Deployment of personnel to military operations: impact on mental health and social functioning

The landscape of military deployment has changed dramatically since 1989. While military deployment by its very nature carries substantial risk of exposure to events and experiences that may physically and mentally impair those directly engaged in combat and those engaged in support functions, there are a number of reasons why the extent of this issue is arguably of even greater importance now.

First, the types of security threats and military operations have changed substantially since 1989. The fall of the Iron Curtain released the tight grip of the former USSR on the Eastern Bloc, and in many developing nations across the globe where the Cold War had been fought by proxy. As a consequence, a dramatic increase in peacekeeping and peace‐enforcing operations ensued, many under the auspices of the United Nations. In the period from 1989 to 1994, the UN Security Council authorized a total of 20 new operations, raising the number of peacekeepers from 11,000 to 75,000 (United Nations [UN], 2014a). In addition, the post‐Cold War period is characterised by a shift away from more conventional conflicts between nations towards, for example, the War on Terror, support for insurgencies or counterinsurgencies, and operations to protect civilians in countries under threat of civil war. During this time ad hoc international military coalitions have been formed, including during the Gulf War (1990‐91) and in the recent operations in Iraq and Afghanistan.

Second, nations such as the US and UK have gone from having a large proportion of their military personnel in the Active Component, towards a strategy with increased reliance on the Reserve Component to meet operational needs (Department of Defense, 2008). In the US, reserves were deployed in large numbers during the Gulf War for the first time since the Korean War. This marked a shift in military personnel strategy where the reserve component was previously seen as a strategic reserve that could be activated in case of large scale war, and towards a conception of the reserves as an integral part of military operations (Klerman, 2008). Since the end of the Cold War the US Army consists of around 50% reserves (Feickert, & Kapp, 2014). In the UK a similar trend can be observed. While the total number of personnel in the UK Forces is shrinking, the volunteer reserve is on the increase, in line with the Future Reserves 2020 programme which aims to increase the size of the Reserve Force in the UK (Ministry of Defence, 2015). The shift in strategy towards viewing the reserve component as an operational force has affected the types of people who are deployed; reservists differ from personnel in the Active Component in terms of training received, physical and mental screening, frequency of civil careers, and potentiallyin unobserved ways as well. For example, as a consequence of the large scale commitment of the US, and in turn that of its allies, to military operations in Afghanistan and Iraq, an increasing share of those deployed consists of reservists and national guards. In January 2014, the UN had 15 peacekeeping missions worldwide2 and a special political mission in Afghanistan3 (UN, 2014b), and NATO hadfive operations internationally with multilateral participation4 (NATO, 2014). Furthermore, there are international coalitions with active military operations in other countries, for example Iraq.5 In the period 2001 to 2008, approximately 1.64 million US troops were deployed to Afghanistan or Iraq (Tanielian & Jaycox, 2008). As recently as 2011, Canada had over 3,500 military personnel deployed overseas (National Defence and Canadian Forces, 2011), Australia had approximately 2,900 soldiers deployed to international missions (Australian Department of Defence, 2011), and Denmark had approximately 1,500 military personnel deployed to international missions and has had approximately 50,000 military personnel deployed to international military missions since 1992 (Danish Armed Forces, 2011). As a consequence of the growing demand for international security, larger proportions of military personnel are being deployed, multiple deployments are becoming more frequent, and breaks between deployments are being shortened in order to meet demand (Hosek, Kavanagh, & Miller, 2006).

Third, technological advancements in body armour and other military technology, medical technologies, and military tactics, have increased chances of survival among those who face military deployment (Regan, 2004; Warden, 2006).

The nature of the issue makes it difficult to establish a causal link between deployment and mental health outcomes. For example randomised controlled trials where military personnel are explicitly randomly assigned to either face deployment to a combat zone or to not be deployed are not available. Instead we have found a large base of observational studies. Within the broad class of observational studies, a distinction can be drawn between (a) correlational studies which simply seek to measure incidence in the military population regarding the outcomes of interest (for example, PTSD), and its correlates ("risk" and "resilience" factors), and (b) studies that attempt to create a credible comparison group to the sample of deployed.

In the latter case, and provided that the comparison group is credible, we are likely to have the best available evidence, to shed light on the impact of deployment on the mental health and social functioning of deployed service members. A credible comparison group might consist of a sample from the military population that did not deploy at the time. If this group is balanced on important confounders, it may be credible to interpret the difference in outcomes between those deployed and those not deployed as the impact of deployment. In situations where military personnel face the possibility of deployment to several different operations, and where this assignment is conditionally independent, it may be reasonable to argue that combat exposure, and hence the risk of trauma, is conditionally independent. In this case a credible measure of the relative impact of deployment can be estimated. Even so, conclusions about causal effects must be very tentative.

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 counterinsurgenciescombating terrorismpeacekeeping operationspeacetime contingency operations

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, for example, US military bases in Europe. This type of deployment is outside the scope of the review.

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 service members, regardless of the deploying nation, are included in the review.

Deployed personnel may derive from different military population pools including personnel from Active and Reserve Components, 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 members of the Active Component 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.

All branches of deployed military personnel are relevant for this review. That is to say, personnel from army, navy, coast guard, Marine Corps, air force, Special Forcesare 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.). 2014001033

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.

The effects of deployment on mental health has 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 depressive disorder (MDD). MDD is a mood disorder that affects the everyday functioning of an individual. Amongst the common symptoms is 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 (Cherry et al. 2001; 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, for example, 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. While stationed in Yugoslavia, 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 networks. Relations with friends and family during, and particularly after deployment, appear to be correlated with psychological stress reactions and affect 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 pre‐existing psychological 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 being equal, longer individual deployments can result in a 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., 2011). 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 operations affect the length of deployment. Generally, however, deployment length varies between six and 12 months. Street et al. (2009) argue that mental "resilience" may decrease over time, therefore the period of time between multiple deployments and the 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 or dependence, which is considered a mental disorder (American Psychiatric Association, 1994)8. 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 the 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.

For completeness, we note that the experience of trauma can also lead to post‐traumatic growth, understood as an individual sense of strength upon having successfully coped with trauma (Ramos & Leal, 2013). 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 the context of military deployment, personnel have reported positive post‐deployment outcomes such as increased self‐esteem, personal development, and strong peer bonding (Danish Ministry of Defense, 2010; Rona et al., 2005; Thoresen, 2006). This review does not consider consequences of deployment for post‐traumatic growth.

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 affected indirectly by psychological trauma experienced during deployment. 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, and so on. Such factors may affect the chance of, for example, gaining employment upon returning from military service abroad, maintaining marital bonds and friendships. 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 narrow subset of objective indicators of social functioning namely: employment and homelessness. It is unclear whether these indicators of reintegration into civilian life 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. Employment status of veterans has been linked to their mental health. 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). Homelessness is more prevalent in post‐deployed military personnel compared to the general population (Perl, 2007; Perl, 2015).Tsai and Rosenheck (2015) review three decades of research on the risk factors for homelessness among US veterans. They identify substance use disorders and mental illness as the strongest factors associated with homelessness. These are also strong risk factors for the general population. Tsai and Rosenheck (2015) find that PTSD is not a particularly important risk factor for homelessness relative to other mental illnesses, in spite of the large prevalence in veteran populations. This could be explained by institutional arrangements whereby veterans with PTSD are more likely to be in contact with VA or DoD services that protect against homelessness. In as far as military deployment entails an increased risk of substance use and mental illness for example as a result of trauma caused by combat exposure, there is an indirect association between deployment and homelessness.

We expected the majority of studies to be based on observational study designs; 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 for example the US Vietnam Draft Lottery), assignment to the deployment condition is unlikely to berandom. 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 was more likely that there were 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, eligibility for individual deployment may be contingent on reaching a particular fitness score.9 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 labour force participation in the 1990s. Each such study was judged on how well it addressed the identification problem based on the risk of bias model outlined below in Section 3.3.3.

The study designs that were eligible for this review included: 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). Non‐randomised studies: the decision to deploy or not deploy individuals is not under the control of the researcher. The study must use a credible comparison group to be eligible.

Studies that contained only deployed personnel and compared outcomes in this group before and after deployment (pre‐post design) were not eligible.

The populations that were eligible for this review were military personnel, from any nation, who had faced deployment to international military operations since 1989. As detailed inthere are several reasons for why we limited the time period to after 1989. 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 workforce demands. Because members of the Active and Reservist Component tend to be different in observable (and potentially 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 survive military confrontations, which in earlier conflicts would have resulted in death. As a result, the composition of physical and psychological trauma in military populations has changed since the end of the Cold War. section 1.1

Studies of deployment to military bases (abroad) not involved in active military operations were excluded. Likewise studies that focused on the deployment of civilian personnel to peace‐keeping or war zone operations were also excluded.

All types of service members were eligible. Specifically, members of the Active and Reserve Components, and national guards were eligible.

All types of military personnel were eligible. Specifically, personnel from army, air force, navy, Marine Corps, coast guard, special forces, were all eligible for inclusion in this review.

Military personnel regardless of age, gender, ethnic background, marital status, education, military rank, and country were eligible.

The "intervention" was deployment of soldiers to an international military operation. Any type of deployment of military personnel to a military operation, both combat and non‐combat operations were eligible for inclusion. For example deployment to peacekeeping operations (such as UN peacekeeping missions in the former Yugoslavia) and deployment to theatres of war (such as deployment to the First Gulf War, Operation Iraqi Freedom, and Operation Enduring Freedom in Afghanistan) were eligible deployments.

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. 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 (Haley, 1998). Individuals who are unable to cope with the stress of military training separate from the military or are discharged and return to civilian life. In addition, deployed military personnel undergo 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, for example, Li & Sung, 1999). We return to this point in Section 3.3.

To address the issues raised above only studies that used a well‐defined comparison group were eligible for inclusion. Such studies, for example: compared deployed military personnel to non‐deployed military personnel serving the same nation in the same era; compared military personnel deployed to high combat intensity missions with military personnel deployed to low combat intensity or non‐combat deployments serving the same nation; compared deployed personnel to non‐deployed personnel; or compared two groups of deployed personnel deployed who experienced different levels of combat exposure in the course of their deployment.

While we can expect that military decision makers select whom to deploy and whom not to deploy, there is evidence that the deployment of individual service members to either combat versus non‐combat is unrelated to individual characteristics (for example, 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 was 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 service members 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 group must be balanced on important confounders viz‐a‐viz the deployed group, 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 include: gender, age, rank, type of service, health. We elaborate on the set of confounders in. Section 3.3.3

An example of an eligible primary study is the study by Unwin et al. (1999). They assess mental health outcomes of UK service members who deployed to the Gulf War using a postal survey. As a comparison group, they survey UK service members who were serving during the Gulf War but did not deploy there. Another eligible study 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 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, service members 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 another deployment. If the deployed group and the comparison group 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 eligible study compares two (or more) deployed groups that have (on average) been exposed to different intensities 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 being equal. In other words, it may be reasonable to argue that the two groups have received different dosages of deployment. At this point 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 by researchers.

In summary, this review considered two types of comparisons: (1) absolute comparisons, and (2) relative comparisons. Studies that reported an absolute comparison compared a group of military personnel that were deployed to a military operation to a group of non‐deployed military personnel. Studies that reported a relative comparison compared either a) a group of military personnel deployed to combat operations to a group of personnel deployed to non‐combat operations, or b) compared a group of deployed military personnel with within group stratification in combat exposure, for example high and low combat exposure.

The review included studies that reported outcomes for individuals who had been deployed. Studies that reported only on the consequences, for example spouse and/or children, were not included. Studies that did not measure at least one outcome among the primary or secondary outcomes listed below were not included. We took a broad scope with respect to the types of participants and military operations under consideration. In order to ensure some degree of comparability between what studies are measuring, we narrowed the set of eligible outcomes in this manner.

Another important factor is the temporal aspect of particularly the measurement of mental health outcomes. The time at which surveys were administered may be important; some mental conditions develop over time, while other conditions may have already been treated if surveys are administered later (Bliese, Wright, Adler, Thomas, & Hoge, 2007; Castro & Hoge, 2005; Hotopf et al., 2006). Hence, studies may reveal a specific country's battery of treatments and their effectiveness, rather than the incidence of mental affliction. We therefore recorded the time at which outcomes were measured relative to the end of the relevant deployment spell. All relevant measures regardless of the time of measurement were eligible for inclusion in the review. See Section 3.4.3 for the specific categorisation of time since exposure used in the synthesis.

Relevant studies were identified through electronic searches of bibliographic databases, government policy databanks and internet search engines. No language or date restrictions were applied to the searches (although studies focusing on deployments prior to 1989 were not included).

The following international bibliographic databases were searched: Academic Search Elite (EBSCO platform) ‐ Searched until April 2017 Cochrane Library ‐Searched until April 2017 EMBASE (EBSCO platform) ‐ Searched until April 2017 ERIC (EBSCO platform) ‐ Searched until April 2017 MEDLINE (Ovid platform) ‐ Searched until April 2017 PsycINFO (EBSCO platform) ‐ Searched until April 2017 Science Citation Index ‐ Searched until April 2017 Social Science Citation Index ‐ Searched until April 2017 SocINDEX (EBSCO platform) ‐ Searched until April 2017

The following Nordic bibliographic databases were searched: Bibliotek.dk ‐ The Danish National Library ‐ Searched until April 2017 BIBSYS – The Norwegian National Library ‐ Searched until April 2017 LIBRIS ‐ The Swedish National Library‐ Searched until April 2017

We report exact search strings and results for all electronic databases in Online Supplement 3 (see Chapter 11).

The review authors checked reference lists in relevant reviews and included primary studies for additional references.

OpenGrey was used to search for European grey literature (http://opengrey.eu/↗). Australian Centre for Posttraumatic Mental Health was used to search for Australian grey literature (www.acpmh.unimelb.edu.au/↗). Likewise we used 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/↗) was searched as well. Copies of relevant documents have been made recording the exact URL and date of access.

Under the supervision of review authors, two members of the review team independently screened titles and abstracts and excluded studies that were clearly irrelevant. Studies considered relevant by at least one of the screeners was retrieved in full text. Review team members were not blind to the authors, institutions, or journals.

Full texts were appraised by two members of the review team, and each team member independently judged whether the study met the inclusion criteria for the review. All studies that were deemed relevant by both screeners were forwarded to the review authors for a final decision regarding eligibility for the review. In the case of any disagreement between screeners the study was also forwarded to review authors.

The final inclusion decision was made by one of the review authors. However, since both numerical coding and risk of bias assessment was conducted by two review authors working separately, effectively the final inclusion decision was made by two review authors. In all instances a consensus between the two review authors could be reached, and accordingly there was no need to consult with a third review author regarding eligibility.

Reason for exclusion of studies that were assessed by review authors against inclusion criteria is documented in the reference section of the review (Section 7.2). The overall search and screening process is illustrated in a flow‐diagram presented in Section 10.3.

The information we extracted from reports were managed in a series of Microsoft Excel sheets. Separate sheets were developed for descriptive, numerical, risk of bias, effect size extraction coding. The internal reference ID's of study reports were used to link the information in each sheet to the relevant study.

We assessed 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.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. 2014001033

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 & Green, 2008). The extension to the model is explained in the three following points: 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 review protocol. 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 Section 9.1). This assessment informed the final risk of bias score for confounding. Another feature of non‐randomised studies that make them at high risk of bias is that they need not have a protocol in advance of starting the recruitment process. The item concerning selective reporting therefore also requires assessment of the extent to which analyses (and potentially, other choices) could have been manipulated to bias the findings reported, for example, choice of method of model fitting, potential confounders considered/included. In addition, the model includes two separate yes/no items asking reviewers whether they think the researchers had a pre‐specified protocol and analysis plan. Finally, the risk of bias assessment is refined, making it possible to discriminate between studies with varying degrees of risk. This refinement is achieved with the addition of a 5‐point scale for certain items (see the following section, risk of bias judgment items for details).

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.

Effect sizes were extracted from included studies by the methods described below. Included study reports provided measurements of treatment effects on both continuous scales (typically adjusted mean differences) and as dichotomous outcome data (typically odds ratios). The direction of all effect sizes was adjusted such that a larger effect size indicated worse mental health, or poorer social functioning.

Because a large majority of studies reported measurements of deployment effects in odds ratios we converted otherwise comparable continuous effect sizes, standardised mean differences, to log odds ratios using the procedures reported by Sánchez‐Meca, Marín‐Martínez, & Chacón‐Moscoso (2003). Details are provided in Section 3.4.2.3.

We recorded attrition data and response rates for all studies, and this information was used in our risk of bias assessment. We did not impute missing data when we performed moderator analysis..

Heterogeneity among primary outcome studies was assessed with χ² (Q‐statistic), and the I², and τ² statistics (Higgins, Thompson, Deeks, & Altman, 2003). The Q‐statistic was used to represent the degree of variability in the treatment effect estimates due to heterogeneity: I2=(Q−df)/Q x 100% where Q is the χ² test‐statistic and df is its degrees of freedom (Higgins & Green, 2008). The value of I² lies between 0% and 100%, with a value of 0% indicating no observed heterogeneity and larger values show increasing heterogeneity (Higgins et al., 2003). In addition we reported the between‐studies variance component (τ²)

We used funnel plots for information about possible publication bias (Higgins & Green, 2008). Publication bias is difficult to assess because asymmetric funnel plots are not necessarily caused by publication bias (and publication bias does not necessarily cause asymmetry in a funnel plot).

We restricted synthesis to those studies that did not receive a score of five on any item in the risk of bias assessment, as stated in the protocol for the review. Studies that were scored with a five on some risk of bias item were included in a sensitivity analysis, see Section 3.4.7.2.

We conducted separate meta‐analyses by types of outcomes (PTSD, Depression, Substance use, and CMD), types of comparison ("absolute", "relative"), and time since exposure ("short", "medium", "long", and "other"). For each analysis effect sizes were averaged as appropriate.

We carried out our meta‐analysis using odds ratios. Odds ratios were log transformed before being analysed. This was because ratio summary statistics all have the common feature that the lowest value that they can take is zero, that the value 1 corresponds to no intervention effect, and that the highest value an odds ratio can ever take is infinity. This number scale is not symmetric. The log transformation makes the scale symmetric: the log of zero is minus infinity, the log of 1 is zero, and the log of infinity is infinity.

All analyses were inverse variance weighted using random effects statistical models that incorporate both the sampling variance and between study variance components into the study level weights. Random effects weighted mean effect sizes were calculated using 95% confidence intervals. Measures of heterogeneity were assessed in each analysis.

Analysis was conducted in RevMan5. Graphical displays (forest plots) for meta‐analysis performed on ratio scales sometimes use a log scale, as the confidence intervals then appear symmetric. This is however not the case for the software Revman 5. The graphical displays using odds ratios and the mean effect size were reported as an odds ratio.

We ran the searches four times. July ‐ August 2011, August ‐ September 2013, in January 2015 and in April 2017.

We searched 13 international and Nordic bibliographic databases, searched for grey literature, and snowballed reference lists for further leads (seefor more information). section 3.3

The total number of potential relevant records was 31,049 after excluding duplicates from the database searches (databases: 30,025, grey and snowball: 1,024.)

All 31,049 records were screened based on title and abstract. The review team screened 3,401 in full text. 2206 studies were initially deemed to fit the inclusion criteria for the review. 35 of the studies did not upon closer inspection meet the inclusion criteria. The references to these studies and the justifications for exclusion are listed in section 7.2. In the end 185 study reports met the inclusion criteria and were data‐extracted by the review team.

Meta‐analysis was performed on40 study reports.

Table 1 presents the study characteristics of the 185 studies that met inclusion criteria. The statistics given in the table are at the study level, except where a study contains multiple groups of participants deployed to different operations. All studies use observational data to quantify the effect of deployment.

Averaged across all studies the mean study was published in 2008 with a standard deviation of six years.

94 studies (51%) assessed the effects of deployment to Iraq ("Operation Iraqi Freedom") in the period after 9/11 2001, also known as the Global War on Terror. Operation Iraqi Freedom began on 20 March, 2003, and officially ended 18 December, 2011. The 2003 invasion of Iraq was led by U.S. Army General Tommy Franks, and codenamed "Operation Iraqi Freedom". The UK codename was "Operation Telic", and the Australian codename was "Operation Falconer". 61 studies (33%) assessed the effects of deployment to the Gulf War (combat phase codenamed "Operation Desert Storm"). The combat phase of the Gulf War took place between 17 January 1991 and 28 February 1991. 69 studies (37%) considered military personnel deployed to Afghanistan ("Operation Enduring Freedom"). This US‐led operation began 10 October, 2001 and officially ended 31 December, 2014. 16 studies (9%) considered other deployments, mainly peacekeeping missions, in particular peacekeeping in the former Yugoslavia, under NATO‐command, to implement The General Framework Agreement for Peace in Bosnia and Herzegovina. Eleven studies did not report which operation participants had been deployed to. Table 2 gives a brief overview of the major operations considered in the included studies.

74% of studies considered deployment of US troops, followed by the UK (11%). Other deploying countries in the sample were Australia, Canada, Denmark, Germany, Italy, Kuwait, Netherlands, Norway, Poland, Saudi Arabia and Sri Lanka (total of 28studies). One study did not report which country troops were deployed from.

Most studies (88%) considered deployment to war zones. The remaining studies (9%) considered deployment to civil conflict zones. Twenty studies did not report on the type of deployment.

62% of deployed participants was army personnel. A smaller share of deployed participants was personnel of other military branches: Navy (14%), Air Force (15%), and Marines (9%). 70 studies did not report on the service branch of participants.

At the study level 83% of the participants were males (30studies did not report on gender composition). Participants were 69% white Caucasian at the study level (not reported in 89studies), had an average age of 32 years (not reported in 52studies), and 56% were married (not reported in 72studies).

At the study level 30% of participants had previously been deployed (not reported in 141 studies). 54% of the deployed participants were from the Active Component (regulars). The remaining share of participants consisted either of members from the Reserve Component (reserves) or members of the National Guard (not reported in 67 studies). Finally, 84% of the participants (at the study level) were enlisted personnel (not reported in 77studies).

This section considers comparisons where all participants were deployed. The comparison is relative, because all participants were deployed, but participants differed in their exposure to risk of trauma. Exposure might be self‐reported for example via questionnaires where participants reported combat exposure. Alternatively, relative exposure was a result of studies comparing one group of participants that deployed to a combat‐zone to another group of participants that were deployed to a non‐combat zone for example deployment to a US military base in Germany.

We would expect substantial between study heterogeneity for these different comparisons, because there was substantial variation in how studies measured combat exposure, the time between potential exposure and reporting, and how participants were stratified by combat exposure (for example, low versus high, or low versus medium). Almost all studies assessed combat exposure via survey questions to participants. As such responses are prone to recall bias, and bias is likely to increase with time since exposure. Responses may also interact with the condition. For example part of the diagnosis of PTSD involves reliving traumatic experiences. As a result participants with the condition may be more likely to recall combat exposure compared to participants that had the same exposure, but no adverse reaction to it.

The included studies differed in terms of their sample characteristics, comparison conditions, and methodology. With between two and nine studies in a single meta‐analysis, the statistical power to detect heterogeneity of effects was quite low; nevertheless, evidence of statistical heterogeneity was found; in some analyses it was substantial.

With the aim of explaining observed heterogeneity, we investigated the following factors: Study‐level summaries of participant characteristics: mental health history, gender, age, ethnicity, military rank, branch of service, and duty/enlistment status.

Among the studies used in the data synthesis, only three studies reported mental health history. Only one study reported results separated by gender, two studies analysed females only and the majority of participants in the remaining studies were male; there was very little variation in this covariate. Ethnicity and age were not reported in many studies (16 and 18 studies respectively) and there was almost no variation in these covariates among the studies reporting them. Military rank was reported in all but ten studies but there was very little variation in this covariate among studies reporting it. Branch of service was reported in all but nine studies. Eleven studies used an Army only sample and in addition two studies reported separate estimates on branch of service. Duty/enlistment status was reported in all but nine studies. Nine studies used samples of Reserves/Guards only, six studies used samples of Regulars only; the remaining studies (reporting this covariate) used samples with on average 69% Regulars and in addition three studies reported separate estimates for Reserves/Guards and Regulars.

Where possible, subgroup analyses were performed using effect estimates separated by Army versus other branches of service and Reserves/Guards versus not Reserves/Guards. We only performed subgroup analysis if there were at least two studies in each subgroup.

Most of the results rely strictly on variation between studies, not within. 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 within study differences (Oxman & Guyatt, 1992). One should therefore be careful when interpreting estimates that rely on variation between studies.

We have drawn no overall conclusion because the analysis is based on a subset of the meta‐analyses. The assessment of any difference between the subgroups is based on 95% confidence intervals and interpretation of relationships is cautious.

Sensitivity analyses were planned to evaluate whether the pooled effect sizes were robust across study design and components of methodological quality. Due to the fact that we found no randomised controlled trials, we could not evaluate the impact of study design. For methodological quality, we carried out sensitivity analyses for the confounding, incomplete data, and other risk of bias components of the risk of bias checklists, respectively. Two sets of sensitivity analyses were performed. First, we examined the robustness of conclusions when we included studies that were excluded due to a score of 5 (too high risk) on the confounding item. Ninety five studies were excluded from synthesis following risk of bias assessment. All of these studies were excluded due to a score of 5 (too high risk) on the confounding item for non‐randomised studies. We were able to extract effect sizes without participant overlap from 26 of the 95 studies. In the sensitivity analysis we pooled these studies with the studies from the synthesis sample. The analyses are performed separately by comparison, outcome, and time since exposure, essentially replicating the meta‐analyses conducted in 4.3.1 and 4.3.2.

Secondly, we examined the robustness of our conclusions when we excluded studies with risk of bias scores of 4 on confounding, incomplete data, or other risk of bias.

We assessed the possibility of publication bias visually by examining funnel plots. Only analyses with at least five studies included were examined. The six funnel plots are displayed in Section 10.2. There are too few studies and insufficient variation in the standard errors to assess whether the funnel plots are symmetric. However, there is no striking asymmetry visible in any of the funnel plots.

Selection bias is understood as systematic baseline differences between groups and can therefore compromise comparability between groups. Baseline differences can be observable (e.g. age and gender) and unobservable (to the researcher; e.g. motivation and 'ability'). There is no single non‐randomised study design that always solves the selection problem. Different designs solve the selection problem under different assumptions and require different types of data. Especially how different designs deal with selection on unobservables varies. The "right" method depends on the model generating participation, i.e. assumptions about the nature of the process by which participants are selected into a programme.

As there is no universal correct way to construct counterfactuals we will assess the extent to which the identifying assumptions (the assumption that makes it possible to identify the counterfactual) are explained and discussed (preferably the authors should make an effort to justify their choice of method). We will look for evidence that authors using e.g. (this is NOT a complete list):

Natural experiments:

Discuss whether they face a truly random allocation of participants and that there is no change of behavior in anticipation of e.g. policy rules.

Instrument variable (IV):

Explain and discuss the assumption that the instrument variable does not affect outcomes other than through their effect on participation.

Matching (including propensity scores):

Explain and discuss the assumption that there is no selection on unobservables, only selection on observables.

(Multivariate) Regression:

Explain and discuss the assumption that there is no selection on unobservables, only selection on observables. Further discuss the extent to which they compare comparable people.

Regression Discontinuity (RD):

Explain and discuss the assumption that there is a (strict!) RD treatment rule. It must not be changeable by the agent in an effort to obtain or avoid treatment. Continuity in the expected impact at the discontinuity is required.

Difference‐in‐difference (Treatment‐control‐before‐after):

Explain and discuss the assumption that outcomes of participants and nonparticipants evolve over time in the same way.