Pharmacotherapy for prevention of post‐traumatic stress disorder
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
1) To provide an estimate of the efficacy of medication in preventing the development of post‐traumatic stress disorder following exposure to a traumatic event. The efficacy of medication in reducing symptom severity for those individuals who subsequently develop PTSD will also be considered.
2) To determine whether particular classes of medication are more effective and/or acceptable than others in the prevention of PTSD.
3) To assess whether depression is a predictor of treatment response in the prevention of PTSD.
Background
Description of the condition
Post ‐traumatic stress disorder (PTSD) is a prevalent disorder which has been recognised in the latest edition of the Diagnostic and Statistical Manual (DSM‐IV) (APA 1994) as a pathological response to severe traumas, such as those experienced during combat, intimate partner violence and sexual abuse (Breslau 1991; Davidson 1991; Kessler 1995). The symptoms experienced by a person with PTSD can be classified within the following symptom clusters: intrusive/re‐experiencing (e.g. flashbacks, nightmares), avoidant/numbing (e.g. loss of interest, detachment), and hyperarousal (e.g. irritability and difficulty concentrating and sleeping).
There is evidence that PTSD is associated with substantial reductions in quality of life, a high co‐morbidity of psychiatric and medical disorders, marked functional impairment, and high economic costs (Solomon 1997; Brunello 2001). A nationally representative mental health survey, the National Comorbidity Survey, discovered that between 50 and 60% of people in the United States are exposed to trauma during their lifetimes, with a lifetime incidence of PTSD of 10.4% for women and 5% for men (Kessler 1995). A more recent replication of this survey discovered that as many as 3.5% of those interviewed developed PTSD within the previous 12 months (Kessler 2005). As the only anxiety disorder which can be defined with reference to an initiating event, much interest has been expressed in interventions to prevent the development of this debilitating disorder within both group and individual settings (Friedman 2002; Boris 2005).
The difficulty of distinguishing between adaptive and pathological stress responses in the immediate aftermath of a traumatic event makes the use of medication to prevent PTSD ethically challenging. Reviews of trials attempting, either retrospectively or prospectively, to identify predictive factors which distinguish between people who subsequently develop PTSD and those who do not (Brewin 2000; Ozer 2003) have identified proximal factors, such as social support and trauma intensity, as more strongly implicated in the subsequent development of PTSD than more distal factors (such as history of family psychopathology). The observation within the review by Ozer (2003) that peri‐traumatic dissociation was the strongest predictor of PTSD supports the inclusion of acute stress disorder (ASD) as a distinct diagnostic entity in DSM‐IV that also has prognostic validity for PTSD. Nevertheless, a review of early predictors of PTSD found that more than half of participants (56%) who go on to develop PTSD are not diagnosed with ASD (Bryant 2003).
Description of the intervention
There are a number of reasons to believe that medication could be effective in preventing the development of PTSD. A recently updated systematic review of pharmacotherapy for PTSD (Stein 2006), concluded that medication, and selective serotonin reuptake inhibitors (SSRIs) in particular, are effective in treating PTSD on both a short ( ≤14 weeks) and a long term basis. This is consistent with increasing evidence for specific dysregulations in certain neurotransmitter systems (including the serotonin, noradrenaline, and dopamine systems). In addition, the observation that depression might be a significantly better predictor of PTSD than other psychological factors (Ozer 2003), suggests that medications with antidepressant effects might have particular utility in preventing the development of PTSD.
Psychotherapy has traditionally been the treatment modality of choice in PTSD interventions, and has recently been recommended in one treatment guideline as the first line agent for PTSD (NICE 2005). Evidence for the effectiveness of psychotherapy in preventing PTSD, in the form of open‐label (Foa 1995; Bryant 1999; Bryant 2003) and randomised trials (Bryant 2005), is most convincing for cognitive behavioural therapy (CBT), with other psychological interventions being less well supported. There is little evidence for the efficacy of psychoeducation (Turpin 2005), and Eye Movement Desensitization and Reprocessing (EMDR) therapy (Ruzek 2001), while a review of one of the most common psychotherapeutic interventions, psychological debriefing, found no support for its efficacy in preventing the development of PTSD (Rose 2004). Indeed, a randomised controlled trial found that psychological debriefing resulted in worse outcomes amongst participants with intrusive and avoidance symptoms (Hobbs 1996; Mayou 2000).
How the intervention might work
Proposed mechanisms for the development of PTSD include kindling of limbic nuclei (Berlant 2002), negative cognitive attributions of the traumatic event (Ehlers 2000), atrophy of the hippocampus through exposure to glucocorticoids (Sapolsky 2000), and consolidation of negative memories through excessive noradrenergic activation (Morgan 2003). Neuroendocrine abnormalities, such as dysregulation of the hypothalamus‐pituitary‐adrenal (HPA) axis, and structural and functional neuroanatomical abnormalities of temporo‐limbic structures (Bremner 2004; Canive 1997; Charney 1993; Connor 1998; Hull 2002; Yehuda 1995) have also been implicated as causative factors in PTSD.
The hypothesis that overconsolidation of traumatic memories serves as a major contributory factor in the subsequent development of PTSD has received some support in a controlled pilot study, where administration of the beta‐adrenergic antagonist propranolol reduced psychophysiological reactivity to mental imagery (Pitman 2002). Reduction in PTSD rate and symptom severity was observed in a non‐randomised controlled trial of propranolol in motor vehicle accident or physical assault victims (Vaiva 2003). Nevertheless, questions remain regarding the relevance of the adrenalin consolidation hypothesis for indirect trauma (Ozer 2003), as well as the possible harmful effects of beta‐blockers such as propranolol in reducing the intensity of memory for traumatic events in the reconsolidation of traumatic memories (McCleery 2004).
Other mechanisms have also been suggested. The down‐regulating effects of cortisol on the production of noradrenaline centrally were postulated as the mechanism underpinning the reduced incidence of PTSD in a case control (Schelling 1999) and randomised controlled trial (Schelling 2001) of hydrocortisol for patients suffering from septic shock, as well as in a later RCT of cardiac surgery survivors (Schelling 2004). While benzodiazepines are widely used in acute trauma settings, the rationale for their use in treating trauma has been undermined by the negative findings of a non‐randomised controlled trial of clonazepam or alprazolam (Gelpin 1996). The anteretrograde amnesia induced by benzodiazepines and evidence from animal studies of their possible potentiation of the acquisition of fear responses (Hebert 1996; Lumley 2000) could explain the increased rates of PTSD observed following early use of benzodiazepines in controlled trials (Gelpin 1996, Mellman 2002). The risk of dependency associated with these medications also makes them a less suitable option.
Why it is important to do this review
A systematc review of PTSD medication prophylaxis would help (a) to delineate the evidence‐base that exists for pharmacotherapy as an early trauma intervention and (b) to establish whether pharmacotherapy should be considered an alternative to psychotherapy as a secondary prevention strategy in the treatment of PTSD. In addition, such a review would provide insight into the status of clinical factors, for example, type of trauma, presence of comorbid depression, and prior trauma as predictors of treatment outcome. Other issues which a systematic assessment would help address include the optimum period after the index event for initiation of medication, and the relative efficacy of different medication agents on core PTSD symptom clusters (re‐experiencing/intrusion, avoidance and hyperarousal).
This review aims to systematically evaluate the efficacy and tolerability of medication in preventing the development of post‐traumatic stress disorder.
Objectives
1) To provide an estimate of the efficacy of medication in preventing the development of post‐traumatic stress disorder following exposure to a traumatic event. The efficacy of medication in reducing symptom severity for those individuals who subsequently develop PTSD will also be considered.
2) To determine whether particular classes of medication are more effective and/or acceptable than others in the prevention of PTSD.
3) To assess whether depression is a predictor of treatment response in the prevention of PTSD.
Methods
Criteria for considering studies for this review
Types of studies
All randomised controlled trials (RCTs) and controlled trials of medication treatment in the prevention of PTSD. Publication is not necessarily related to study quality and indeed publication may imply certain biases (Easterbrook 1991; Dickersin 1992; Scherer 1994), so unpublished abstracts and reports will also be considered. Trial reports in all languages will be included.
Types of participants
Adult participants (18 ‐ 65 years) who have been exposed to traumatic events, but who do not meet diagnostic criteria for post‐traumatic stress disorder. These individuals may or may not have been diagnosed with acute stress disorder, or with comorbid psychopathological disorders.
Types of interventions
RCTs of any medication administered to prevent the onset of post‐traumatic stress disorder. The comparison group may be a placebo or alternative "standard" medication therapy.
Specific medication interventions will be grouped according to medication class. These include the following:
(a) antipsychotics (haloperidol, olanzapine, quetiapine, risperidone)
(b) benzodiazepines (alprazolam, bromazepam, clonazepam)
(c) selective serotonin reuptake inhibitors (SSRIs)(citalopram, escitalopram,
(d) fluoxetine, fluvoxamine, paroxetine, sertraline)
(e) serotonin and norepinephrine reuptake inhibitors (SNRIs)(venlafaxine)
(f) trycyclic antidepressants (TCAs)(amitriptyline, clomipramine, desipramine, imipramine)
(g) mono‐amine oxidase inhibitors (MAOIs)(brofaromine, moclobemide, phenelzine)
Medications which do not fall into these categories will be classified as "Other medications" (buspirone, inositol, lithium, pindolol, prazosin).
Control interventions include:
(i) placebo
(ii) other medication groups
Types of outcome measures
Studies will be included if they provide post‐treatment medication and placebo treatment response on categorical outcome measures, or symptom severity means/standard deviations on continuous outcome measures.
Primary outcomes
Treatment response will be determined from the number of participants who develop PTSD after a minimum period of three months (so as to distinguish between PTSD and acute stress disorder (ASD)) after the traumatic event. Diagnosis will be determined according to the relevant DSM criteria.
Secondary outcomes
1) Treatment response will be determined from the Clinical Global Impressions scale ‐ Improvement item (CGI‐I) (or closely related measure), a widely used global outcome measure (Guy 1976).
PTSD symptom and symptom cluster response will be assessed on the Clinician Administered PTSD Scale (CAPS) (Blake 1995), a symptom severity measure that is increasingly used in RCTs of PTSD.
2)The response of comorbid symptoms will be measured by:
(a) depression scales, such as the Beck Depression Inventory (BDI) (Beck 1961), the Hamilton Depression Scale (HAM‐D) (Hamilton 1959), and the Montgomery‐Asberg Depression Rating Scale (MADRS) (Montgomery 1979)
(b) anxiety scales, such as the Hamilton Anxiety Scale (HAM‐A) (Hamilton 1960).
3) Quality of life measures.
4) Measures of functional disability, such as the Sheehan Disability Scale (SDS), which includes subscales to assess work, social and family related impairment (Sheehan 1996), will also be included when provided.
5) Medication acceptability:The total proportion of participants who withdrew from the RCTs due to treatment emergent adverse events will be included in the analysis as a surrogate measure of medication acceptability, in the absence of other more direct indicators of acceptability.
6) Adverse events: The most common drug‐related adverse events for both the included and excluded studies (defined as those occuring in at least 20% of the participants given medication) , as well as significant differences in the rate of occurence of drug‐related adverse events between medication and control groups will be described as part of the narrative review.
Search methods for identification of studies
Electronic Searches
1) The Cochrane Collaboration Depression, Anxiety and Neurosis Controlled Trials Register (CCDANCTR‐Studies) with be searched.
CCDANCTR‐Studies
Diagnosis = Post‐Traumatic Stress Disorders
and
Notes = Prevent*
CCDANCTR‐References
Keyword = Post‐Traumatic Stress Disorders
and
Free‐text = Prevent*
2) Additional searches will be carried out on Medline (via PubMed) (January 1985 to December 2005) and PsycINFO (1983 to 2005, Part B).
The complete Medline search query, as derived from the search strategy developed by Robinson and Dickersin (2002), is provided below:
(randomized controlled trial [pt] OR controlled clinical trial [pt] OR randomized controlled trials [mh] OR random allocation [mh] OR double‐blind method [mh] OR single‐blind method [mh] OR clinical trial [pt] OR clinical trials [mh] OR ("clinical trial" [tw]) OR ((singl* [tw] OR doubl* [tw] OR trebl* [tw] OR tripl* [tw]) AND (mask* [tw] OR blind* [tw])) OR ("latin square" [tw]) OR placebos [mh] OR placebo* [tw] OR random* [tw] OR research design [mh:noexp] OR comparative study [mh] OR evaluation studies [mh] OR follow‐up studies [mh] OR prospective studies [mh] OR cross‐over studies [mh] OR control* [tw] OR prospectiv* [tw] OR volunteer* [tw]) NOT (animal [mh] NOT human [mh]) AND (Stress Disorders, Traumatic [mh] OR "acute stress disorder" [tw] OR ASD [tw] OR "posttraumatic stress disorder" [tw] OR "post traumatic stress disorder" [tw] OR PTSD [tw]) AND (prevent* [tw] OR prophy* [tw])
The PsycINFO search strategy will include the following search query: ("randomisation" OR "randomization") OR "controlled" AND ("post traumatic stress disorder" OR "PTSD").
3) Ongoing trials will be located using the metaRegister of Controlled Trials database (mRCT) (http://www.controlled‐trials.com), as well as the National Institute of Health's Computer Retrieval of Information on Scientific Projects (CRISP) service (1972‐2005) (http://crisp.cit.nih.gov/).The search terms '"posttraumatic stress disorder" OR "post traumatic stress disorder" OR "PTSD" will be entered into the search interface for these databases.
Reference Lists
The bibliographies of all identified trials will be scanned for additional studies.
Personal Communication
(1) Published and unpublished trials will also be obtained from key researchers, as identified by the frequency with which they are cited in the bibliographies of RCTs and open‐label studies.
(2) Pharmaceutical companies will also be contacted. They will be identified through the source of funding cited in published RCTs, as well as the companies with which the authors are affiliated.
Data collection and analysis
Selection of studies
RCTs identified from the search will be independently assessed for inclusion by two raters, based on information included in the abstract and/or method section of the trial report. The raters will also independently collate the data listed under "Data extraction and management" from RCTs which they both regard as satisfying the inclusion criteria specified in the "criteria for considering studies" section. Studies for which additional information is required in order to determine their suitability for inclusion in the review will be listed in the "studies awaiting assessment" table in the Review Manager (RevMan) software, pending the availability of this information. Any disagreements in the independent trial assessment and data collation procedures will be resolved by discussion with a third reviewer (DS).
Data extraction and management
Spreadsheet forms will be designed for the purpose of recording descriptive information, summary statistics of the outcome measures, the quality scale ratings, and associated commentary. Once this data has been entered, it will be exported to the Review Manager (RevMan) software, which will be used to conduct the meta‐analysis. Where information is missing, the reviewers will contact investigators by email in an attempt to obtain this information.
The following information will be collated from each trial:
(a) Description of the trials, including the primary researcher, the year of publication, and the source of funding.
(b) Characteristics of the interventions, including the dose of medication, the period over which it was administered and the name of the particular medication tested.
(c) Characteristics of trial methodology, including the diagnostic (e.g. DSM‐IV (APA 1994)) and exclusionary criteria employed, the screening instrument used (e.g. the Structured Clinical Interview for DSM‐IV (SCID) (Spitzer 1996)) for both the primary and comorbid diagnoses, the presence of comorbid major depressive disorder (MDD), the use of a placebo run‐in, whether a minimal severity criterion was employed, the number of centres involved, and the trial's total score on the CCDAN quality rating scale.
(d) Characteristics of participants, including the number of participants randomised to the treatment and control groups, their age and gender distributions, whether they have been treated with the medication in the past (treatment naivety), whether they have a history of trauma, the number of participants in the sample with MDD, the type of trauma to which they were exposed, and the average time between trauma and treatment.
(e) Outcome measures employed (primary and secondary), and summary continuous (means and standard deviations) and dichotomous (number of responders) data. Additional information will be included, such as the number of total drop‐outs per group as well as the number that dropped out due to adverse effects. Records will be kept of whether the data reflected the intent‐to‐treat (ITT) with last observation carried forward (LOCF) or completer/observed cases (OC) sample, and the minimal period required for inclusion of participants in the LOCF analyses. Other methods of estimating the outcome for participants who dropped out of the study, such as the mixed effects (ME) model, will also be recorded.
(f) Quality assessment, including the number of randomised participants who were not included in the analysis (lost to follow‐up (LTF)), whether blinding occurred for the assessor/s, participants, or those who administered medication, as well as whether the allocation of medication was randomised and the allocation sequence was concealed (the methods used in implementing these respective bias reduction measures will also be documented).
Assessment of methodological quality of included studies
The quality of the trials will be assessed by one of the reviewers using the CCDAN Quality Rating Scale (CCDAN‐QRS) (Moncrieff 2001) (http://www.iop.kcl.ac.uk/IoP/ccdan/qrs.htm). This 23 item scale assesses a range of features such as sample size, the duration of the intervention, inclusion and exclusion criteria, and whether or not the power of the trial to detect a treatment effect was calculated. In addition, data for other trial characteristics which have been recognised as potential sources of bias, such as the method used in generating the allocation sequence, the concealment of allocation, whether outcome assessment was blinded, and the number of participants lost to follow up, will be independently collated by two reviewers as part of the general data collection process (see Data extraction and management section). This is regarded as necessary given doubts concerning the usefulness of an overall quality score from a scale composed of multiple items (Alderson 2003).
Measures of treatment effect
Categorical data
Relative risk of response to treatment and number needed to treat (NNT) will be calculated for the dichotomous outcomes of interest. Relative risk will be used instead of odds ratios, as odd ratios are less easily interpreted. Odds ratios also tend to overestimate the size of the treatment effect when confused with relative risks. This is especially the case when the occurrence of the outcome of interest is common (as anticipated in this review, with an expected response greater than 20%) (Deeks 2003). NNT is defined as the inverse of the absolute risk difference due to the medication intervention. In this review it will be used to indicate the number of people who require treatment with medication, relative to a control, before a single additional person in the medication group responds to treatment.
Continuous data
Weighted mean differences (WMD) will be calculated for continuous summary data derived from the same scale, such as the Clinician Administered PTSD Scale (CAPS) for symptom severity. In cases in which a range of scales are employed for each outcome, such as in the assessment of comorbid depression on the MADRS and HAM‐D, the standardised mean difference (SMD) will be determined. This method of analysis standardises the differences between the means of the treatment and control groups in terms of the variability observed in the trial.
Studies with multiple treatment groups
In placebo‐controlled trials comparing the efficacy of multiple medications in preventing PTSD, placebo‐medication outcome comparisons will be restricted to one of the agents. Data from only one medication group will be used so as to avoid possible bias through multiple comparisons with the same placebo group. Separate head‐to‐head primary outcome comparisons of the respective agents will be conducted for trials comparing multiple medications.
In the case of data from trials employing multiple fixed doses of medication, the bias introduced through comparing the summary statistics for multiple groups against the same placebo control will be avoided by pooling the means and standard deviations across all of the treatment arms as a function of the number of participants in each arm.
Dealing with missing data
All analyses of dichotomous data will be intention‐to‐treat (ITT). The total number of participants randomised to the different comparison groups will be used as the denominator in comparisons of treatment response. Only data from trials which provide information on the original group size (prior to drop‐outs) will be included in the analyses of treatment response. Preference will be given to the inclusion of summary statistics for continuous outcome measures derived from mixed effects models, followed by last observation carried forward (LOCF) and observed cases (OC) summary statistics (in that order). This is in line with evidence that ME methods are more robust to bias than LOCF analyses (Verbeke 2000).
Assessment of heterogeneity
Heterogeneity of treatment response and symptom severity will be assessed visually from the forest plot of relative risk. This will help determine whether the differences between the results of trials were greater than would be expected by chance alone. Heterogeneity will also be assessed by means of the chi‐square test of heterogeneity. If the chi‐square test has a p‐value of less than 0.10, this will be interpreted as evidence of heterogeneity, given the low power of the chi‐square statistic when the number of trials is small (Deeks 2003).
In addition, the I‐square heterogeneity statistic reported by RevMan will be used to quantify the inconsistency of the trial results within each subgroup analysis (Higgins 2003). Differences on continuous measures in medication efficacy between these subgroups will be assessed by means of Deeks' stratified test of heterogeneity (Deeks 2001). This method subtracts the sum of the chi‐square statistics available for each of the subgroups in the study from the chi‐statistic available for all the trials, to provide a measure (Qb) of heterogeneity between groups. Differences in treatment response on the CGI‐I will be determined by whether the confidence intervals for the effect sizes of the subgroups overlap. This method was chosen in preference to the stratified test, due to inaccuracies in the calculation in RevMan of the chi‐square statistic for dichotomous measures (Deeks 2003).
Assessment of reporting bias
Publication is not necessarily related to study quality and indeed publication may imply certain biases (Easterbrook 1991; Dickersin 1992; Scherer 1994). Publication bias will be determined by visual inspection of a funnel plot of treatment response. A more objective measure of bias for treatment response and reduction of symptom severity will be obtained by regressing the standardised treatment effects for the RCTs on the inverse of the standard error of their treatment estimate (Egger 1997). This procedure will be performed using the meta package of the R statistical language (R 2005).
Data synthesis
Categorical and continuous treatment effects will be obtained from a random effects model (the random effects model includes both within‐study sampling error and between‐studies variation in determining the precision of the confidence interval around the overall effect size, whereas the fixed effects model takes only within‐study variation into account). The outcomes will be expressed in terms of an average effect size for each subgroup, as well as by means of 95% confidence intervals.
Subgroup analysis and investigation of heterogeneity
Subgroup analyses (Thompson 1994) will be undertaken in order to assess the degree to which methodological differences between trials might have systematically influenced differences observed in the primary treatment outcomes.
The trials are to be grouped according to the following methodological sources of heterogeneity (number of trials permitting):
(a) The involvement of participants from a single centre or multiple centres. Single centre trials are more likely to be associated with lower sample size but less variability in clinician ratings.
(b) Whether or not trials were industry funded. In general, published trials which are sponsored by pharmaceutical companies appear more likely to report positive findings than trials which are not supported by for‐profit companies (Als‐Nielsen 2003; Baker 2003).
(c) Whether a placebo or alternative medication was used as a control group.
In addition, the following criteria will be used to assess the extent of clinical sources of heterogeneity:
(a) Whether or not the sample included individuals diagnosed with major depression. Such an analysis might assist in determining the extent to which the efficacy of a medication agent in preventing PTSD is independent of its ability to reduce symptoms of depression, an important consideration given the classification of many of these medications as antidepressants.
Sensitivity analysis
Sensitivity analyses determine the robustness of the review author's conclusion to methodological assumptions made in conducting the meta‐analysis. A sensitivity analyses will be conducted to determine whether treatment response varies as a function of the use of treatment response versus non‐response as an outcome statistic. This comparison may be necessary in the light of evidence that treatment response may result in less consistent outcome statistics than non‐response (Deeks 2002) when the control group event rate is higher than 50%. This sensitivity analysis will accordingly only be performed if the majority of trials report a control group event rate higher than 50%.
