PROTOCOL: Deployment of Personnel to Military Operations: Impact on Mental Health and Social Functioning

1.2.1 Type of Mission

International military missions may be peacekeeping or peace-enforcing missions under the UN, NATO, multilateral military coalitions or other international agencies. Such operations may involve the deployment of air, navy and army personnel as well as support staff who are not directly involved in military confrontation.

International military operations as studied in this review fall in the categories of low intensity conflicts (LIC) or conventional warfare. Conventional warfare is defined as warfare, other than guerrilla/counterinsurgent warfare, conducted without the use of nuclear, biological, or chemical weapons (Oxford University Press, 2001). Low intensity conflict is defined by the US department of defense: “Low intensity conflict is a political-military confrontation between contending states or groups below conventional war and above the routine, peaceful competition among states” (Department of Defense, 2011). LIC can be classified in four major operational categories (Department of Defense, 2011; Global Security, 2011):

support for insurgencies and counterinsurgencies

LIC frequently involves protracted struggles between competing principles and ideologies. LIC ranges from subversion to the use of armed force. It is waged by a combination of means, employing political, economic, informational, and military instruments. Low intensity conflicts are often localized, generally in developing countries, but contain regional and global security implications (Global Security, 2011).

Within low intensity conflict and conventional war there can be great variation in levels of combat intensity. Peacekeeping missions may be non-combat or low combat intensity deployments and relatively free from conflict exposure and be relatively stress free. An example of a non-combat mission is the UN peacekeeping mission in Cyprus. At the other end of the range we find high combat intensity missions as seen in missions by NATO and coalition forces deployed to the Middle East. Military operations in Afghanistan and Iraq are examples of deployments that involve high and frequent combat exposure.

Military personnel may also be deployed to areas struck by natural disaster or military bases overseas not included in a military mission or operation, e.g., US military bases in Europe. This type of deployment is outside the scope of the review.

1.2.2 Type of Service

Deployed personnel may come from different military populations, depending on country of origin and scale of operations. Some countries operate volunteer military such as the UK and the US, while other countries rely fully or partially on mandatory conscription to the military. As a consequence, the underlying characteristics of military personnel, including mental health characteristics, are not uniform. All deployed servicemen and women, regardless of deploying nation, are included in the review.

Deployed personnel may derive from different military population pools including personnel on active duty, reserves forces, and national guards. Military reserve forces are members of the armed forces who combine a civil career with a military career. Reserve forces have a signed contract with the military and may be called in for active duty if needed. At any given time the demand for military personnel affects which subpopulation is at risk of deployment. For instance, at times of low demand only active duty members face risk of deployment, whereas under times of high demand, such as for example under Operation Enduring Freedom to Afghanistan, large contingents of military reserve forces and national guards of the US face risk of deployment (Tanielian & Jaycox, 2008). Military personnel, regardless of type of service, are relevant to this review provided they have faced deployment to international military operations.

1.2.3 Type of Branch

All branches of deployed military personnel are relevant for this review. That is to say, personnel from army, navy, Marine Corps, air force, Special Forces, etc. are all relevant. Both combat and non-combat personnel face deployment to international missions and are thus relevant to the review. Deployed non-combat personnel include personnel with transport/logistics functions, health and medical staff, information technology and communication staff, and general technical support personnel. As an example, the NATO mission to Afghanistan included components of deployed personnel overseeing training of local national police and military units (NATO, n.d.).

Deployed personnel regardless of military rank are relevant to the review. Military rank affects the types of operation-specific tasks assigned to deployed personnel, and therefore rank can affect the mix of stress factors to which personnel are exposed. We therefore consider military rank to be an important control.

1.3.1 Impact on Mental Health

The effects of deployment on mental health received relatively little attention prior to World War I (WW1), although attempts at diagnosing war syndromes go at least back as far as the U.S. Civil War (Hyams et al., 1996). During WW1, deployed personnel suffered from what became known as “soldier's heart.” Affected soldiers reported, amongst other symptoms, fatigue, headache, confusion, and lack of concentration. An acute combat stress reaction (CSR) was also diagnosed (“shell shock”). In response, a clinical research program was developed during the war. After the Vietnam War, returning veterans were diagnosed with post-traumatic stress disorder (PTSD), which was subsequently detected among veterans of the Korean Conflict and WW2 (Weisæth, 2002; Jones et al., 2002). Unlike acute combat stress reaction, which is an immediate result of psychological trauma, PTSD refers to the long term consequences of psychological stress (Hyams et al., 1996). PTSD is characterised by a range of symptoms: “[…] distressing thoughts, feelings, and images that recapitulate the traumatic event, avoidance of stimuli associated with the event, emotional numbing of responsiveness, […]” (Fairbank, Ebert, & Cadell, 2001, p. 184). PTSD is diagnosed only after symptoms have persisted for at least 30 days (Tanelian & Jaycox, 2008). Another comorbidity of deployment is major depression disorder (MDD). MDD is a mood disorder that affects the everyday functioning of an individual. Amongst the common symptoms are disinterest in activities, significant weight gain/loss, insomnia/hypersomnia, feelings of worthlessness, thoughts of suicide, and/or suicide plans.

Deployment mainly affects the mental health of those deployed through increased risk of exposure to trauma (Dohrenwendt et al., 2006; Larson et al., 2008). Exposure to trauma, either by participating in armed combat or as a witness to combat or the consequences of combat, e.g., military medical teams and logistic officers, may adversely affect mental health.

Deployed military personnel, particularly combat soldiers, experience risk of fatality, and some will see their peers wounded, maimed or killed.

Specific circumstances may represent specific stress factors. An example is the UN peacekeeping mission in former Yugoslavia. The mission operated under a limited UN mandate, which allowed only neutral surveillance and the prohibition of the use of force. There, deployed soldiers witnessed extremely stressful situations when they observed direct attacks upon the civilian population. Another potentially contributing factor is the fact that deployment by its very nature implies the (temporary) removal of individuals from their everyday environment, including separation from family, friends, colleagues and support network. Relations to friends and family during, and particularly after deployment, appear to be correlated with psychological stress reactions and impact social functioning (Christensen, 2001; King, King, Fairbank, Keane, & Adams, 1998). Similarly, Fontana and Rosenheck (1994) found that the homecoming experience of veterans played in important role in the development of PTSD.

The epidemiological literature on PTSD has revealed a number of risk factors for the development of PTSD following trauma in the general population as well as in military populations. Some of the relevant risk factors for this review are: being female, having a preexisting disorder, having a family history of anxiety and depression, past exposure to trauma, degree and nature of war zone exposure (Fairbank et al., 2001). All else equal, longer individual deployments result in higher risk of occurrence of at least one traumatic incident. Deployment length is therefore an important variable of interest. Deployment length varies by country and by type of service (Buckman et al., 2010). For example the UK Army typically deploys for 6 months, while the US Army typically deploys for a period of between 12 to 15 months. The UK Navy may face deployments of up to 22 months for every 36 month period (unless deployed on land), while the US Navy and Marines deploy for 7 months. The UK Air Force deploys for 9.3 months in every 24-month period, while in the US deployments are of 4 month duration. Within these expected deployment lengths duration may vary considerably from sometimes only a few days to well above a year (US Army, 2011). Both troop demands and the nature of operation affect the length of deployment. Generally, however, deployment lengths vary between 6 and 12 months. Street et al. (2009) argue that mental “resilience” may decrease over time, therefore time between re-deployments and number of deployments may also be important factors for predicting the experience of trauma. This is particularly relevant since, as a result of the large scale troop demands for recent operations in Iraq and Afghanistan, military personnel in general are deployed longer than before and have shorter rest-periods between deployments (Tanielian & Jaycox, 2008).

Deployment may also lead to substance abuse, which can be considered a mental disorder (American Psychiatric Association, 1994). Long term effects of deployment may be increased alcohol intake, especially linked to combat exposure, PTSD, and depression (Jacobson et al., 2008). Deployed military personnel are more likely to experience new onset heavy weekly drinking, binge drinking, and alcohol related problems, compared with non-deployed military personnel (Hoge et al., 2004; Jacobson et al., 2008). This is particularly evident for deployed individuals with combat exposure (Fear et al., 2010; Jacobson et al., 2008). Deployed individuals diagnosed with PTSD and depression have increased odds of new onset and continued alcohol-related problems (Fear et al., 2010; Jacobson et al., 2008). A few studies suggest that drug use is an increasing concern, particularly for individuals deployed to Afghanistan and Iraq, where heroin is readily available (Karney, Ramchand, Osilla, Caldarone, & Burns, 2008; Thomsen et al., 2010).

Traumatic Brain Injury (TBI), more specifically the cognitive consequences of TBI, has received attention following the military operations in Iraq and Afghanistan. In those campaigns, insurgents have increasingly made use of IEDs (Improvised Explosive Devices) in their fight against international coalitional forces. Tanielian and Jaycox (2008) found that 19.5% of a representative sample of the US military population which had served in Iraq or Afghanistan had probable TBI.

The experience of trauma can potentially have positive consequences, termed posttraumatic growth (PTG). Tedeschi and Calhoun (1996, 2004) identify five domains where PTG may occur: “personal strength,” ”new possibilities,” “relating to others,” ”appreciation of life,” and “spiritual change.” In their review of PTG, Ramos and Leal (2013) identify five validated self-report measures to asses PTG.

1.3.2 Impact on Social Functioning

There is little evidence for the direct link between deployment and social functioning. Nevertheless, we are interested in exploring the effects of deployment on social functioning, which may work through multiple channels. For example, social functioning may be affected both directly and indirectly by the traumas of war. Social functioning may be impacted indirectly by psychological trauma experienced during deployment. Such trauma may result in the development of mental afflictions which may, in turn, affect the social functioning of veterans. More direct channels in which deployment affects social functioning recognise that deployment to a combat zone leads to increased risk of loss of limbs, paralysis, TBI, etc. Such factors may affect the chance of gaining employment upon returning from military service abroad, maintaining marital bonds, friendships, etc. Deployment may also entail loss of firm specific human capital leading to adverse effects on salary or employment (Harvey et al., 2011).

We understand social functioning as the ability to undertake tasks and duties in civil society. Social functioning includes the ability to carry out work and home tasks, the degree to which financial concerns are experienced, relationships with family, satisfying sexual relationships, social contacts, and pleasure in spare time activities. Here we specifically focus on a subset of objective indicators of social functioning namely: employment and homelessness.

Employment is linked to deployed military personnel with PTSD and mental health problems, showing increased unemployment in deployed populations with PTSD and depression (Karney et al., 2008; Zatzick et al., 1997). Homelessness is more prevalent in post-deployed military personnel compared to the general population (Perl, 2007). It is, however, unclear whether these indicators of reintegration into civil society are linked directly to deployment (Karney et al., 2008). Absence from the civil labour market during deployment (and military service in general) may affect employment after deployment. Studies indicate that deployed military personnel with PTSD are less likely to be employed than deployed military personnel without PTSD (Karney et al., 2008; Zatzick et al., 1997). There is little data on the rates of homelessness among individuals with PTSD and the link between deployment and homelessness (Karney et al., 2008).

3.1.1 Types of Studies

We expect the majority of studies to be based on observational data; it is difficult to imagine that a military decision-maker would be willing to randomise between deploying and not deploying individual military personnel to an operation. In other words, even though assignment to military service may have derived from a draft lottery (such as e.g. the US Vietnam Draft Lottery), assignment to the deployment condition is likely not random. The decision procedures of military commanders typically involve a trade-off between the benefits of deploying experienced and effective personnel, often based on group cohesion, to the cost of deployment on physical and mental stress (Wessely, 2006). In other words, individual assignment to deployment, even if that individual is eligible as per contract, is not random. Naturally, randomised studies would be eligible for this review should our search strategy uncover any such studies. It is more likely that there are studies where assignment locally produces high quality quasi-experiments. Such studies may be available if the authors of primary studies have direct access to the decision rules of the decision maker responsible for assignment. For example, individual deployment may be contingent on reaching a particular fitness score.⁸ If this is the case, and authors have access to this score, then it is possible to construct a valid comparison group by comparing individuals just above a pre-specified cut-off with those just below the cut-off. In cases where the authors of primary studies do not have access to such information, or procedures do not allow authors to identify the relevant sub-population, identification must rely on other strategies for constructing a credible comparison group. For example, Angrist, Chen, and Frandsen (2010) use the Vietnam Draft Lottery as an instrumental variable to identify the causal effect of exposure to the draft on labor force participation in the 1990s. Each such study will be judged on how well it addresses the identification problem based on the risk of bias model outlined below in Section 3.3.3.

The study designs that are eligible for this review are:

Controlled trials: Randomised controlled trials, quasi-randomised trials (where participants are allocated by non-random means such as alternate allocation, birth date, day of the week, case number or alphabetical order), non-randomised trials (where participants are allocated by other actions controlled by the researcher).

Military populations can be expected to differ from the general population. This is particularly relevant to this review, since it affects what constitutes an appropriate comparison group for deployed military personnel. Military personnel are on average in better mental and physical health than the civilian population. This is due to a selection mechanism: entrance into military service requires passing a medical screening. This screening device sorts out applicants who are not fit to serve in the military for physical or psychological reasons (Haley, 1998). Two factors contribute to this difference. First, individuals who select themselves into a military career are not a random sample of the general population. Second, military training of recruits acts as a selection device that tends to select those who are physically and mentally strong. Individuals who are unable to cope with the stress of military training leave active duty or are discharged and return to civilian life. In addition, deployed military personnel have undergone additional physical and (sometimes) mental screening prior to being selected for deployment (Warner, Appenzeller, Parker, Warner, & Hoge, 2011). As a result, it can be expected that even within the subpopulation of military personnel, deployed and non-deployed will differ in both observed and un-observed characteristics. This effect is well known in occupational health studies, and is known as the “healthy worker effect” (see, e.g., Li & Sung, 1999). We return to this point in Section 3.3.

We will only include studies that use a well-defined comparison group. Such studies, for example, may

compare deployed military personnel with non-deployed military personnel serving the same nation in the same era;

While on the one hand we can expect that military decision makers select whom to deploy and whom not to deploy, there is also evidence to suggest that the deployment of individual servicemen to either combat vs. non-combat is unrelated to individual characteristics (e.g., Cesur, Sabia, & Tekin, 2012). We argue that a distinction must be made between non-randomised studies that simply seek to document correlation between observable characteristics of participants and outcome(s), and non-randomised studies that attempt to mimic an experimental situation by constructing and documenting a plausible comparison group. Only the latter type of study design is eligible for this review. We now elaborate on the characteristics of plausible comparison conditions. As stated earlier, the military population differs in important ways from the civil population, not least because servicemen are frequently screened mentally and physically. Therefore, a credible comparison group to a deployed group must also be sampled from the military population. Even within the military population, selection procedures, including physical and mental screening, determine who does and who does not get deployed. Therefore restricting the comparison group to be sampled from the military population is not sufficient to remove selection bias, but goes some way toward resolving this problem. In addition, a comparison sample must be balanced on important confounders viz-a-viz the deployed sample, such that at least in observable characteristics, the deployed and the comparison group differ only in the assignment to having been deployed and not having been deployed. Some important confounders are: gender, age, rank, type of service, health, etc. We elaborate on the set of confounders in Section 3.3.3. An example of a primary study that is eligible for this review is Unwin et al. (1999). They assess mental health outcomes of UK servicemen who deployed to the Gulf War using postal survey. As a comparison group, they survey UK servicemen who were serving during the Gulf War but did not deploy there. Another study that would be eligible for inclusion is Cesur et al. (2012). They compare personnel that were deployed to combat zones during recent military operations in Afghanistan and Iraq with non-combat deployed personnel. They argue that in their sample the assignment of personnel to either combat zone or non-combat zone is orthogonal to individual characteristics. Their estimates therefore have a (plausible) causal interpretation.

It is also possible that mandated government policies assist researchers in creating a reasonable comparison group. For example, servicemen who would otherwise be eligible for deployment may not have been deployed at the time of the study because they were not yet eligible for re-deployment. If the deployed sample and the comparison sample are balanced with regard to number of previous deployments then this may be a valid comparison group. An example of a study that appears to have this type of information available to the researchers is Hotopf et al. (2006).

Another type of study that would be eligible for inclusion are studies that compare two (or more) different deployed samples that have (on average) been exposed to different degrees of combat exposure. If deployment mainly affects mental health and other outcomes through an increased risk of trauma, then a larger degree of combat exposure increases the likelihood of trauma, all else equal. In other words, it may be reasonable to argue that the two different samples have received different dosages of deployment. Also here caution must be exercised since commanding officers may use selection procedures to assign individuals to more or less severe combat exposures based on characteristics that are unobserved to researchers. Studies that contain only a sample of deployed and compare outcomes before and after deployment are not eligible.

3.1.2 Types of Participants

The populations that are eligible for this review are military personnel, from any nation, who have faced deployment to international military operations since 1989. As detailed in section 1.1 there are several reasons for this choice of period. First, 1989 marks the end of the Cold War period and as a consequence the types of military engagements have changed considerably since then. Second, modern military engagement relies heavily on activating reservist components to fill manpower demands. Because active duty and reservists components tend to be different in observable (and probably unobservable) ways deployment can be expected to have different effects on modern armies. Third, as a consequence of technological developments in body armour more military personnel now potentially become survivors of military confrontations, which would have led to death in earlier conflicts. As a result the composition of physical and psychological trauma in military populations have changed since the end of the Cold War.

Studies of deployment to military bases (abroad) not involved in active military operations will be excluded. Studies that focus on the deployment of civilian personnel to peace-keeping or war zone operations will be excluded.

All types of service members are eligible. Specifically, active duty, reserve, and national guards are eligible.

All types of military personnel are eligible. Specifically, personnel from army, air force, navy, marine corps, special forces, are all eligible for inclusion in this review.

Military personnel regardless of age, gender, ethnic background, marital status, education, military rank, and country will be included.

3.1.3 Types of Interventions

The “intervention” is deployment to an international military operation.

3.1.4 Types of Outcomes

This review will include studies that focus on outcomes for the individual who has been deployed. Studies that solely focus on the consequences for the spouse and/or children will not be included.

3.2.1 Electronic Searches

Relevant studies will be identified through electronic searches of bibliographic databases, government policy databanks and internet search engines. No language or date restrictions will be applied to the searches.

The following bibliographic databases will be searched:

Medline

3.2.2 Search Terms

An example of the search strategy for MEDLINE searched through the Ovid platform is listed below. This strategy will be modified for the different databases. We will report details of the modifications used for other databases in the completed review. 1

Military Personnel/

3.2.3 Searching Other Resources

The review authors will check reference lists in relevant reviews and included primary studies for new leads. We will contact international experts to identify unpublished and ongoing studies, and provide them with the inclusion criteria for the review along with the list of included studies, asking for any other published, unpublished or ongoing studies relevant for the review.

3.2.4 Grey Literature

OpenGrey will also be used to search for European grey literature (http://opengrey.eu/). Australian Centre for Posttraumatic Mental Health will also be used to search for Australian grey literature (www.acpmh.unimelb.edu.au/). Likewise we will use Rand for US grey literature (www.rand.org) and US department of defense (www.dod.gov) and Walter Reed Army Institute of research (http://wrair-www.army.mil/) for relevant US military grey literature. DTIC (http://www.dtic.mil/dtic/) will be searched as well.

Copies of relevant documents will be made recording the exact URL and date of access.

3.3.1 Selection of Studies

Under the supervision of MB, two members of the review team will independently screen titles and abstracts and exclude studies that are clearly irrelevant. Studies considered relevant by at least one of the reviewers will be retrieved in full text. The full texts will then be appraised by two members of the review team. The same persons will decide whether the studies meet the inclusion criteria. Any disagreements about eligibility will be resolved by consulting a third reviewer. Reasons for exclusion will be documented for each study that is retrieved in full text. The study inclusion coding sheet will be piloted and adjusted if required by the review authors (see Appendix 6.1).

The inclusion coding questions for both the title and abstract screening for relevance and the full-text screening for eligibility will be piloted and adjusted if required (see appendix 7.1) and changes will be reported. If necessary, primary investigators will be contacted to clarify study eligibility. In the event of disagreements, a third reviewer and content specialist will be consulted to obtain a consensus. Disagreements resolved by a third reviewer will be reported. Exclusion reasons for studies that otherwise might be expected to be eligible will be documented and presented in an appendix. The overall search and screening process will be illustrated in a flow-diagram. None of the review authors will be blind to the authors, institutions, or the journals responsible for the publication of the articles.

3.3.2 Data Extraction and Management

At least two review authors will independently code and extract data from the included studies. Data and descriptive information will be extracted on: characteristics of participants (gender, age, ethnicity, rank nationality, etc.), intervention characteristics (mission location, type, command, combat exposure, duration, etc.), control conditions (non-deployed, deployed to non-combat or low intensity mission), research design, confounding factors, sample size, risk of bias, outcomes and results. Extracted data will be stored electronically. A data extraction sheet will be piloted on several studies and revised as necessary (see Appendix 6.2). Disagreements will be resolved by consulting a third review author with extensive content and methods expertise. Disagreements resolved by a third reviewer will be reported. Analysis will be conducted in RevMan5, SAS and Stata.

3.3.3 Assessment of Risk of Bias in Included Studies

We will assess the methodological quality of studies using a risk of bias model developed by Prof. Barnaby Reeves in association with the Cochrane Non-Randomised Studies Methods Group.⁹ This model is an extension of the Cochrane Collaboration's risk of bias tool and covers risk of bias in non-randomised studies that have a well-defined control group.

The extended model is organised and follows the same steps as the existing risk of bias model according to the Cochrane Handbook, chapter 8 (Higgins and Green, 2008). The extension to the model is explained in the three following points: 1)

The extended model specifically incorporates a formalised and structured approach for the assessment of selection bias in non-randomised studies by adding an explicit item about confounding. This is based on a list of confounders considered to be important and defined in the protocol for the review. The assessment of confounding is made using a worksheet where, for each confounder, it is marked whether the confounder was considered by the researchers, the precision with which it was measured, the imbalance between groups, and the care with which adjustment was carried out (see appendix 6.3). This assessment will inform the final risk of bias score for confounding.

The refined assessment is pertinent when thinking of data synthesis as it operationalizes the identification of studies (especially in relation to non-randomised studies) with a very high risk of bias. The refinement increases transparency in assessment judgments.

3.3.4 Measures of the Effect of Deployment

Continuous Data

For continuous outcomes, effect sizes with 95 % confidence intervals will be calculated if means and standard deviations are available. If means and standard deviations are not available, the review authors will request this information from principle investigators. If no information is yielded, we will use methods by Lipsey and Wilson (2001) to calculate standardized mean difference effect sizes from, e.g., F-ratios, t-values, chi-squared values and correlation coefficients. Hedges' small sample correction will be employed (i.e., Hedges' g). If there is a mix of studies with some reporting change scores and others reporting final values, we will contact authors and request the final values. If we do not obtain these values, we will analyse change scores and final values separately (Higgins & Green, 2008, section 9.4.5.2). Any scales related to combat social functioning, PTSD, MDD, alcohol and substance abuse, etc. are examples of relevant continuous outcomes in this review.

Discrete Data

For dichotomous outcomes, we will calculate odds ratios with 95% confidence intervals. Employment and marital status are examples of relevant dichotomous outcomes for this review.

There are statistical approaches available to re-express dichotomous and continuous data such that they can be pooled (Sánchez-Meca, Marín-Martínez, & Chacón-Moscoso, 2003). In order to calculate common metrics, odds ratios will be converted to SMD effect sizes using the Cox transformation. We will only transform dichotomous effect sizes to SMD if appropriate, e.g., as may be the case with PTSD which may be measured either as a dichotomous outcome or on a continuous scale. We will only transform the data if a large majority of studies report continuous effect sizes, otherwise we will perform separate analysis for each measure.

When effect sizes cannot be pooled, study-level effects will be reported in as much detail as possible. Software for storing data and statistical analyses will be RevMan 5.0, Excel and Stata 12.

3.3.5 Unit of Analysis Issues

Multiple intervention and control groups

Multiple intervention groups within a study with one control group will be pooled if appropriate (if they include different individuals) and compared to that control group. Multiple controls groups will only be pooled if appropriate (if they include different individuals).

A synthetic (average) effect size will be calculated and used to avoid dependence problems. This method provides an unbiased estimate of the mean effect size parameter but overestimates the standard error. Random effects models applied when synthetic effect sizes are involved actually perform better in terms of standard errors than do fixed effects models (Hedges, 2007). However, tests of heterogeneity when synthetic effect sizes are included are rejected less often than the nominal significance level.

If pooling is not appropriate (e.g., the multiple interventions and/or control groups include the same individuals), only one intervention group will be coded and compared to the control group to avoid overlapping samples. The choice of which estimate to include will be based on our risk of bias assessment and upon theoretical relevance. We will choose the estimate that we judge to have the least risk of bias (primarily, selection bias and in case of equal scoring the incomplete data item will be used) and that is most likely to provide the best information about the outcome being assessed.

Multiple studies using the same sample of data

In some cases, several studies may have used the same sample of data. We will review all such studies, but in the meta-analysis we will only include one estimate of the effect from each sample of data. This will be done to avoid dependencies between the “observations” (i.e. the estimates of the effect) in the meta-analysis. The choice of which estimate to include will be based on our risk of bias assessment of the studies. We will choose the estimate from the study that we judge to have the least risk of bias (primarily selection bias), the number of observations, and precision of estimates.

We consider the risk of bias measure to be an important instrument when selecting among studies using the same primary data. As an example, suppose two different studies, A and B, measure the same outcomes in the same population. Both studies control for confounders but only study A controls for an important confounder, say type of service. We believe that study A should take precedence because that study is much more likely to provide an effect estimate closer to the “truth”. If studies score identically on risk of bias we will also consider number of observations and precision of estimate as important instruments when choosing which study to include.

Multiple time points

If outcomes are measured at multiple time points, each time specific outcome will be analysed first in a separate meta-analysis with other comparable studies taking measures at a reasonably similar time point. Secondly, we will explore the extent to which the multiple outcomes can be included in a meta-analysis using time of measurement as a moderating variable.

We remain flexible as to which classifications to consider. We will record the time of measurement from the end of deployment. As a guideline we will consider: short-term (0- <6 months after deployment), medium term (6- 24 months after deployment) long term (at least 24 months after deployment). We will report any changes to this classification.

3.3.6 Dealing with missing data and incomplete data

Missing data and attrition rates will be assessed in the included studies. Notably due to the nature of the field, studies of deployment typically estimate the effect on data collected from administrative registers and, even more frequently, by questionnaires. Studies using data collected from questionnaires are especially subject to missing data (non-response). For studies using questionnaire data, a sensitivity analysis will be used to assess potential bias, and the extent to which the results might be biased by missing data will be discussed.

The review authors will record attrition/response rates and (if possible) reasons for attrition from included studies.

Another potential source of bias is the procedures under which questionnaire data are collected and by whom. For example, response rates and reporting may be affected by whether questionnaires are anonymous or not. Even if collection is anonymous, but collected by, say, the Department of Defense, personnel may be worried that their responses will be used against them if filing a claim, or will affect opportunities for promotion.

3.3.7 Assessment of heterogeneity

Heterogeneity among primary outcome studies will be assessed with Chi-squared (Q) test, and the I-squared, and τ-squared statistics (Higgins, Thompson, Deeks, & Altman, 2003). Any interpretation of the Chi-squared test will be made cautiously on account of its low statistical power.

3.3.8 Assessment of reporting biases

Reporting bias refers to both publication bias and selective reporting of outcome data and results. Here, we state how we will assess publication bias.

We will use funnel plots for information about possible publication bias if we find sufficient studies (Higgins & Green, 2008). However, asymmetric funnel plots are not necessarily caused by publication bias (and publication bias does not necessarily cause asymmetry in a funnel plot). If asymmetry is present, we will consider possible reasons for this.

3.4.1 Moderator Analysis and Investigation of Heterogeneity

We will investigate the following (subset of) factors with the aim of explaining observed heterogeneity: Study-level summaries of participant characteristics: mental health history, gender, age, ethnicity, military rank, branch of service, and duty/enlistment status. Many of the proposed variables have a strong link to policy. For example, if age turns out to be an important factor for the incidence of PTSD, new rotational procedures can be devised which delay deployment for personnel at certain ages.

In addition, and if available in summary format, the number and duration of previous deployments, and duration of most recent deployment, will be investigated as moderating variables. These are very direct policy instruments, and it is therefore of great interest to explore these relationships, although caution must be exercised in placing a too literal interpretation on the potential moderating effects of deployment length. The longer personnel are deployed, the higher the risk that they will experience at least one trauma, all else being equal, and, as a consequence, may develop adverse mental health responses. Therefore, in a mechanical way, we would expect that longer deployment lengths are associated with higher incidence of mental health problems. It does not follow from this, however, that deployment length is suboptimal. The comparison would be accurate only if we were to compare groups of individuals deployed for the same total length of time but with one group experiencing two shorter deployments and the other experiencing a single longer deployment. If incidence of PTSD in the long deployment group is larger than the effect of total deployment, then we might conclude that deployment length is sub-optimally long. A situation where this might be the case is a situation where mental resilience builds up among the non-deployed (Atkinson et al., 2009). In this case, two shorter deployments may be preferred to one long deployment of equal total length. Similarly, Cesur et al. (2012) show that combat exposure, not deployment length in itself, has a statistically significant impact on developing PTSD.

We will also explore how combat exposure moderates outcomes. It is well known that the degree of combat exposure increases the risk of trauma. The Combat Exposure Scale (CES) is a validated instrument of combat exposure (Keane et al., 1989). The scale includes several items related to specific combat related experiences (Fairbank et al., 2001). As an example Tanielian and Jaycox (2008) used the Combat Trauma Exposure scale (adapted from Hoge et al., 2004).

If the number of included studies is sufficient (at least 10 degrees of freedom) and given there is variation in the covariates, we will perform moderator analyses (multiple meta-regression using the mixed model) to explore how observed variables are related to heterogeneity. We will estimate the (new) residual variance component to be used in a weighted least squares analysis conditional on this variance component estimate. The residual variance component will be estimated using the method-of-moments estimator (Hartung, Knapp, & Sinha, 2008; Konstantopoulos, 2006). We will report the 95% confidence intervals for regression parameters. We will estimate the correlations between the covariates and consider the possibility of confounding. Conclusions from meta-regression analysis will be cautiously drawn and will not be based on significance tests.

Otherwise, single factor subgroup analysis will be performed. The assessment of any difference between subgroups will be based on 95% confidence intervals. No conclusions from subgroup analyses will be drawn and interpretation of relationships will be cautious, as they are based on subdivision of studies and indirect comparisons.

In general, the strength of inference regarding differences in effects among subgroups is controversial. However, making inferences about different effect sizes among subgroups on the basis of between-study differences entails a higher risk compared to inferences made on the basis of with-in study differences (Oxman & Guyatt, 1992). We will therefore use within study differences where possible.

3.4.2 Sensitivity Analysis

Sensitivity analysis will be carried out by restricting the meta-analysis to a subset of the totality of studies included in the original meta-analysis. For example if several studies are excluded due to receiving a 5 on the risk of bias scale, we will present a sensitivity analysis where those studies are included.

Sensitivity analysis will be used to evaluate whether the pooled effect sizes are robust across study design and components of methodological quality. For methodological quality, we will consider sensitivity analysis for each major component of the risk of bias checklists and restrict the analysis to studies with a low risk of bias.

Sensitivity analysis will further be used to examine the rigour of conclusions in relation to the quality of data (whether data is based on questionnaires or administrative registers). For example, if there is significant variation in how primary studies detect (probable) mental disorders, then we will perform sensitivity analysis with respect to each instrument.