Screening women for intimate partner violence in healthcare settings

  • Review
  • Intervention

Authors


Abstract

Background

Intimate partner violence (IPV) damages individuals, their children, communities, and the wider economic and social fabric of society. Some governments and professional organisations recommend screening all women for intimate partner violence rather than asking only women with symptoms (case-finding); however, what is the evidence that screening interventions will increase identification, and referral to support agencies, or improve women's subsequent wellbeing and not cause harm?

Objectives

To assess the effectiveness of screening for intimate partner violence conducted within healthcare settings for identification, referral to support agencies and health outcomes for women.

Search methods

We searched the following databases in July 2012: CENTRAL (2012, Issue 6), MEDLINE (1948 to September Week June Week 3 2012), EMBASE (1980 to Week 28 2012), MEDLINE In–Process (3 July 2012), DARE (2012, Issue 2), CINAHL (1937 to current), PsycINFO (1806 to June Week 4 2012), Sociological Abstracts (1952 to current) and ASSIA (1987 to October 2010). In addition we searched the following trials registers: metaRegister of Controlled Trials (mRCT) (to July 2012), and International Clinical Trials Registry Platform (ICTRP), ClinicalTrials.gov, Australian New Zealand Clinical Trials Registry and the International Standard Randomised Controlled Trial Number Register to August 2010. We also searched the reference lists of articles and websites of relevant organisations.

Selection criteria

Randomised or quasi-randomised trials assessing the effectiveness of IPV screening where healthcare professionals screened women face-to-face or were informed of results of screening questionnaires, compared with usual care ( which included screening for other purposes).

Data collection and analysis

Two review authors independently assessed the risk of bias in the trials and undertook data extraction. For binary outcomes, we calculated a standardised estimation of the risk ratio (RR) and for continuous data, either a mean difference (MD) or standardised mean difference (SMD). All are presented with a 95% confidence interval (CI).

Main results

We included 11 trials that recruited 13,027 women overall. Six of 10 studies were assessed as being at high risk of bias.

When data from six comparable studies were combined (n = 3564), screening increased identification of victims/survivors (RR 2.33; 95% CI 1.40 to 3.89), particularly in antenatal settings (RR 4.26; 95% CI 1.76 to 10.31).

Only three studies measured referrals to support agencies (n = 1400). There is no evidence that screening increases such referrals, as although referral numbers increased in the screened group, actual numbers were very small and crossed the line of no effect (RR 2.67; 95% CI 0.99 to 7.20).

Only two studies measured women's experience of violence after screening (one at three months, the other at six, 12 and 18 months after screening) and found no significant reduction of abuse.

Only one study measured adverse effects and data from this study suggested that screening may not cause harm. This same study showed a trend towards mental health benefit, but the results did not reach statistical significance.

There was insufficient evidence on which to judge whether screening increases take up of specialist services, and no studies included economic evaluation.

Authors' conclusions

Screening is likely to increase identification rates but rates of referral to support agencies are low and as yet we know little about the proportions of false measurement (negatives or positives). Screening does not appear to cause harm, but only one study examined this outcome. As there is an absence of evidence of long-term benefit for women, there is insufficient evidence to justify universal screening in healthcare settings. Studies comparing screening versus case finding (with or without advocacy or therapeutic interventions) for women's long-term wellbeing would better inform future policies in healthcare settings.

Résumé scientifique

Dépistage des femmes victimes de violence exercée par un partenaire masculin intime dans des établissements de soins

Contexte

La violence exercée par un partenaire masculin intime porte gravement atteinte aux individus, à leurs enfants, à la communauté toute entière, et à l'ensemble du tissu social et économique. Certains gouvernements et organismes de santé recommandent un dépistage de la violence exercée par un partenaire masculin intime pour toutes les femmes au lieu de limiter le dépistage uniquement aux femmes présentant des symptômes (recherche des cas) ; cependant, quelles sont les preuves que les interventions de dépistage augmenteront le nombre de cas identifiés, et le nombre de femmes adressées à des services de soutien, ou qu'elles amélioreront le bien-être consécutif des femmes et qu'elles n'entraîneront pas de risques ?

Objectifs

Évaluer l'efficacité du dépistage de la violence exercée par un partenaire masculin intime effectué dans des établissements de soins pour identifier les femmes battues, les adresser à des services de soutien, ainsi que sur les résultats sur la santé des femmes.

Stratégie de recherche documentaire

En juillet 2012, nous avons effectué des recherches dans les bases de données suivantes : CENTRAL (2012, numéro 6), MEDLINE (de 1948 jusqu'à la 3ème semaine de septembre et de juin 2012), EMBASE (de 1980 jusqu'à la 28ème semaine de l'année 2012), MEDLINE In–Process (3.07.2012), DARE (2012, numéro 2), CINAHL (de 1937 à aujourd'hui), PsycINFO (de 1806 jusqu'à la 4ème semaine de juin 2012), Sociological Abstracts (de 1952 à aujourd'hui) et ASSIA (de 1987 jusqu'à octobre 2010). En outre, nous avons consulté les registres d'essais suivants : le métaRegistre des essais contrôlés (mREC) (jusqu'à juillet 2012), et le système d’enregistrement international des essais cliniques (International Clinical Trials Registry Platform, (ICTRP)) ClinicalTrials.gov, Australian New Zealand Clinical Trials Registry et le registre ISRCTN (International Standard Randomised Controlled Trial Number Register) jusqu'à août 2010. Nous avons également cherché dans les références bibliographiques des articles et les sites web des organismes de santé compétents.

Critères de sélection

Des essais randomisés ou quasi-randomisés évaluant l'efficacité du dépistage de la violence exercée par un partenaire masculin intime dans lesquels le personnel médical a dépisté des femmes directement en personne ou était informé des résultats des questionnaires de dépistage, comparativement aux soins habituels (qui incluaient un dépistage mais à d'autres fins).

Recueil et analyse des données

Deux auteurs ont, de manière indépendante, évalué les risques de biais des essais et extrait des données. Pour les résultats binaires, nous avons calculé une estimation standardisée du risque relatif (RR) et pour les variables continues, nous avons calculé soit la différence moyenne (DM) soit la différence moyenne standardisée (DMS). Toutes les mesures sont présentées avec un intervalle de confiance (IC) à 95 %.

Résultats principaux

Nous avons inclus 11 essais ayant recruté 13 027 femmes globalement. Six des dix études ont été évaluées comme présentant un risque élevé de biais.

Après combinaison des données issues de six études comparables (n = 3564), il en est ressorti que le dépistage a augmenté le nombre de victimes/survivantes identifiées (RR 2,33 ; IC à 95 % 1,40 à 3,89), surtout dans les cliniques prénatales (RR 4,26 ; IC à 95 % 1,76 à 10,31).

Trois études seulement ont mesuré le nombre de femmes adressées à des services de soutien (n = 1400). Il n'y a pas de preuves indiquant que le dépistage augmente le nombre des femmes adressées à des services d'aide car, même si le nombre de ces femmes a augmenté dans le groupe de femmes dépistées, le nombre réel était très faible et dépassait la ligne d'absence d'effet (RR 2,67 ; IC 95 % 0,99 à 7,20).

Deux études seulement ont mesuré la violence subie par les femmes après le dépistage (une à trois mois, l'autre à six mois, 12 mois et 18 mois après le dépistage) et n'ont détecté aucune diminution significative de la violence subie.

Une étude seulement a mesuré les effets indésirables et les données issues de cette étude laissent entendre que le dépistage peut ne pas entraîner de risques. Cette même étude a révélé une tendance vers des bénéfices sur la santé mentale, mais les résultats n'ont pas atteints de signification statistique.

Il n'y avait pas suffisamment de données probantes pour établir si le dépistage augmente le recours à des services d'aide spécialisés, et aucune étude n'a inclus une évaluation économique.

Conclusions des auteurs

Le dépistage est susceptible d'augmenter les taux d'identification de femmes battues mais les taux de femmes adressées à des services de soutien restent faibles et nous en savons toujours très peu sur les proportions de faux résultats (faux négatifs ou faux positifs). Il semble que le dépistage n'entraîne pas de risques, mais une étude seulement a examiné ce critère. Compte tenu de l'absence de preuves d'effets bénéfiques à long terme chez les femmes, il n'y a pas suffisamment de données probantes pour justifier un dépistage universel dans les établissements de soins. Des études comparant le dépistage à la recherche des cas (avec ou sans recommandations ou interventions thérapeutiques) pour le bien-être des femmes à long terme devraient permettre de mieux orienter les futures politiques dans les établissements de soins.

Plain language summary

Screening women for intimate partner violence in healthcare settings

Women who have experienced physical, psychological or sexual violence from an intimate partner (for example, husband, boyfriend, ex-husband or ex-boyfriend) can suffer poor physical and mental health, poor pregnancy outcomes and premature death. Their children and families can also suffer. The effects of violence often result in women attending healthcare settings. Some people have argued that healthcare professionals should routinely ask all women attending a healthcare setting whether they have experienced violence from their partner or ex-partner. They argue that this approach (known as universal screening) might encourage women who would not otherwise do so, to disclose abuse, or to recognise their experience as ‘abuse’. In turn, this would enable the healthcare professional to provide immediate support or refer them to specialist help, or both. Some governments and health organisations recommend universal screening for intimate partner violence (IPV). Others argue that such screening should be targeted to high risk groups, such as pregnant women attending antenatal clinics (targeted screening is known as ‘selective screening’).

We carried out this review to find out two things. First, whether there was any evidence that IPV screening increases the number of women identified and the number referred on to specialist services. Second, whether screening results in health benefits to women or causes any harm.

We found 11 studies that assessed the effectiveness of IPV screening where healthcare professionals screened women face-to-face or were informed of results of screening questionnaires, compared with usual care. No study compared the benefit of universal screening versus selective screening. All the studies were conducted in high income countries. The studies looked at screening in hospitals and in community settings. Screening methods included questionnaires (paper and computer based) completed by women themselves or face-to-face screening. No study took into account differences in how much abuse women were experiencing, or whether they were able or ready to take action – something that might affect the likelihood of disclosing abuse. Further, none looked at the sustainability of screening by healthcare professionals.

Screening doubled the likelihood that abused women were identified, but did not increase the numbers referred for specialist help. Both the numbers identified and referred for support were low. Screening did not reduce the level of violence experienced by women or improve women’s health and wellbeing at any time point from three to 18 months after the screening. One study reported no evidence of harm. The remaining ten studies did not address the issue of harmful consequences. We do not know if screening increases take up of specialist services. None of the studies measured how much it costs to deliver screening.

We conclude that there is insufficient evidence to justify universal screening for intimate partner violence in healthcare settings.

Résumé simplifié

Dépistage des femmes victimes de violence exercée par un partenaire masculin intime dans des établissements de soins

Les femmes ayant subi des violences physiques, psychologiques ou sexuelles exercées par un partenaire masculin intime (par exemple, le mari, le petit copain, l'ex-mari ou l'ex-petit copain) peuvent souffrir d'une mauvaise santé physique et mentale, redouter de mauvais résultats de grossesse et un décès prématuré. Leurs enfants et les familles peuvent aussi en souffrir. Les effets de la violence subie par les femmes impliquent souvent des consultations dans les établissements de soins. Certaines personnes ont plaidé en faveur d'une disposition obligeant le personnel médical à demander systématiquement à toutes les femmes en consultation dans un établissement de soins si elles ont subi des violences exercées par leur partenaire ou ex-partenaire. Ces personnes avancent que cette approche (appelée dépistage universel) pourrait encourager les femmes qui sinon ne le feraient pas, à dénoncer la violence subie, ou à admettre qu'elles subissent des "violences’. À ce stade, cela pourrait permettre au personnel médical de leur apporter un soutien immédiat ou de les adresser à des services d'aide spécialisés, ou les deux. Certains gouvernements et organismes de santé recommandent un dépistage universel de la violence exercée par un partenaire masculin intime. D'autres avancent qu'un tel dépistage devrait cibler les groupes à haut risque, tels que les femmes enceintes en consultation dans les cliniques prénatales (on appelle le dépistage ciblé ‘dépistage sélectif’).

Nous avons effectué cette revue pour déterminer deux points. Premièrement, s'il existait des preuves que le dépistage de la violence exercée par un partenaire masculin intime augmente le nombre de femmes identifiées et le nombre de femmes adressées à des services d'aide spécialisés. Deuxièmement, si le dépistage favorise des bénéfices pour la santé chez les femmes ou s'il entraîne des risques.

Nous avons trouvé 11 études ayant évalué l'efficacité du dépistage de la violence exercée par un partenaire masculin intime dans lesquelles le personnel médical a dépisté des femmes directement en personne ou était informé des résultats des questionnaires de dépistage, comparativement aux soins habituels. Aucune étude n'a comparé les bénéfices d'un dépistage universel à ceux d'un dépistage sélectif. Toutes les études ont été menées dans des pays à haut revenu. Les études ont examiné le dépistage dans les milieux hospitaliers et dans la communauté. Les méthodes de dépistage incluaient des questionnaires (sur papier et au format électronique) complétées du dépistage par les femmes elles-mêmes ou du dépistage des femmes directement en personne. Aucune étude n'a pris en compte les différences dans les diverses formes de violence subies par les femmes battues, ou le fait qu'elles étaient ou non aptes ou prêtes à prendre des mesures, la moindre réaction qui pourrait modifier la probabilité de dénoncer la violence. En outre, aucune n'a examiné la pérennité du dépistage effectué par le personnel médical.

Le dépistage a multiplié par deux la probabilité que les femmes battues soient identifiées, mais n'a pas augmenté le nombre de femmes adressées à des services d'aide spécialisés. Le nombre de femmes identifiées et le nombre de femmes adressées à des services de soutien étaient faibles. Le dépistage n'a pas réduit le niveau de la violence subie par les femmes, ni amélioré la santé et le bien-être des femmes à aucun moment entre 3 et 18 mois après le dépistage. Dans une étude, aucune preuve de risques n'a été rapportée. Les dix autres études n'ont pas abordé la question des conséquences dangereuses. Nous ne savons pas si le dépistage augmente le recours à des services d'aide spécialisés. Aucune des études n'a évalué les coûts de la mise en place du dépistage.

Nous en concluons qu'il n'y a pas suffisamment de données probantes pour justifier le dépistage universel de la violence exercée par un partenaire masculin intime dans des établissements de soins.

Notes de traduction

Traduit par: French Cochrane Centre 17th May, 2013
Traduction financée par: Pour la France : Minist�re de la Sant�. Pour le Canada : Instituts de recherche en sant� du Canada, minist�re de la Sant� du Qu�bec, Fonds de recherche de Qu�bec-Sant� et Institut national d'excellence en sant� et en services sociaux.

Summary of findings(Explanation)

Summary of findings for the main comparison. 
Screening for intimate partner violence compared with no screening or screening for other purposes
Patient or population: women presenting in healthcare settings
Settings: healthcare
Intervention: face-to-face screening or written/computerised screening with result passed to the healthcare professional
Comparison: unscreened women or those whose screening result was not passed on to the healthcare professional or who were screened for issues other than IPV
OutcomesIllustrative comparative benefit* (95% CI) Relative effect
(95% CI)
No of participants
(studies)
Quality of the evidence
(GRADE)
Comments

Assumed benefit

Unscreened per 1000

Corresponding benefit

Screened per 1000

Absolute Benefit

Per 1000

Identification

(Immediate follow-up to 1 month post-screening)

3174 (60 to 167)43 (12 to 89)RR 2.33 (1.40 to 3.89)3564
(6)
⊕⊕⊕⊝
moderate
 

Referrals by health professionals

(immediate follow-up)

719 (3 to 42)12 (0 to 43)RR 2.67 (0.99 to 7.20)1400
(2)
⊕⊕⊝⊝
low
 
*The assumed benefit was calculated for the rate per 1000. The corresponding benefit was calculated by multiplying the assumed benefit by the risk ratio of unscreened to screened women.
CI: confidence interval; RR: risk ratio
GRADE Working Group grades of evidence
High quality: Further research is very unlikely to change our confidence in the estimate of effect
Moderate quality: Further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate
Low quality: Further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate
Very low quality: We are very uncertain about the estimate

Background

Description of the condition

Intimate partner violence

For the purpose of this review, the definition of intimate partner violence (IPV) (often termed domestic violence) is that used by the World Health Organization (WHO), that is, any behaviour within an intimate relationship that causes physical, psychological or sexual harm to those in the relationship (Krug 2002). IPV often involves a combination of abuse behaviours. These include threats of and actual physical violence, sexual violence, emotionally abusive behaviours, economic restrictions and other controlling behaviours. Many survivors of IPV report that the physical violence is not the most damaging: it is the relentless psychological abuse that leaves the woman with long lasting adverse effects (Campbell 2002).

Domestic violence against men is not included in this review because the majority of abuse with serious health and other consequences is that committed by men against their female partners, which is why most screening interventions target women (Taft 2001). While women may be abused by many other family members other than their partner, such as in-laws or children, these are not included in the review. We include same-sex violence in this review and abuse perpetrated by ex-partners, since women who are separating or have just left their partner are at increased risk of violence (Wilson 1993; Campbell 2004).

Prevalence of intimate partner violence

Abuse of women by their partners or ex-partners is a common worldwide phenomenon (Garcia-Moreno 2006). The 2002 WHO World Report on Violence and Health (Krug 2002) revealed that in 48 population-based surveys around the world, 10% to 69% of women had been physically assaulted by their partners at some stage in their lives. Some comparative examples of prevalence from the WHO studies are outlined in Table 1. Definitions used in prevalence studies range from physical abuse in current relationships to the inclusion of physical, emotional, sexual, or a combination of abuses in past relationships (Hegarty 2006). Estimates of the magnitude of IPV are obtained from community surveys, clinical samples and public records. It is likely that some of the discrepancy in prevalence rates is due to differences in definitions of partner violence, populations sampled and cross-cultural differences.

Table 1. Comparative rates of intimate partner violence prevalence
CountryLifetime prevalencePrevious 12 months
Switzerland21%7%
Egypt34%-
Zimbabwe17%-
India40%14%
Cambodia16%-
Nicaragua28%12%
Canada29%3%

Impact on women's health and their use of services

IPV can have short-term and long-term negative health consequences for survivors, even after the abuse has ended (Campbell 2002). World Development reports (World Bank 2006) and statements from the United Nations (Ingram 2005) emphasise that IPV is a significant cause of death and disability on a worldwide scale (Ellsberg 2008) and the WHO highlights violence against women as a priority health issue (Krug 2002). Women experiencing IPV present very frequently to health services and require wide-ranging medical services (Davidson 2000).

Psychosocial health of abused women

The most prevalent mental health sequelae of IPV for female victims are depression, anxiety, post-traumatic stress disorder (PTSD) and substance use (Golding 2002; Hegarty 2004; Rees 2011), and women often suffer from low self-esteem and hopelessness (Kirkwood 1993). Suicide and attempted suicide are also associated with IPV in both industrialised and non-industrialised countries (Golding 2002; Ellsberg 2008). Any of these effects also impact detrimentally on women's ability to parent and thus impact on their children (McCosker-Howard 2006).

Physical health of abused women

Abused women often experience many chronic health problems. The most consistent and largest physical health difference between abused and non-abused women is the experience of gynaecological symptoms (McCauley 1995; Campbell 2002). Other conditions include chronic pain and central nervous system symptoms (Diaz 1999; Campbell 2002), self-reported gastrointestinal symptoms, diagnosed functional gastrointestinal disorders (Coker 2000) and self-reported cardiac symptoms (Tollestrup 1999).

IPV is also one of the most common causes of injury in women (Stark 1996; Richardson 2002) and femicide, with over 50% of all female murders committed by their partners or ex-partners in the UK and USA (Brock 1999; Shackelford 2005; Home Office 2010). In Australia, as elsewhere, a far higher percentage of indigenous compared with non-indigenous women are murdered by their partners (Mouzos 2003). Women and their fetuses are also at risk before, during and after pregnancy (Martin 2001;Silverman 2006). The most serious outcome is the death of the mother or the fetus (Jejeebhoy 1998; Parsons 1999). However, violence by a partner is also associated with high rates of pregnancy at a young age (Moore 2010), miscarriage, abortion (Taft 2004; Pallitto 2013), low birth weight (Murphy 2001), premature birth and fetal injury (Mezey 1997).

Description of the intervention

Interventions by healthcare practitioners to improve the health consequences for women experiencing domestic violence

Due to the poor health status of abused women and their consequent frequent attendance at healthcare services, these services play a central role in abused women's care, but the quality of healthcare professionals' responses has been a focus of concern since the 1970s (Stark 1996; Feder 2006). Over the last few decades there has been a concerted effort by women's and justice organisations and the voluntary sector to respond to the needs of women who are experiencing or who have experienced violence. In contrast, the response of health services has been slow (Feder 2009). While most health professionals believe that IPV is a healthcare issue (Richardson 2001), there has been a reluctance to confront the problem. A number of barriers contribute to this ambivalence on the part of practitioners (Hegarty 2001). These include a perceived lack of time and support resources, fear of offending the woman, a lack of knowledge and training about what to do for the woman and a belief that the woman will not leave the abusive relationship (Waalen 2000). A further barrier is the lack of evidence for effective interventions.

Despite these barriers, there has been progress in the overall response of health systems to IPV and since the late 1990s, many health professional associations around the world have published guidelines for clinicians on how to identify women who have been abused (Davidson 2000; Family Violence Prevention Fund 2004; Hegarty 2008). Implicit in many of these recommendations is the assumption that screening or asking routinely about abuse will increase identification of women who are experiencing violence, lead to appropriate interventions and support, and ultimately decrease exposure to violence and its detrimental health consequences, both physical and psychological (Taket 2004). Screening is predicated on the assumptions that identifying and responding supportively to, and referring on women experiencing violence is fulfilling health professionals' duty of care, but that further advocacy or therapy requires appropriate training and time clinicians do not have. Further, that clinicians are just a part of a wider system response and need to be able to refer to domestic violence services who have specialist training, connections to community-based services and more time. Training and knowledge of referral services should improve clinicians' motivation to identify, when they are not responsible for ongoing domestic violence counselling and advocacy. This review is focused on screening only and does not include advocacy or psychotherapeutic interventions, which are the topics of separate reviews.

Screening

Screening aims to identify women who have experienced, or are experiencing, IPV from a partner or ex-partner in order to offer interventions leading to beneficial outcomes. However, within the field of domestic/family violence, both the immediate- and longer-term benefit of screening to women remains unproven (Taket 2004; Spangaro 2009). Many factors influence whether or not women choose to disclose their abuse, for example, fear or readiness to take action, and these, will affect accurate measurement of screening rates. Screening for IPV, therefore, is a problematic concept when traditional screening criteria are applied (Hegarty 2006), as it is a complex social phenomenon, not a disease. It still, however, requires rigorous evidence for its effectiveness if it is to be implemented as policy.

It is important to distinguish between universal screening (the application of a standardised question to all symptom-free women according to a procedure that does not vary from place to place), selective screening (where high-risk groups, such as pregnant women or those seeking pregnancy terminations are screened), routine enquiry (when all women are asked but the method or question may vary according to the provider or woman's situation) and case finding (asking questions if indicators are present).

For this review, screening is defined as any method that aims for every woman patient in a healthcare setting to be asked about their experiences of IPV, both past and present. Screening may be conducted directly by a healthcare professional or indirectly through a self-completed questionnaire (often by computer) with the healthcare professional informed of the questionnaire results. This may include the use of screening tools (Rabin 2009), which vary in their validity and reliability and therefore in their effectiveness in accurately detecting abuse. These tools (and there are many) are reviewed in Feder 2009 and Basile 2007. Alternatively, clinicians may ask one or a range of questions related to IPV only at one time point or several . It is very unlikely that one single question will address the range of women's experiences of partner abuse. Whether a woman is currently experiencing IPV from a current partner or an ex-partner (for example, harassment) or has previously experienced IPV, the goal of screening is the same - to identify her and to offer her support appropriate to her needs that will prevent any further abuse (for example, advocacy, legal or police help) and reduce any consequent problems she is experiencing (for example, offering therapeutic support) or a combination of these.

There has long been debate about the value of screening per se (Taket 2004; Feder 2009), with some arguing that asking questions can raise awareness in women experiencing partner violence who are contemplating their situation. Below, we examine women's attitudes to screening, including the question of women's preferred method for being screened (Feder 2009). Generally, most women are in favour of universal screening, although this varies with abuse status and age (Feder 2009). However, studies have found that women's preferences vary according to the method of screening used (MacMillan 2006; Feder 2009, p. 39). Readers are referred to several studies that have examined this question but were excluded from this review (Furbee 1998; Bair-Merritt 2006; Chen 2007; Rickert 2009). Bair-Merritt 2006 found a similar disclosure rate in audiotaped (11%) compared with written questionnaires (9%) with both methods preferred to direct physician inquiry. Chen 2007 found that there was little difference between self-completion and healthcare staff or physician inquiry in terms of participant comfort, time taken and effectiveness, but that women who had experienced IPV were less comfortable with physician screening; MacMillan 2006 reported that women found self-completion methods easier, more private and confidential.

Identifying IPV is only the first step in intervention. Klevens 2012b tested computer-assisted screening accompanied by referral information, or no screening and referral information only, compared with usual care (i.e.) and 12 months later found no difference between the three groups in physical or mental health and other quality of life measures. Women may have experienced long-standing abuse or it may have commenced recently; they may be unaware that the behaviour constitutes abuse or be actively seeking support for change and therefore responses to their needs may need to differ (Chang 2006).

Two reviews of studies addressing the UK National Screening Committee criteria (Ramsay 2002; Feder 2009) found that screening by health professionals leads to a modest increase in the number of abused women being identified following screening, but that screening was not acceptable to the majority of health professionals surveyed. Hegarty 2006 outlines the many clinician barriers (for example, time, lack of ongoing or effective training and resources) and system barriers (for example, different health priorities, lack of referral resources in the community) that impede effective screening and routine inquiry and that need to be addressed before clinicians will feel comfortable to ask women about their abuse experiences. In addition, women experience barriers to disclosure, especially during pregnancy, with the presence of abusive partners or their monitoring of her attendance at healthcare services where she might disclose. Most reviews have concluded there is no evidence that women experience better outcomes from interventions following screening (Ramsay 2002; Wathen 2003). This lack of evidence has not deterred many governments around the world implementing universal IPV screening or selective screening in high-risk populations. Previous US and Canadian Task Forces on Preventive Health Care conducted thorough systematic reviews of the evidence and concluded that there was insufficient evidence to recommend for or against routine screening for violence against women (Wathen 2003; Nelson 2004); however, the US Preventive Services Task Force revised their decision (Nelson 2012) and now recommend screening based on scant evidence from one effectiveness study (MacMillan 2009). Some would argue that it is unethical to implement screening for IPV in the absence of evidence of effectiveness as it may cause harm (Jewkes 2002; Wathen 2012).

How the intervention might work

Screening women using face-to-face methods implies the clinician is directly asking all women who attend for a given consultation whether they are experiencing or have ever experienced abusive behaviours from their partner or ex-partner, thus necessitating the woman either to disclose or not to disclose, depending on her situation. Alternatively all women attending a consultation can be offered different methods of self-completion of a screening instrument where abusive behaviour can be disclosed or not. These self-completion results are then assessed by a healthcare professional for follow-up support or referral. The option of administrative or computerised follow-up has , bypassing the clinician altogether, also been explored (Klevens 2012b). Universal screening aims for 100% of women to be asked about IPV and those experiencing IPV to disclose it. Universal screening may apply to all women in a healthcare setting, such as a hospital or selective screening could be applied to those in high-risk groups, such as those in antenatal or abortion clinics or pregnant women attending community-based family practice clinics.

Why it is important to do this review

There is an urgent need to assess and identify health sector screening interventions for IPV for several reasons (Davidson 2000; Feder 2009): in order to have clear evidence about what health professionals can do safely and effectively to decrease the impact of IPV on women; to determine what is cost-effective; and to inform health professionals and policy makers about the cost/benefit of screening interventions. In particular, this systematic review examines the most rigorous evidence around health service screening interventions for IPV to ascertain whether the potential benefits of IPV screening for women's health and wellbeing outweigh any potential for harm. We examine screening effectiveness overall (when it is included in broad psychosocial screening or IPV-specific screening interventions), as well as in subgroups of settings, and document the duration of follow-up in all included studies.

Objectives

To assess the effectiveness of screening for IPV conducted within healthcare settings on identification, referral and health outcomes for women.

Methods

Criteria for considering studies for this review

Types of studies

Any studies that allocate individual women or clusters of women by a random or a quasi-random method (such as alternate allocation, allocation by birth date, etc.) to a screening intervention compared with usual care or where healthcare professionals were not informed of women's screening results.

Types of participants

Women (aged 16 years and above) attending a healthcare setting. Healthcare setting is defined as any health setting where health services of any kind are delivered including the following and home visits by these services:

  • general (family) practice;

  • antenatal and postnatal services;

  • hospital emergency, inpatient or outpatient services;

  • private specialists (for example, obstetrics and gynaecology, psychiatry);

  • community health services;

  • drug and alcohol services;

  • mental health services.

Types of interventions

Any IPV screening in a healthcare setting as listed above. Screening is defined as any of a range of methods (face-to-face, survey or other method - IPV-specific or where IPV was included in more general psychosocial screening) that aims for all women patients in a healthcare setting to be asked about having experienced or currently experiencing IPV, including the use of screening tools as well as asking one or a range of screening questions related to IPV on only one occasion or at subsequent visits. We only included studies where the treating healthcare professional conducted the screening or the healthcare professional was informed of the screening result at the time of the relevant consultation. There may, therefore, be studies with 'treatment as usual' conditions where screening for research purposes was undertaken but healthcare professionals were not informed of the screening results and have, therefore, provided 'usual care'.

We excluded extended interventions that went beyond screening and an immediate response to disclosure, that is, that included follow-up consultations with the physician and the physician offering further counselling or psychological treatment.

Types of outcome measures

Primary outcomes

A. Identification of IPV by health professionals

Identification was defined as any form of acknowledgement by a healthcare professional during a consultation that the woman had experienced exposure to IPV. Identification therefore assumes communication between provider and participant that acknowledges the abuse. Studies variously refer to identification, discussion and patient disclosure of IPV. We carefully assessed how stated outcomes were operationalised across trials in order to determine if they met our definition of identification. Studies could collect identification data using a variety of methods (for example, audio recordings of encounters, surveying women and providers about what was discussed during the encounter and medical record review).

B. Information-giving and referrals to support agencies by healthcare professionals (including take-up rates when available)

We included in this category any recording, documentation or organisational validation that women had been given information about, or referral to, support agencies.

Secondary outcomes

C. IPV measured by:

i. validated instruments (for example, Composite Abuse Scale (CAS), Index of Spouse Abuse);
ii. self-reported IPV, even if using an unvalidated scale.

D. Women's perceived and diagnosed physical health outcomes, using measures of:

i. physical health (for example, Short-Form-36 physical subscale, General Health Questionnaire)
ii. physical injuries, such as fractures and bruises (self-reported or documented in medical records)
iii. chronic health disorders, such as gynaecological problems, chronic pain and gastrointestinal disorders (self-reported or clinical symptoms, or both, documented in medical records)

E. Women's psychosocial health using measures of:

i. depression (for example, Beck Depression Inventory, Center for Epidemiologic Studies Depression Scale);
ii. post-traumatic stress (for example, Impact of Events Scale, Post-traumatic Stress Disorder Checklist);
iii. anxiety (such as Spielberger's State-Trait Anxiety Inventory, Beck Anxiety Inventory);
iv. self-efficacy (for example, Generalized Perceived Self-Efficacy Scale, Sherer's Self-Efficacy Scale);
v. self-esteem (for example, Rosenberg Self-Esteem Scale, Coopersmith's Self-Esteem Inventory);
vi. quality of life (for example, World Health Organization Quality of Life WHOQOL-Bref);
vii. perceived social support (for example, Medical Outcomes Scale, Sarason's Social Support Questionnaire);
viii. alcohol or drug abuse (for example, Addiction Severity Index, Alcohol and other Drug Abuse Scale).

F. Occurrence of adverse outcomes, such as:

i. increased deaths, all-cause or IPV-related (documented in medical records or routinely collected data);
ii. increase of IPV as measured by any of the above;
iii. increase of physical or psychosocial morbidity as listed above;
iv. false negatives and false positives of screening tests.

G. Services and resource use:

i. family/domestic violence services;
ii. police/legal services;
iii. counselling or therapeutic services;
iv health service use;
v. other services.

H. Cost/benefit outcomes, measured using:

i. health service use;
ii. days out-of-role;
iii. medication use.

Timing of outcome assessment

We documented the duration of follow-up in all included studies. For the purposes of this review, we defined short-term follow-up as less than six months since the screening intervention, medium-term follow-up as between six and 12 months, and long-term follow-up as more than 12 months.

Search methods for identification of studies

Searches were made of the international literature for peer-reviewed and non-peer reviewed studies and published and unpublished studies. There were no language restrictions applied to the search strategies used. We chose not to use a trials filter as we wanted the search to be as inclusive as possible and an initial check of the differences between using and not using the RCT filter uncovered a trial not included when the RCT filter was applied. A variety of sources were used to identify studies. The initial searches for this review were run in September 2009 and updated in October 2010. We discarded the records found in 2010 because of an error, and re-ran the searches in September 2011 to find records published since 2009. Searches were updated again in July 2012.

Electronic searches

We searched the following databases.

  • Cochrane Central Register of Controlled Trials (CENTRAL) 2012 (Issue 6) part of The Cochrane Library, searched 5 July 2012

  • MEDLINE (1948 to June week 3 2012), searched 5 July 2012

  • MEDLINE(R) In–Process (3 July 2012), searched 5 July 2012

  • EMBASE (1980 to week 28 2012), searched 5 July 2012

  • Database of Abstracts of Reviews for Effectiveness (DARE), 2012 (Issue 2), part of The Cochrane Library, searched 5 July 2012

  • CINAHL PLUS (1937 to current), searched searched 5 July 2012

  • PsycINFO via OVID (1806 to June Week 4 2012), last searched 5 July 2012

  • ASSIA (1987 to current), last searched 5 October 2010

  • Sociological Abstracts (1952 to current), last searched 5 July 2012

  • metaRegister of Controlled Trials (mRCT), last searched 6 July 2012

  • WHO International Clinical Trials Registry Platform, searched August 2010

  • ClinicalTrials.gov searched August 2010

  • Australian New Zealand Clinical Trials Registry searched August 2010

  • International Standard Randomised Controlled Trial Number Register searched August 2010

The search strategies used to search each database can be found in Appendix 1. The searches were originally run by Joanne Abbott, former Trials Search Co-ordinator (TSC) of the Cochrane Developmental, Psychosocial and Learning Problems Group (CDPLPG). Subsequent searches were conducted by Margaret Anderson, current TSC of CDPLPG.

Authors searched the website of the WHO (www.who.int/topics/violence/en/), the Violence Against Women Online Resources (www.vaw.umn.edu/) and Domestic Violence Data Source (www.lho.org.uk/viewResource.aspx?id=9443).

Searching other resources

Handsearching

We were unable to undertake planned handsearching of Journal of Family Violence, Journal of Interpersonal Violence, Violence and Victims, Women's Health, American Journal of Preventive Medicine, American Journal of Public Health, Annals of Emergency Medicine, Archives of Internal Medicine, Australian & New Zealand Journal of Public Health and Journal of the American Medical Association due to insufficient resources.

Citation tracking

We examined the reference lists of acquired papers and tracked citations forwards and backwards.

Personal communication with the first authors of all included articles

We emailed the authors of primary studies included in the review to check for any omissions (and, in particular omissions of non-peer reviewed studies). We contacted the WHO Violence and Injury Programme to inquire about any screening studies fitting our criteria of which we were unaware, especially in low- and middle-income countries.

Data collection and analysis

Selection of studies

Searches were run three times for this review (September 2009, September 2011 and July 2012; see Figure 1). Abstracts were reviewed independently by two review author pairs (LOD and AT, LOD and KH). Where possible, disagreement about abstract inclusion between any two review authors was resolved by reading the full study followed by discussion. When agreement could not be reached then a third review author (AT or KH) was asked to assess whether the study fulfilled the inclusion criteria or not. Once the list of included studies based on abstracts was complete, we retrieved the full-text articles. The complex nature of the 'screening' definition required that the entire team met in order to discuss at length and finalise the revised definition of a screening intervention now governing criteria for this review. Each study included to this stage was assessed independently by two review authors (LOD and AT) against the inclusion criteria. As with the earlier stage of the study review process, any disagreement was resolved by discussing studies in-depth with a third review author (KH). Where additional information was required to adequately understand the nature of the screening intervention and design, contact was made with the first author of the study in question. This led to all outstanding issues being resolved. The reasons behind decisions to exclude otherwise plausible studies are offered in the Characteristics of excluded studies table.

Figure 1.

Flow diagram for selection of studies

Data extraction and management

Data from included studies were extracted independently by two review authors (LOD and AT) and entered into electronic data collection forms. Any missing information or clarification was requested from the first or corresponding authors of papers and six (Rhodes 2002 ; Carroll 2005 ; MacMillan 2009; Koziol-McLain 2010; Humphreys 2011; Klevens 2012a) of seven authors contacted replied. Any disagreements between the two review authors with regard to data extraction were resolved through discussion and no adjudication by a third review author was necessary. All instances of additional statistical data being provided by study investigators were noted and are distinguished as such in the text (Effects of interventions). Once agreed, all relevant data were entered into Review Manager 5.1 software (RevMan) (RevMan 2011).

We recorded the following information in the Characteristics of included studies table.

  • Method: randomisation or quasi-randomisation method, intention-to-treat analysis, power calculation.

  • Participants: setting, country, inclusion and exclusion criteria, numbers recruited, numbers dropped out, numbers analysed, age, marital status, ethnicity, socioeconomic status and educational background.

  • Interventions: brief description of intervention including screening tool and method and method of usual care.

  • Outcomes: timing of follow-up events, outcomes assessed and scales used.

  • Notes: further information to aid understanding of the study.

Assessment of risk of bias in included studies

Risk of bias of all included studies was assessed independently by two review authors (LOD and AT) using criteria outlined below and cross-checked in accordance with the updated methodological criteria in Section 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We summarise these below. Each domain is rated either 'high', 'low' or 'unclear' risk of bias.

Sequence generation

Description: the method used to generate the allocation sequences was described in sufficient detail so as to enable an assessment to be made as to whether it should have produced comparable groups. Review authors' judgement: was there selection bias (biased allocation to interventions) due to inadequate generation of a randomised sequence?

Allocation concealment

Description: the method used to conceal allocation sequences was described in sufficient detail to assess whether intervention schedules could have been foreseen in advance of, or during, recruitment. Review authors' judgement: was there selection bias (biased allocation to interventions) due to inadequate concealment of allocations prior to assignment?

Blinding

Description:

(a) performance bias - any measures used to blind healthcare professionals or participants to their randomisation status were described to know whether the outcomes may have been affected by this knowledge; review authors' judgement: was there performance bias due to knowledge of the allocated interventions by participants and personnel during the study?

(b) detection bias - any measures used to blind outcome assessors were described in sufficient detail so as to assess possible knowledge of which intervention a given participant might have received. Review authors' judgement: was there detection bias due to knowledge of the allocated interventions by outcome assessors?

Incomplete outcome data

Description: data on attrition were reported as well as the numbers involved (compared with total randomised) and reasons for attrition were reported or obtained from investigators. Review authors' judgement: was there attrition bias due to amount, nature or handling of incomplete outcome data?

Selective outcome reporting

Description: attempts were made to assess the possibility of selective outcome reporting by authors. Where available, protocols and trial databases were checked for prior outcome specification. Where a protocol was not available, we searched the databases of registered trials to check pre-specified outcome measures. Where neither were available, we were unable to assess this and therefore nominated this as 'uncertain'. Review authors' judgement: were reports of the study free of suggestion of selective outcome reporting?

Other sources of bias

Was the study apparently free of other problems that could put the outcomes at high risk of bias? In common with our associated review on advocacy (Ramsay 2009a), we specified the following three criteria under this heading.

Baseline measurement of outcome measures

Were baseline data evenly distributed? (if available)

Reliability of outcome measures

Were outcome measures well validated and referenced?

Protection against contamination

Was there adequate protection against the study being contaminated?

Measures of treatment effect

Continuous data were analysed if (i) means and standard deviations (SDs) were available or obtainable from the authors of studies, and (ii) the data were said to be normally distributed. If the second standard was not met then such data was not entered into RevMan (RevMan 2011) (as it assumes a normal distribution). We intended that where measurements were comparable and on the same scale, then these were combined to obtain mean differences. Where scales measured the same clinical outcomes in different ways (for example, depression, quality of life), mean differences were to be standardised in order to combine results across scales. There have been insufficient data in studies in the current review and these methods will be retained for any subsequent revision.

For binary outcomes (for example,woman identified/not identified, referred/not referred), a standard estimation of the risk ratio (RR) with random effects and a 95% confidence interval (CI) was calculated (Higgins 2011). In those studies where odds ratios (OR) were provided, we used the individual patient data given for the specified outcome and used the RR calculations provided by Rev Man. Where data required to calculate the RR were neither reported nor available from the authors of studies, we did not try to calculate these but have provided the findings as published by the authors. While we previously specified in the protocol that we would use OR for analysis of binary outcomes, we have altered this to RRs as Higgins 2011 (p. 267) advises these are more easily interpretable.

Unit of analysis issues

Cluster-randomised trials

Statistical methods for cluster-randomised trials used in the review are described in Section 8.11.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We examined studies to see whether they had accounted for the effects of clustering in their trials. If they had not, we planned to apply the criteria in Table 2, to re-analyse data using methods recommended by Donner 1980.

Table 2. Recommendations concerning cluster-randomised controlled trials
RecommendationOrder
Use of a clustered design is justified1
Effects of clustering are allowed for in analysis2
Stratification is carried out or justified if not3
The number of clusters included is sufficient to enable appropriate analyses and ensure sufficient study power (at least 4 clusters per intervention group)4
Analysis allows for effect of confounders or justified if not5

Dealing with missing data

Missing data and dropout rates were assessed for each of the included studies. If studies had been required to impute missing data in published articles, and tables of outcomes with and without imputation were provided, we have used imputed figures. The Characteristics of included studies tables specify the number of women who were included in the final analysis as a proportion of all women in the study. Where available, reasons given for missing data are provided in the narrative summary along with assessment of the extent to which the results may have been influenced by missing data. No study conformed to all intention-to-treat analysis criteria. We have included those in which all completed cases have been analysed in the groups to which they were randomised (available case analysis, Higgins 2011, Section 16.2), irrespective of whether they received the screening intervention or not. For dichotomous measures, where authors had not been required to do so, best-case and worst-case scenario analyses were undertaken to estimate the effect of the missing data on the results of all studies that were pooled. This meant that we were able to ascertain if observed effect sizes increased or decreased as a function of the extent of attrition in the two arms of the trial and these have been reported.

Assessment of heterogeneity

Consistency of results has been assessed visually and by examining the I2 statistic (Higgins 2002), a quantity that describes approximately the proportion of variation in point estimates that is due to heterogeneity rather than sampling error. Where significant statistical heterogeneity was detected (I2) differences in the characteristics of the studies or other factors were explored as possible sources of explanation with modified analyses. Any differences were summarised in the narrative synthesis.

Assessment of reporting biases

We planned to draw funnel plots to investigate any relationship between effect size and study precision (closely related to sample size) (Egger 1997) to investigate a relationship that could be due to publication or related biases or due to systematic differences between small and large studies. At this point, there are too few studies (a minimum of 10 studies included in meta-analysis) to undertake such an investigation.

Data synthesis

We have only performed meta-analysis where there were sufficient data and it was appropriate to do so. The decision whether to pool data in this way was determined by the compatibility of populations, denominators and screening methods (clinical heterogeneity), of the duration of follow-up (methodological heterogeneity) and of the outcomes. As fixed-effect models ignore heterogeneity, we have used the random-effects models to take account of the identified heterogeneity of the screening interventions. The Mantel-Haenszel method, a default programme in RevMan (RevMan 2011), can take account of few events or small study sizes and can be used with random-effects models. Where it was inappropriate to combine the data in a meta-analysis, we describe the effect sizes as specified in the original study and 95% CIs or SDs for individual outcomes in individual studies in a narrative fashion.

Subgroup analysis and investigation of heterogeneity

We performed subgroup analyses for type of healthcare setting.

Not enough studies were identified to perform all subgroup analyses planned in the protocol for this review. Single secondary outcome results are described in the narrative.

Sensitivity analysis

Primary analyses were based on available data from all included studies relevant to the comparison of interest. To assess the robustness of conclusions to quality of data and approaches to analysis, sensitivity analyses were performed. These analyses included the following:

  1. study quality;

  2. differential dropout;

  3. intention-to-treat;

  4. duration of follow-up.

Results

Description of studies

See: Characteristics of included studies; Characteristics of excluded studies; Characteristics of ongoing studies.

Results of the search

Our searches of the listed electronic databases (see Figure 1) generated 8426 records of which 1920 were duplicates; 6506 abstracts were therefore screened. Authors agreed on 6368 abstracts that were irrelevant and 138 that required joint review. Following discussions, a further 86 were excluded. Full-text papers were subsequently retrieved for 53 records. Based on the reference lists of these papers and contact with authors, we identified seven additional records. Of the total 60 records, it was determined that twelve were ineligible and a further 34 did not meet the inclusion criteria and reasons for their exclusion should be detailed in the Characteristics of excluded studies section. Eleven studies (that were published in 14 papers) met the inclusion criteria.

Included studies

Study designs

Nine randomised controlled trials (Carroll 2005; MacMillan 2006; Rhodes 2006; Ahmad 2009; MacMillan 2009; Kataoka 2010; Koziol-McLain 2010; Humphreys 2011; Klevens 2012a) and two quasi-experimental controlled studies (Rhodes 2002, Trautman 2007) met the criteria for inclusion in the review. All 11 studies were reported in peer-reviewed journals. All citations in the narrative refer to the major outcomes papers.

Location

Four studies were conducted in Canada (Carroll 2005; MacMillan 2006; Ahmad 2009; MacMillan 2009), five in the USA (Rhodes 2002 , Rhodes 2006; Trautman 2007; Humphreys 2011; Klevens 2012a), one in Japan (Kataoka 2010) and one in New Zealand (Koziol-McLain 2010). Several were cluster trials in diverse healthcare settings (Carroll 2005; MacMillan 2006; MacMillan 2009), which accounted for clustering in their analyses. Rhodes 2006 stratified by clinic location (inner urban or suburban) and randomised within location.

Healthcare settings

In three studies, women were recruited from antenatal clinics (Carroll 2005; Humphreys 2011 and Kataoka 2010), while MacMillan 2009 included an obstetrics and gynaecology clinic. Four were located in emergency departments (EDs) only (Rhodes 2002 , Rhodes 2006; Trautman 2007; Koziol-McLain 2010). Ahmad 2009 was conducted in a hospital-affiliated family practice and both MacMillan 2006 and MacMillan 2009 combined primary and tertiary care sites (family practices, EDs and women's health services). Klevens 2012a was conducted in assorted women's health clinics in a hospital.

Characteristics of participants

Both clinicians and their patients participated in the following studies.

Healthcare professionals

In two studies (Carroll 2005; Ahmad 2009), the first type of participant to be recruited was the clinician. They were trained prior to the identification and recruitment of patient participants.

Ahmad 2009 recruited 11/14 eligible family physicians from urban academic hospital-affiliated family practice clinics. Seven were white female clinicians who had an average age of 46 years and averaged 16 years in practice. Carroll 2005 recruited 48 family physicians, obstetricians and midwives from four practices diverse in location and populations, which provided antenatal and intrapartum care of transfer after birth. These different clinicians were paired by their age, sex, clinician type and health service location where possible and then randomised in pairs. Thirty-six of 48 (75%) were family physicians, the mean age was 42 years and 50% were female. They averaged 13.5 years in practice.

Participants

The 13,027 women recruited to the 11 studies were very diverse in sociodemographic characteristics, and while some studies described the whole screened population, others only described those whose abuse status was identified through screening. The majority of women were Canadian and over 9201 were recruited to MacMillan 2006 and MacMillan 2009.

Pregnant women screened in antenatal settings (Carroll 2005; Kataoka 2010; Humphreys 2011) were aged 30 years or less. In Carroll 2005, among the 253 women, 84% were Canadian born; the majority were married with an even income spread and no or minor concerns about their pregnancy. Similarly, although located in an urban Japanese clinic, the 323 women in Kataoka 2010 were overwhelmingly married (over 90%), around 60% were having their first child and around 80% had post secondary school qualifications, with 42% having college graduate or postgraduate qualifications.

In contrast, Humphreys 2011 described only those 50/410 pregnant women who were identified in screening conducted in the five San Francisco bay antenatal clinics and their profile is consistent with disadvantage. These 50 women were ethnically diverse: 17 were Hispanic, 11 black or African-American, 15 white and seven from other backgrounds. Twenty-three had never married and 29/50 had only high school education or less. The mean age was 28 years and 38 women had been previously pregnant. Women's mean gestational age was 20 weeks and 14 had smoked tobacco in the past 30 days. Forty-three had been abused in the year before pregnancy and 19 since pregnancy. Twelve had been abused one to three times; four had been abused four to six times and one more than six times (two had missing data for frequency).

Klevens 2012a recruited 126 predominantly disadvantaged black women (78.6%) from diverse women's health clinics (obstetric, gynaecological and family planning) of a Chicago public hospital. The women had a mean age of 35.8 years, with either high school education or less (42.4%) or vocational/college (41.9%); were uninsured (57.1%) or had Medicaid (37.3%).

Women in ED settings only (Rhodes 2002 , Rhodes 2006; Trautman 2007; Koziol-McLain 2010) were recruited from urban hospitals with ethnically diverse populations. These women tended to be older. In the New Zealand study (Koziol-McLain 2010), 37.6% of 399 women were Maori, their median age was 40 years; women's incomes were evenly spread but tended to be in a low income bracket. Just under half (45.6%) had completed a post-school qualification other than a university degree (8.3%). About 67.4% currently had partners and 64.9% were from the main urban area. In a Baltimore Level 1 trauma hospital, the 411 women in Trautman 2007 were overwhelmingly 'non-white' (83.9%); 41% were aged 35 to 54 years; the majority (50.9%) had children at home; 34.8% were on Medicaid insurance; and, while 42.3% were high school graduates, 30.5% had not graduated from high school; and 42.4% had an income in the lowest quintile. Around one-half had physical and mental health summary scores one or two SDs below norms. The 323 women recruited in Rhodes 2002 had similar characteristics to the urban women in Rhodes 2006. 1281 women in Rhodes 2006 were very diverse according to whether they were recruited in an urban or suburban ED setting. In the urban ED, 86% of 883 women were African-American (90% in 2002); had a mean age of 32 years (37 years in 2002); 35% had a high-school diploma or less, and 38% qualifications after high school, but 53% had an income in the lowest quartile; 46% relied on Medicaid (39% in 2002); and 51% were single (59% in 2002). By contrast, in the suburban ED clinic, the median age of the 398 women was 36 years; 80% were white; 71% had post high-school qualifications; the income spread was more even; 65% had private insurance, and 43% were married and only 31% single.

Ahmad 2009 was the only study to be based solely in a family practice clinic affiliated with an urban academic hospital in Toronto, Canada. The mean age of the 293 women was 44 years; 34.5% of women were born outside Canada; over half were married with 29% having children under 15 years of age living at home. Two-thirds were employed full or part time with an even spread of income, although just under one-third were in the lowest quintile.

MacMillan 2006 recruited 2461 women from mixed settings: two family practices, two EDs and two women's health clinics. Their mean age was 37.1 years; 87% were born in Canada; 55% were married; 46.6% had children at home; 52.2% were educated for more than 14 years; 46.9% were working full or part-time, and 17.6% had incomes in the lowest quintile.

In the MacMillan 2009 study, 6743 women were also recruited from mixed settings: 12 primary care clinics, 11 EDs and three obstetric/gynaecology clinics. Characteristics were only described for the 411 women retained and 296 women lost to follow-up (LTFU) since recruitment, but show a clear trend to greater abuse and disadvantage among those LTFU compared with those retained. The mean age of those retained was 34 while those LTFU was 32. While 37% of those retained had never married, 46% of LTFU had not married. Of those retained, 6.5% were pregnant compared with 9% of LTFU. Mean scores on the CAS were higher in the LTFU group (34.8) than those retained (26.5).

Screening intervention methods
Screening tools

Screening tested in these studies was very heterogeneous in both method and screening tools utilised. While the majority tested a range of IPV-specific validated screening tools, some studies used more than one tool, often comparing one with the other, but studies were only included where the results of only one method were notified to the clinician. The tools used were: Woman Abuse Screening Tool (WAST) (MacMillan 2006; MacMillan 2009); Abuse Assessment Screen (AAS) (Rhodes 2006; Ahmad 2009; Koziol-McLain 2010; Humphreys 2011); Partner Violence Screen (PVS) (MacMillan 2006; Trautman 2007; Ahmad 2009; Koziol-McLain 2010; Klevens 2012a); Violence Against Women Screen (VAWS) (Kataoka 2010) and the CAS (MacMillan 2009). Rhodes 2002 adapted questions from the AAS and PVS and others. In several cases, omnibus screening aimed to assess a range of psychosocial problems, among which IPV was only one, for example, Ahmad 2009 and Humphreys 2011, either to assess a range of health issues in pregnancy or to diminish stigma around the true purpose of the study. In Carroll 2005, the Antenatal Psychosocial Health Assessment (ALPHA) tool assessed a range of psychosocial issues, for example, child abuse and depression, but based the IPV questions on the WAST (Carroll 2005). The validity of these tools is also heterogeneous and thoroughly reviewed in Feder 2009 (p. 29).

Screening method

The majority of included studies opted for a computer-assisted self-completion screening process with positive results being conveyed to providers (MacMillan 2006; Rhodes 2002 , Rhodes 2006; Trautman 2007; Ahmad 2009; Humphreys 2011). Written self-completion was the method in MacMillan 2006 and MacMillan 2009. Carroll 2005, MacMillan 2006, Kataoka 2010 and Koziol-McLain 2010 included face-to-face screening. Kataoka 2010 selected written enquiry method as the comparison compared with face-to-face screening, but since it was the face-to-face method that guaranteed the result was processed by a healthcare professional, in the Kataoka study we treated face-to-face screening as the intervention. Klevens 2012a compared health professional screening with audio computer-assisted self-interviews (A-CASI) screening.

Comparisons

Six studies (Carroll 2005; Rhodes 2002; Rhodes 2006; Ahmad 2009; MacMillan 2009; Koziol-McLain 2010) compared IPV screening with usual care. Humphreys 2011 compared IPV screening and clinician follow-up, with researcher-based IPV screening where results were not provided to the clinician. MacMillan 2006 compared face-to-face IPV screening where the clinician could follow up with women, against other IPV research-focused screening where the screening was not passed on to clinicians. Trautman 2007 compared screening that included questions about IPV, with screening for other issues that did not include IPV, and both sets of results were passed on to clinicians. Kataoka 2010 compared face-to-face screening interview by a healthcare professional with a self-administered questionnaire and Klevens 2012a compared A-CASI screening with the same screen administered by the clinician. We treated researcher-only screening (for example, self-completion) where clinicians were not informed of screening outcomes, or screening where IPV was not included, as 'usual care'.

Outcomes and outcome measures
Identification (including discussion or detection)

Identification was a primary outcome for Carroll 2005, Rhodes 2002 , Rhodes 2006, MacMillan 2006, Trautman 2007, Ahmad 2009, Kataoka 2010, Humphreys 2011 and Klevens 2012a.

Referral

Trautman 2007 measured the proportions screened, identified and referred. Klevens 2012a measured three types of referral - healthcare professional, A-CASI plus provider support and A-CASI alone. Ahmad 2009 also measured referrals but as a secondary outcome.

Women's health and quality of life

For Koziol-McLain 2010 and MacMillan 2009, level of exposure to IPV (using the CAS, Hegarty 2005) was a primary outcome.

MacMillan 2009 measured quality of life (World Health Organization Quality of Life (WHOQOL)-Bref) as a primary outcome, but included in their secondary outcomes general health (Short Form (SF)-12), depressive symptoms (Center for Epidemiologic Studies Depression Scale (CES-D)), post-traumatic stress (Startle, Physiological arousal, Anger, and Numbness (SPAN)) and alcohol use or dependency (Tolerance, Worried, Eye-opener, Amnesia, K/Cut Down (TWEAK) and Drug Abuse Screening Test (DAST)).

Other outcomes

Ahmad 2009 included advice for follow-up, patient comfort with screening and need to consult with the nurse after screening. Carroll 2005, MacMillan 2006, Kataoka 2010 and Klevens 2012a measured comfort, preference for mode or satisfaction with the screening process.

Koziol-McLain 2010 measured safety behaviours and resource use.

Rhodes 2006 measured provision of domestic violence services and Trautman 2007 and Klevens 2012a measured services usage rates.

Excluded studies

Thirty-four studies were excluded for the following reasons. Nine (Duggan 2004; Green 2005; Curry 2006; Jewkes 2008; Gillum 2009; Cripe 2010; Kiely 2010; Tiwari 2010; Florsheim 2011) were excluded as the screening was accompanied by an intervention that exceeded criteria for a 'brief intervention' (see altered screening criteria in 'Types of interventions'). Seven (Furbee 1998; Larkin 1999; Knight 2000; Bonds 2006; Halpern 2009; Hewitt 2011; Kapur 2011) did not meet criteria as randomised or quasi-randomised trials. In four studies (Coonrod 2000; Brienza 2005; Fernandez-Alonso 2006; Garg 2007), data on women were not provided or could not be separated out. In Chen 2007, Ernst 2007 and Rickert 2009 there was no usual care comparison, while in Hollander 2001, screening results were passed on to the healthcare professional in both the usual care as well as the intervention group. Campbell 2001, Thompson 2000 and Feder 2011 were case-finding not screening trials. Robinson-Whelan 2010 was not conducted in a healthcare setting. Three studies (Dubowitz 2011; Feigelman 2011; Dubowitz 2012) were excluded as they were targeted at children and clinicians. Three studies (Bair-Merritt 2006; Houry 2011; Klevens 2012b) were excluded as the results were not passed on to the healthcare professional according to our criteria. We will reconsider this criterion in the next update of this review.

Risk of bias in included studies

Four studies (MacMillan 2006; Kataoka 2010; Koziol-McLain 2010; Klevens 2012a) scored 'low risk' on four risk of bias criteria and two (Ahmad 2009; MacMillan 2009) scored 'low risk' on three risk of bias criteria. Summaries are included in Figure 2 and Figure 3. Judgements are summarised here and explained in the 'Risk of bias' tables below.

Figure 2.

Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies

Figure 3.

Risk of bias summary: review authors' judgements about each risk of bias item for each included study

Allocation

Random sequence generation

Nine studies described reliable low-risk random sampling strategies, but two used methods with a high likelihood of systematic bias. (Trautman 2007) used consecutive enrolment periods and Rhodes 2002 used alternate allocation.

Allocation concealment

Rhodes 2006, Ahmad 2009, Koziol-McLain 2010, Humphreys 2011 and Klevens 2012a described reliable procedures to conceal the allocation of participant status. In Carroll 2005 and Rhodes 2002, there was inadequate information to judge whether or not bias could have been introduced. In MacMillan 2006 and MacMillan 2009, monthly calendars showing shift allocation for site co-ordinators was the chosen method. Recruiters with knowledge of this allocation could have introduced bias with selective recruitment. A process with similar potential for bias was used in Trautman 2007, while Kataoka 2010 did not indicate whether the sealed envelopes used were opaque.

Blinding

Blinding of participants and personnel (performance bias)

It is very difficult to blind healthcare professionals in a screening trial, especially when computer screening results are attached to the patients' files. In Kataoka 2010, we judged that it was unclear whether bias could have affected outcomes, however we judged that it may have introduced bias in Rhodes 2002, as there was alternate allocation and physicians may have seen patients alternately with and without screening results. Stated protocols to minimise performance bias (Koziol-McLain 2010) and blinding clinicians to the overall purpose of the study (Ahmad 2009) were stated strategies to minimise this possibility, but similar to the remaining studies, knowledge that they were in a trial and patients' screening results attached to their files increased the possibility of performance bias.

Blinding of outcome assessment (detection bias)

Detection bias was judged to be low in Ahmad 2009, MacMillan 2009, Kataoka 2010; Rhodes 2002 and Koziol-McLain 2010, and unclear in Rhodes 2006 and Trautman 2007. Healthcare professionals aware of participant IPV status gave estimates of their levels of concern in Carroll 2005 and may have overestimated their levels of concern. In Humphreys 2011 and Klevens 2012a, research staff collecting outcome data may have been able to detect which study arm the woman was in (as there was no indication they were blinded) and this may have biased outcome detection.

Incomplete outcome data

Kataoka 2010 had no more than 10% loss to follow-up (LTFU) across both intervention and control groups and MacMillan 2006 had approximately 5% depending on the screening tool used. These and Klevens 2012a were judged to be low risk of bias from LTFU. Although Trautman 2007 attained 100% retention as data were collected immediately, it is unclear how missing data within variables were dealt with, and Humphreys 2011, while making conservative assumptions about missing data, also did not give the reasons for attrition, making it difficult to judge whether the assumption was appropriate. Koziol-McLain 2010 reported 13.8% LTFU missing at random but no LTFU reasons are given making it difficult to judge. In Ahmad 2009, LTFU was also low, but sensitivity analyses suggest missing data potentially affected the results and imputation in an intention-to-treat analysis confirmed this. Unbalanced provider attrition (nine in intervention group versus three in control group) in Carroll 2005 risks bias, even though participant data loss was low and evenly spread (7.5%). The study conducted by MacMillan 2009 resulted in 42% attrition overall with participants missing not at random (more severely abused women likely to be lost) suggesting the observed effect may be biased. Multiple imputation in MacMillan 2009 for missing data did reduce the effect size. Rhodes 2002 gave an inadequate account of reasons for the 20% missing chart reviews and the 32% patient attrition and 21% providers refusing recording probably biased the effects found in Rhodes 2006.

Selective reporting

Publication of protocols and trial registration reduces the risk of selective reporting. MacMillan 2006, Ahmad 2009 and MacMillan 2009 were the only registered trials in the selected studies, but analysis and primary outcomes are difficult to access once the trial is closed. No protocols have been published for these trials. MacMillan 2006, MacMillan 2009 , Rhodes 2002 and Kataoka 2010 are the trials considered low risk. Carroll 2005 and Rhodes 2006 are considered high risk and the remainder unclear.

Other potential sources of bias

We judged the potential for contamination was high in Rhodes 2006, Trautman 2007, Ahmad 2009, MacMillan 2009, Humphreys 2011 and Klevens 2012a and low in Koziol-McLain 2010. A high proportion (21.5% compared to 15.7%) of low-income women in the computer group may have biased screening results in MacMillan 2006, and Kataoka 2010 acknowledges her measurement had psychometric property limitations with low specificity.

Effects of interventions

See: Summary of findings for the main comparison

Screening versus control (no screening; clinician not notified of screening results; screening for other purposes)

Primary outcomes
A. Identification of abused women by health professionals

Only six studies measured identification of female patients experiencing IPV in ways that could be combined (Carroll 2005; Rhodes 2002, Rhodes 2006; Trautman 2007; Ahmad 2009; Humphreys 2011). We have made conservative assumptions about identification in three cases. In Ahmad 2009, we have taken cases as detected, rather than the broader 'discussion opportunity' as the measure of identification. In Trautman 2007, we were not able to distinguish identification by healthcare professionals from those detected by research staff in the study report, and therefore only included numbers of cases documented in patient records, as these are entered by healthcare professionals only. In Rhodes 2002, we have only included those detected by chart review. We confirmed our calculations of the women included in the study with the author.

From the six studies that we were able to pool, there is evidence that screening increases health professional identification of women experiencing abuse by 103% (RR 2.33; 95% CI 1.40 to 3.89; Analysis 1.1) compared to usual care.

Subgroup analyses

Type of healthcare setting - antenatal clinics

Two studies tested screening in antenatal settings (Carroll 2005; Humphreys 2011). The RR for screening to identify victims of abuse compared to no screening is 4.26 (95% CI 1.76 to 10.31; Analysis 1.2). In this setting, we have estimated there could be an over 300% likelihood of increased identification by healthcare professionals in screened pregnant populations, although we are cautious about this inference as the CIs are wide.

Type of healthcare setting - emergency departments (EDs)

Three studies (Rhodes 2002, Rhodes 2006; Trautman 2007) evaluated identification from screening in ED settings. In this setting the RR was 2.61 (95% CI 1.01 to 6.71, Analysis 1.2). In assuming the more conservative estimate of cases identified in the medical records for the Trautman 2007 study, we found evidence that screening in EDs offered a 161% greater likelihood of health professionals identifying women experiencing IPV.

While the effect size is larger in antenatal settings, as the CIs overlap, there appears to be no significant difference between the antenatal and emergency care settings.

Individual studies

We were unable to include MacMillan 2006, MacMillan 2009 and Klevens 2012a in the meta-analyses. MacMillan 2006 reported proportions by healthcare setting and by screening method. The highest proportions were identified in the emergency departments (n = 768), ranging from 10.9% to 17.7%, by computerised methods (16.9% (WAST) to 17.7% (PVS)). In family practices (n = 814), proportions ranged from 5.4% to 11.6% and the most effective method was face-to-face (11.6% WAST to 9.0 PVS). Women's health clinics (n = 879) reported the lowest prevalence from 4.1% (PVS) to 10.0% (WAST). While MacMillan 2009 did not specify identification as a primary outcome, we could estimate figures using the reported proportions of women who discussed IPV with their clinicians who had been given their screening outcomes (44% (88/199) screened compared with 8% (17/212) unscreened); however, the denominator was only women identified who had already screened positive, rather than all women attending. In Klevens 2012a, healthcare professionals identified only 4/46 (8%) compared with the 17/80 (21.3%) women attending who were screened using the A-CASI. In most cases the actual numbers and proportions of women identified are small.

B. Information-giving and referral to support agencies by health professionals and take-up by female participants

Only Klevens 2012a measured information-giving specifically. Clinician information-giving had greater effect than computer information among participants in this study. After one week, 14/36 (38.9%) women given a list of referrals by their clinician shared it with someone compared with 11/34 (34.4%) of A-CASI referred with clinician support and 5/32 (16.7%) of A-CASI referred and video support. Of these groups, 4/36 (11.1%) of clinician referred used the list to contact services compared with 1/34 (3.1%) of A-CASI and clinician and 1/32 (3.3%) of A-CASI and video referred.

Safety planning and safety behaviours after planning

We consider that when clinicians discuss safety with abused women, this is a form of information-giving. In descriptive reporting of physicians assessing patient safety following identification, only Ahmad 2009 assessed this outcome and confirmed that physicians discussed safety with nine women of 25 detected in the screened group and with only one woman in the comparison group.

The following outcomes are all in the desired direction but are not significant at the traditional 95% CI.

Koziol-McLain 2010 assessed whether women reported using more safety behaviours in the screened versus comparison group and they report an OR of 1.41 (CI 0.71 to 2.81), suggesting a 41% increased likelihood but the CIs crossed the line of no effect, suggesting no significant difference between groups.

Health professional referrals and follow-up

Two studies could be included in our investigation of health professional referrals (Trautman 2007; Ahmad 2009) (Analysis 1.3). In the case of Trautman 2007, we only included cases verified by medical records, which may be an underestimate. While the pooled effect (RR 2.23; 95% CI 0.64 to 7.73) is in favour of the screening programme increasing referrals to supportive services in hospital or the community, the numbers of women actually referred are very low and the CIs at 95% cross the line of no effect.

In a descriptive account, Ahmad 2009 reported that of the 25 women identified as abused in the screened group, 20 (80%) were asked for follow-up appointments in the intervention arm, whereas only eight (67%) of the 12 identified in the comparison arm were invited for follow-up appointments. In Klevens 2012a, despite the follow-up by clinician informed compared with A-CASI informed, no women in any of the three groups contacted the domestic violence advocacy programme in the hospital, but the study was unable to investigate the reasons.

Secondary outcomes
C. Reduction in intimate partner violence

Two studies measured the effect of screening on reduction of IPV among screened compared to unscreened women and used the same measure (CAS) (MacMillan 2009; Koziol-McLain 2010). Unfortunately, the denominators and timelines were different. Koziol-McLain 2010 measured IPV reduction at three months post baseline among all women. MacMillan 2009 measured reduction of IPV among abused women at six, 12 and 18 months following screening. We have therefore presented their results separately. What is notable is the similarity of non-effect. At three months in New Zealand, Koziol-McLain 2010 found an adjusted OR of 0.86 (95% CI 0.39 to 1.92), denoting no significant effect at the 5% level. The same is true in MacMillan 2009 at six months (OR 0.93; 95% CI 0.61 to 1.41), 12 months (OR 0.90; 95% CI 0.50 to 1.63) and 18 months (OR 0.88; 95% CI 0.43 to 1.82).

D. Women's perceived and diagnosed physical health outcomes

Only one study (MacMillan 2009) measured any difference in physical health (SF-12) after screening. At each of six, 12 and 18 months, the effect favours those who received screening, with increases at each time point, but at 18 months, the effect size (OR 1.20; 95% CI -1.29 to 3.69) denotes no significant effect at the 5% level.

E. Women's psychosocial health

The same study (MacMillan 2009) is the only one to have measured our other secondary outcomes in the important area of psychosocial health. While the study authors have measured all factors (quality of life, post-traumatic stress, alcohol problem, drug problem, depression and mental health in general) at each time point, we only report those at 18 months, which was the study's final measurement point. We cite the imputed and more conservative figures. The study suffered considerable attrition; however, while the complete case effect sizes are greater than those imputed in the published paper, the imputation method (requested from the author) assumed missing at random and those LTFU had higher scores on the CAS, which suggests a potential underestimation of effect.

  • Quality of life (WHOQOL-Bref) - for this measure, a primary outcome in MacMillan 2009, while there is a suggested improvement in a mean difference in the WHO Quality of Life Scale of 2.29 (95% CI -1.71 to 6.28) among screened versus unscreened abused women, the results cross the traditional line of no effect.

  • PTSD - this measure suggests a reduction but does not reach traditional statistical significance (OR 0.63; 95% CI 0.36 to 1.10).

  • Alcohol problems - there is no evidence that screening reduces the risk of alcohol problems (OR 1.23; 95% CI 0.62 to 2.44).

  • Drug problems - there is no evidence that screening has any impact on the risk of reducing drug problems (OR 0.83; 95% CI 0.41 to 1.71).

  • Depression - the observed figures found a mean difference of -2.32 (95% CI -4.61 to -0.03) among screened versus unscreened abused women reducing to -1.97 (95% CI -4.33 to 0.39) with imputation for LTFU.

  • Mental health (SF-12) - screening does not significantly improve the mental health of screened, abused women as the mean improvement in SF-12 scores of 1.05 (95% CI -1.70 to 3.79) crosses the line of no significance in both observed and imputed analyses.

F. Occurrence of adverse outcomes

Only one study (MacMillan 2009) included a specially developed measure of adverse outcomes. Within the Consequences of Screening Tool (COST) questions, which included satisfaction with care, eight questions related to possible harm were scaled from 2 to -2 (range +16 to -16), where a negative score reflects harm. This was measured among 591 women - a subset of women interviewed at baseline comprising 227 women who screened positive for abuse, 206 with mixed screen results and 158 who screened negative. The mean score of 3.52 (SD 3.24) supports the view that there was very little impact of screening and it was not negative. There was little variation either when measured by abuse group, the scores were 3.7 (SD 3.2) for women who scored negative on both WAST and CAS measures, 3.3 (SD 3.3) for those who had mixed results and 3.5 (SD 3.4) for those positive on both measures.

G. Take-up of services and resource use

Rhodes 2006 assessed the receipt of services by those identified in the screened versus usual care group in separate groups of urban and suburban women. Of screened urban women, 21/262 received services compared to 10/275 unscreened and among suburban screened women 4/159 received services compared to 0/171 unscreened. Trautman 2007 found that in the usual care group, 2/194 women who were screened received social work IPV assistance whereas 18/411 screened women were assisted.

H. Cost-benefit measures

We found no studies that reported any cost-benefit measures or any other economic evaluation of interventions.

Discussion

Summary of main results

We identified 11 controlled studies that recruited 13,027 women. Studies were diverse in healthcare settings (emergency clinics, antenatal or women's health clinics, primary care centres). They were conducted in predominantly high-income countries and in urban and rural settings. These were countries with domestic violence legislation and developed support services to which healthcare professionals could refer. Follow-up periods also varied from immediate to one, three, six, 12 and 18 months. The screening strategies employed were mostly computer or paper based rather than face-to-face screening methods, and used a range of screening tools (MacMillan 2006). Ten of 11 studies did not discuss the implications of non-disclosure or false measurement on the outcomes. There was variable description provided about the wider organisational contexts and how healthcare professionals were trained and supported to undertake screening. The evaluation of screening in healthcare settings is that of a complex intervention in a complex context, and an optimal evaluation may require multidisciplinary methods to illuminate the reasons for any successes or failures (Spangaro 2009; May 2011). Globally, the barriers to screening by healthcare professionals may reside at the individual professional level (lack of training and resources, unfavourable attitudes to the problem), at the clinic or team level (lack of systems for safety and links with referral agencies) or at the wider political level (violence tolerant societies, other healthcare priorities for funding and services, such as lack of funding for law enforcement or domestic violence services) (Colombini 2008). This understanding of an intervention was not adequately acknowledged in the included studies and is often overlooked in trial reporting. Very few conduct or report on process evaluation.

In surveys and qualitative studies, women report that screening for IPV is acceptable (Koziol-McLain 2008), although this can vary according to their abuse status. Although some governments and healthcare policymakers are in favour, the majority of healthcare professionals are not as supportive, and many barriers to screening have been identified (Hegarty 2006; Feder 2009). This reluctance is borne out by the findings in this review where, even though identification increases, the actual numbers of women identified are modest in comparison to the numbers of women screened and the likely prevalence of partner violence. Evidence supporting beneficial follow-on effects of referral and outcomes for women is negligible.

Does screening for intimate partner violence increase identification of victims?

Based on the studies in this review, there appears to be clear evidence that screening in high-income countries with developed referral services increases victim identification rates compared to usual care. However, the numbers and proportions of women are modest when considered against the estimated prevalence in healthcare settings. While mindful of the possibility of bias in some studies, and the fact that there are only 11 studies, the evidence from this review suggests that screening in antenatal settings may be effective. Further rigorous studies need to be undertaken to confirm this finding in this setting. A gap in the identified studies is that only one report (Wathen 2008) associated with the MacMillan 2006 study directly addressed the issue of how false positives and false negatives are managed and their impact on women and on screening effectiveness.

What kind of screening technique is preferred in the identification of abused women?

Studies outlined in the introduction indicated that women prefer, and are more comfortable with, less direct methods of screening, not, for example, face to face. However, while one high-quality study found fewer women were identified with face-to-face screening compared with computer-based screening (Kataoka 2010); another found that greater identification was influenced by the use of different screening tools (MacMillan 2006), settings and methods. An interesting development of computer-only screening and referral described in Klevens 2012b found no evidence of effect.

Does screening increase referral to support services?

There is little evidence that screening increases referrals to support services and one study involved is at high risk of bias. Compared with the numbers identified, the absolute numbers of referrals were small in the two studies that examined it and the findings not significant. Evidence of the effect of screening on referrals is therefore inconclusive. However, women may not yet be ready to take up a referral at the time of immediate disclosure and alternative outcomes, such as safety-planning or safety behaviours, may be more appropriate measures (Wathen 2012). We also need further evidence for the effect of screening on healthcare professionals' assessment of women's safety, offer of follow-up appointments and women's subsequent service use.

Does screening reduce intimate partner violence?

The two studies that have measured the impact of screening on a reduction of partner violence over time provided no evidence that it can reduce abuse without any further intervention. This result is unsurprising and further work is necessary to evaluate the effectiveness of screening linked with advocacy (Ramsay 2009b), social support (Taft 2011) or healthcare professional intervention (Hegarty 2010).

Is screening beneficial for women's psychosocial health?

Only one study measured this and the findings were inconclusive, with marginal effects on depression, but no evidence of effects on PTSD, quality of life or mental wellbeing (MacMillan 2009). These data were open to some bias and further studies are needed to validate them.

Does screening harm women?

One of the criticisms commonly raised against the implementation of screening is that we do not know whether it is harmful or not (Jewkes 2002). The first screening trial to assess this outcome (MacMillan 2009) appears to have found no evidence of harm. Further research on the potential harms of screening is still needed.

Overall completeness and applicability of evidence

The studies in this review are all from high-income countries and the conclusions cannot be generalised to medium- and low-resource settings, where there may not be support services to which healthcare professionals can refer. There is a need for studies that can investigate the differential impact of screening on women experiencing different levels of severity or different types of abuse. Given the costs to healthcare systems to provide support for sustainable and effective screening programmes, it would be helpful to have studies that compared screening to case finding strategies (such as Feder 2011) including economic analyses. Nevertheless, there are sufficient studies to suggest that screening is effective in raising identification rates; however, a significant limitation of all the identified studies is the failure to adequately examine the ethics and effects of false identification. This evidence is important. Both the proportions of women choosing not to disclose and the impact of false identification on women's lives need further investigation before we can understand the effectiveness of screening fully.

There is insufficient evidence that screening increases rates of referrals. From the available evidence, screening alone does not reduce violence. However, we need more studies to estimate the risk of harm and the benefit to women's longer-term physical and psychosocial health. While the increased rate of identification from screening is encouraging, it is unclear whether the healthcare professionals would continue to screen if they are not part of a study and for how long. The question of sustainability of screening or other healthcare behaviour change interventions is a vexed one and calls for greater understanding if we hope to implement such programmes at a state or national level effectively (Colombini 2008; May 2011).

Quality of the evidence

Only four studies were assessed as being at low risk of bias for four of the seven domains. One further study was at low risk of bias for three out of seven criteria (< 50%) and the remaining six were at generally high risk of bias. In the case of one specific criterion, that of the blinding of randomisation status, this is virtually impossible for the clinicians and for the participants if they give informed consent in screening trials in healthcare settings.

As we stated previously, understanding the context of a complex intervention such as screening requires better theoretical underpinning. It also requires detailing (in process evaluation and protocol articles) the steps leading to the establishment and implementation of a screening programme to be tested, so that those wishing to replicate a given study are able to understand the full scale of what is required. If not included in the peer-reviewed publication itself, this information should be available via a web link.

Potential biases in the review process

We believe that all of the published randomised or quasi-randomised trials of screening interventions as defined in the review and published until the most recent search date were identified by the review process. All of the authors included in the review and other experts in the field responded to our request for knowledge of other trials we may have missed, but they did not identify any further missed trials. We also scoured all trial databases for those that may have been about to be published. Decisions about inclusion or exclusion of studies were made by two review authors and any changes to the protocol made with all authors' involvement. Assessment of study quality was also made by two review authors independently. We requested additional data from four author groups and three authors responded to these requests.

Agreements and disagreements with other studies or reviews

This review reinforces the findings of other major systematic reviews, especially those conducted by national governments (Wathen 2003; US Preventive Services Taskforce 2004; Feder 2009) to inform policy and programmes, that insufficient evidence exists to justify screening for IPV in healthcare settings on the basis of demonstrated benefit to women. We do not agree with the Nelson 2012 review, which concluded, mainly from MacMillan 2009, that screening is effective, as the evidence does not yet warrant this conclusion. The earlier reviews of screening for IPV found no evidence of benefit to women and no evidence that it does not harm, despite evidence that it may increase identification and referral. By conducting more recent searches and combining the results of those few studies where it was feasible to do so, this review has extended the evidence provided to examine longer-term follow-up of effects on women's health, limited evidence that screening is not harmful and confirmation of the modest effects of screening on increasing identification.

Authors' conclusions

Implications for practice

As present, our conclusions are that there is insufficient evidence to justify the use of screening for women in healthcare settings. This review cannot, however, reach any conclusions about the benefit of screening combined with advocacy or other interventions by healthcare professionals. Further trials would be required to test this hypothesis.

Implications for research

Much further research is required to extend the limited evidence identified in this review. More studies that examine the complexities of screening in diverse settings, with diverse populations and that examine what the social or economic benefits are for the differing strategies of screening versus case-finding are also necessary. We need further studies of what proportion of women are successfully screened in pragmatic settings and over what period that can be sustained. The question of which subgroups of women, at which stage of their journeys, may benefit from screening programmes also remains.

Acknowledgements

The authors acknowledge with thanks the support of the Australasian Cochrane Centre for training and support; the Cochrane Developmental, Psychosocial and Learning Problems Group for their support and assistance with searches, and La Trobe University and Cochrane Collaboration for funding support.

Data and analyses

Download statistical data

Comparison 1. Universal screening for IPV versus control
Outcome or subgroup titleNo. of studiesNo. of participantsStatistical methodEffect size
1 Identification of abused women63564Risk Ratio (M-H, Random, 95% CI)2.33 [1.39, 3.89]
2 Identification of abused women by location (subgroup analysis 2)63564Risk Ratio (M-H, Random, 95% CI)2.33 [1.39, 3.89]
2.1 Hospital primary care1293Risk Ratio (M-H, Random, 95% CI)1.44 [0.82, 2.52]
2.2 Antenatal2663Risk Ratio (M-H, Random, 95% CI)4.26 [1.76, 10.31]
2.3 Emergency32608Risk Ratio (M-H, Random, 95% CI)2.61 [1.01, 6.71]
3 Referrals31400Risk Ratio (M-H, Random, 95% CI)2.67 [0.99, 7.20]
Analysis 1.1.

Comparison 1 Universal screening for IPV versus control, Outcome 1 Identification of abused women.

Analysis 1.2.

Comparison 1 Universal screening for IPV versus control, Outcome 2 Identification of abused women by location (subgroup analysis 2).

Analysis 1.3.

Comparison 1 Universal screening for IPV versus control, Outcome 3 Referrals.

Appendices

Appendix 1. Search strategies

Cochrane Central Register of Controlled Trials (CENTRAL), last searched 5 July 2012

#1 MeSH descriptor Battered Women explode all trees
#2 MeSH descriptor Domestic Violence, this term only
#3 MeSH descriptor Spouse Abuse, this term only
#4 abuse* near/3 wom*n
#5 abuse* near/3 spous*
#6 abuse* near/3 partner*
#7 wife near/3 abuse*
#8 wives near/3 abuse*
#9 wife near/3 batter*
#10 wives near/3 batter*
#11 partner* near/3 violen*
#12 spous* near/3 violen*
#13 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8 OR #9 OR #10 OR #11 OR #12)
#14 MeSH descriptor Mass Screening, this term only
#15 screen*
#16 identif*
#17 routine* near/3 ask*
#18 routine* near/3 question*
#19 detect*
#20 (#14 OR #15 OR #16 OR #17 OR #18 OR #19)
#21 MeSH descriptor Women explode all trees
#22 MeSH descriptor Adolescent explode all trees
#23 wom*n or female*
#24 adolescen*
#25 teen*
#26 (#21 OR #22 OR #23 OR #24 OR #25)
#27 (#13 AND #20 AND #26)

Ovid MEDLINE(R), last searched 5 July 2012
1 Battered Women/
2 Domestic Violence/
3 Spouse Abuse/
4 (abuse$ adj3 wom#n).tw.
5 (abuse$ adj3 spous$).tw.
6 (abuse$ adj3 partner$).tw.
7 ((wife or wives) adj3 abuse$).tw.
8 ((wife or wives) adj3 batter$).tw.
9 (partner$ adj3 violen$).tw.
10 (spous$ adj3 violen$).tw.
11 or/1-10
12 Mass Screening/
13 screen$.tw.
14 identif$.tw.
15 detect$.tw.
16 (routine$ adj3 (ask$ or question$)).tw.
17 or/12-16
18 exp Women/
19 Adolescent/
20 (wom#n or female$).tw.
21 adolescen$.tw.
22 teen$.tw.
23 or/18-22
24 11 and 17 and 23

Ovid MEDLINE(R) In-Process and Other Non-Indexed Citations, last searched 5 July 2012
1 (abuse$ adj3 wom#n).tw.
2 (abuse$ adj3 spous$).tw.
3 (abuse$ adj3 partner$).tw.
4 ((wife or wives) adj3 abuse$).tw.
5 ((wife or wives) adj3 batter$).tw.
6 (partner$ adj3 violen$).tw.
7 (spous$ adj3 violen$).tw.
8 or/1-7
9 screen$.tw.
10 identif$.tw.
11 (routine$ adj3 (ask$ or question$)).tw.
12 detect$.tw.
13 or/9-12
14 (wom#n or female$).tw.
15 adolescen$.tw.
16 teen$.tw.
17 or/14-16
18 8 and 13 and 17

EMBASE (Ovid), last searched 5 July 2012
1 Battered Women/
2 Domestic Violence/
3 Spouse Abuse/
4 (abuse$ adj3 wom#n).tw.
5 (abuse$ adj3 spous$).tw.
6 (abuse$ adj3 partner$).tw.
7 ((wife or wives) adj3 abuse$).tw.
8 ((wife or wives) adj3 batter$).tw.
9 (partner$ adj3 violen$).tw.
10 (spous$ adj3 violen$).tw.
11 or/1-10
12 Mass Screening/
13 screen$.tw.
14 identif$.tw.
15 (routine$ adj3 (ask$ or question$)).tw.
16 detect$.tw.
17 or/12-16
18 exp Women/
19 Adolescent/
20 (wom#n or female$).tw.
21 adolescen$.tw.
22 teen$.tw.
23 or/18-22
24 11 and 17 and 23

CINAHL Plus (EBSCOhost), last searched 5 July 2012
S24 S17 and S23
S23 S18 or S19 or S20 or S21 or S22
S22 adolescen* or teen*
S21 AG adolescent
S20 women or woman or female*
S19 (MH "Women+")
S18 (MH "Female")
S17 S9 and S16
S16 S10 or S11 or S12 or S13 or S14 or S15
S15 (MH "Health Screening")
S14 identif*
S13 MH "Experimental Studies"
S12 detect*
S11 (routin* N3 ask*) or (routin* N3 question*)
S10 screen*
S9 S1 or S2 or S3 or S4 or S5 or S6 or S7 or S8
S8 (partner* N3 violen*) or (spouse* N3 violen*)
S7 (wife N3 batter*) or (wives N3 batter*)
S6 abuse* N3 spouse*
S5 abuse* N3 partner*
S4 abuse* N3 wom?n
S3 MH "Intimate Partner Violence"
S2 MH "Domestic Violence"
S1 MH "Battered Women"

PsycINFO (Ovid), last searched 5 July 2012
1 Battered Women/ (2689)
2 Domestic Violence/ (7821)
3 Spouse Abuse/ (4154)
4 (abuse$ adj3 wom#n).tw. (2995)
5 (abuse$ adj3 spous$).tw. (908)
6 (abuse$ adj3 partner$).tw. (1266)
7 ((wife or wives) adj3 abuse$).tw. (570)
8 ((wife or wives) adj3 batter$).tw. (316)
9 (partner$ adj3 violen$).tw. (3626)
10 (spous$ adj3 violen$).tw. (351)
11 or/1-10 (15402)
12 Screening/ (5344)
13 screen$.tw. (48857)
14 identif$.tw. (287698)
15 (routine$ adj3 (ask$ or question$)).tw. (244)
16 detect$.tw. (73953)
17 or/12-16 (383820)
18 exp Women/ (97549)
19 (wom#n or female$).tw. (380933)
20 adolescen$.tw. (157334)
21 teen$.tw. (13531)
22 or/18-21 (535027)
23 11 and 17 and 22 (2087)

ASSIA (CSA), searched up to 2009 only
Query: ((DE="domestic violence") or(DE="battered women") or(abuse* within
3 wom*n) or(abuse* within 3 spous*) or(abuse* within 3 partner*) or((wife
within 3 abuse*) or (wives within3 abuse*)) or((wife within 3 batter*) or
(wives within 3 batter*)) or(partner* within 3 violen*) or(spous* within
3 violen*)) and((screen*) or(identif*) or((routine* within 3 question*)
or (routine* within 3 ask*)) or(detect*)) and((DE="women")
or(DE="adolescents") or(wom*n or female*) or(adolescen*) or(teen*))

Sociological Abstracts (Proquest), last searched 5 July 2012
((SU.EXACT("Females") or SU.EXACT("adolescents") or (wom*n or female*) or (adolescent*or teen*)) AND ((screen*)or (identif*) or ((routine* NEAR/3 question*) or (routine* NEAR/3 ask*)) or (detect*))) AND (SU.EXACT(("Familyviolence")) or SU.EXACT(("Partner Abuse") or ("Battered Women")) or (abuse NEAR/3 wom*n) or (abuse NEAR/3spouse*) or (abuse NEAR/3 partner*) or (wife NEAR/3 abuse*) or (wives NEAR/3 abuse*) or (wife NEAR/3 batter*) or(wives NEAR/3 batter*) or (partner* NEAR/3 violent*) or (spouse* NEAR/3 violent*))

Sociological Abstracts (CSA), searched up to 2009
Query: ((DE="domestic violence") or(DE="battered women") or(abuse* within
3 wom*n) or(abuse* within 3 spous*) or(abuse* within 3 partner*) or((wife
within 3 abuse*) or (wives within3 abuse*)) or((wife within 3 batter*) or
(wives within 3 batter*)) or(partner* within 3 violen*) or(spous* within
3 violen*)) and((screen*) or(identif*) or((routine* within 3 question*)
or (rountine* within 3 ask*)) or(detect*)) and((DE="women")
or(DE="adolescents") or(wom*n or female*) or(adolescen*) or(teen*))

Database of Abstracts of Reviews of Effects (DARE), last searched 5 July 2012
#1 MeSH descriptor Battered Women explode all trees
#2 MeSH descriptor Domestic Violence, this term only
#3 MeSH descriptor Spouse Abuse, this term only
#4 abuse* near/3 wom*n
#5 abuse* near/3 spous*
#6 abuse* near/3 partner*
#7 wife near/3 abuse*
#8 wives near/3 abuse*
#9 wife near/3 batter*
#10 wives near/3 batter*
#11 partner* near/3 violen*
#12 spous* near/3 violen*
#13 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8 OR #9 OR #10 OR #11 OR #12)
#14 MeSH descriptor Mass Screening, this term only
#15 screen*
#16 identif*
#17 routine* near/3 ask*
#18 routine* near/3 question*
#19 detect*
#20 (#14 OR #15 OR #16 OR #17 OR #18 OR #19)
#21 MeSH descriptor Women explode all trees
#22 MeSH descriptor Adolescent explode all trees
#23 wom*n or female*
#24 adolescen*
#25 teen*
#26 (#21 OR #22 OR #23 OR #24 OR #25)
#27 (#13 AND #20 AND #26)

meta Register of Controlled Trials (mRCT), last searched July 2012
Search string: intimate partner violence OR domestic violence

History

Protocol first published: Issue 1, 2008
Review first published: Issue 4, 2013

DateEventDescription
16 September 2008AmendedConverted to new review format.

Contributions of authors

AT originally developed the search strategy together with Liesje Toomey and Jo Abbott, the Trial Search Co-ordinator (TSC) of the Cochrane Developmental, Psychosocial and Learning Problems Group at the time. Jo ran the initial search and the current TSC, Margaret Anderson, updated the searches. LOD and AT selected the studies prior to 2009; AT, LOD and KH selected studies post 2009; LOD and AT extracted the data; AT undertook the analysis with the help of LOD and KH and drafted the review. All authors provided topic expertise and contributed to writing and editing the review.

The review was produced within the Cochrane Developmental, Psychosocial and Learning Problems Group.

Declarations of interest

Angela Taft - has received an Australian Research Council Grant to undertake a screening trial, which may be eligible for inclusion in the published review in future updates.
Lorna O'Doherty - was contracted to La Trobe University by the University of Melbourne to work on this Cochrane Review. She also regularly contributed to the review in her free time. She does not have any competing interest to declare.
Kelsey Hegarty - is currently funded to undertake a randomised controlled trial in the IPV field and to participate in the World Health Organization Guideline Group on health practitioners' response to IPV.
Jean Ramsay - none known.
Gene Feder - none known.
Leslie Davidson - none known.

Sources of support

Internal sources

  • No sources of support supplied

External sources

  • La Trobe University, Australia.

Differences between protocol and review

1. Altered screening criteria

The treating healthcare professional must have been informed of the result of the screening assessment undertaken as described above at the time of the relevant consultation if they did not conduct the screening themselves face-to-face. The 'treatment as usual' arms may therefore include studies where screening for research purposes was undertaken but healthcare professionals were not informed of the screening results and have therefore provided standard treatment. We excluded interventions where the timing of these consultations went beyond an immediate response and referral phase and included further counselling or therapeutic sessions.

2. Secondary outcome added

We added the outcome below as it has bearing on the potential for beneficial support to women at a later date.

G. Services and resource use:
i. family/domestic violence services;
ii. police/legal services;
iii. counselling or therapeutic services;
iv. other services.

3. Search strategy amendment

We were unable to complete the planned handsearching of several journals.

4. Analysis amendment

While we previously specified in the protocol that we would use OR for analysis of binary outcomes, we have altered this to RRs as Higgins 2011 (p. 267) advises these are more easily interpretable.

Characteristics of studies

Characteristics of included studies [ordered by study ID]

Ahmad 2009

Methods

Design: Randomised controlled trial

Randomisation method: random-number sampling scheme stratified by participating physicians. Before recruitment, the randomisation assignment was computer-generated using varying block sizes of 2 and 4. Women were individually randomised

Power calculation: yes

Participants

Setting: urban, hospital-affiliated academic family practice clinic

Country: Canada

Inclusion criteria: women; 18 years and over; in relationship in last 12 months; able to read and write English

Exclusion criteria: none stated

Number (%) of eligible recruited: 314/586 (53.6%)

Numbers recruited 314: 156 IG; 158 CG

Number of dropouts 34: 17 IG; 17 CG

Numbers analysed (and % recruited) 280: 139 (89%) IG; 141 (89%) CG

Numbers analysed (sensitivity analysis) 293: 144 IG; 149 CG

Age: mean 44 years, SD 14 years

Marital status: 74% married/living with a partner, 21% single, 5% separated/divorced/widowed

Ethnicity: 34% outside Canada

Socioeconomic status: 28% ≤ USD 40,000, 18% USD 40,001-60,000, 14% USD 60,001-80,001, 16% USD 80,001-100,001, 24% > USD 100,000

Education background: 18% ≤ high school, 33% ≤ college, 34% ≤ university, 15% ≤ postgraduate

Children: 58% children at home aged < 15 years

Positive IPV result exit survey 62/286: 28/140 IG; 34/146 CG

Interventions

1. Computer-assisted screening for IPV and control, which included items from the Abuse Assessment Screen and PVS embedded among items assessing range of health issues. A 'yes' response to any IPV items was reported on a 1-page risk report 'Possible partner abuse-assess for victimisation' that was provided to physicians. Relevant community referrals were printed at the end of the report (IG)

2. Standard medical care (CG)

Outcomes

Primary:

1. Initiation of discussion about risk for IPV by either participant or provider (discussion opportunity)

2. Detection of women at risk

Secondary:

1. Provider assessment of participant safety

2. Referrals

3. Advice for follow-up

4. Participant acceptance (collected in exit survey)

Data collected through audio-recording (short-term)

NotesDiscussion and detection of other health risks were also measured but not relevant to this study
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskA random-number sampling scheme for eligible women stratified by participating physician was used. The randomisation assignment was computer-generated by an off-site biostatistician using varying block sizes of 2 and 4
Allocation concealment (selection bias)Low riskWomen who had provided informed consent were randomly assigned to IG or CG. "Patient assignments were sealed in opaque envelopes that were marked on the outside with a physician number and sequence number. The envelopes were opened by the recruiter after patients' written consent"
Blinding of participants and personnel (performance bias)
All outcomes
High riskAll physicians initially received study information, and those willing to participate provided written consent. Training was provided during clinical team meetings at the time of consent. "Physician participants were blinded to the study's primary purpose throughout the trial by emphasizing all health risks included in the multirisk computer survey and by using a nonspecific study title". However, they would not have been entirely blinded to the intervention. For example, the prompt in the IG women's records would have alerted providers to who was in the IG and conceivably have influenced their performance. Women were blinded to the study’s primary purpose by using strategies similar to those used for physician participants and embedding questions about women's risk for IPV allowed the authors to conceal the study focus from both physician and patient participants. However, the patients were still aware that the computer survey was part of the intervention that could have influenced their behaviour. Awareness of being a CG participant (i.e. not doing the computer survey) may have altered the CG participants' behaviour in some way that related to the outcome
Blinding of outcome assessment (detection bias)
All outcomes
Low risk2 people undertook primary outcome assessment, working independently to code the audio-recordings of the clinical encounters. Although efforts were made to blind coders to the patients' group assignments, this may have been compromised by what they heard (i.e. some information during the consultation that revealed the patient's allocation. However, this was unlikely to have affected their observation of the primary outcomes (initiation of discussions on IPV and detection of IPV). After their visit, women completed a pencil-and-paper exit survey and received brochures on cancer screening, cardiac and mental health, and IPV, at which time the research staff disclosed the purpose of the study to women. Although women were not blinded in answering the exit surveys, the outcomes measured via the exit survey were not primary to this study or our review
Incomplete outcome data (attrition bias)
All outcomes
High riskImmediately following randomisation, 12/156 women in the IG and 9/158 women in the CG were excluded/withdrew. In the IG, 9 did not complete the computer assessment; 2 had their visits cancelled and 1 withdrew. In the CG, 2 women had their visit cancelled, and 6 womenwithdrew and 1 physician withdrew 1 woman who had mental health issues. The authors observed that women generally showed interest in the computer screening, and some expressed disappointment when they were not assigned to the computer-screened group, which may have explained the higher number of withdrawals in the CG. It is unclear what the actual level of attrition was, given that individual participant numbers for analyses are inconsistent across the flowchart depiction (141 IG; 144 CG), and the results text (143 IG; 144 CG). Numbers in Table 3 (RR analyses; 139 IG; 141 CG) also differed but this was due to missing data (missing covariate values for 3 visits and outcomes coded as "other" 2 cases). In the final analysis, reasons for exclusions of participants appear balanced across the 2 groups occurring due to missing data, recording failures and language barriers. Overall the attrition rate was low at 10.8% (34/314). "Sensitivity analyses were conducted to gauge the potential effect of missing values. 2 extreme situations were considered in which each missing value was replaced with an extreme value of the variable that was most likely to diminish the observed RR toward the null value or most likely to accentuate the observed RR away from the null. These 2 extremes provide a range of likely values for each effect." The sensitivity analyses suggest that the missing data were enough to potentially affect the results. Other imputed missing data were accounted for in the appendicised re-analysed outcome data which was undertaken by ITT
Selective reporting (reporting bias)Unclear riskNone noted but study protocol not available
Other biasHigh risk

Protection against contamination:

There was a high risk of bias in terms of what the CG participants received. Given that the same providers delivered both conditions to different women suggests the way in which they interacted with CG women may have been influenced by their experience of delivering the intervention and thus underestimating the effect

Carroll 2005

Methods

Design: cluster-randomised controlled trial

Randomisation method: to obtain a balanced sample, each participating provider was paired to the greatest extent possible with another provider by practice location, type of provider, sex and age. 1 member of each pair was randomly assigned to the ALPHA group (IG) or CG by a biostatistician using computer-generated random numbers

Power calculation: yes

Participants

Setting: 4 communities in Ontario, including urban, suburban and rural practices with women from diverse socioeconomic and ethnic backgrounds

Country: Canada

Inclusion criteria (providers): any HCP (e.g. physicians, obstetricians, midwives) who practised antenatal and intrapartum care, or antenatal plus transfer at 28 weeks, saw at least 10 antenatal women a year and were not using any antenatal psychosocial screening tool other than the standard Ontario Antenatal Record

Inclusion criteria (individuals): female; 12-30 weeks' gestation; able to read and write English; able to provide informed consent

Exclusion criteria: high obstetric risk as defined by Ontario Antenatal Record

Numbers recruited (providers) 60: 30 IG, 30 CG

Number of dropouts (providers) 12: 9 IG; 3 CG

Numbers (%) of eligible individuals recruited: 253/273 (92.7%)

Numbers recruited (individuals) 253: 112 IG, 141 CG

Number of dropouts (individuals) 26: 14 IG; 12 CG

Numbers analysed (and % recruited) 227: 98 (43%) IG; 129 (57%) CG

Age: mean 29.1 (range 17-47 years) IG; 29.4 (range 17-44) CG

Ethnicity: 85.7% IG; 84.5% CG born in Canada

Socioeconomic status:

IG 10.3%; CG 4.7% < USD 25,000

IG and CG 22.7% USD 25,000-49,999

IG 29.9%; CG 32.8% USD 50,000-74,999

IG 19.6%; CG 24.2%, USD 75,000-99,999

IG 17.5%; CG 15.6% > USD 100,000

Education background: 19.4% IG; 26.6% CG high school or less, 25.5% IG; 20.3% CG some college or university, 55.1% IG; 53.1% CG degree

Pregnancy problems: no concerns 55.1% IG; 50% CG, minor concerns 39.8% IG; 46.9% CG, major concerns 5.1% IG; 3.1% CG

Interventions

1. Providers in the IG administered the ALPHA tool face-to-face, which screened for 15 risk factors including IPV

2. Providers in the CG provided usual antenatal care

Outcomes

Providers were followed-up 1 month' postpartum

All antenatal risk factors were equally weighted in this study and considered 'present' on the basis of providers having 'some' or 'high' concern about the risk factor

Family violence was measured using 5 items 1 of which directly assessed concern with current or past woman abuse

At 4 months' postpartum, the study nurse contacted all women in the trial to again complete a number of psychosocial instruments. Women with providers in the ALPHA group were asked to give feedback about the ALPHA form

NotesData on psychosocial outcomes at 4 months' post-partum has not been reported and needs to be collected from the authors. Data on sample characteristics only reported for the people who completed
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskTo obtain a balanced sample, each participating provider was paired to the greatest extent possible with another provider by practice location, type of provider, sex and age. 1 member of each pair was randomly assigned to the ALPHA group (IG) or CG by a biostatistician using computer-generated random numbers
Allocation concealment (selection bias)Unclear riskThere is a lack of information about the level of allocation knowledge of those who enrolled the provider. Presumably providers recruited women after their randomisation had occurred. If providers knew their status, this could have influenced how and which women were recruited based on their own allocation status
Blinding of participants and personnel (performance bias)
All outcomes
High riskProvider participants were aware of the purpose of the study and their status as IG or CG, which may have influenced their performance. Providers were also responsible for first telling women about the study. Interested women received an explanatory brochure and consent form from their provider and a telephone call from the study nurse to further explain the study and secure consent. We are not told in the report what level of awareness women had about the purpose of the trial. Knowing that the trial included a focus on IPV could have influenced how they responded to their treatment or non-treatment. However, IPV was just 1 of 15 psychosocial issues and therefore may have not been singled out. Individual IG women may have been aware that they were in a treatment group based on the introduction of the ALPHA tool into the consultation, which may have influenced their responses to the ALPHA tool. There is no mention about the blinding of other study personnel
Blinding of outcome assessment (detection bias)
All outcomes
High riskHealthcare professional participants provided the primary outcome data in that they reported back on their level of concern with their participating patients. Both IG and CG providers may have overestimated their level of concern as they would have been prompted by the questions asked in the data collection form. We are told a nurse undertook a follow-up of women but are not given information on level of awareness of women's allocations. The women themselves would not have been blinded in outcome reporting
Incomplete outcome data (attrition bias)
All outcomes
High risk9/30 (30%) IG providers compared to 3/30 (10%) CG providers withdrew from the study. IG: withdrawn because of illness, maternity leave or ineligibility because of language barrier (n = 5); no reason given for withdrawal (n = 4); CG: withdrawn because of illness (n = 1); no reason given for withdrawal (n = 2). 6 family physicians withdrew from IG compared to 1 in CG. There were no data reported on participants of the 12 providers that withdrew. This high level of attrition in the provider IG could indicate deliberate withdrawal associated with the outcome (creating high risk of bias). Among providers who remained in the study, and in terms of the primary outcome, attrition of individual women was low - providers did not complete/return data collection forms on 7.5% of participants. No data were reported on the numbers of women who were assessed at the 4-month post-partum point to allow us to evaluate bias at the participant reporting level. Only 14/21 IG providers gave feedback on experience of using the ALPHA tool. Analysis included sensitivity analysis to accommodate loss of provider participants. Results were not robust enough to withstand the loss of providers.
Selective reporting (reporting bias)High riskImportantly, there is an absence of information on the postpartum psychosocial outcomes of women. Data on characteristics of the sample are only reported on those who were included in the final analysis. The reporting of results highlighted the 1 significant finding (family violence, including child abuse) as the great majority of others were non-significant
Other biasUnclear risk

Protection against contamination:

CG women may have seen IG providers during subsequent consultations, which may have contaminated women's psychosocial outcome data. There is a lack of information about how the situation of the CG using the ALPHA tool was avoided.

Reliability of outcome measures:

While the primary outcome (akin to identification/detection) was adequately measured as 'some' or 'high' concern about a particular psychosocial issue, the time lapse between the delivery of the intervention and the data collection may have introduced bias through recall bias. IG might have had more notes on which to base recall than that the CG providers

Humphreys 2011

Methods

Design: randomised controlled trial

Randomisation method: women reporting risks for smoking, alcohol, drug use and IPV were stratified by risk combination and randomly assigned by the computer (on which they completed a risk assessment) to intervention or usual care

Power calculation: none reported

Participants

Setting: 5 antenatal clinics in San Francisco

Country: USA

Inclusion criteria: females aged 18 years and over, English speaking and < 26 weeks pregnant, receiving antenatal care at 1 of the participating clinics, and not presenting for first antenatal visit.

Exclusion criteria: none stated

Numbers recruited/assessed for IPV risk: 410

Numbers randomised 50: 25 IG; 25 CG

Number dropouts at exit interview: 3 IG; 1 CG

Numbers analysed (and % recruited) at exit interview: 22 IG (88%); 24 CG (96%)

Number drop-outs at second interview: 5 IG; 8 CG

Numbers analysed (and % recruited) at second interview: 20 IG (80%); 17 CG (68%)

Numbers analysed (sensitivity analysis) 50: 25 IG; 25 CG

Age: mean 27.7 years SD 7.1, range 18-43 years

Marital status: 38% married/living with partner, 46% never married, 16% divorced/separated

Ethnicity: 34% Latino, 22% black, 30% white, 14% other

Education: 22% < high school, 36% high school, 28% some college, 12% college degree

Interventions

1. Computer-based assessment (to check eligibility based on Abuse Assessment Screen and randomise women) was followed by Video doctor plus Provider Cueing prior to antenatal consultation

2. Computer-based assessment (to check eligibility based on Abuse Assessment Screen and randomise women) was not followed by the Video Doctor/provider cueing sheet; women simply proceeded to their antenatal appointment

Outcomes

Short-term assessment of outcomes (immediately after the intervention and again following antenatal visit 1 month later; data collected from women)

1. Patient-provider discussion of IPV

2. Helpfulness of IPV discussion

NotesNo adjustment for clustering
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskWomen were randomly assigned by the computer (on which they completed a risk assessment) to IG or CG. "Women reporting risks were stratified by risk combination and randomly assigned by the computer to intervention or usual care groups"
Allocation concealment (selection bias)Low riskAllocation was adequately concealed as only the computer has knowledge of the assignment as there was no opportunity to influence what groups women went into as the computer did the allocation immediately
Blinding of participants and personnel (performance bias)
All outcomes
High riskWhile some personnel may have become aware of the participant allocation (e.g. in order to place computer reports in medical records) the review authors judged that the outcome is not likely to be influenced by this lack of blinding. The printed report would have alerted physicians to the IG status of the woman and may have enhanced performance above and beyond how they might otherwise perform if there were to observe such a report but not be part of a research study
Blinding of outcome assessment (detection bias)
All outcomes
High riskDuring post-visit interviews at baseline and 1-month follow-up, participants were asked "Did you talk about domestic violence with your doctor today?" which was used to indicate that a patient–provider discussion of IPV occurred. We were not given information on the level of blinding of the research assistant and, in any case, the allocation of the woman could very easily have been revealed during the outcome evaluation potentially biasing the research assistant's observations
Incomplete outcome data (attrition bias)
All outcomes
Unclear riskOf the 25 women in the IG, 3 (12%) did not provide baseline data and 5 (20%) did not provide data at 1-month follow-up. Of the 25 women in the CG, 1 (4%) did not provide baseline data and 8 (32%) did not provide data at 1-month follow-up. The sensitivity of the results to losses to follow-up was assessed "by making the assumption that in the absence of outcome data, no discussion occurred." Reasons for dropout were not provided and it is therefore difficult to judge if there was a differential dropout across the groups
Selective reporting (reporting bias)Unclear riskNo protocol available. Unclear what the primary outcomes of the original trial were
Other biasHigh risk

Protection against contamination:

Women assigned to the CG could have received an 'enhanced' usual care given that providers were consulting with both IG women and CG women

Kataoka 2010

Methods

Design: randomised controlled trial

Randomisation method: random numbers table

Power calculation: none reported

Participants

Setting: antenatal clinic of an urban general hospital

Country: Japan

Inclusion criteria: women, < 25 weeks pregnant

Exclusion criteria: none stated

Number (%) of eligible recruited: 328/355 (92.4%)

Numbers randomised 328: 165 interview; 163 questionnaire

Number of dropouts at second time point: 10 interview; 3 questionnaire

Numbers analysed (and % recruited) at second time point 315: 155 interview (93.9%); 160 questionnaire (98.2%)

Number of dropouts at third time point: 7 interview; 11 questionnaire

Numbers analysed (and % recruited) at third time point 297: 148 interview (89.7%); 149 questionnaire (91.4%)

Age: 30.5% 20-29 years, 66.2% 30-39 years, 3% ≥ 40 years

Marital status: 96.3% married, 2.1% single

Education: 13.4% high school, 43.6% junior college, 41.8% university degree

Employment: 33.8% full-time, 17.7% part-time, 46.9% not working

Lifetime experience of physical violence by male partner: 20 (5.8%): interview 8 (4.8%); questionnaire 11 (6.8%)

Interventions

1. Face-to-face screening using the 7-item Japanese VAWS with brief counselling and a community resource card on 3 occasions

2. Women in the questionnaire group self-completed the VAWS in an antenatal clinic interview room where the community resource cards were available on 3 occasions

Outcomes

Primary outcome:

1. Identification (from screen questionnaires)
Secondary outcomes:

2. Comfort level

3. Need to consult with the nurse after screening (all participants completed a questionnaire immediately after the intervention)

Notes 
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskResearchers "used a random number table in blocks of four to ensure that approximately equal numbers of women were allocated to each group"
Allocation concealment (selection bias)Unclear riskAlthough it is indicated that numbered sealed envelopes were used, it is unclear whether opaque envelopes were used
Blinding of participants and personnel (performance bias)
All outcomes
Unclear riskThe researchers indicate "because of the nature of the screening methods, participants could not be blinded to the group assignment." However any such bias was likely distributed equally across the 2 groups. Although the extent of the knowledge about participants' assignment, especially given the repeat visits among personnel is unclear, it is unlikely to have influenced the outcomes differentially in the groups.
Blinding of outcome assessment (detection bias)
All outcomes
Low riskThere was no blinding of outcome assessment; however, the outcome measurement is not likely to be differentially influenced in the 2 groups by lack of blinding. 'The same researcher performed the allocation procedure and data analysis'
Incomplete outcome data (attrition bias)
All outcomes
Low riskAttrition rates were low and balanced in the 2 groups (10.3% IG; 8.6% CG). 2 people in the interview group refused to continue compared to 0 in the questionnaire group
Selective reporting (reporting bias)Low riskPrimary and secondary outcomes reported as specified in protocol
Other biasHigh risk"Measurements of primary and secondary outcomes had psychometric property limitations"

Klevens 2012a

Methods

design: Randomised controlled trial

Randomisation method: the audio computer-assisted self-interview computer program applied simple randomisation (simple randomisation was written into the code of the software program), which facilitated individual randomisation of women to 1 of 3 trial arms

Power calculation: none provided

Participants

Setting: women's health clinics (obstetrical, gynaecological and family planning clinics) at a public hospital

Country: USA

Inclusion criteria: females, at least 18 years

of age.

Exclusion criteria: women who did not speak English; were accompanied by their partner or a child over 3 years of age; who were visually, hearing, or mentally impaired; women who had no access to a telephone or were over 36 weeks pregnant

Number (%) of eligible recruited: 126/228 (55%)

Numbers recruited 126: 46 IG; 80 CG

Number of dropouts 24: 10 IG; 14 CG

Numbers analysed (and % recruited) 102: 36 (78%) IG; 66 (83%) CG

Age: mean 35.8 years, SD 14.4 years

Ethnicity: white 6.3%, black 78.6%, Latina 11.9%, Asian 3.2%

Education background: 42.4% ≤ high school, 41.9% ≤ college/vocational training

Insurance status: Medicaid/care 37.3%, private insurance 5.6%, uninsured 57.1%

Interventions

1. IPV screening by HCP using the PVS, and if positive, HCP support (IG)

2. A-CASI IPV screening (PVS), and if positive, a computer printout of locally available resources for her referral, A-CASI encouragement to show HCP her results and HCP encouragement to contact IPV services if the woman shared her results

3. A-CASI IPV screening (PVS), if positive for IPV, a short video clip provided support and encouraged help seeking, and the computer-printed a list of available IPV resources for referral

(the 2 A-CASI arms were combined as CG)

Outcomes

3 screening outcomes

1. Rates of IPV disclosure based on PVS

2. Screening mode preference

3. Impact of IPV screening (positive and negative reactions).

4 referral outcomes

At the 1-week follow-up telephone call, women were asked to report

1. recall of receiving list of services that provide help to women

2. if women recalled receiving the list, did they share it with anyone

3. contact with services

At 3 months, the local IPV advocacy staff were asked to report

4. records of any telephone or face-to-face contact from study participants who screened positive

Notes 
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskSimple randomisation was written into the code of the computer program used to screen women and individually assigned participants to 1 of the 3 trial arms
Allocation concealment (selection bias)Low riskResearch assistants obtained informed consent from participants prior to any knowledge of the allocation. The allocation was revealed to the participant directly via the computer program used to conduct the health interview
Blinding of participants and personnel (performance bias)
All outcomes
Low riskParticipants were not blinded. They would have been aware that the computer health survey and screening were not part of usual care, which could have influenced their behaviour/performance. However all 3 groups interacted with the computer and had some form of screening. Therefore the outcome was unlikely to be differentially affected by the lack of blinding
Blinding of outcome assessment (detection bias)
All outcomes
High riskExcept for data on women's contact with local advocacy services, which was provided by blinded advocacy staff, assessment of outcomes was not blinded. The research assistant collecting the data was aware of the assignment of individuals and therefore there was potential for introducing a bias into the assessment of outcomes. Also "HCPs were asked to respond to a checklist for compliance with the screening and referral protocol, HCPs were not actually observed to establish the validity of this checklist and the accuracy of their reporting"
Incomplete outcome data (attrition bias)
All outcomes
Low risk"Participants lost to follow-up were similar in level of education and insurance status, but were significantly younger. However, there were no differences between assigned study groups for demographic characteristics among the 24 women lost to follow-up"
Selective reporting (reporting bias)Unclear riskNone noted but study protocol not available
Other biasHigh risk

Protection against contamination:

There was a high risk of potential for contamination across conditions given that all 3 conditions were delivered in the same clinics. Also, a decision was made to combine data from the 2 A-CASI (A-CASI with HCP endorsement and A-CASI alone) arms in the analysis; it is unclear if this was a decision made a priori. It is possible that such a measure could have led to contamination given the similarities between A-CASI with HCP endorsement and the HCP alone conditions

Koziol-McLain 2010

Methods

Design: Randomised controlled trial

Randomisation method: randomly assigned individually 1:1 to IG or CG

Analysis by ITT

Power calculation

Participants

Setting: North Island New Zealand hospital ED

Inclusion criteria: women aged 16 years and over, presenting to the ED for care during selected shifts were eligible

Exclusion criteria: acute presentations precluding informed consent, functional or organic impairment based on clinician assessment, emergency health needs, non-English speaking or entered study during previous visit

Number (%) of eligible recruited: 399/983 (40.6%)

Numbers randomised 399: 199 IG, 200 CG

Number of dropouts at exit interview: 32 IG; 39 CG

Numbers analysed (and % randomised) 344: 167 IG (84%); 177 CG (88.5%)

Age: median 40 years, range 16-94 years, interquartile range 27-59 years

Relationship status: 67.4% current relationship, 8.3% relationship within past year, 22.3% no relationship in past year, 2% never had a partner

Ethnicity: 37.6% Maori, 60.4% New Zealand European, Other, 2% white

Socioeconomic status (annual individual income): 15.2% NZD 0-10,000; 32.1% NZD 10,001-20,000; 26.1% NZD 20,001-35,001; 20.3% > NZD 35,000, 5.8% do not know

Employed: yes 49.1%, no 31.6%, retired 19.3%

Education: 23.3% < high school, 22.8% high school, 45.6% other completed qualification, 8.3% college degree

Depression (CES-D): mean 14.0

Mental health (SF-12): mean 64.8 (SD 24.6)

General health (SF-12): mean 61.9 (SD 30.9)

Acute injury: 79 (19.9%): 34 (17.3%) IG; 45 (22.9%) CG

1 or more children in household: 73.4%

Level of violence (treatment group only): 18% screen result positive, 51% lifetime result positive

Interventions

1. Standardised 3-item IPV screen incorporating the PVS and the Abuse Assessment Screen, statements about the unacceptability of violence, risk assessment and referral (IG)

2. Usual emergency care (CG)

Outcomes

3 months after index ED visit women had a face-to-face structured follow-up interview

Primary:

1. Violence exposure by a current or past partner in the last 3 months

Secondary:

1. Safety behaviours

2. Resource use

Other:

Medical ED charts of all presumed eligible participants were abstracted to collect data including documentation of IPV; however, these data were not reported as a comparison

Notes 
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskThe biostatistician i) computer-generated a series of randomly selected shifts across 7 days of the week and times of the day during which recruitment was to be undertaken and ii) provided a computer-generated randomised sequence for group assignment within those periods
Allocation concealment (selection bias)Low riskThe concealment of allocation followed strict protocols. The randomisation schedule was not available to anyone other than the biostatistician. The biostatistician oversaw the preparation of sealed, opaque, tamper-proof, sequentially numbered envelopes containing the randomised treatment allocation. Research log sheets were used for the real-time documentation of recruitment and the use of envelopes to provide a clear audit trail that was closely monitored by the site project leader
Blinding of participants and personnel (performance bias)
All outcomes
High riskIt was not feasible to blind the IG participants from the purpose of the intervention. Also, personnel may have become aware of the participant's allocation (e.g. through medical record) which may have influenced their treatment of that participant. The study did employ strict protocols in order to attempt to reduce the risk of differential behaviour by participants and personnel.
Blinding of outcome assessment (detection bias)
All outcomes
Low risk"All follow-up staff were blinded to group assignment" at 3 months in collecting the primary and secondary outcome data. Medical records were abstracted by a nurse blinded to group assignment to determine if it was documented that there was an IPV screen or diagnosis.
Incomplete outcome data (attrition bias)
All outcomes
Unclear risk32/199 (16.1%) LTFU in the IG; 23/200 (11.5%) LTFU in the CG. There is a lack of information about whether or not reasons for withdrawal/loss to follow-up differed between the groups. However, the researchers indicate "logistic regression of missing data because of attrition demonstrated no significant associations with variables associated with the primary outcome measure, supporting their being missing completely at random"
Selective reporting (reporting bias)Unclear riskThere is no reference to a trial protocol and thus we cannot confirm that the original trial aims and primary outcomes were as reported here
Other biasLow riskNo evidence of contamination, measures are valid and reliable but some baseline differences reported. "There were some potentially important group differences: compared with women in the usual care group, women in the treatment group were somewhat older (42 vs 38.5); more likely to be New Zealand European (63% vs 58%) and more likely to have been admitted to hospital (43% vs 36%)." They were also less likely to be poorly educated (with less than secondary school) (17.1% vs. 29.5%) but study analysis tested and adjusted for baseline differences. "Age and ethnicity were individually associated with violence in the follow-up period and included in the final model as design effects caused by differences at baseline... the final best subset model included measures of socioeconomic status... Hosmer and Lemeshow test statistic was NS"

MacMillan 2006

Methods

Design: Quasi-randomised controlled trial

Randomisation method: randomised clinic days or shifts

Power calculation: Yes

Participants

Setting: 2 EDs, family practices and women's health clinics

Country: Canada

Inclusion criteria: women were eligible for participation if they were: (1) 18-64 years old, (2) at the site for their own healthcare visit, (3) able to separate themselves from individuals who accompanied them, (4) able to speak and read English, (5) able to provide informed consent

Exclusion criteria: too ill to participate

Number (%) of eligible recruited: 2461/2602 (94.4%)

Numbers assigned: 2461: 853 IG; 769 CG1; 839 CG2

Number of dropouts (varied by screening tool): 3.7-5.2% IG; 3.5-5.7%CG1; 1.5-3.0% CG2

Numbers analysed (varied by screening tool) 788 IG; 741 CG 1; 810 CG2 (CAS), 404 IG; 725 CG1; 814 CG2 (PVS), 411 IG; 742 CG1; 826 CG2 (WAST)

Marital status: 41% single/never married

Ethnicity: 11% born outside Canada

Employment: 52% working full- or part-time

Income: 47% annual income < CAD 25,000

Education: 52% achieved education > 14 years

Children: 52% ≥ 1 child at home

Interventions

1. Face-to-face screening by the HCP using 1 of the 2 screening instruments randomly determined. Any disclosure became part of the clinical encounter and women were offered usual care (IG)

2. Computer-based self-completed screening using the PVS and the WAST randomly ordered (CG1)

3. Written self-completed screening using the PVS and the WAST randomly ordered (CG2)

Outcomes

1. Identification (12-month prevalence based on instrument compared to CAS)

2. Extent of missing data

3. Women's preference for screening approach

Notes 
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskA random number table was used to assign clinic shifts
Allocation concealment (selection bias)High risk"The research coordinator created calendars that informed site coordinators of the assignments." There is, therefore, a risk that advance awareness of shift/day allocations may have introduced selection bias in intervention assignment by not protecting the allocation sequence before and until assignment, for example, recruiters appear to have had knowledge of the allocation prior to inviting individuals into the study, which could have influenced their behaviours differentially
Blinding of participants and personnel (performance bias)
All outcomes
High riskThe study did not specify a control condition and it was not feasible to blind participants from the method of screening they would receive. While any impact of non-blinding on performance was likely to have been distributed similarly across the written and computerised groups (who were told their HCPs would be unaware of their responses), it may have influenced the performance of participants in the face-to-face arm since their providers conducted the screening and therefore "would necessarily be aware of women's responses." In this arm, it was also not feasible to blind personnel to the allocation following assignment as they would have been informed by the recruiter of the woman's participation
Blinding of outcome assessment (detection bias)
All outcomes
High riskOutcome assessment was unable to be blinded and based on women's responses to the screening instruments, self-completion of the CAS, and their evaluation of the method. It was therefore subjective, although the extent of any systematic differences in responses is likely to be randomly distributed
Incomplete outcome data (attrition bias)
All outcomes
Unclear riskData collection was conducted immediately following the treatment. Although there was slightly higher attrition (4%) in the face-to-face arm of the trial, overall attrition was low at 5%. Reasons for missing data were not supplied
Selective reporting (reporting bias)Low riskAll specified outcomes reported
Other biasHigh riskA higher proportion of women in the computer group were from the lowest income quintile and may have been more likely to both be abused and to disclose by computer

MacMillan 2009

Methods

Design: randomised controlled trial

Randomisation method: a table for each day/shift of the week was created for an 8-week period and a random number table was used to determine the order of weeks 1 through 8 in the cells

Power calculation: yes

Participants

Setting: 12 primary care sites (family practices and community health centres), 11 acute care sites (EDs) and 3 speciality care sites (obstetrics/gynaecology)

Country: Canada

Inclusion criteria: women aged 18-64 years, had a male partner at some time in the last 12 months, presented for their own healthcare visit, able to separate themselves from individuals who accompanied them, were living with 120 km of the site and were able to speak and read English and able to provide informed consent

Exclusion criteria: too ill to participate

Number (%) of eligible recruited: 6743/8293 (81.3%)

Numbers assigned: 6743: 3271 IG; 3472 CG

Number (%) of assigned that completed all healthcare visit questionnaires: 5681/6743 (84.3%): 2733 IG; 2948 CG

Number (%) with positive results and followed-up: 707 (12.4%): 347 IG; 360 CG

Number of dropouts: 148 IG; 148 CG

Numbers analysed (and % with positive result) 411: 199 (57%) IG; 212 (59%) CG

*Age: mean number of years: 33.8 (SD 10.8) IG; 33.9 (SD 10.7) CG

Marital status: 41% single/never married

Ethnicity: 11% born outside Canada

Employment: 52% working full- or part-time

Income: 47% annual income < CAD 25,000

Education: mean number of years: 13.7 (SD 2.8) IG; 13.5; (SD 2.8) CG

Children: 52% ≥ 1 child at home

Interventions

1. Women in the screened group (IG) self-completed the WAST; if a woman screened positive this information was provided to her clinician before the healthcare visit. Subsequent discussions or referrals, or both, were at the discretion of the HCP. After the visit, women completed the CAS

2. Women in the non-screened (CG) self-completed the WAST and CAS after their visit

Outcomes

Followed up baseline (< 14 days), 6, 12, 18 months post intervention (collected through self-report by women)

1. Recurrence of IPV (CAS)

2. Quality of life (WHO Quality of Life-Bref)

Notes*Characteristics of participants are provided for the 707 women who had positive results for IPV in last 12 months. Age and education details for the group were obtained through personal communication
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskRandomisation was by day or shift. "A table for each day of the week was created for an 8-week period, and a random number table was used to determine the order of weeks 1 through 8 in the cells." This suggests there was balance across shifts and days of the week, and that systematic differences in presentation by day or shift were avoided
Allocation concealment (selection bias)High risk"The research coordinator created monthly calendars showing shift allocations for site coordinators." There is, therefore, a risk that advance awareness of shift/day allocations may have introduced selection bias in intervention assignment by not protecting the allocation sequence before and until assignment. For example, recruiters would likely have had knowledge of the allocation prior to inviting individuals into the study, which could have influenced their behaviours differentially 
Blinding of participants and personnel (performance bias)
All outcomes
High riskIt was not possible to protect the allocation sequence after assignment given that participants "were told that they might be asked questions about their relationships by completing a form that may be passed on during this visit to the clinician, who might discuss their situation in more detail." Thus, participants may have had awareness that they were receiving an intervention (or not), which could have affected their performance. It was also not feasible to blind personnel to the allocation following assignment as they would have been prompted by the questionnaire placed in the patient record
Blinding of outcome assessment (detection bias)
All outcomes
Low risk"Interviewers blinded to group assignment met with women within 14 days of the index visit to conduct a baseline interview and again at 6, 12, and 18."
Incomplete outcome data (attrition bias)
All outcomes
Low risk"Participant loss to follow-up was high but evenly balanced: 43% (148/347) in screened women and 41% (148/360) in non-screened women" over 18 months making a true ITT analysis difficult. It was noted by authors that women in the screened group who were LTFU reported higher scores on the WAST and CAS. Such differences between retained and lost were not observed in the non-screened group. Thus, there is a possibility that the observed effect estimate is biased. In contrast, there were no group differences in proportions lost, or reasons for dropout, although those LTFU in the IG were more likely to be more severely abused. To deal with missing data, average growth measures were estimated from 5 complete files generated through multiple imputation to test the robustness of the observed findings for all enrolled women
Selective reporting (reporting bias)Low riskAll outcomes for all time points reported
Other biasHigh riskContamination: sites involved both screening (IG) and non-screening (CG) shifts/days and therefore there is a risk that those who were in the CG could have received care that was influenced by physicians' prior experience of delivering the intervention

Rhodes 2002

Methods

Design: quasi-randomised controlled trial

Randomisation method: alternate allocation of individual patients

Power calculation: no

Participants

Setting: One urban university hospital emergency department

Country: USA

Inclusion criteria: English-speaking women and men aged 18-65 years, who presented for emergency care with a non-urgent complaint and triaged into lowest two categories of 5 level system

Exclusion criteria: Those in pain, blind, overtly psychotic, or unable to read

Number (%) of eligible recruited: 470/542 (86.7%) of which 322 were female (68.5%)

Numbers (of women) assigned: 170 IG; 152 CG

Number of dropouts: 20% of charts were missing, differences by arm unspecified

Numbers analysed: by groups into which they were allocated: 170 (IG); 152 (CG)

Age: mean number of years for women: 33 IG; 41CG

Marital status (men and women): Married 19% IG, 27% CG; single 60% IG, 58% CG; widowed/separated or divorced 21% IG, 15% CG

Ethnicity (all patients): Black 91% IG; 90% CG

Insurance status (all patients): Medicaid 37% IG, 40% CG; Medicare 17% IG, 19% CG; private 34% IG, 27% CG; none 12% IG, 14% CG

Reason for visit (all patients):

Medical, 50% IG; 58% CG

Injury 27% IG; 23% CG

Gynecologic or urinary 20% IG; 18% CG

Other 3% IG; 1% CG

InterventionsWomen in the IG completed a c omputer - based screen which included other health lifestyle and behavioural risks. Patients were then offered a computer printout to take with them. Results on a one-page computer printout were attached to the patient 's ED chart. This included a prompt to assess for DV if one or more DV questions were answered positively. R esources for IPV support in ho spital and in the community were listed on the prompt.
Outcomes

1. Screen positive data in IG were assessed from computer re spo nses

2. Documentation by physicians was assessed by blinded chart review

NotesThis study also examined other ps ychosocial risks for both victimisation and perpetration
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)High riskRandomisation method: "Patients were alternately assigned to a computer-based intervention or usual care." This method is open to selection bias and there is inadequate description of protection from such bias.
Allocation concealment (selection bias)Unclear riskNot all eligible patients were enrolled due to limited computer availability. Furthermore, "to avoid selection bias, when the computer was available, the patient to be recruited was the one most recently arrived and assigned as non-urgent at triage." This method remains fallible to bias, but it is unclear whether it would have biased selection.
Blinding of participants and personnel (performance bias)
All outcomes
High riskResults of screening were attached to the patient file in order to alert the treating physician to psychosocial issues as part of the intervention. This meant that the treating physician was also made aware that the patient was in the intervention group. There was therefore a high risk of performance bias.
Blinding of outcome assessment (detection bias)
All outcomes
Low risk"Chart reviewers were blinded to whether a patient had participated in the computer screening and whether these results were shared with the treating physician and were blinded to the assessment of the other chart reviewer."
Incomplete outcome data (attrition bias)
All outcomes
Unclear risk"Findings are based on a review of 80% of charts. The percentage did not vary by whether the patient had received computer screening" - but detailed figures of and reasons for the missing 20% are not given.
Selective reporting (reporting bias)Low riskThe trial was not registered so we were unable to check the selected outcomes, but as it is a screening trial, identification, documentation and information giving are expected outcome measures.
Other biasHigh riskCharacteristics of participants both male and female were evenly distributed across intervention and control groups, but it is unclear if this pertained to only females. As the study used an unvalidated mix of validated screening tools, the reliability and validity of the one used is unclear. There is a high risk of contamination as the participants were screened or not screened alternately and then saw their physician at the one clinic visit, with physicians seeing both intervention and control participants.

Rhodes 2006

Methods

Design: randomised controlled trial

Randomisation method: consenting women were randomly assigned in a 1:1 ratio. Treatment assignment was ascertained by the research assistant by opening sealed randomisation envelopes in sequential order. The envelopes were prepared from a randomisation list generated by computer in blocks of size 10 to ensure balance between groups over short time spans such as shifts and days of the week as well as over the entire course of the study

Power calculation: no

Participants

Setting: 2 socioeconomically diverse EDs – an urban academic medical centre serving mainly publicly insured inner city African-American population and a suburban community hospital serving a privately insured suburban white population

Country: USA

Inclusion criteria: consenting women; aged 18-65 years; triaged as medically non-emergent

Exclusion criteria: none stated

Number (%) of eligible recruited: 1281/2165 (59.2%)

Numbers recruited 1281: 637 IG; 644 CG

Number of dropouts: 216 IG; 194 CG

Numbers analysed (and % recruited) 871: 421 (66.1%) IG; 450 (70%) CG

Age: mean 33.3 years, SD 12 years

Marital status: 21% married, 45% single, 13% divorced/separated/widowed, 21% unknown

Ethnicity: 60% African-American, 29% white, 7% other, 4% unknown

Socioeconomic status: 40% < USD 20,000; 24% USD 20,000-39,999; 16% USD 40,000-79,999; 8% ≥ USD 80,000

Education: 10% < high school diploma, 18% high school or equivalent, 48% > high school, 24% unknown

Positive IPV screen result on exit questionnaire 218/903 (24%): 151/578 (26%) urban, 67/325 (20.6%) suburban

Interventions

1. Self-administered computer-based health risk assessment (Promote Health Survey), which generated health recommendations for participants and alerted physicians to various potential health risks, including domestic violence. If the woman answered 'yes' to any of the 8 IPV assessment items, then the report generated for the physician had a prompt 'Possible partner violence: assess for current abuse' and suggested referral options

2. Usual ED care

Outcomes

Data were collected through audio-recording of consultations (primary method)

1. Discussion of IPV

2. Disclosure of IPV to HCP

3. Provision of domestic violence services

Data were also abstracted from medical records and collected directly from participants

Notes 
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)Low riskThe randomisation for participating patients was generated by "computer in blocks of size 10 to ensure balance between groups over short time spans, such as shifts and days of the week, as well as over the entire course of the study."
Allocation concealment (selection bias)Low riskWomen were recruited and consented prior to the "research assistant opening sealed randomization envelopes in sequential order." "Consenting patients were then randomly assigned"
Blinding of participants and personnel (performance bias)
All outcomes
High riskProviders were not blinded to the purpose of the study or the intervention, "health care providers were informed that the study objective was to study the effect of a computer prompt on IPV communication and were encouraged to screen all women for abuse." However this was unlikely to have led to benefits for IG women extraneous to the intended effect of the intervention; the outcome of interest is unlikely to have been influenced by lack of blinding. Women were blinded to the purpose of the study being told it was a "study of physician-patient communication." Women in the IG may have realised that the computer-based health risk assessment was part of the intervention thus influencing how they behaved. However, we would not expect that the outcome would have been influenced by this incomplete blinding. For example, changes in women's behaviour such as being more encouraged to discuss IPV with the HCP would not differ from what would be expected to arise from the intervention. Lack of blinding in the situation where CG participants inadvertently became aware of the intervention through interactions with other women or staff could conceivably have influenced the outcome. We are not given sufficient information about the degree of awareness of other staff regarding women's allocations, which could have influenced their interactions with women and, therefore, the outcomes
Blinding of outcome assessment (detection bias)
All outcomes
Unclear riskWe are not told about who edited the audio-recordings of the ED visits "a 7-hour ED visit might be edited to 20 minutes of actual health care provider–patient interaction"; it would have been important for them to be blinded as knowing the allocation could have affected the editing process. Although research assistants who were to undertake the primary data collection via coding of audio-recordings of both IG and CG consultations were said to be blinded, the allocation of participants could have been revealed during the remaining audio data and thereby influenced coders' interpretation of what they heard. It is also not known if the person who edited differed from the coders. If the coder was also the editor then it would have increased the likelihood that the allocation of the participant would have become known. "Charts of all enrolled patients were coded using a structured chart abstraction form to assess evidence of DV documentation ;" however, there is no indication of blinding of assessors. It is likely that the allocations of IG women were quite evident by virtue of presence of the IPV risk report and it is unclear if presence of a report was considered different to other documentation of IPV. Finally, both groups of women self-completed an exit survey and were not blinded; however, any effect was likely equal in both groups
Incomplete outcome data (attrition bias)
All outcomes
Unclear risk21/101 (21%) providers did not consent to having their consultations recorded and thus there was incomplete outcome data for their participants. However, this lack of recording should have been equal in both groups since providers were seeing both IG and CG participants. The overall attrition of participants was 32% and we are not given clear information about the extent to which the providers' refusal to audio-record sessions accounted for this rate (i.e. what proportion of patients declined the audio-recording post-randomisation). While the attrition levels in audio-recording appear balanced across the 2 groups: 216/637 (IG; 34%), 194/644 (CG; 30.1%) there was no sensitivity analysis included in the report to ascertain the impact of those missing data on the robustness of the effect. Attrition rates on chart review were similarly spread and low at 8%, and moderately high but spread on the exit survey. There is a lack of information on reasons for these (albeit low) attrition rates in the chart review. There were 4 CG cases that appear in the participant flowchart but are absent from the observed rates in Table 3
Selective reporting (reporting bias)High riskData on medical records was not furnished except that it is indicated in text that there was no difference between groups on the documentation of IPV. No reference to a trial protocol and thus no confirmation that the original trial aims and primary outcomes were as reported here. Analysis was reported separately by site and may not be significant overall
Other biasHigh risk

Protection against contamination:

The same providers delivered the intervention or usual care to participants. While they should have remained unaware of who the CG participants were, their experience of consulting with IG participants could have influenced their performance with the CG participants

Trautman 2007

  1. a

    A-CASI: audio computer-assisted self-interviews; ALPHA: Antenatal Psychosocial Health Assessment; CAS: Composite Abuse Scale; CES-D: Centre for Epidemiological Studies - Depression; CG: control group; ED: emergency department; HCP: healthcare professional; IG: intervention group; IPV: intimate partner violence; ITT: intention to treat; LTFU: loss to follow-up; PVS: Partner Violence Screen; RR: risk ratio; SD: standard deviation; SF: Short Form; TCG: treatment control group; VAWS: Violence Against Women Scale; WAST: Woman Abuse Screening Tool

Methods

Design: quasi-experimental control study

Randomisation method: there were 3 distinct consecutive 2-weeks enrolment periods. In the second enrolment period all eligible women who presented to the ED were assigned to the IG. During the first and third enrolment periods all eligible presenting women were allocated to a TCG 

Power calculation: yes

Participants

Setting: adult urban ED of a large university hospital serving a primarily socioeconomically disadvantaged, minority population.

Country: USA

Inclusion criteria: women aged ≥ 18 years who presented to the ED for medical treatment

Exclusion criteria: acute or critically ill presentation; illiteracy; impaired mental status, disorientation or apparent intoxication; would not separate from their partner; or already enrolled

Numbers (%) of eligible recruited: 1005/1395 (72%)

Numbers recruited: 1005: 411 IG, 594 CG

Number of dropouts: 0 IG; 0 CG

Numbers analysed (and % recruited) 1005: 411 (100%) IG; 594 (100%) CG

Age range (years): 22.9% 18-24, 23.3% 25-34, 41.4% 35-54, 12.4% ≥ 55

Marital status: 20% married/living with partner, 53.8% never married, 21% divorced/separated, 5.2% widowed

Ethnicity: 16.1% white, 83.9% non-white

Socioeconomic status (annual household income): 42.4% < USD 10,000; 20.6% USD 10,000-15,999; 12.2% USD 16,000-20,999; 14.8% USD 21,000-35,999 10% ≥ USD 36,000

Education: 30.5% < high school, 42.3% high school or equivalent, 27.2% > high school

Children in household: 50.9% yes

Interventions

1. Self-administered computer-based health survey including 4 items about IPV. If the woman answered yes to any of the 4 IPV assessment items, then 2 reports were generated. 1 copy was attached to the woman's medical record to alert treating staff and the second copy was placed in a box for social work referral (IG)

2. Self-administered computer-based health survey containing no items about IPV and usual ED care (consisting of current ED policy that recommended but did not enforce routine IPV screening (TCG))

Outcomes

Immediate abstraction of data from medical records

1. Screening

2. Detection

3. Referral

4. Service rates

Notes 
Risk of bias
BiasAuthors' judgementSupport for judgement
Random sequence generation (selection bias)High riskDuring 3 distinct, consecutive, 2-week enrolment periods, all eligible women were asked to complete a computer-based health survey. During the first and third enrolment periods, the computer-based health survey did not include any IPV items. During the second enrolment period, it did include IPV screening items. It is likely that this type of allocation process introduced a high risk of bias due to systematic differences between the IG and CG
Allocation concealment (selection bias)High riskPatient service co-ordinators recruited and obtained consent from participants. There was no blinding of recruiters to the potential allocation of women as the allocation for the period during which women presented to the ED was defined in advance and not concealed in any way explained in the report. Therefore, awareness of the allocation could have influenced how women were recruited. Furthermore, the experimental allocation for that period may have become inadvertently known to some women through interactions with other participants and staff influencing their decision to participate or not
Blinding of participants and personnel (performance bias)
All outcomes
High riskWomen approached were told that this was a study about women's health whereby they would be "asked to answer questions about themselves on a computer and to allow their medical record to be reviewed by study personnel." Thus there was some blinding of women to the purpose of the study. However, healthcare personnel were unblinded as 'the medical records of all subjects were attached by coordinators to participants medical records to alert treating staff'
Blinding of outcome assessment (detection bias)
All outcomes
Unclear riskNot stated that research assistant unblinded as "the medical records of all subjects were reviewed by a research assistant to determine whether there was any documentation in the record"
Incomplete outcome data (attrition bias)
All outcomes
Unclear riskUnclear how missing data within variables were dealt with
Selective reporting (reporting bias)Unclear riskThere was no reference to a study protocol and therefore insufficient information to permit judgement of 'Low risk' or 'High risk'
Other biasHigh risk

Protection against contamination:

The process of the providers consulting with CG women in the third, 2-week block following the 2-week IG block could have contaminated their interactions with CG participants. In fact, the authors state, "Three study periods were used to determine whether usual care related to intimate partner violence would return to baseline (i.e. first enrolment period) in the third enrolment period when the intimate partner violence questions were removed or whether it would be higher as a result of the computerized intimate partner violence screening during the second study period"

Characteristics of excluded studies [ordered by study ID]

StudyReason for exclusion
Ahmad 2010Qualitative study of physician views of screening linked to Ahmad 2009
Bair-Merritt 2006Screening results not passed on to healthcare professional
Bonds 2006Not a randomised or quasi-random method
Brienza 2005No data on women participants
Campbell 2001Case-finding not screening
Chen 2007No usual care group comparison
Coonrod 2000No data on women participants
Cripe 2010Intervention exceeded 'brief' intervention
Curry 2006Intervention exceeded 'brief' intervention
Dubowitz 2011Intervention targeted to children and clinicians
Dubowitz 2012Intervention targeted to children and clinicians
Duggan 2004Intervention exceeded 'brief' intervention
Ernst 2007No usual care group comparison
Feder 2011Case finding not screening trial
Feigelman 2011Intervention targeted to children and clinicians
Fernandez-Alonso 2006No data on women participants
Florsheim 2011Intervention exceeded 'brief' intervention
Furbee 1998Not a randomised or quasi-random method
Garg 2007Participant data included both sexes and could not be separated
Gillum 2009Intervention exceeded 'brief' intervention
Green 2005Intervention exceeded 'brief' intervention
Halpern 2009Not a randomised or quasi-randomised method
Hewitt 2011Not a randomised or quasi-randomised method
Hollander 2001Usual care included screening results given to healthcare professional
Houry 2011Screening results not passed on to healthcare professional
Jewkes 2008Intervention exceeded 'brief' intervention
Kapur 2011Not a randomised or quasi-randomised method
Kiely 2010Intervention exceeded 'brief' intervention
Klevens 2012bScreening results not passed on to healthcare professional
Knight 2000Not a randomised or quasi-randomised method
Koziol-McLain 2004Prevalence study. Not an RCT
Koziol-McLain 2008Qualitative study linked to Koziol-McLain 2004
Larkin 1999Not a randomised or quasi-randomised method
Rickert 2009No usual care group comparison
Robinson-Whelan 2010Not in a healthcare setting
Thompson 2000Case-finding not screening
Tiwari 2010Intervention exceeded 'brief' intervention

Characteristics of ongoing studies [ordered by study ID]

Taft 2012

Trial name or titleEnhanced maternal and child health nurse care for women experiencing intimate partner/family violence: MOVE, a cluster randomised trial of screening and referral in primary health care
MethodsCluster-randomised trial
Participants80 maternal and child health nurse clinics randomised in 8 maternal and child health nurse teams
InterventionsSystems approach at individual, team and local government levels, with enhanced formal referral links to family violence services, a maternal health self-completion screening checklist and clinical guidelines
OutcomesNA
Starting date2010
Contact informationa.taft@latrobe.edu.au
Notes 

Ancillary