE 2018a; Coventry Reference Coventry, Meader and Melton2020). These guidelines also mention several other helpful medications, including venlafaxine and antipsychotics, that were found in the secondary outcomes of this review. The review also found positive evidence for mirtazapine and amitriptyline.
The high level of heterogeneity between studies and low quality of data, with mostly low certainty and generally unclear risk of bias, makes it difficult to reach any definitive conclusions. Further RCTs with lower risk of bias, improved study design and involving a more generalisable population are therefore needed.
Acknowledgement
I would like to thank Dr Riccardo De Giorgi for his advice and support with this commentary.
Funding
This research received no specific grant from any funding agency, commercial or not-for-profit sectors.
Declaration of interest
None.
eLetters
No eLetters have been published for this article.