Educational and skills‐based interventions for preventing relationship and dating violence in adolescents and young adults Authors: Youngjoo Kang, Shakiba Habibula, Catherine Heffernan, Caroline Farmer, G.J. Melendez-Torres, Joanna Nurse, Gracia Fellmeth Published: 2026 ABSTRACT ObjectivesThis is a protocol for a Cochrane Review (intervention). The objectives are as follows:To evaluate the benefits and harms of educational and skills‐based interventions for the prevention of dating and relationship violence in adolescents and young adults, comparing these interventions with inactive controls (placebo, standard care, waiting list, or no intervention). Background Description of the condition Dating and relationship violence (DRV) is defined as physical, psychological, or sexual abuse and violence including stalking, threatening, coercive, or controlling behaviour perpetrated by current or former intimate or dating partners [1, 2, 3]. It lies on a continuum with intimate partner violence (IPV), which encompasses the same abusive behaviours in current and former intimate relationships; however, DRV uniquely captures relational contexts relevant to adolescents and young adults [4, 5]. DRV and IPV are also related to and intersect with gender‐based violence (GBV), which arises from inequalities in sexuality and gender and includes violence occurring outside the context of relationships [6, 7, 8]. These forms of violence share common societal and individual‐level risk factors, such as past experiences of violence (e.g. child maltreatment [9, 10, 11], witnessing domestic violence [9, 11], and child marriage [11, 12]), alcohol and substance misuse [9], and socio‐economic deprivation [10, 11, 12]. Perceived norms on the social acceptability of sexual violence and violence within a relationship are also linked to an increased likelihood of experiencing IPV and GBV [13, 14, 15]. DRV includes a wide range of behaviours that may occur in person and online [16, 17]. Physical DRV is the intentional use of physical force with the potential to cause death, disability, injury, or harm [1]. It also includes coercion of another person to commit these behaviours. Sexual DRV is violence of a sexual nature and includes attempted and committed sexual acts against a person's will or against someone unable to consent or refuse [1]. It also includes non‐consensual sexual experiences without physical contact, such as voyeurism, taking or sharing sexual photographs or films without consent, verbal threats of sexual violence, and creating a sexually hostile climate. Psychological or emotional DRV is characterised by behaviours that coerce and control or attempt to coerce or control another person, such as verbal and non‐verbal aggression and exploitation of vulnerability, with the intention of emotional or psychological harm [1]. DRV prevalence varies significantly according to the type of violence, geographical location, and whether the estimate is based on perpetration or victimisation. Psychological DRV is the most common form, with reported victimisation rates ranging between 6% and 96% among teenagers in Europe [18], and between 17% and 88% among teenagers in the UK, the USA, and Canada [19]. Lifetime prevalence of experiencing physical, sexual, or both forms of IPV among girls aged 15 to 19 years is estimated at 24% globally [12]. One study of high schoolers in the USA reported a 3% prevalence of sexual DRV perpetration amongst male and female students [20]. In Malawi, one study found that 15% of adolescents (both sexes) reported some form of DRV perpetration, while 10% reported both victimisation and perpetration [21]. Therefore, DRV prevalence is highly contextual and linked to systems of inequality that produce unequal power dynamics and social marginalisation. IPV prevalence is highest in low‐ and middle‐income countries (LMICs), including those in Oceania, sub‐Saharan Africa, and South Asia [12]. Social disadvantage is associated with higher DRV prevalence [19, 22], and higher household income and educational attainment are associated with lower likelihood of IPV victimisation [23]. There are also gender inequities, with adolescent girls reporting higher rates of sexual DRV victimisation and DRV‐related adverse outcomes than boys [24, 25]. Youths who are non‐binary or from sexual and ethnic minorities report higher levels of sexual and physical DRV than their White, heterosexual, cisgender peers [10, 26, 27]. Adolescents identifying as immigrants and belonging to minority ethnic groups are at higher risk of DRV perpetration and victimisation [28], as are adolescents with mental health and neurodevelopmental conditions [29]. Trends in DRV are challenging to assess due to differences in national reporting mechanisms and the evolution of DRV definitions over time. Data from the World Health Organization (WHO) and other United Nations (UN) agencies suggest limited progress in reducing global IPV, with an annual decrease of only 0.2% over the past two decades [30]. This aggregate rate likely encompasses important geographical and subgroup differences. For example, a national survey of IPV victimisation among women in Zimbabwe reported an initial decrease in prevalence from 2005 to 2010, followed by an increase from 2010 to 2015 [31]. Over a similar period, a survey of IPV among adolescents in Spain found an overall decrease from 2006 to 2016, but the rate of decline slowed from 2010 to 2016 [32]. In contrast, 10‐year trends of national surveys from Norway (2013–2022) and Brazil (2014–2023) indicate an overall increase in IPV [33, 34]. Where overall decline has been reported for adolescent DRV, there is evidence of gender differences, with declining victimisation for boys but not girls [35, 36]. The convergence of digital and in‐person social interaction also shapes these trends, particularly among adolescents and young adults. Evidence increasingly points to technology and online platforms reinforcing gender inequalities and normalising DRV, particularly through online communities such as the 'manosphere' [37, 38]. When exposed to misogynistic social media content, children and young people are five times more likely to think physical violence is acceptable, and a significant proportion of young people are unable to identify cyber dating abuse, such as technology‐facilitated coercive and controlling behaviours in a relationship [39]. DRV is associated with severe and long‐lasting consequences. Adolescents who experience DRV are at increased risk of depression, anxiety, post‐traumatic stress disorder (PTSD), suicidality, and self‐harm [24, 40, 41]. They are more likely to engage in risky sexual behaviour, misuse substances [24, 40, 41], report poor physical health, and perform poorly at school and university [41, 42]. Adolescent DRV is strongly associated with future violence in relationships, predicting both perpetration and victimisation, potentially decades ahead [40]. Description of the intervention and how it might work This review focusses on educational and skills‐based interventions to prevent DRV among adolescents and young adults aged 12 to 25 years. Such interventions are often implemented in educational settings such as schools [43, 44], colleges, and universities [25, 45]; though other interventions are designed for community, workplace, or care settings [25, 44]. Interventions can have a universal primary prevention approach (i.e. broadly designed for general populations rather than targeting those at higher risk) or secondary or tertiary prevention approaches [46]. Programmes may be administered in person or digitally. The educational content of DRV interventions often addresses knowledge, skills, attitudes, and norms. It may teach the warning signs of abuse, challenge beliefs around DRV, and provide knowledge about its prevalence and forms [5, 45]. Skills‐based interventions focus on behaviours such as assertiveness and safe behavioural and communication responses to DRV risk. Reflecting the multifactorial aetiology of DRV, many theoretical models target the causal pathways linking intervention components to behaviour change at multiple levels [47]. At an individual level, psychological theories, such as the theory of planned behaviour, relate positive individual attitudes, social norms, and perceived control of a behaviour to increased intentions and likelihood of performing that behaviour [48, 49]. The theory of planned behaviour may also be applied to help‐seeking behaviours and perceptions around help‐seeking [50]. Bystander training attributes the roots of sexual violence partly to community norms and targets community members' knowledge and skills with the aim of increasing prosocial intervention and other protective bystander behaviours [51, 52]. Multi‐component interventions, which are more common than single‐component interventions [5, 25], apply an ecological theoretical framework to DRV prevention, addressing individual‐level attitudes and beliefs; relational factors between peers, family, and community; and wider cultural norms and policy structures [53]. A recent systematic review examining school‐based interventions found some evidence that interventions reduced DRV through a "basic safety mechanism" in which communicating to students that violence was unacceptable disrupted violence incidence [47]. Why it is important to do this review This is an update of a Cochrane review published in 2013 [54]. Since its publication, numerous new studies have contributed evidence that could change our previous conclusions. For example, over 75% of results from a crude PubMed search using the keywords "dating relationship violence adolescent intervention" were published after the previous review's search date [55]. Despite recognition of DRV as an urgent public health priority, the burden of IPV experienced by adolescents has increased in one‐third of countries globally [56]. The UN Sustainable Development Goals, adopted in 2015, aim to eliminate violence against women and girls by 2030 [57], yet no country is on track to reach this target [12]. Finding effective interventions to prevent DRV for adolescents and young people therefore remains globally relevant. Furthermore, in the past decade, the social landscape in which DRV can occur has significantly changed to include social media and digital platforms [17], where controlling and coercive abuse is increasingly normalised [58]. Our understanding of DRV has evolved to recognise that DRV starts early, with earlier incidence linked to increased risks of poor health, re‐victimisation, and interacting forms of inequality [24, 27]. The evidence for interventions in LMIC settings has grown significantly [25], which is particularly relevant given the higher IPV rates reported in these regions [12]. Recent systematic reviews have focused on specific settings (e.g. schools, universities) [43, 45], included English‐language publications only [25, 44], included non‐experimental study designs [45], or focused on adolescents only [43, 44, 46]. Longitudinal data on DRV incidence show a peak in young adults in their early 20s [20, 59, 60], and the cumulative incidence of DRV suggests preventive interventions for the young adult age bracket are urgently needed [20]. Objectives To evaluate the benefits and harms of educational and skills‐based interventions for the prevention of dating and relationship violence in adolescents and young adults, comparing these interventions with inactive controls (placebo, standard care, waiting list, or no intervention). Methods We will follow the Methodological Expectations of Cochrane Intervention Reviews (MECIR) when conducting the review [61], and PRISMA 2020 guidance for reporting [62], in line with Chapter 3 of the Cochrane Handbook for Systematic Reviews of Interventions [63]. Criteria for considering studies for this review Types of studies We will include studies with the following experimental designs, regardless of setting, country, publication language, and publication status. Randomised controlled trials (RCTs).Quasi‐RCTs, where allocation may not be truly random (e.g. by date of birth, alternating order of enrolment, day of the week, or student number).Cluster‐RCTs, where a cluster may be a class, school, or other predefined group. Randomised controlled trials (RCTs). Randomised controlled trials (RCTs). Quasi‐RCTs, where allocation may not be truly random (e.g. by date of birth, alternating order of enrolment, day of the week, or student number). Quasi‐RCTs, where allocation may not be truly random (e.g. by date of birth, alternating order of enrolment, day of the week, or student number). Cluster‐RCTs, where a cluster may be a class, school, or other predefined group. Cluster‐RCTs, where a cluster may be a class, school, or other predefined group. Given DRV's multifactorial aetiology, randomisation to control for known and unknown confounders is particularly important for unbiased results. However, individual randomisation may not be feasible in educational settings where many interventions are implemented, hence the inclusion of quasi‐ and cluster‐RCTs. Types of participants We will include studies with adolescent and young adult participants aged 12 to 25 years. Age limits defining adolescence, youth, and young adulthood vary internationally [64, 65, 66, 67]. For the purposes of our review, we have selected the lower limit of 12 years as the age when dating relationships are more likely to begin [68, 69], and the upper age limit of 25 years to include the peak of cumulative DRV incidence, according to the literature. We define adolescence as 12 to 18 years and young adulthood as 19 to 25 years. We will include studies with a wider age range of young participants if data can be extracted or obtained for our age groups of interest, or if more than 80% of participants in the study are aged 12 to 25 years. Interventions, particularly multi‐component interventions, may also include adult participants with links to adolescents, such as family members or carers or professionals within the intervention setting (e.g. educational staff, security staff, community members, police). We will only include studies with such interventions if they also have adolescents or young adults, or both, as primary participants. Types of interventions Eligible interventions are actively delivered educational or skills‐based programmes with the explicit aim of DRV prevention. We will include primary prevention interventions (which target general populations) and secondary prevention interventions (which target populations at higher risk of DRV). We will include interventions delivered in any setting, including educational settings (e.g. schools, colleges, universities), community settings (e.g. community centres), healthcare settings (e.g. maternity care clinics), and other settings (e.g. prison, home). We will exclude interventions that exclusively target people who are currently experiencing or have previously experienced DRV. If some participants in general or higher‐risk study populations report current or past experience of DRV, we will include the studies if at least 80% of participants have no current or past experience of DRV. We will include interventions of any duration and with any length of follow‐up, delivery modality (e.g. online, in person, app‐based), format (e.g. role play, discussion, lecture, group activities), and type of facilitator. Interventional content may vary but must directly address DRV. Multi‐component interventions must meet the following conditions. The overarching aim of the multi‐component intervention is to prevent DRV.Most components are actively delivered educational or skills‐based programmes directly addressing DRV. The overarching aim of the multi‐component intervention is to prevent DRV. The overarching aim of the multi‐component intervention is to prevent DRV. Most components are actively delivered educational or skills‐based programmes directly addressing DRV. Most components are actively delivered educational or skills‐based programmes directly addressing DRV. We will exclude interventions with the following characteristics. No mention of DRV prevention in the aims or objectives.Interventions that only screen for the occurrence of DRV and then refer to a support agency, unless the intervention actively provides an educational or skills‐based component following screening.Tertiary prevention interventions, which target populations with current or past experience of DRV to prevent DRV re‐occurrence. No mention of DRV prevention in the aims or objectives. No mention of DRV prevention in the aims or objectives. Interventions that only screen for the occurrence of DRV and then refer to a support agency, unless the intervention actively provides an educational or skills‐based component following screening. Interventions that only screen for the occurrence of DRV and then refer to a support agency, unless the intervention actively provides an educational or skills‐based component following screening. Tertiary prevention interventions, which target populations with current or past experience of DRV to prevent DRV re‐occurrence. Tertiary prevention interventions, which target populations with current or past experience of DRV to prevent DRV re‐occurrence. Studies must compare interventions with an inactive control, such as a placebo intervention (e.g. first aid classes), standard care, waiting list, or no intervention. We will evaluate all educational and skills‐based interventions grouped together versus all inactive controls grouped together. Studies that evaluate active comparisons head to head without an inactive control will be ineligible. Outcome measures Outcomes measured are not part of the review's inclusion criteria. As there are no core outcome sets for DRV or IPV in the Core Outcome Measures in Effectiveness Trials (COMET) initiative [70], we identified critical and important outcomes by examining outcomes in recent systematic reviews and interventional studies on DRV prevention and by reviewing the core outcome set studies for child domestic violence. We prioritised outcomes that are most relevant for public health policy and clinical impact. Critical outcomes DRV occurrence The main outcome of interest is DRV occurrence in all its forms. We will report DRV victimisation, defined as any self‐reported experience of physical, sexual, psychological, emotional, controlling, or cyber abuse or violence from a current dating or intimate partner; and DRV perpetration, defined as any self‐reported use of these same behaviours against a former or current dating or intimate partner [3]. Within this domain, we will report the following measures. Prevalence of DRV victimisation (proportion of participants who report at least one occurrence of DRV victimisation, as a proportion of all participants assessed).Prevalence of DRV perpetration (proportion of participants who report at least one occurrence of DRV perpetration, as a proportion of all participants assessed).Number of DRV victimisation occurrences (total number of DRV victimisation occurrences reported by participants over the specified period, reported as average number of occurrences per participant or as a rate).Number of DRV perpetration occurrences (total number of DRV perpetration occurrences reported by participants over the specified period, reported as average number of occurrences per participant or as a rate). Prevalence of DRV victimisation (proportion of participants who report at least one occurrence of DRV victimisation, as a proportion of all participants assessed). Prevalence of DRV victimisation (proportion of participants who report at least one occurrence of DRV victimisation, as a proportion of all participants assessed). Prevalence of DRV perpetration (proportion of participants who report at least one occurrence of DRV perpetration, as a proportion of all participants assessed). Prevalence of DRV perpetration (proportion of participants who report at least one occurrence of DRV perpetration, as a proportion of all participants assessed). Number of DRV victimisation occurrences (total number of DRV victimisation occurrences reported by participants over the specified period, reported as average number of occurrences per participant or as a rate). Number of DRV victimisation occurrences (total number of DRV victimisation occurrences reported by participants over the specified period, reported as average number of occurrences per participant or as a rate). Number of DRV perpetration occurrences (total number of DRV perpetration occurrences reported by participants over the specified period, reported as average number of occurrences per participant or as a rate). Number of DRV perpetration occurrences (total number of DRV perpetration occurrences reported by participants over the specified period, reported as average number of occurrences per participant or as a rate). For these four critical outcome measures, we will report overall DRV (including any subtype) as well as DRV by subtype (i.e. physical, sexual, psychological/emotional, and cyber abuse), if feasible. Where the subtype of DRV is specified, we will accept the study's definition thereof. Combined forms of DRV will be treated as separate outcomes (i.e. physical and sexual violence measured as one outcome will be treated as a discrete outcome from physical violence). Adverse events/effects We define an adverse event as an unfavourable or harmful outcome that occurs during or after the use of an intervention but is not necessarily caused by it, and an adverse effect as an adverse event for which the causal relation between the intervention and the event is at least a reasonable possibility [71]. We will extract information relating to how included studies have investigated adverse events, and we will report the following adverse events. Increase in the number of DRV occurrences (self‐reported by participants or as reported in official records).Increase in physical injuries resulting from DRV (self‐reported by participants or as reported in official records). Increase in the number of DRV occurrences (self‐reported by participants or as reported in official records). Increase in the number of DRV occurrences (self‐reported by participants or as reported in official records). Increase in physical injuries resulting from DRV (self‐reported by participants or as reported in official records). Increase in physical injuries resulting from DRV (self‐reported by participants or as reported in official records). Where a study reports reasonable links between the adverse event and the intervention, we will report the adverse event as an adverse effect. We will include adverse effects within adverse events. Important outcomes Physical injuries resulting from DRV (self‐reported by participants or as reported by official records)Improvement in mental health and psychosocial well‐being (self‐reported by participants or as reported by official records (e.g. health records) using a validated measure (e.g. Patient Health Questionnaire))Change mechanism‐related factorsIncreased knowledge about DRV (self‐reported using a validated measure, e.g. Seventh Grade Inventory of Knowledge and Attitudes [72])Improvement in behaviours around DRV (self‐reported using a validated measure, e.g. Dating Behaviour Survey (DBS) [73])Improvement in attitudes towards DRV (self‐reported using a validated measure, e.g. Rape Myth Acceptance Scale (RMAS) [74])Improvement in skills relating to DRV (self‐reported using a validated measure, e.g. Sexual Communication Survey (SCS) [73])Intervention‐related factorsCost of the programmeTime commitment requiredAcceptability of the programme as measured by participant dropout rate Physical injuries resulting from DRV (self‐reported by participants or as reported by official records) Physical injuries resulting from DRV (self‐reported by participants or as reported by official records) Improvement in mental health and psychosocial well‐being (self‐reported by participants or as reported by official records (e.g. health records) using a validated measure (e.g. Patient Health Questionnaire)) Improvement in mental health and psychosocial well‐being (self‐reported by participants or as reported by official records (e.g. health records) using a validated measure (e.g. Patient Health Questionnaire)) Change mechanism‐related factorsIncreased knowledge about DRV (self‐reported using a validated measure, e.g. Seventh Grade Inventory of Knowledge and Attitudes [72])Improvement in behaviours around DRV (self‐reported using a validated measure, e.g. Dating Behaviour Survey (DBS) [73])Improvement in attitudes towards DRV (self‐reported using a validated measure, e.g. Rape Myth Acceptance Scale (RMAS) [74])Improvement in skills relating to DRV (self‐reported using a validated measure, e.g. Sexual Communication Survey (SCS) [73]) Change mechanism‐related factors Increased knowledge about DRV (self‐reported using a validated measure, e.g. Seventh Grade Inventory of Knowledge and Attitudes [72]) Increased knowledge about DRV (self‐reported using a validated measure, e.g. Seventh Grade Inventory of Knowledge and Attitudes [72]) Improvement in behaviours around DRV (self‐reported using a validated measure, e.g. Dating Behaviour Survey (DBS) [73]) Improvement in behaviours around DRV (self‐reported using a validated measure, e.g. Dating Behaviour Survey (DBS) [73]) Improvement in attitudes towards DRV (self‐reported using a validated measure, e.g. Rape Myth Acceptance Scale (RMAS) [74]) Improvement in attitudes towards DRV (self‐reported using a validated measure, e.g. Rape Myth Acceptance Scale (RMAS) [74]) Improvement in skills relating to DRV (self‐reported using a validated measure, e.g. Sexual Communication Survey (SCS) [73]) Improvement in skills relating to DRV (self‐reported using a validated measure, e.g. Sexual Communication Survey (SCS) [73]) Intervention‐related factorsCost of the programmeTime commitment requiredAcceptability of the programme as measured by participant dropout rate Intervention‐related factors Cost of the programme Cost of the programme Time commitment required Time commitment required Acceptability of the programme as measured by participant dropout rate Acceptability of the programme as measured by participant dropout rate Measurement scales A wide variety of measurement scales are available to assess DRV occurrence; participant health; and the knowledge, behaviours, attitudes, and skills gained from educational and skills‐based interventions for DRV prevention. There is no single, internationally established standard. Scales may rely on participants' self‐report or official (e.g. police) records. We will include scales where study authors state or reference evidence of reliability and validity; if further evaluations of the reliability or validity of a measurement scale exist in the literature, we will draw upon these to help determine the suitability and applicability of the scale in relation to the given outcome and context in which it was administered. We will only include data from studies in which a full description of the measurement scale and its scoring system is available. We will provide reasons for our rejection of any measurement scales from our analysis. Timing of outcome assessment We will group outcomes into three time periods, as follows. Short term (outcomes assessed from immediately following the intervention to less than six months following the intervention).Medium term (outcomes assessed between six and 12 months following the intervention).Long term (outcomes assessed more than 12 months following the intervention). Short term (outcomes assessed from immediately following the intervention to less than six months following the intervention). Short term (outcomes assessed from immediately following the intervention to less than six months following the intervention). Medium term (outcomes assessed between six and 12 months following the intervention). Medium term (outcomes assessed between six and 12 months following the intervention). Long term (outcomes assessed more than 12 months following the intervention). Long term (outcomes assessed more than 12 months following the intervention). If studies report multiple measurements within a time period, we will extract all measurements and use the furthest measurement within that time period for data synthesis (e.g. if an outcome is measured at three months and five months, we will use the outcome measure at five months). Hierarchy of outcome measures We will extract all available measures for each outcome. Studies with multiple measures from the same domain (e.g. sexual DRV occurrence and physical DRV occurrence) will be combined in a single meta‐analysis for overall DRV occurrence using robust variance estimation; if feasible, they will also contribute to separate comparisons based on DRV subtype. Where studies report multiple measures for the same outcome (e.g. different scales for the same DRV subtype), we will prioritise the outcome measure used most frequently across our included studies for data synthesis. If no single measure predominates across the included studies, we will select the measure with the most evidence of reliability and validity. Search methods for identification of studies We will refine our original search strategy to include new databases and additional relevant MeSH (Medical Subject Headings) terms. We will consider both published and unpublished work eligible for inclusion in the review. A Cochrane Information Specialist will advise on the search strategy, applying the peer review of electronic search strategies (PRESS) checklist for peer review [75]. There will be no restriction on language or date of publication. We will assess articles published in languages other than those spoken by the review authors by seeking support from Cochrane Engage and using online translation tools (e.g. Google Translate). Where possible, we will seek support from fluent speakers to verify key information. If it is not possible to translate articles or determine their eligibility, we will list them as 'studies awaiting classification'. We will document all translation procedures to ensure transparency. Electronic searches We will search the following electronic sources. Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library.US National Institutes of Health Ongoing Trials Registry ClinicalTrials.gov (https://clinicaltrials.gov).WHO International Clinical Trials Registry Platform (ICTRP; https://trialsearch.who.int/).MEDLINE (Ovid; from 1946).Embase (Ovid; from 1974).CINAHL (Cumulative Index to Nursing and Allied Health Literature; from 1937).PsycINFO (Ovid; from 1806).Applied Social Sciences Index and Abstracts (ASSIA; ProQuest; from 1987).Sociological Abstracts (ProQuest; from 1952).Social Science Citation Index (Web of Science; from 1970).Education Resources Information Center (ERIC; ProQuest; from 1966).National Criminal Justice Reference Service Abstracts (ProQuest; from 1970).metaREGISTER (mRCT; Current Controlled Trials; from 1998).ZETOC (conference proceedings; Zetoc; from 1993). Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library. Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library. US National Institutes of Health Ongoing Trials Registry ClinicalTrials.gov (https://clinicaltrials.gov). US National Institutes of Health Ongoing Trials Registry ClinicalTrials.gov (https://clinicaltrials.gov). WHO International Clinical Trials Registry Platform (ICTRP; https://trialsearch.who.int/). WHO International Clinical Trials Registry Platform (ICTRP; https://trialsearch.who.int/). MEDLINE (Ovid; from 1946). MEDLINE (Ovid; from 1946). Embase (Ovid; from 1974). Embase (Ovid; from 1974). CINAHL (Cumulative Index to Nursing and Allied Health Literature; from 1937). CINAHL (Cumulative Index to Nursing and Allied Health Literature; from 1937). PsycINFO (Ovid; from 1806). PsycINFO (Ovid; from 1806). Applied Social Sciences Index and Abstracts (ASSIA; ProQuest; from 1987). Applied Social Sciences Index and Abstracts (ASSIA; ProQuest; from 1987). Sociological Abstracts (ProQuest; from 1952). Sociological Abstracts (ProQuest; from 1952). Social Science Citation Index (Web of Science; from 1970). Social Science Citation Index (Web of Science; from 1970). Education Resources Information Center (ERIC; ProQuest; from 1966). Education Resources Information Center (ERIC; ProQuest; from 1966). National Criminal Justice Reference Service Abstracts (ProQuest; from 1970). National Criminal Justice Reference Service Abstracts (ProQuest; from 1970). metaREGISTER (mRCT; Current Controlled Trials; from 1998). metaREGISTER (mRCT; Current Controlled Trials; from 1998). ZETOC (conference proceedings; Zetoc; from 1993). ZETOC (conference proceedings; Zetoc; from 1993). Search Strategy We will use the search strategy outlined in Supplementary material 1 to search MEDLINE and adapt it to other databases. We will apply the Cochrane Highly Sensitive Search Strategy (HSSS) for identifying randomised controlled trials in MEDLINE: sensitivity‐maximising version (2023 revision) [76]. Searching other resources We will handsearch for relevant publications from the past five years in key journals, including Journal of Interpersonal Violence, Child Abuse and Neglect, Trauma Violence & Abuse, Aggression and Violent Behaviour, Lancet Child & Adolescent Health, Journal of Youth and Adolescence, and Pediatrics. We will screen the reference lists of recent systematic reviews on this topic [5, 43, 47, 77], as well as further relevant reviews identified through our literature search, for potentially relevant studies. We will also screen the proceedings from the past five years of relevant conferences (e.g. Sexual Violence Research Initiative (SVRI) Forum, VISION Annual Conference) to identify relevant unpublished material. We will contact experts in the field and key national and international organisations to ask them to share any published, unpublished, and ongoing work relevant to the review. Finally, we will examine postpublication amendments to all included and potentially eligible studies – including retractions, expressions of concern, errata, and corrigenda – by checking publication records in bibliographic databases, reviewing journal websites, and consulting relevant retraction databases (e.g. Retraction Watch Database). If we find that a study has been retracted or is subject to serious concerns, we will exclude it or handle it according to guidance outlined in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions [76]. We will document any amendments in the review. Data collection and analysis We will use Covidence to collate the search results across databases, remove duplicates, screen results, and extract data [78]. We will use RevMan for data management and synthesis [79]. Selection of studies Two review authors (GF and YK, SH, CH, CF, GJMT, or JN) will independently screen the titles and abstracts of articles identified by the search to exclude clearly irrelevant results. We will reject articles at this stage if the title or abstract does not focus on prevention of DRV in adolescents or young adults. If insufficient information in the title and abstract precludes a decision, we will retrieve the article for full‐text screening. Two review authors (GF and YK, SH, CH, CF, GJMT, or JN) will independently screen the full‐text articles against our full eligibility criteria. We will conduct a pilot of the full eligibility criteria against 10 records to ensure they can be applied consistently; if any disagreements arise due to lack of clarity, we will refine the criteria. We will collate multiple articles from the same study to ensure the study is the unit of interest in our review. At both stages of screening, we will resolve any disagreements by consultation with a third review author. If needed, we will consult study authors for more information. Where a review author has been involved in the conduct, analysis, or publication of a potentially eligible study, they will recuse themselves from the selection process for that study. We will list all studies excluded during full‐text screening in a 'Characteristics of excluded studies' table and document the main reason for exclusion. We will produce a PRISMA flowchart to illustrate the study selection process. Data extraction and management We will develop a data collection form to extract data from our included studies, and we will pilot the form on five studies. We will test‐populate a 'Characteristics of included studies' table and a risk of bias assessment with the pilot data and adjust the form as needed. Two review authors (GF and YK, SH, CH, CF, GJMT, or JN) will independently extract study characteristics including study design, participants, interventions, controls, and outcomes. We will compare results in RevMan to assure agreement, resolving any discrepancies by discussion or by consulting a third review author. If any discrepancy remains unresolved after this process, we will contact the study authors for clarification. Any discrepancies remaining thereafter will be noted alongside the extracted data in a 'Characteristics of included studies' table. Where a review author has been involved in the conduct, analysis, or publication of an included study, they will recuse themselves from the data extraction and discrepancy resolution for that study. For studies with multiple reports, the two review authors responsible for data extraction will review the reports to select and agree on a primary article for sourcing the data. Where data are missing, we will contact the study authors for clarification and tag studies as awaiting classification. We will also re‐attempt to extract full data from the studies listed as awaiting classification in the previous review. Where study authors are unable to provide the missing data or do not respond, the two extracting review authors will consider whether reasonable assumptions regarding the missing data can be made to allow for inclusion. These assumptions will be reported alongside extracted data in the 'Characteristics of included studies' table. Studies with unobtainable data that also lack grounds for reasonable assumptions will be listed in a 'Characteristics of studies awaiting classification' table. Risk of bias assessment in included studies For each study result that contributes to an outcome in our summary of findings table (Certainty of the evidence assessment), two review authors (GF and YK, SH, CH, CF, GJMT, or JN) will assess the risk of bias using the Cochrane risk of bias tool (RoB 2) for individually randomised trials [80], and RoB 2 for cluster‐randomised trials [81]. We will assess the risk of bias for our critical outcomes across three time points (short term, medium term, and long term, as defined in the 'Timing of outcome assessment' section (Important outcomes)). The effect of interest for this review is the effect of assignment to the intervention (i.e. the intention‐to‐treat (ITT) effect). We will initially pilot RoB 2 on five studies to ensure criteria are applied consistently. The pairs of review authors will discuss any disagreements, referring to the full guidance on the RoB 2 website (https://www.riskofbias.info/) and the relevant chapters of the Cochrane Handbook for Systematic Reviews of Interventions [82, 83]. If necessary, a third review author will adjudicate. Where a review author has been involved in the conduct, analysis, or publication of an included study, they will recuse themselves from the risk of bias assessment and disagreement resolution for that study. RoB 2 covers the following five domains. Bias arising from the randomisation process.Bias due to deviations from intended interventions.Bias due to missing outcome data.Bias in measurement of the outcome.Bias in selection of the reported result. Bias arising from the randomisation process. Bias arising from the randomisation process. Bias due to deviations from intended interventions. Bias due to deviations from intended interventions. Bias due to missing outcome data. Bias due to missing outcome data. Bias in measurement of the outcome. Bias in measurement of the outcome. Bias in selection of the reported result. Bias in selection of the reported result. We will answer the signalling questions for each domain with the response options 'yes', 'probably yes', 'probably no', 'no', and 'no information', providing supporting information (e.g. brief quotes from study texts) for our answers. We will apply the RoB 2 algorithms to map these responses to proposed risk of bias judgements across three levels: 'high risk of bias', 'some concerns', or 'low risk of bias'. Reviewing the five domain‐level risk of bias judgments, we will use the RoB 2 criteria to propose an overall risk of bias judgment for the outcome. The assessing review authors will verify both domain and overall judgments; if appropriate and justified, they may overrule the algorithm‐proposed judgment. Where reasonable, we will propose a direction of the bias for each domain judgment and overall outcome judgment. We will report the proposed judgments, the justifying information, and the source of the justifying information in full risk of bias tables and present the overall judgments graphically in the forest plots of the meta‐analyses. Measures of treatment effect Dichotomous data To summarise dichotomous data, we will calculate odds ratios (ORs) with 95% confidence intervals (CIs) if events are infrequent. Otherwise, we will calculate risk ratios (RRs) with 95% CIs, because they are easier to understand. Continuous data We will report continuous data as mean differences (MDs) with 95% CIs where studies have used the same measurement scale, and standardised mean differences (SMDs) with 95% CIs where studies have used different scales. Where scales measuring the same outcome differ in directionality (i.e. a high score on one scale indicates worse outcomes and a high score on another scale indicates better outcomes), we will multiply the mean values of one set of studies by −1 to ensure all continuous outcomes have the same directionality and meaning prior to standardisation [84]. Ordinal data We will report ordinal data (e.g. measurement scale scores) as continuous when the scale has many levels, and as dichotomous when the categories are few and an established, defensible cut‐point exists for splitting them [85]. Skewed data As meta‐analyses of means rely upon the assumption of an approximately normal distribution of outcome data, we will assess all continuous outcomes for skew using the outcomes' means and standard deviations (SDs) [86]. If there is strong evidence of a skewed distribution, we will report the results of these included studies narratively. Unit of analysis issues Cluster‐randomised trials If we find eligible cluster‐randomised trials, we will follow the guidance on relevant statistical methods outlined in the Cochrane Handbook for Systematic Reviews of Interventions [83]. Where study analyses have adequately accounted for cluster design, we will extract the effect estimate from the study directly. If study analyses have not accounted for cluster design, we will extract the following information to conduct appropriate adjustments to study data. The mean size of each cluster, or data to calculate this (i.e. number of groups/clusters randomised to each intervention and the total number of study participants).Outcome data for the total number of individuals (e.g. proportions for dichotomous outcomes, mean and SD for continuous outcomes).An estimate of the intraclass correlation coefficient (ICC), which describes the relative variability in outcomes within and between clusters. The mean size of each cluster, or data to calculate this (i.e. number of groups/clusters randomised to each intervention and the total number of study participants). The mean size of each cluster, or data to calculate this (i.e. number of groups/clusters randomised to each intervention and the total number of study participants). Outcome data for the total number of individuals (e.g. proportions for dichotomous outcomes, mean and SD for continuous outcomes). Outcome data for the total number of individuals (e.g. proportions for dichotomous outcomes, mean and SD for continuous outcomes). An estimate of the intraclass correlation coefficient (ICC), which describes the relative variability in outcomes within and between clusters. An estimate of the intraclass correlation coefficient (ICC), which describes the relative variability in outcomes within and between clusters. We will calculate the 'design effect' for the study and use it to inflate the standard error (SE) of the effect estimate from the study analysis, ignoring clustering (i.e. the effect measure from an analysis as an individually randomised trial). We will combine these estimates and their adjusted SE with those from parallel designs using the generic inverse variance method in RevMan. If the ICC is not provided, we will contact the study authors or use external estimates obtained from similar studies. We will use existing databases of ICCs to identify an ICC that matches our outcome measures and cluster types most closely. If we are unable to identify an appropriate ICC, we will perform sensitivity analyses using a high ICC of 0.1, a moderate ICC of 0.01, and a small ICC of 0.001. Multiple intervention groups If any studies have multiple intervention groups, we will make single pairwise comparisons. In other words, we will combine all relevant intervention groups (i.e. educational and skills‐based interventions aiming to prevent relationship or dating violence) into a single group, and all relevant control groups into a single group. We will then make comparisons between the combined intervention group and the combined control group. For dichotomous outcomes, we will sum the sample sizes and number of outcomes across groups. For continuous outcomes, we will combine means and SDs [84]. If this limits the investigation of potential sources of heterogeneity, we will compare each intervention group separately against a proportion of the common control group to avoid double‐counting of individuals in the common control group. Repeated observations Where studies measure more than one outcome of interest, we will ensure each outcome is included in a separate meta‐analysis. For outcomes measured at multiple time points, we will use one appropriate outcome measure, as outlined above in the 'Timing of outcome assessment' section (Important outcomes), and we will conduct separate meta‐analyses for the three follow‐up time frames of interest (short‐term, medium‐term, and long‐term follow‐up), ensuring each study only contributes one outcome. Re‐occurring events Given our definition of DRV occurrences, violence outcomes could be reported as count data. We will treat count data as continuous data to avoid a unit of analysis error [84]. Dealing with missing data Where data are missing from a study report, we will attempt to retrieve them through other sources such as trial register results, protocols, and conference proceedings. If necessary, we will contact trial authors by email to request the missing data. If we receive no reply after sending two reminders, or if the trial authors state missing data are not available, we will take the following steps. Where missing data are reported in graphs without exact values, we will extract approximate values using digital software, such as Plot Digitizer [87].Where summary data are missing but an effect estimate is reported, we will attempt to calculate the summary data using the existing data or attempt to include the study in the meta‐analysis using the generic inverse variance method as described in section 6.3 of the Cochrane Handbook for Systematic Reviews of Interventions [84].We will examine trial data on an ITT basis as far as possible, by including all participants randomised to each group in the analysis, and by analysing all participants in the group to which they were allocated, regardless of whether they received the allocated intervention.We will report the level of missing data and consider its effect on the certainty of the evidence for the affected outcomes.We will prefer multiple imputation over complete‐case analysis, where these data are reported. Where missing data are reported in graphs without exact values, we will extract approximate values using digital software, such as Plot Digitizer [87]. Where missing data are reported in graphs without exact values, we will extract approximate values using digital software, such as Plot Digitizer [87]. Where summary data are missing but an effect estimate is reported, we will attempt to calculate the summary data using the existing data or attempt to include the study in the meta‐analysis using the generic inverse variance method as described in section 6.3 of the Cochrane Handbook for Systematic Reviews of Interventions [84]. Where summary data are missing but an effect estimate is reported, we will attempt to calculate the summary data using the existing data or attempt to include the study in the meta‐analysis using the generic inverse variance method as described in section 6.3 of the Cochrane Handbook for Systematic Reviews of Interventions [84]. We will examine trial data on an ITT basis as far as possible, by including all participants randomised to each group in the analysis, and by analysing all participants in the group to which they were allocated, regardless of whether they received the allocated intervention. We will examine trial data on an ITT basis as far as possible, by including all participants randomised to each group in the analysis, and by analysing all participants in the group to which they were allocated, regardless of whether they received the allocated intervention. We will report the level of missing data and consider its effect on the certainty of the evidence for the affected outcomes. We will report the level of missing data and consider its effect on the certainty of the evidence for the affected outcomes. We will prefer multiple imputation over complete‐case analysis, where these data are reported. We will prefer multiple imputation over complete‐case analysis, where these data are reported. Where study authors provide data following direct correspondence, we will make a note of this in our data collection form and risk of bias assessments. Reporting bias assessment For meta‐analyses including at least 10 studies, we will draw funnel plots to assess the presence of possible publication bias. While funnel plot asymmetry may indicate publication bias, we will consider other possible explanations and discuss these in the text of the review [88]. We will assess the risk of bias due to selective reporting or non‐reporting of results using the ROB‐ME (Risk of Bias due to Missing Evidence) [89] tool. Two review authors will independently conduct ROB‐ME assessments, resolving any disagreements by discussion or by consulting a third review author. For review findings reported narratively, we will assess the risk of bias due to missing evidence by considering whether there are any missing outcome data in these studies, and whether there is a reasonable likelihood that the outcomes are missing due to their P value, magnitude, or direction. We will discuss the possible impact of missing results on the narrative summary findings. Synthesis methods We will use a random‐effects model, as we expect to find clinical diversity and methodological heterogeneity across studies, such as differences in settings, populations, and intervention characteristics [90]. This model assumes that the true effect may vary between studies. We will use the Restricted Maximum Likelihood (REML) estimator to estimate between‐trial variance. To calculate a CI for the meta‐analysis effect estimate when there are at least three studies and the estimate of heterogeneity is greater than zero, we will use the Hartung‐Knapp‐Sidik‐Jonkman method [85]. In other scenarios (i.e. in pooled analyses of two studies, or where the estimate of heterogeneity is equal to zero), we will use the Wald‐type method. If combining data across studies in a meta‐analysis is inappropriate due to substantial heterogeneity, as defined in the Investigation of heterogeneity and subgroup analysis section below, we will display the results of included studies in a forest plot without the pooled estimate. Alternatively, we will provide a descriptive summary, grouping studies by intervention type, population characteristics, and outcomes, and summarising effect estimates, direction of effect, and patterns across studies. We will clearly document all synthesis decisions. Investigation of heterogeneity and subgroup analysis We will formally assess heterogeneity using the Chi2 test (for evidence that the differences in effect estimates could be due to chance alone) and the I2 statistic (to quantify the proportion of variability in effect estimates due to heterogeneity rather than chance). We will apply a threshold of P < 0.10 for the Chi2 test given its low power for studies with small sample sizes. To interpret I2 values, we will use the following rough thresholds from the Cochrane Handbook for Systematic Reviews of Interventions [85]. 0% to 40%: might not be important.30% to 60%: may represent moderate heterogeneity.50% to 90%: may represent substantial heterogeneity.75% to 100%: considerable heterogeneity. 0% to 40%: might not be important. 0% to 40%: might not be important. 30% to 60%: may represent moderate heterogeneity. 30% to 60%: may represent moderate heterogeneity. 50% to 90%: may represent substantial heterogeneity. 50% to 90%: may represent substantial heterogeneity. 75% to 100%: considerable heterogeneity. 75% to 100%: considerable heterogeneity. We anticipate substantial clinical and methodological heterogeneity between studies due to differences in setting, study population characteristics, and intervention characteristics. We will investigate potential sources of heterogeneity using subgroup analysis and meta‐regression. We plan to conduct the following prespecified subgroup analyses, provided there are at least 10 studies per comparison. Age group (adolescents versus young adults). Interventions may have different effects according to age due to factors such as developmental stage, relationship experience, and receptivity to prevention messages.Gender. Interventions may have different effects according to gender, as patterns and rates of DRV differ by gender, and different genders might respond differently to the same intervention.Intervention structure (single‐ versus multi‐component interventions). Single‐component and multi‐component interventions may have different effects due to differences in intensity and duration.Income classification of countries (LMICs versus high‐income countries (HICs)). Intervention effectiveness may differ between LMICs and HICs due to differences in resources, service availability, social norms, and implementation context.Setting (higher education versus secondary education versus other setting). We will explore whether interventions have different effects according to the setting in which they are delivered.Level of prevention (primary prevention versus secondary prevention). We will explore whether interventions have different effects according to whether they are primary prevention interventions (aimed at general populations) or secondary prevention interventions (aimed at higher‐risk populations). Age group (adolescents versus young adults). Interventions may have different effects according to age due to factors such as developmental stage, relationship experience, and receptivity to prevention messages. Age group (adolescents versus young adults). Interventions may have different effects according to age due to factors such as developmental stage, relationship experience, and receptivity to prevention messages. Gender. Interventions may have different effects according to gender, as patterns and rates of DRV differ by gender, and different genders might respond differently to the same intervention. Gender. Interventions may have different effects according to gender, as patterns and rates of DRV differ by gender, and different genders might respond differently to the same intervention. Intervention structure (single‐ versus multi‐component interventions). Single‐component and multi‐component interventions may have different effects due to differences in intensity and duration. Intervention structure (single‐ versus multi‐component interventions). Single‐component and multi‐component interventions may have different effects due to differences in intensity and duration. Income classification of countries (LMICs versus high‐income countries (HICs)). Intervention effectiveness may differ between LMICs and HICs due to differences in resources, service availability, social norms, and implementation context. Income classification of countries (LMICs versus high‐income countries (HICs)). Intervention effectiveness may differ between LMICs and HICs due to differences in resources, service availability, social norms, and implementation context. Setting (higher education versus secondary education versus other setting). We will explore whether interventions have different effects according to the setting in which they are delivered. Setting (higher education versus secondary education versus other setting). We will explore whether interventions have different effects according to the setting in which they are delivered. Level of prevention (primary prevention versus secondary prevention). We will explore whether interventions have different effects according to whether they are primary prevention interventions (aimed at general populations) or secondary prevention interventions (aimed at higher‐risk populations). Level of prevention (primary prevention versus secondary prevention). We will explore whether interventions have different effects according to whether they are primary prevention interventions (aimed at general populations) or secondary prevention interventions (aimed at higher‐risk populations). Subgroup analyses will be based on study‐level variables. This approach allows for formal testing of effect modification using the Chi2 test and the I2 statistic for subgroup differences. If data are not amenable to meta‐analysis, we will explore heterogeneity using summary tables of study results by subpopulation or intervention factors, and forest plots without summary statistics for visual assessment of trends in results across studies. Sensitivity analysis We will assess the robustness of our findings through the following approaches. We will examine funnel plot asymmetry and investigate potential causes for the asymmetry using meta‐regression and sensitivity analysis, comparing differences in effect estimates by trial size. For the sensitivity analysis, we will repeat the primary analysis after excluding small trials, defined as trials with fewer than 100 participants in total [91].If using external estimates of ICC for cluster‐randomised trials, we will conduct sensitivity analyses of effect estimates at varying values of ICC, as outlined in the Unit of analysis issues section. These analyses will include the same trials as the primary analysis but will vary the ICC used to adjust the effective sample size.We will conduct sensitivity analyses to examine how summary findings may differ when trials at risk of bias are removed. We will repeat the primary analysis after removing trials with an overall high risk of bias judgement, and then after removing trials with either an overall high risk of bias judgement or some concerns.In the event of missing outcome data, we will explore use of informative missingness parameters to assess how robust the results are to different assumptions about how the underlying distributions of observed and unobserved data may differ [92, 93]. For the sensitivity analysis, we will repeat the primary analysis using a range of plausible values for the informative missingness parameters. We will examine funnel plot asymmetry and investigate potential causes for the asymmetry using meta‐regression and sensitivity analysis, comparing differences in effect estimates by trial size. For the sensitivity analysis, we will repeat the primary analysis after excluding small trials, defined as trials with fewer than 100 participants in total [91]. We will examine funnel plot asymmetry and investigate potential causes for the asymmetry using meta‐regression and sensitivity analysis, comparing differences in effect estimates by trial size. For the sensitivity analysis, we will repeat the primary analysis after excluding small trials, defined as trials with fewer than 100 participants in total [91]. If using external estimates of ICC for cluster‐randomised trials, we will conduct sensitivity analyses of effect estimates at varying values of ICC, as outlined in the Unit of analysis issues section. These analyses will include the same trials as the primary analysis but will vary the ICC used to adjust the effective sample size. If using external estimates of ICC for cluster‐randomised trials, we will conduct sensitivity analyses of effect estimates at varying values of ICC, as outlined in the Unit of analysis issues section. These analyses will include the same trials as the primary analysis but will vary the ICC used to adjust the effective sample size. We will conduct sensitivity analyses to examine how summary findings may differ when trials at risk of bias are removed. We will repeat the primary analysis after removing trials with an overall high risk of bias judgement, and then after removing trials with either an overall high risk of bias judgement or some concerns. We will conduct sensitivity analyses to examine how summary findings may differ when trials at risk of bias are removed. We will repeat the primary analysis after removing trials with an overall high risk of bias judgement, and then after removing trials with either an overall high risk of bias judgement or some concerns. In the event of missing outcome data, we will explore use of informative missingness parameters to assess how robust the results are to different assumptions about how the underlying distributions of observed and unobserved data may differ [92, 93]. For the sensitivity analysis, we will repeat the primary analysis using a range of plausible values for the informative missingness parameters. In the event of missing outcome data, we will explore use of informative missingness parameters to assess how robust the results are to different assumptions about how the underlying distributions of observed and unobserved data may differ [92, 93]. For the sensitivity analysis, we will repeat the primary analysis using a range of plausible values for the informative missingness parameters. Certainty of the evidence assessment We will assess the certainty of evidence for our critical outcomes using the GRADE approach, as outlined in the GRADE handbook [94]. The GRADE approach considers five domains that may influence the certainty of evidence: risk of bias, inconsistency, indirectness, imprecision, and publication bias. Using GRADEpro GDT software [95], two review authors (GF and YK, SH, CH, CF, GJMT, or JN) will independently consider these domains for the body of evidence of each critical outcome and specify a level of certainty (high, moderate, low, or very low). They will resolve any discrepancies in judgement by discussion or by consulting a third review author. Where a review author has been involved in the conduct, analysis, or publication of an included study, they will recuse themselves from the GRADE assessment and disagreement resolution for that study. We will report the critical outcomes for our main comparison (educational and skills‐based interventions versus inactive controls for adolescents and young adults) in a summary of findings table. The summary of findings table will include relative and absolute effect estimates, the number of participants and studies contributing to each outcome, and the certainty of the evidence based on GRADE criteria. We will justify all decisions to downgrade evidence certainty in footnotes. If meta‐analysis of outcomes is not possible, we will create a narrative summary of findings table. Equity considerations We will consider the impact of health inequities in this review following guidance in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions. We will use the PROGRESS‐Plus framework (equity framework covering Place of residence, Race/ethnicity/culture/language, Occupation, Gender/sex, Religion, Education, Socioeconomic status, Social capital, plus other discrimination‐ and time‐dependent factors) to identify and assess populations who may be more likely to experience DRV or less likely to benefit from interventions [96]. We will assess differences by age, gender, sexual orientation, ethnicity, household income (or equivalent measures of socioeconomic status), and country income classification. During data extraction, we will record these equity‐relevant characteristics and include them in the 'Characteristics of included studies' table. Where sufficient data are available, we will assess whether intervention effects differ across these characteristics. For age, gender, and country income classification, this assessment will be part of our planned subgroup analyses, as described in the Investigation of heterogeneity and subgroup analysis section. We will describe the extent to which included studies report data on these equity‐relevant characteristics and consider the applicability of the findings to populations who may experience disadvantage or inequity. If we find evidence of differential intervention effects in our subgroup analyses, we will report these in the 'Synthesis of results' section. If data are insufficient to conduct the planned subgroup analyses, we will report this as a limitation and provide descriptive data of these factors. Consumer involvement We will share the preliminary results of our data synthesis with consumers (e.g. survivors of DRV, professionals working with survivors, and policymakers) in small group sessions. We will seek views on the impact of our results for these consumer groups and what priorities consumers see for DRV interventional research given the results. We will seek feedback on the accessibility of our draft tables and review article for consumers and adjust as needed to improve readability and access. Given the health inequities in DRV prevalence and outcomes, we will seek to invite a diverse group of consumers as per PROGRESS‐Plus characteristics. Supporting Information Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016376. Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material. Supplementary material 1 Search strategies