Intimate partner violence (IPV) is the most common form of violence against women worldwide (World Health Organization 2021). IPV encompasses physical violence, sexual abuse, psychological intimidation, economic coercion, and other forms of controlling behavior.Footnote 1 Survivors of IPV may experience a variety of physical and psychological ailments, including recurring headaches, chronic pain, depression, and anxiety (World Health Organization 2013). Survivors may also suffer severe economic consequences, forgoing education and income or exiting the labor force entirely (Peterson et al. Reference Peterson, Kearns, McIntosh, Estefan, Nicolaidis, McCollister, Gordon and Florence2018).
In recent decades, employment programs targeting women have become one of the most prominent policy tools for elevating women’s status and improving their welfare, especially in low- and middle-income countries (Brodmann et al. Reference Brodmann, Galasso and Devoto2017). Theoretically, there are multiple mechanisms through which women’s employment might mitigate IPV. Employment might strengthen women’s bargaining power within the household, allowing them to demand more equitable treatment from their spouses (Aizer Reference Aizer2010; Farmer and Tiefenthaler Reference Farmer and Tiefenthaler1997). It might also help alleviate the stress – and, potentially, aggression – associated with poverty (Jewkes Reference Jewkes2002; Mani et al. Reference Mani, Mullainathan, Shafir and Zhao2013). Alternatively, employment might limit the time women spend in physical proximity to their intimate partners, thus curtailing opportunities for abuse (Dugan et al. Reference Dugan, Nagin and Rosenfeld1999). These mechanisms predict a negative relationship between women’s employment and IPV – a prediction that has found empirical support in some settings (Aizer Reference Aizer2010; Anderberg et al. Reference Anderberg, Rainer, Wadsworth and Wilson2016; Chin Reference Chin2012; Gulesci et al. Reference Gulesci, Puente–Beccar and Ubfal2021; Sanin Reference Sanin2023).
But the impact of women’s economic empowerment on IPV remains ambiguous, both theoretically and empirically. Some economists argue that if men use violence ‘instrumentally’ to reassert control over the allocation of household resources as women’s bargaining power improves, then women’s employment may exacerbate IPV (Angelucci Reference Angelucci2008; Eswaran and Malhotra Reference Eswaran and Malhotra2011; Ramos Reference Ramos2018). Sociologists similarly argue that women’s employment may provoke ‘backlash’ from men who use IPV to maintain dominance in the household (Erten and Keskin Reference Erten and Keskin2021; Field et al. Reference Field, Pande, Rigol, Schaner and Troyer Moore2021). These theories predict a positive relationship between women’s employment and IPV – a prediction that has also found some empirical support (Amaral et al. Reference Amaral, Bandyopadhyay and Sensarma2015; Bhalotra et al. Reference Bhalotra, Kambhampati, Rawlings and Siddique2021; Heath Reference Heath2014). Which of these theories is more correct, and under what conditions, remains a matter of debate. As Keith et al. (Reference Keith, Hyslop and Richmond2023, 1457) note in a recent review, existing studies are ‘equivocal’ at best.
But these studies, while valuable, are limited in at least five ways. First, most studies of women’s economic empowerment focus on cash transfers and microcredit rather than employment.Footnote 2 Employment constitutes a more direct threat to men’s status as breadwinners, potentially exacerbating male backlash, especially since – relative to cash – employment is harder for women to hide (Kotsadam and Villanger Reference Kotsadam and Villanger2022). Conversely, employment reduces the time women spend in physical proximity to their intimate partners in a way that cash does not, thus potentially limiting opportunities for IPV. Employment may also provide social and emotional benefits beyond income alone, including feelings of confidence, resilience, connectedness, and autonomy (Barnett, A. Jamal and Monroe Reference Barnett, Jamal and Monroe2021), which may increase women’s willingness to confront their spouses about abuse (Rothman et al. Reference Rothman, Hathaway, Stidsen and de Vries2007). Some employment programs (including the ones we study here) also generate public goods, which may create more pronounced spillover effects than cash or microcredit alone (Gehrke and Hartwig Reference Gehrke and Hartwig2018).
Second, most studies are observational, requiring strong and sometimes implausible assumptions about exogeneity and excludability.Footnote 3 Third, household bargaining models predict that employment opportunities for women should affect IPV even among women who do not immediately take advantage of those opportunities. Few studies are able to test this subtle but crucial implication of the household bargaining framework. Fourth, the impact of women’s employment programs on IPV may depend on the extent to which they also benefit men. The literature has generally overlooked this key question for program design.Footnote 4 Finally, few studies focus on the contexts in which patriarchal norms are most deeply entrenched. It is precisely in these settings where women’s economic empowerment is most urgent and controversial.
We contribute to this body of research through parallel experimental evaluations of the Emergency Labor-Intensive Investment Project (ELIIP) in Egypt and the Community Works and Local Participation (CWLP) program in Tunisia. Both interventions provided jobs for the ‘ultra-poor’ through externally funded, locally implemented public works projects. The programs shared many similarities and, as we show below, both succeeded in their primary purpose of increasing employment, income, and savings among participating women. In this paper we explore whether these beneficial economic effects were accompanied by equally beneficial (or possibly adverse) effects on IPV.
Despite their similarities, ELIIP provided longer-term jobs that disproportionately benefited women in sectors (for example, childcare) in which women were more likely to seek and find employment after the program ended, and to experience the positive ‘downstream effects on women’s empowerment’ associated with employment in traditionally female-dominated industries in Middle East and North African (MENA) countries (Barnett et al. Reference Barnett, Jamal and Monroe2021, 967). ELIIP thus constituted a stronger shock to the balance of power within participating households. Importantly, however, our goal is not to demonstrate conclusively that the programs’ disparate effects on IPV are a function of these differences in program design. Instead, our aim is to offer a unified theoretical framework drawn from multiple literatures to understand the relationship between women’s employment and IPV; use that framework to generate empirical predictions about the impact of each intervention on IPV; and assess which theory best fits the data.
We evaluate the interventions using randomized controlled trials with similar randomization, sampling, measurement, and estimation strategies. We randomized participation at both the community and individual levels and surveyed four distinct populations at endline, allowing us to estimate causally identified intention-to-treat, spillover, and general equilibrium effects. We also measured outcomes in both the short (roughly one to seven months after implementation was complete) and long (more than two years after implementation) terms, allowing us to test whether the impact of women’s employment on IPV shifts or decays over time (Bobonis et al. Reference Bobonis, González-Brenes and Castro2013; Kotsadam and Villanger Reference Kotsadam and Villanger2022). We discuss the ethics of the study in the Research Design section and in Section A of the Supplementary Information (SI).
Our results are consistent with a bargaining model in which men perpetrate IPV ‘instrumentally’ to maintain dominance in the household as women’s outside options improve and their bargaining power increases. We find that ELIIP in Egypt exacerbated IPV in the short term – an effect driven in particular by psychological intimidation and economic coercion. This effect does not appear to be an artifact of increased reporting of IPV among survivors. We also find that ELIIP’s adverse effects on IPV spilled over onto women in treatment villages who were eligible for the program but were not randomly selected to participate. This too is consistent with bargaining models in which IPV is instrumental and spouses’ reservation utilities are a function of potential rather than actual income – a subtle but essential component of the household bargaining framework (Aizer Reference Aizer2010). Also consistent with this framework, we find no evidence that CWLP in Tunisia affected IPV in either direction, at least in the short run.
We then test mechanisms and consider alternative explanations. Again consistent with a bargaining model in which men perpetrate IPV instrumentally to counteract women’s economic empowerment, we find that ELIIP increased women’s discretion over their own spending – a measure of control over household resources, the primary mechanism linking women’s employment to instrumental IPV – while CWLP had no effect on women’s discretion over spending in either direction. We show that these distinct effects in Tunisia are unlikely to be a function of similarly differential effects on women’s employment, income, or savings; on social norms elevating women’s rights; or on the rate of divorce or separation among participating women. In SI Section M we also conduct a variety of plausibility probes to substantiate the assumptions underlying our theoretical framework and empirical predictions.
In extensions of these analyses, we show that ELIIP heightened psychological distress among eligible women in treatment villages, regardless of whether or not they were randomly selected to participate. In contrast, CWLP appears to have improved women’s psychological wellbeing in the short term, perhaps because its beneficial effects on women’s employment, income, and savings were not offset by an increase in IPV. We find no evidence that ELIIP’s adverse effects on IPV spilled over onto randomly sampled women from the community writ large. These effects did, however, persist and potentially become more severe over time, as evidenced by an increase in physical violence in the long term. A possible (albeit speculative) explanation for this result is that men used psychological intimidation and economic coercion to attempt to restore the balance of power in the household, then resorted to physical violence over time as those attempts failed (Bobonis et al. Reference Bobonis, González-Brenes and Castro2013). We again find no evidence that CWLP affected IPV in either direction in the long term.
Our paper contributes to multiple literatures. First and most directly, we contribute to research on the effects of women’s economic empowerment on IPV (see Baranov et al. Reference Baranov, Cameron, Contreras Suarez and Thibout2021 for a summary and review). Second, we build on studies of public works programs, most of which focus on economic outcomes alone (Gehrke and Hartwig Reference Gehrke and Hartwig2018). Third, we complement a small but growing literature on IPV and other forms of violence against women in political science (see Blaydes et al. Reference Blaydes, Fearon and MacDoland2025 for a review). Recent years have witnessed a proliferation of studies by political scientists on the causes of sexual violence during civil war (Cohen Reference Cohen2013, Reference Cohen2016); the effects of civil war on attitudes towards violence against women (Lindsey Reference Lindsey2022); the use of mass media to change social norms around reporting of IPV (Green et al. Reference Green, Wilke and Cooper2020); and the impact of ‘gender balancing’ on police responsiveness to domestic violence (Jassal Reference Jassal2020; Karim et al. Reference Karim, Gilligan, Blair and Beardsley2018). We extend this literature by exploring the implications of women’s economic empowerment for IPV in a region characterized by severe gender imbalances and deeply entrenched patriarchal norms.
Theoretical Framework
Women’s economic empowerment has become one of the most widely embraced mechanisms for mitigating IPV worldwide.Footnote 5 Yet the magnitude and even direction of this relationship remains theoretically and empirically contested (Angelucci and Heath Reference Angelucci and Heath2020). In the standard household bargaining model in economics, intimate partners are assumed to have divergent preferences over the allocation of household resources.Footnote 6 Their relative bargaining power is a function of their reservation utilities (or ‘threat points’): the more attractive each partner’s options outside the relationship, the more credible their threat to leave, and the greater their bargaining power. Reservation utilities are typically modeled as the ratio of the two partners’ potential incomes if the relationship dissolves, which may or may not correspond to their actual incomes while together (Aizer Reference Aizer2010; McElroy and Horney Reference McElroy and Horney1981; Ramos Reference Ramos2018).
IPV can be incorporated into this model in multiple ways. The simplest approach is to assume that violence is purely ‘expressive’, such that it enters each partner’s utility function directly (Farmer and Tiefenthaler Reference Farmer and Tiefenthaler1997): the perpetrator (who, for compactness, we assume is the man in a heterosexual relationshipFootnote 7 ) derives some emotional or psychological utility from IPV, while the survivor (who we assume is the woman) derives some disutility. In other words, the man enjoys perpetrating IPV – perhaps because he is a sadist, or because he believes violence releases stress and frustration (Baranov et al. Reference Baranov, Cameron, Contreras Suarez and Thibout2021; Angelucci and Heath Reference Angelucci and Heath2020; Tauchen et al. Reference Tauchen, Witte and Long1991)Footnote 8 – while the woman suffers from being victimized. The man can compensate for the suffering he inflicts by transferring resources until the woman’s utility reaches her threat point, the threshold at which she is indifferent between staying and leaving.
If violence is purely expressive, then an improvement in women’s employment opportunities should mitigate IPV. The intuition is straightforward: the better the woman’s employment opportunities, the more attractive her outside options, and the more credible her threat to leave. To forestall this outcome, the man must reduce the amount of violence he inflicts. This intuition is consistent with qualitative studies documenting the myriad ways that employment can empower women to demand less abusive treatment from their spouses (Rothman et al. Reference Rothman, Hathaway, Stidsen and de Vries2007). Subtly but importantly, this result should obtain even for women who are not currently employed, as long as a positive labor demand shock increases their potential income outside the marriage; as Aizer (Reference Aizer2010, 1847) notes, ‘potential, not actual, wages determine bargaining power and levels of violence’ (emphasis in the original; see also Angelucci and Heath, Reference Angelucci and Heath2020; Baranov et al. Reference Baranov, Cameron, Contreras Suarez and Thibout2021). Thus, for example, an increase in demand for labor in industries traditionally dominated by women should reduce IPV, even for women who do not currently work in those industries.
Equally importantly, this result should only obtain when the increase in demand for women’s labor is large enough to strengthen their bargaining power and thus shift their reservation utilities. If the increase in demand for women’s labor is accompanied by an offsetting positive demand shock for men’s labor, then as long as men can reasonably expect to continue earning more than their spouses in the future,Footnote 9 their reservation utilities should remain largely unchanged. This follows from the fact that reservation utilities depend on the ratio of the two partners’ potential incomes. Theories of expressive violence thus predict that (H1a) employment opportunities that disproportionately empower women should reduce IPV, (H1b) regardless of women’s actual employment status, while (H1c) employment opportunities that empower men and women equally should have no or only weak effects on IPV.
Theories of expressive violence assume that IPV is an end in itself. IPV may also, however, be a means of extracting resources and controlling women’s behavior (Eswaran and Malhotra Reference Eswaran and Malhotra2011; Gelles Reference Gelles1974; Tauchen et al. Reference Tauchen, Witte and Long1991). In this variation on the household bargaining model, as the woman’s bargaining power increases and she exercises more discretion over the allocation of household resources, the man inflicts more violence to ‘re-assert his dominance’ (Angelucci Reference Angelucci2008, 9). This view of IPV as instrumental is related to sociological theories of ‘male backlash’ and ‘status inconsistency’, which posit that women’s employment undermines men’s status as breadwinners, and that men respond by using IPV to restore the (patriarchal) balance of power and exert control over their spouses (Erten and Keskin Reference Erten and Keskin2021; Field et al. Reference Field, Pande, Rigol, Schaner and Troyer Moore2021).
Theories of expressive and instrumental violence thus generate opposing predictions about the effects of women’s employment on IPV. Under theories of instrumental violence, since the woman gains utility from controlling household resources but loses utility from suffering abuse, the equilibrium outcome may be more rather than less IPV, as long as she remains above her threat point (Eswaran and Malhotra Reference Eswaran and Malhotra2011, 1226). As in the case of expressive violence, this result should obtain when potential employment opportunities for women improve, even if their actual employment status does not change. And as with expressive violence, new employment opportunities for both men and women should have no or only weak effects on IPV, since both partners’ reservation utilities should remain largely unaffected. Theories of instrumental violence thus predict that (H2a) employment opportunities that disproportionately empower women should increase IPV, (H2b) regardless of women’s actual employment status. In contrast, (H2c) employment opportunities that benefit men and women equally should have no or only weak effects on IPV.
Household bargaining models can also be broadened to incorporate other factors that might strengthen (or weaken) the effects of women’s employment on IPV – for example, women’s ownership of property and other durable assets (Dong Reference Dong2022); men’s dependence on their spouses’ capacity to work (Sanin Reference Sanin2023); the composition of local marriage markets (Stopnitzky Reference Stopnitzky2017); the legal landscape surrounding marriage and divorce (Gray Reference Gray1998); and the existence of other constraints that women might face when contemplating divorce or separation (for example, the presence of children in the household). We discuss differences between our study sites along some of these dimensions in SI Section B. Our goal in this paper is not to diminish the importance of these other factors, but rather to isolate the effects of employment opportunities for women on household bargaining and, by extension, IPV. Differences between women or villages within each of our study sites (for example, property ownership or the presence of children) are held constant through randomization, as discussed below.
The relationship between women’s employment and IPV can also be understood outside the context of household bargaining. Criminologists have argued that IPV is a function of ‘exposure’ – that is, the amount of time men and women spend together (Chin Reference Chin2012; Dugan et al. Reference Dugan, Nagin and Rosenfeld1999). According to this theory, employment opportunities for men or women should reduce IPV by limiting the time they spend in physical proximity to one another. Intuitively, this result should depend on actual rather than potential employment, since only actual employment should decrease exposure. Sociologists have also argued that IPV is a function of stress, which, in turn, is a function of poverty, and possibly of unemployment itself (Gelles Reference Gelles1974; Fox et al. Reference Fox, Benson, DeMaris and Van Wyk2002). Employment opportunities for men or women should thus reduce IPV by alleviating poverty – a result that should again depend on actual rather than potential employment, since only actual employment should affect poverty levels. Both of these theories predict that (H3a) employment opportunities that disproportionately empower women should decrease IPV, and that (H3b) employment opportunities that empower men and women equally should decrease IPV as well.
Importantly, none of these theories specify the type of IPV that men inflict on women. In the expressive framework, for example, men may derive utility (and women disutility) not just from physical violence, but also from psychological abuse and economic coercion. In the instrumental framework, men may manipulate the allocation of household resources not just by physically attacking their partners, but also by threatening their psychological welfare or controlling their economic behavior. The effects of women’s employment on different forms of IPV may also change over time. In the instrumental framework, for example, employment opportunities for women may increase some types of IPV in the short term and others in the longer run, for example if men use psychological intimidation to ‘coercively demand transfers’ from their spouses, then resort to physical violence ‘strategically’, depending on whether or not their spouses comply (Bobonis et al. Reference Bobonis, González-Brenes and Castro2013, 181). Our research design allows us to test for these possibilities.
Setting and Interventions
Our study involves parallel randomized controlled trials with harmonized research designs and measurement strategies in Egypt and Tunisia. As we discuss in further detail in SI Section B, while these two countries of course differ in myriad ways, they also share important similarities along dimensions that are most relevant to our study. Both countries suffer from high levels of youth unemployment, especially in rural areas, and especially among women. According to World Bank estimates, just 25 per cent of all Egyptian women aged 15–64 participated in the labor force in 2016, the year of our first endline survey – one of the lowest rates in the world.Footnote 10 Tunisia’s rate of 29 per cent was not much higher.Footnote 11
Divorce has become increasingly common in both countries, especially after a 2000 law in Egypt granted women access to khul, which allows wives to initiate divorce without their husbands’ consent. This is important because household bargaining models hinge on the availability of exit options for married couples. The crude divorce rate in Egypt and Tunisia in 2016 was 1.92 and 1.33, respectively. By way of comparison, the 2016 crude divorce rate in the United States – which perennially ranks among the countries with the highest rates in the world – was 3.21, suggesting that while divorce is less prevalent in Egypt and Tunisia than in a country like the United States, it is common enough to offer a viable exit strategy for married women.
Nonetheless, patriarchal norms remain firmly entrenched in both countries. Egypt consistently falls near the bottom of women’s empowerment rankings: in 2016, for example, it ranked 132nd out of 144 countries on the World Economic Forum’s Global Gender Gap Index.Footnote 12 Tunisia ranked 131st, with a score (0.444) that is identical to Egypt’s to three decimal places.Footnote 13 Egypt and Tunisia also scored 148th and 156th, respectively, on the Council of Foreign Relations’ Women’s Workplace Equality Index.Footnote 14
These similarities notwithstanding, Tunisia is in some respects a less repressive environment for women than Egypt. Tunisia’s Code of Personal Status laws provide women with equal rights in cases of divorce. While some degree of equality for men and women is constitutionally guaranteed in Egypt as well, change has been slower to materialize.Footnote 15 Perhaps not coincidentally, according to wave IV of the Arab Barometer survey, conducted in 2016–17 (around the same time as our first round of endline data collection), 73 per cent of Egyptians (75 per cent of men and 71 per cent of women) report that husbands should have the ‘final say’ in household decision making, compared with 58 per cent of Tunisians (65 per cent of men and 52 per cent of women).Footnote 16 And while it is increasingly culturally acceptable for women to initiate divorce in both countries, rates of approval are higher in Tunisia than in Egypt.Footnote 17
But these same surveys also highlight other important contextual similarities between the two countries. For example, 86 per cent of Egyptians (80 per cent of men and 93 per cent of women) and 88 per cent of Tunisians (81 per cent of men and 94 per cent of women) believe it is acceptable for women to work outside the home. Moreover, IPV and other forms of domestic abuse remain endemic in both countries. In its Freedom in the World report covering events of 2016, Freedom House describes IPV in Egypt as ‘widespread’.Footnote 18 Levels of IPV in Tunisia remain ‘shockingly high’ as well (Powell Reference Powell2017). Tunisian women also continue to be subjected to forced household labor and other forms of economic coercion.Footnote 19 The laws of both countries nominally protect women from some types of abuse, but enforcement is inconsistent at best. According to the Women’s Workplace Equality Index, Egypt ranks higher than Tunisia on ‘protecting women from violence’, though both countries fall below the median worldwide.Footnote 20 We provide further details on gender dynamics in these two countries in SI Section B.
The ELIIP Program in Egypt
In Egypt, we experimentally evaluate the impact of social service jobs created through the Emergency Labor-Intensive Investment Project (ELIIP), a cornerstone of Egypt’s social safety net administered by the Egyptian government’s Micro, Small and Medium Enterprises Development Agency (MSMEDA). Unlike most public works projects, which focus on the construction of roads and other ‘hard infrastructure’ (Bertrand et al. Reference Bertrand, Crépon, Marguerie and Premand2021; Rosas and Sabarwal Reference Rosas and Sabarwal2016), ELIIP provided social services across a variety of sectors through private home visits and public education campaigns. These services included (1) cleanliness and environmental stewardship (9 per cent of all ELIIP projects); (2) early childhood education (10 per cent); (3) maternal and child health awareness (35 per cent); (4) literacy (38 per cent); and (5) youth engagement in community initiatives (for example, service in orphanages) in rural and peri-urban areas (8 per cent). All projects were implemented by local Egyptian NGOs.
ELIIP projects were required to be labor-intensive, with at least 60 per cent of costs spent on labor. Projects were designed to benefit youths in particular – 80 per cent of beneficiaries had to be between 18 and 29 years old – and the ‘poorest of the poor’. Crucially for our study, 70 per cent of workers were required to be female. In practice the proportion of women recruited for ELIIP (87 per cent) exceeded even this ambitious target. We discuss the program’s eligibility criteria in further detail in SI Section B.5. Projects in our study were implemented beginning in December 2015; participating women worked 14.3 months on average and were paid an average wage of 640 Egyptian pounds (EGP) per week (approximately $83 USD at the timeFootnote 21 ). This compares to the national minimum wage of 1,200 EGP per month in 2015;Footnote 22 in our sample, it compares to average monthly earnings of 709.12 EGP among women in control villages who would have been eligible for ELIIP had their villages been randomized into treatment, or 1,034.55 EGP among randomly selected women from control villages writ large.Footnote 23 (We describe our sampling strategy in further detail below.) Projects were completed by April 2017.
By offering reasonably long-term employment in sectors in which female labor force participation is relatively high and culturally accepted, ELIIP aimed to help women gain sustainable access to work, earnings, and savings while also building confidence and developing social networks with other participating women. ELIIP jobs were designed to require few skills, and to provide social services that communities could maintain for themselves even after the program ended, and jobs that would (eventually) be accessible even to residents who were not randomly selected to participate. This is relevant for our purposes because it suggests that ELIIP should have increased potential earnings for eligible women in treatment villages even if they did not benefit from the program in a direct or immediate way.
The CWLP Program in Tunisia
In Tunisia, we experimentally evaluate the Community Works and Local Participation (CWLP) program, implemented through the Tunisian Ministry of Vocational Training and Employment. The program offered short-term jobs to unemployed residents of rural regions. Workers were required to be between 18 and 60 years old, and to have been out of work for at least twelve months. CWLP focused on Jendouba, which is among the poorest, most rural, and most underserved of Tunisia’s twenty-four governorates. A first round of CWLP projects was implemented between 2012 and 2014. Our study focuses on the second round, which began in April 2015.
Participants worked roughly three months on average, and projects were completed by September 2015. Priority was given to women, the poorest of the poor, and heads of households. Those who completed the program received a total of 825 Tunisian dinars (TND, approximately $421 USDFootnote 24 ). This compares to the national minimum wage of 12.3 TND per day in 2015, or roughly 246 TND per month.Footnote 25 In our sample, it compares to average monthly earnings of 162 TND among women in control villages who would have been eligible for the intervention had their villages been randomized into treatment, or 334.53 TND among randomly selected women in control villages more broadly.
CWLP shared many similarities with ELIIP in Egypt. Like ELIIP, the goal of CWLP was not just to provide employment experience for participants, but also to generate public goods that would enhance the quality of services available to the community as a whole; that would persist after the program ended; and that would improve future employment prospects even for eligible residents who were not randomly selected to participate. Also like ELIIP, the majority of costs associated with CWLP had to be spent on labor, and all projects had to be implemented with the assistance of local NGOs. Though CWLP did not impose quotas by age or socio-economic status, both programs focused on the poorest youths. Both programs also nominally prioritized employment opportunities for women.
But the two interventions also differed in three crucial ways. First, while ELIIP focused on delivering social services, CWLP focused on building and rehabilitating infrastructure (for example, parks, health clinics, and roads) through hard labor – jobs that women typically do not fill in these contexts. This is important because positive demand shocks in traditionally female-dominated sectors are more likely to strengthen women’s bargaining power within the household (Aizer Reference Aizer2010). It is also important because the prospect of working alongside men in traditionally male-dominated industries (for example, construction) has been found to be a ‘particularly strong deterrent to women’s interest in paid employment opportunities’, at least in the MENA region (Barnett et al. Reference Barnett, Jamal and Monroe2021, 955). In contrast, working alongside other women in traditionally female-dominated sectors has been shown to help women in highly patriarchal societies ‘adapt to work outside the home, take on new responsibilities, acquire new skills, [and] gain confidence and autonomy’, potentially opening a ‘wider range’ of subsequent employment options (Barnett et al. Reference Barnett, Jamal and Monroe2021, 967).
Second and related, while in principle both interventions targeted women, in practice the proportion of women in ELIIP far exceeded the proportion in CWLP. (Roughly 87 per cent of all ELIIP workers were women, compared with just 50 per cent of all CWLP workers.) This is important because the effects of new employment opportunities on IPV, whether positive or negative, may depend crucially on the extent to which they also benefit men. Finally, while ELIIP projects lasted over a year on average (14.3 months), CWLP projects lasted just three months. The benefits of ELIIP were thus larger and flowed disproportionately to women, while the benefits of CWLP were smaller and flowed to men and women more equally. (All ELIIP and CWLP workers earned the same wage, regardless of sex.)
The two programs thus had distinct distributional consequences for participants and their families. In the language of our theoretical framework, to the extent that both ELIIP and CWLP offered paid work outside the home, we should expect both interventions to alleviate the stress associated with poverty and to reduce the amount of time intimate partners spent together. But we should also expect ELIIP to have more pronounced effects on women’s outside options and thus their reservation utilities. Relatedly, we should expect ELIIP to have more marked effects on ‘status inconsistency’ by strengthening women’s bargaining power and increasing their control over the allocation of household resources.
Importantly, while (some of) the theories described above yield distinct predictions for ELIIP and CWLP, ultimately we cannot be sure whether the disparate effects of the two interventions on IPV are attributable to differences in program design or to some other discrepancy between contexts. The cleanest way to disentangle these possibilities would be to randomize the relevant program design characteristics (for example, gender quotas) within each country. Unfortunately this was not possible for a combination of political, administrative, and logistical reasons. Our goal is not to demonstrate conclusively that differences in program design were responsible for any disparities in treatment effects. Rather, our goal is to use our theoretical framework to generate predictions about the likely effects of each intervention, then test those predictions against the data. As we will see, our results are clearly consistent with only one of the theories summarized above.
Research Design
Ethics
Our study was subjected to extensive technical and ethical vetting, and included a variety of safeguards to maximize benefits and minimize risks. We summarize some of these safeguards here, and discuss them at greater length in SI Section A. Participation in both the interventions and our evaluations of them was entirely voluntary. At the implementation stage, the local NGOs responsible for executing ELIIP and CWLP projects filed regular reports on any observed harms to participants through a centralized Monitoring Information System, and established connections with local counseling and clinical service providers for referrals when necessary.
At the endline data collection stage, our surveys were vetted by professional psychologists and pretested to minimize the risk of re-traumatization. The survey firms established connections with local counseling and clinical service providers as well, and survey enumerators received extensive specialized training on interviewing techniques for sensitive questions. All surveys were administered in private, female respondents were given the option of being interviewed by female enumerators,Footnote 26 and all respondents were repeatedly reminded that they could skip any question or module or discontinue their participation entirely.
Randomization
Our Egyptian study sample consists of 156 villages distributed across nine of the country’s twenty-seven governorates.Footnote 27 Villages are the smallest administrative unit in Egypt. Randomization proceeded in two stages: first at the village level, then at the individual level. For the village-level randomization, we first created matched pairs of villages based on district, governorate, population, number of households, number of households that fell below the poverty line in 2013, mean household expenditures, a village-level analog to the Gini coefficient, and an indicator for whether the village was located in an urban or rural area (though most were rural). We then randomly assigned one village in each matched pair to treatment and the other to control.Footnote 28
For the individual-level randomization, local NGOs worked with local leaders in treatment villages (typically village chiefs) to generate lists of workers who met MSMEDA’s eligibility criteria. We requested lists with 1.5 times as many eligible workers as were needed for each project. We then randomly selected roughly two-thirds of all eligible workers in each treatment village to participate in the program, and assigned the remaining one-third to control. We also consulted local leaders and NGOs in control villages to compile lists of residents who would have met MSMEDA’s eligibility criteria had their villages been randomized into treatment. Importantly, control village lists were compiled in preparation for endline data collection, after treatment was assigned at the village level and after many projects were completed. In SI Section D.1 we run a variety of diagnostic tests to show that this discrepancy in timing is very unlikely to bias our results. In accordance with MSMEDA’s requirements, 80 per cent of all residents on each list had to be youths between 18 and 29 years old; 70 per cent had to be women; and all had to be among the poorest of the poor in the village.Footnote 29
Our study sample in Tunisia consists of all eighty rural imadas in the Jendouba governorate. As in Egypt, imadas are the lowest administrative unit in Tunisia, analogous to villages. Jendouba comprises ninety-five imadas, fifteen of which are classified as urban. The latter were excluded from our study. Randomization again proceeded in two stages. For the village-level randomization, we first stratified the eighty imadas into three groups by population – less populated, moderately populated, and more populatedFootnote 30 – and by participation in the first round of CWLP, which was completed prior to our study. We then randomly assigned villages to treatment or control within strata. In total, forty villages were assigned to treatment and forty to control.
For the individual-level randomization, local NGOs collaborated with local leaders (again, typically village chiefs) to compile lists of sixty to sixty-five eligible workers from among the poorest unemployed residents of each village; these lists were roughly 1.5 times longer than the number of CWLP spots available. We then randomly selected roughly two-thirds of eligible workers in each treatment village to participate in the program. As in Egypt, local leaders and NGOs also compiled lists of control village residents who would have been eligible for the program if their villages had been assigned to treatment. Again, these lists were compiled in preparation for endline data collection; in SI Section D.1 we again demonstrate that this discrepancy in timing is very unlikely to bias our results. We discuss treatment compliance in SI Section E and report balance tests in SI Section F.
Data
Due to time and financial constraints, we did not conduct baseline surveys in either Egypt or Tunisia. Fortunately, baseline data are not necessary for unbiased estimation of any of our treatment effects. We collected two rounds of endline survey data in each country. For the first round in Egypt, we surveyed all eligible workers in treatment villages who were selected to participate in ELIIP, as well as a random sample of fifteen eligible workers who were not selected. We describe these as ‘treatment’ and ‘partial control’ residents, respectively; the latter were randomized into control at the individual level but into treatment at the village level, making them potentially susceptible to spillover effects within villages. We also surveyed a random sample of five eligible workers in each control village. We refer to these residents as ‘pure controls’.
To test for general equilibrium effects within villages,Footnote 31 we surveyed a random sample of five residents per community. We refer to these residents simply as ‘community members’, since they were not individually randomized into treatment or control. This sample was designed to be representative at the village level. The first round of endline data was collected in May 2017, roughly one month after completion of the last ELIIP project. The second round was collected in June and July 2019, more than two years after implementation. We rely primarily on the first endline in this paper, and use the second only to test for decay in our treatment effect estimates over time. We describe our sampling frame and survey procedures in further detail in SI Section D.1 and report descriptive statistics in SI Section D.2. We discuss attrition below and in SI Section G.
In Tunisia we surveyed all eligible workers in treatment villages, regardless of whether or not they were selected to participate in CWLP. In each control village we surveyed twenty randomly selected residents who would have been eligible to participate if their village had been assigned to treatment. To estimate general equilibrium effects, we surveyed fifteen randomly selected residents of each community. We collected the first round of endline data between April 2016 and January 2017, beginning roughly seven months after completion of the last CWLP project. The gap between implementation and endline data collection was thus shorter in Egypt than in Tunisia. As we discuss below, however, ELIIP’s adverse effects on IPV remain detectable even after more than two years, suggesting that the disparate effects of the two interventions are not artifacts of differences in the timing of the endlines. We collected the second round of endline data in Tunisia between December 2020 and April 2021.
Measurement
We use our endline surveys to measure indicators for three categories of IPV: physical violence, psychological abuse, and economic coercion. To measure physical violence, female survey respondents in Tunisia were asked if they had been kicked, hit, punched, pushed, slapped, pulled by the hair, suffocated, or burned by a spouse or other intimate partner. Egyptian respondents were asked if they had been subjected to any form of physical violence, without specifying the form it took.Footnote 32 Because IPV is a relatively rare event, we code an indicator for respondents who reported experiencing physical violence of any kind. We discuss the precautions we took to prevent re-traumatization and provide resources for survivors of IPV in SI Section A.
To measure psychological abuse, Tunisian respondents were asked if they had been threatened, intimidated, frightened, belittled, or humiliated by an intimate partner. Egyptian respondents were asked the same questions. We again code an indicator for respondents who reported experiencing psychological abuse of any kind. To measure economic coercion, Tunisian respondents were asked if they had been kicked out of their home, prevented from working, or deprived of their earnings against their will. Egyptian respondents were again asked the same questions, and we again code an indicator for any economic coercion.
We also measure several mechanisms and secondary outcomes, which we discuss in further detail below. As a proxy for women’s control over household resources, we code an indicator for respondents who reported exercising discretion over how they spend their own money.Footnote 33 We also measure whether respondents had any income-generating activity; the number of days worked in the past month; whether they earned any income in the past month; the amount they earned; whether they have any savings; and the amount they saved in the previous three months in Egypt, or the previous year in Tunisia.Footnote 34 To measure belief in women’s equality, we code an indicator for respondents who agreed that women should have the ‘same rights and responsibilities as men’.Footnote 35 We also code indicators for respondents who were divorced or separated at endline. Finally, to capture psychological welfare, we code indicators for respondents who reported feeling depressed, unimportant, or exploited, or who experienced difficulty being accepted by their families.
Estimation
We estimate four sets of intention-to-treat (ITT) effects in each country, focusing on female survey respondents. First, we compare eligible women in treatment villages who were selected to participate (‘treatment’ residents) to eligible women in control villages (‘pure control’). We call this the ‘between’ specification; it exploits the village-level randomization, and yields estimates for the direct effects of the interventions. Formally, we estimate an ordinary least squares (OLS) regression of the form
$$ y_{ivs} = \theta T_{vs} + \alpha _s + \epsilon _{ivs} $$
where y
ivs
denotes the dependent variable for female survey respondent i in village v in stratum s; T
vs
denotes assignment to treatment at the village level; α
s
denotes a vector of stratum fixed effects;Footnote
36
and ϵ
ivs
denotes an individual-level error term, clustered at the village level in this and all other specifications.
$\theta$
is the ITT.
Second, we compare treatment residents to eligible women in treatment villages who were not selected to participate (‘partial control’). We call this the ‘within’ specification; it exploits the individual-level randomization, and yields estimates for the combined direct and spillover effects of the interventions within treatment villages. We estimate
$ y_{ivs} = \theta t_{ivs} + \alpha _s + \epsilon _{ivs} $
where t vs denotes assignment to treatment at the individual level and all other parameters are defined as in Equation (1).
Third, we compare partial control to pure control residents. We call this the ‘spillovers’ specification; it again exploits the village-level randomization, and yields estimates for the spillover effects of the interventions onto eligible women in treatment villages who were not selected to participate. This specification is similar to Equation (1), except that it replaces treatment residents with partial controls. We show in SI Section J that our results are robust to an alternative specification that accounts for the possibility of spillover between (rather than within) villages.
Finally, we compare randomly selected women in treatment villages to randomly selected women in control villages (‘community members’). We call this the ‘general equilibrium’ specification; it exploits the village-level randomization, and yields estimates for the spillover effects of the interventions onto women in treatment villages who were not individually randomized into treatment or control. Our theoretical framework does not generate clear empirical predictions for the community members sample: since manyFootnote 37 randomly selected women would not have been eligible for either intervention, their reservation utilities should have remained largely unchanged even in treatment villages. Nonetheless, ELIIP and CWLP could have affected IPV among these women by, for example, shifting market wages or disseminating information about health concerns that disproportionately affect women (for example, through the maternal and child health awareness component of the ELIIP program). The general equilibrium specification is identical to Equation (1) except that it includes only the community members sample. We report minimum detectable effects in SI Section H and deviations from our pre-analysis plan (PAP) in SI Section L.Footnote 38
Attrition
We observed some attrition between randomization and our first endline in Tunisia. Unfortunately we have limited information on attriters – we only know their gender, location, and treatment assignment – and the information is only reliable in treatment villages. Because the response rate is somewhat higher among treatment respondents (85.0 per cent) than their partial control counterparts (73.7 per cent), in SI Section G we use Lee (Reference Lee2009) ‘trimming’ bounds to show that the (null) effects of the CWLP program on IPV within treatment villages are unlikely to be artifacts of attrition. We observed almost no attrition between randomization and the first endline in Egypt, and so focus our bounding exercise on Tunisia. We did, however, observe some attrition between the first and second endlines in both countries. Fortunately, attrition of this sort will only affect our estimates for decay in Table 7; it will not affect any of the other results in this paper. Nonetheless, in SI Section G we also construct Lee bounds around our second endline ITT estimates for both programs. We again show that the effects on IPV are unlikely to be artifacts of attrition.
Results
Summary of Predictions
Table 1 maps the empirical predictions from our theoretical framework onto our research design. The household bargaining model with expressive violence predicts that ELIIP in Egypt should have mitigated IPV among eligible women in treatment villages, regardless of whether or not they were selected to participate. The model thus predicts that we should observe a reduction in IPV when we compare (1) ‘treatment’ to ‘pure control’ residents (‘between’ specification) or (2) ‘partial control’ to ‘pure control’ residents (‘spillovers’ specification). The latter prediction follows from the intuition that reservation utilities are a function of potential (rather than actual) incomes, which should have increased among both treatment and partial control residents in treatment villages. This also implies that we should observe no change in IPV when we compare treatment to partial control residents (‘within’ specification). The model predicts that we should observe no change in IPV in Tunisia in any specification, since CWLP benefited men and women roughly equally, leaving their reservation utilities largely unchanged.
Summary of hypothesized effects on IPV
Conversely, the household bargaining model with instrumental violence predicts that ELIIP should have exacerbated IPV among eligible women in treatment villages, again regardless of whether or not they were selected to participate. We should therefore observe an increase in IPV in the between and spillovers specifications in Egypt, and no change in the within specification (again, because reservation utilities are a function of potential rather than actual incomes). We should observe no change in IPV in any specification in Tunisia. Finally, exposure and stress theories predict that both ELIIP and CWLP should have mitigated IPV among eligible women in treatment villages, but only among those who were selected to participate. This follows from the intuition that employment opportunities should only reduce poverty and limit exposure among women who are actually employed.
Effects on IPV
Table 2 reports the ITT of the ELIIP program in Egypt (top panel) and the CWLP program in Tunisia (bottom panel) on indicators for physical violence, psychological abuse, and economic coercion at our first endline. We report results for the between (columns 1–4), within (columns 5–8), and spillovers (columns 9–12) specifications, as defined above. We find that ELIIP exacerbated IPV – an effect driven primarily by psychological abuse and economic coercion. From the between specification, eligible women in treatment villages who were selected to participate in the program were 7.4 percentage points more likely to report psychological abuse and 2.9 percentage points more likely to report economic coercion than eligible women in control villages. These are substantively large increases of 104 per cent and 580 per cent, respectively, over the corresponding control group means (0.071 and 0.005). Eligible women in treatment villages who were selected to participate were also 0.8 percentage points (80 per cent) more likely to report physical violence, but this effect is not statistically significant at conventional levels. In SI Section K we show that our results are robust to indexing and to a Bonferroni correction for multiple comparisons.
Treatment effects on IPV
Note: coefficients from OLS regressions with stratum fixed effects. Columns 1–4 compare ‘treatment’ to ‘pure control’ residents; columns 5–8 compare ‘treatment’ to ‘partial control’ residents; columns 9–12 compare ‘partial control’ to ‘pure control’ residents. Standard errors are clustered at the village level. * * *p < 0.01, **p < 0.05, *p < 0.1.
ELIIP’s adverse effects on IPV are consistent with theories of instrumental violence (H2a), which predict that employment opportunities for women should exacerbate IPV, but not with theories of expressive violence (H1a), nor with theories of stress or exposure (H3a), which predict the opposite. Our finding that these adverse effects are driven primarily by psychological abuse and economic coercion is theoretically important, as it suggests that men may rely on mechanisms other than physical violence to preserve their status within the household. Bobonis et al. (Reference Bobonis, González-Brenes and Castro2013, 181), for example, argue that men may use threats to extract rents from their spouses, resorting to physical violence only if their spouses resist these demands; women’s economic empowerment may therefore induce ‘an increase in the threat of spousal abuse with no associated physical violence’. Our results are consistent with this intuition.
The null effect on physical violence in Egypt is empirically relevant as well, as it helps us rule out the possibility that ELIIP’s apparently adverse effects on IPV are artifacts of increased recognition and reporting among survivors. It is not obvious why ELIIP would increase willingness to report some forms of IPV but not others to enumerators, especially in the context of a private, anonymous survey. If our results were artifacts of reporting bias, then intuitively we would expect to observe a more uniform increase in all forms of IPV. But we do not. (We address the possibility of reporting bias in further detail in SI Section I.) This finding also helps us rule out the possibility that the differential effects of the two programs are artifacts of discrepancies in outcome measurement since, unlike physical violence, psychological abuse and economic coercion were measured identically in Egypt and Tunisia.
Importantly, we observe substantively large and statistically significant increases in psychological abuse and economic coercion among eligible women in treatment villages regardless of whether or not they were selected to participate in the ELIIP program. From the spillovers specification, eligible women in treatment villages who were not selected to participate were 7.2 percentage points (101 per cent) more likely to report psychological abuse and 3.0 percentage points (600 per cent) more likely to report economic coercion than eligible women in control villages. They were also 3.0 percentage points (300 per cent) more likely to report physical violence. The ITTs are null in the within specification, implying that ELIIP’s effects on IPV are statistically indistinguishable among eligible women in treatment villages who were and were not selected to participate. These results are again consistent with theories of instrumental violence (H2b), and with the notion that potential rather than actual income determines reservation utilities and thus the incidence of IPV.
Finally, we find no evidence that CWLP in Tunisia exacerbated (or mitigated) IPV of any kind among eligible women in treatment villages, regardless of whether or not they were selected to participate in the program. This is consistent with theories of both expressive (H1c) and instrumental (H2c) violence, both of which predict that employment opportunities that empower men and women roughly equally should have minimal effects on reservation utilities, and thus minimal effects on IPV. CWLP’s null effects on IPV are inconsistent with theories of exposure and stress (H3b), which predict that employment opportunities for both men and women should reduce IPV.
Mechanisms and Alternative Explanations
Effects on control over household resources
In theories of instrumental violence, bargaining power is the key mechanism connecting women’s economic empowerment to IPV. These theories predict that employment opportunities should allow women to demand more control over the allocation of household resources – a demand that men then attempt to counteract by inflicting IPV instrumentally. The result is a non-cooperative equilibrium characterized by greater autonomy for women but also more IPV; the equilibrium holds when, from the woman’s perspective, the increase in autonomy more than compensates for the increase in IPV (Eswaran and Malhotra Reference Eswaran and Malhotra2011, 1234). In the context of our study, in general we should therefore expect ELIIP to increase women’s control over household resources and CWLP to have no effect in either direction.Footnote 39
We explore this possibility in Table 3 by testing the effects of each program on an indicator for female survey respondents who reported exercising discretion over how they spend their own money. In Egypt, we find that eligible women in treatment villages who were selected to participate in the program were 7.6 percentage points (84 per cent) more likely to report exercising discretion over spending than eligible women in control villages. This is consistent with theories of instrumental violence. In Tunisia, in contrast, eligible women in treatment villages were no more or less likely to report exercising discretion over spending, regardless of whether or not they were selected to participate. This too is consistent with theories of instrumental violence.
Treatment effects on control over household resources
Note: coefficients from OLS regressions with stratum fixed effects. Columns 1–4 compare ‘treatment’ to ‘pure control’ residents; columns 5–8 compare ‘treatment’ to ‘partial control’ residents; columns 9–12 compare ‘partial control’ to ‘pure control’ residents. Standard errors are clustered at the village level. * * *p < 0.01, **p < 0.05, *p < 0.1.
Importantly, only a very small fraction of eligible Tunisian women in control villages reported exerting discretion over spending. But the null effects in Tunisia seem unlikely to be an artifact of sparseness in the data. If anything, given the rarity of the outcome, even a very modest increase in the number of eligible women reporting discretion over spending should suffice to generate a substantively large ITT. Moreover, as we discuss below, CWLP had positive and statistically significant effects on even rarer outcomes – for example, savings – suggesting that the null effect on discretion is not an artifact of sparseness in the data.
Also importantly, from the within specification in Egypt, eligible women in treatment villages who were selected to participate in the program were 8.9 percentage points (127 per cent) more likely to report exercising discretion over spending than eligible women who were not selected. Combined with our results in Table 2, this suggests somewhat counterintuitively that ELIIP’s beneficial effects on discretion over spending depended on participation in the program while its adverse effects on IPV did not. We consider potential explanations for this combination of results below.
Effects on employment, income, and savings
While we focus in this paper on IPV, the primary purpose of both ELIIP and CWLP was to increase participants’ access to employment, earnings, and savings. Our surveys allow us to test whether the programs achieved this goal. This is important not just for understanding the impact of the two interventions on women’s economic welfare, but also for addressing perhaps the most obvious alternative explanation for the programs’ differential effects on IPV and control over household resources: if ELIIP improved women’s earnings potential while CWLP did not – perhaps because CWLP was shorter, or for some other reason – then CWLP should have posed little threat to men’s status in the household, regardless of its effects on men’s economic wellbeing.
In Table 4 we report the ITT of each program on an indicator for any income-generating activity among female survey respondents (first row in each panel); the number of days worked in the previous month (second row); an indicator for any earnings in the previous month (third row); the amount earned in the previous month (fourth row); an indicator for any savings (fifth row); and the amount saved in the previous three months in Egypt, or the previous year in Tunisia (sixth row). Importantly, since the endlines were conducted at least one month after completion of the last project in each country, these measures capture the extent to which women maintained access to employment and income after the interventions ended.
Treatment effects on income-generating activities, earnings, and savings
Note: coefficients from OLS regressions with stratum fixed effects. Columns 1–4 compare ‘treatment’ to ‘pure control’ residents; columns 5–8 compare ‘treatment’ to ‘partial control’ residents; columns 9–12 compare ‘partial control’ to ‘pure control’ residents. Standard errors are clustered at the village level. * * *p < 0.01, **p < 0.05, *p < 0.1.
From the between specification in Egypt, we find that eligible women in treatment villages who were selected to participate in the program were 19.1 percentage points (66 per cent) more likely than eligible women in control villages to have an income-generating activity, and that they worked 3.8 more days (53 per cent) on average in the previous month. They were also 17.2 percentage points (61 per cent) more likely to have any earnings and 4.7 percentage points (336 per cent) more likely to have any savings, and they earned 42.8 EGP (21 per cent) more (though this latter effect is not statistically significant) and saved 25.0 EGP (250 per cent) more than eligible women in control villages.
From the within and spillovers specifications, we find that ELIIP’s effects on employment, earnings, and savings depended on participation in the program. This is perhaps unsurprising, as treatment women were the only ones who benefited directly and immediately from the employment experience that ELIIP provided. In SI Section N we further show that ELIIP had no effect on employment or earnings among female survey respondents’ spouses or household heads. (Unfortunately we did not measure these outcomes in Tunisia.) This is consistent with the notion that ELIIP disproportionately benefited women, thus shifting the balance of power within participating households.
Taking our results in Tables 2, 3, and 4 together, we find that eligible women who were selected to participate in ELIIP (1) benefited from increased access to employment, earnings, and savings and (2) exerted more control over their own spending, but that all eligible women (3) suffered from increased IPV, regardless of whether or not they were selected to participate in the program. One possible explanation for this combination of results is that Egyptian men responded violently to perceived threats to their status within the household even before those threats materialized in any tangible way. Another possible explanation, consistent with Bobonis et al. (Reference Bobonis, González-Brenes and Castro2013), is that the increase in physical violence among eligible women who were not selected to participate (Table 2, columns 9–12) was sufficient to suppress their demands for discretion over spending (Table 3, columns 9–12), while the increase in psychological abuse and economic coercion among eligible women who were selected (Table 2, columns 1–4) was not (Table 3, columns 1–4). In this case, we would expect to observe a long-term increase in physical violence against eligible women who were selected to participate in response to their short-run demands for discretion over spending. As we will see in Table 7 below, this is indeed what we observe.
In Tunisia, we find from the between specification that eligible women in treatment villages who were selected to participate were 5.2 percentage points (473 per cent) more likely to have an income-generating activity, 3.3 percentage points (300 per cent) more likely to have any earnings, and 2.6 percentage points (236 per cent) more likely to have any savings than eligible women in control villages. They also worked 0.47 (694 per cent) more days, earned 4.12 TND (222 per cent) more, and saved 2.72 TND (662 per cent) more on average. Interestingly, from the spillovers specification, even eligible women in treatment villages who were not selected to participate were nonetheless 4.0 percentage points (364 per cent) more likely to have an income-generating activity, 2.5 percentage points (227 per cent) more likely to have any earnings, and 1.2 percentage points (600 per cent) more likely to have any savings, though this latter effect is only marginally statistically significant.
In other words, unlike in Egypt, even eligible women in treatment villages who were not selected to participate appear to have benefited somewhat from the CWLP program in Tunisia. But even in Tunisia, the differences between treatment and pure control respondents (columns 1–4) are substantively larger and more consistently statistically significant than the differences between partial control and pure control respondents (columns 9–12). As with ELIIP, this suggests that the effects of CWLP were driven primarily (though not entirely) by treatment women. More importantly, our results in Table 4 suggest that CWLP was successful in improving women’s economic wellbeing – perhaps even more successful than ELIIP. This may be because control group employment, earnings, and savings in Egypt were much higher than in Tunisia, creating ceiling effects. Whatever the explanation, our results in Table 4 suggest that CWLP’s null effects on IPV are not an artifact of similarly null effects on women’s economic welfare.
Effects on belief in women’s equality
The prevalence of IPV tends to be higher in settings where prevailing social norms tolerate or even glorify violence against women (Chester and DeWall Reference Chester and DeWall2018). This suggests a second alternative explanation for the two programs’ differential effects on IPV: CWLP may have fostered new social norms that elevated women’s status, thus stigmatizing IPV and neutralizing the program’s potential adverse effects. For example, by recruiting women to work in traditionally male-dominated sectors (like construction), CWLP may have encouraged residents to view women as deserving of the same rights and responsibilities as men. Women who adopted these new social norms (or were aware of others adopting them) may have felt empowered to demand that their spouses refrain from IPV, while men who adopted them (or were aware of others adopting them) may have felt inhibited from perpetrating IPV in the first place.
This strikes us as unlikely given our results in Table 3: if CWLP inculcated new social norms around women’s equality, then intuitively we would expect it to have increased women’s control over their own spending. But it did not. Nonetheless, we evaluate this alternative explanation more directly in Table SI.19 by testing the effects of each program on an indicator for female survey respondents who expressed a belief in women’s equality. Since the strength of new social norms depends on the extent to which they are shared by others (including men) in the community, in Table SI.20 we also test the effects of each program on belief in women’s equality among both women and men in the community writ large. (For compactness and because these analyses were not pre-specified, we report them in the SI only.) We find little to no evidence that either program affected belief in women’s equality in either direction, suggesting that CWLP’s null effects on IPV are not a function of new social norms around women’s rights and responsibilities.
Effects on divorce and separation
Relatedly, IPV tends to be more common in contexts where divorce is rare or culturally taboo (Bulte and Lensink Reference Bulte and Lensink2019). In a household bargaining framework, if married women cannot credibly threaten to leave their husbands, then they will have little leverage to demand less oppressive treatment. As we discuss above and in SI Section B, divorce rates in both Egypt and Tunisia are high enough to suggest that divorce is indeed a viable exit strategy for many women. Nonetheless, CWLP may have motivated participating women to seek divorce or separation in a way that ELIIP did not, perhaps because it is more culturally acceptable for women to initiate divorce in Tunisia, or because entry into a traditionally male-dominated profession diminished participating women’s adherence to cultural taboos more generally.
Again, this alternative explanation strikes us as unlikely: if CWLP increased the incidence of divorce or separation, then intuitively we would expect it to have reduced IPV as well, as participating women exited abusive marriages. But it did not. Moreover, separation and (especially) divorce can be long processes, while the time between the interventions and endline data collection was relatively short. Nonetheless, in Table SI.21 we explore this alternative explanation by testing the effects of each program on an indicator for female survey respondents who were divorced or separated at endline. (Again, we report these analyses in the SI for compactness and because they were not pre-specified.) We find no evidence that either program affected the probability of divorce or separation in either direction. These results suggest that CWLP’s null effects on IPV are not a function of divorce or separation among participating women.
Extensions
Effects on psychological distress
As noted in the introduction, both IPV and employment have been associated with psychological welfare, though in opposite directions. On the one hand, meta-analyses and systematic reviews have found a positive correlation between IPV and psychological distress (Beydoun et al. Reference Beydoun, Beydoun, Kaufman, Lo and Zonderman2012; Devries et al. Reference Devries, Mak, Bacchus, Child, Falder, Petzold, Astbury and Watts2013). These studies might lead us to expect ELIIP to diminish psychological wellbeing and CWLP in Tunisia to have at worst no effect. On the other hand, systematic reviews have also found that poverty and unemployment are positively correlated with psychological distress, and that programs designed to alleviate poverty tend to improve psychological welfare (Ridley et al. Reference Ridley, Rao, Schilbach and Patel2020). Moreover, some scholars attribute the positive correlation between IPV and depression to feelings of powerlessness among women (Filson et al. Reference Filson, Ulloa, Runfola and Hokoda2010). These studies might lead us to expect ELIIP’s beneficial effects on employment, earnings, savings, and control over household resources to offset its adverse effects on IPV, producing a null or positive effect on psychological wellbeing.
Our surveys allow us to test these competing predictions. From the between specification in Egypt in Table 5, we find that eligible women in treatment villages who were selected to participate in the ELIIP program were 11.7 percentage points (74 per cent) more likely to report feeling depressed than eligible women in control villages; 10.3 percentage points (105 per cent) more likely to report feeling unimportant; 5.6 percentage points (45 per cent) more likely to report feeling exploited; and 1.4 percentage points more likely to experience difficulty being accepted by their families. (No eligible women in the control group reported experiencing difficulty being accepted by their families in Egypt.)
Treatment effects on psychological distress
Note: coefficients from OLS regressions with stratum fixed effects. Columns 1–4 compare ‘treatment’ to ‘pure control’ residents; columns 5–8 compare ‘treatment’ to ‘partial control’ residents; columns 9–12 compare ‘partial control’ to ‘pure control’ residents. Standard errors are clustered at the village level. * * *p < 0.01, **p < 0.05, *p < 0.1.
Given that ELIIP’s adverse effects on IPV spilled over onto eligible women in treatment villages who were not randomly selected to participate, it is perhaps unsurprising that the program’s adverse effects on feelings of depression and unimportance spilled over as well. (The effects on exploitation and acceptance are consistent with these latter results but are not statistically significant in the spillovers specification.) While we cannot be certain that these effects are a function of increased IPV, they are consistent with the proposition that IPV diminishes women’s psychological wellbeing, and that this effect is not offset by improved economic opportunity or autonomy. In contrast, if anything we find that CWLP in Tunisia improved eligible women’s psychological welfare, perhaps as a result of the program’s beneficial effects on employment, earnings, and savings. This is consistent with the notion that improved economic opportunity increases psychological wellbeing, at least when it is not accompanied by increased IPV.
General equilibrium effects on IPV
Our surveys also allow us to test whether ELIIP’s adverse effects on IPV spilled over onto women who were not individually randomized into treatment or control (‘community members’). In Table 6 we find that randomly sampled women in treatment villages were 1.8 percentage points (49 per cent) and 2.3 percentage points (61 per cent) less likely to report physical violence in Egypt and Tunisia, respectively, though these effects are only weakly statistically significant at conventional levels. They were also 2.1 percentage points (19 per cent) and 1.2 percentage points (8 per cent) less likely to report psychological abuse in Egypt and Tunisia, respectively, and 0.50 percentage points (100 per cent) and 2.4 percentage points (53 per cent) less likely to report economic coercion, though none of these latter effects is statistically significant.
Treatment effects on IPV among randomly selected women
Note: coefficients from OLS regressions with stratum fixed effects. Columns 1–4 compare ‘community members’ in treatment villages to ‘community members’ in control villages. Standard errors are clustered at the village level. * * *p < 0.01, **p < 0.05, *p < 0.1.
We are careful not to over-interpret these results, which are imprecisely estimated and thus only suggestive. Moreover, as we show in SI Sections K and N.8, respectively, the apparently beneficial effects on physical violence in Table 6 do not survive a multiple comparisons correction in either country, and only the effect in Tunisia is robust to covariate adjustment. With these caveats, in SI Section N.4 we consider several reasons that the interventions might have mitigated physical violence among randomly sampled women. We provide some suggestive evidence that, at least in Egypt, ELIIP may have conveyed information about women’s health that improved randomly sampled women’s ability to advocate for themselves without threatening their partners’ status. But again, these results are only suggestive. At worst we find no evidence that ELIIP’s adverse effects on IPV spilled over onto randomly sampled women.
Persistence of treatment effects on IPV
Note: coefficients from OLS regressions with stratum fixed effects. Columns 1–4 compare ‘treatment’ to ‘pure control’ residents; columns 5–8 compare ‘treatment’ to ‘partial control’ residents; columns 9–12 compare ‘partial control’ to ‘pure control’ residents. Standard errors are clustered at the village level. * * *p < 0.01, **p < 0.05, *p < 0.1.
Persistence of effects on IPV over time
Finally, our surveys allow us to test whether ELIIP’s adverse effects on IPV persisted even years after implementation was complete. This is important because previous studies have found that the effects of women’s employment on IPV may be unstable over time (Kotsadam and Villanger Reference Kotsadam and Villanger2022), and that employment may affect some forms of IPV in the short term but others in the longer run (Bobonis et al. Reference Bobonis, González-Brenes and Castro2013). IPV was measured nearly identically in the first and second endlines, facilitating comparison between rounds of data collection. Importantly, however, the gap between endlines was longer in Tunisia (more than four years) than in Egypt (roughly two years). We therefore focus on comparing results between rounds within each country.
In Table 7 we find that ELIIP’s adverse effects on psychological abuse weakened to nulls over time. The adverse effects on economic coercion remain detectable more than two years later, though they are substantively smaller and only marginally statistically significant. More troubling, the program’s adverse effects on physical violence appear to have strengthened over time. From the between specification, eligible women in treatment villages who were selected to participate in ELIIP were 2.2 percentage points (52 per cent) more likely to report physical violence than eligible women in control villages. From the spillovers specification, eligible women in treatment villages who were not selected to participate were also 4.6 percentage points (110 per cent) more likely to report physical violence, though this latter effect is only marginally statistically significant.
One possible explanation for these findings is that economic empowerment allowed women to demand more control over household resources even in the face of heightened psychological abuse and economic coercion, and that men responded by using physical violence to suppress these demands. Consistent with this explanation, in Table SI.42 we show that ELIIP’s beneficial effect on women’s bargaining power decayed to a null over time. (We examine persistence of effects on other outcomes in SI Section N.9.) A related possible explanation is that men used psychological abuse and economic coercion to attempt to extract women’s newly earned wages, and resorted to physical violence over time as their partners resisted these extractions. This would be consistent with Bobonis et al.’s (Reference Bobonis, González-Brenes and Castro2013, 181) argument that men ‘use threats of abuse to coercively demand transfers from their wives, and strategically use physical violence (as a punishment) depending on whether their wife complies’. Whatever the explanation, our results in Table 7 are again consistent with theories of instrumental violence (H2a) but not with theories of expressive violence (H1a), nor with theories of stress or exposure (H3a). Also consistent with theories of instrumental violence (H2c), we find no evidence of increased IPV in Tunisia over time.
Discussion
We theorize and test the impact of employment opportunities for women on IPV using harmonized experimental evaluations of public works programs in Egypt and Tunisia. Our results have both theoretical and practical implications. Theoretically, our results are most consistent with a household bargaining model in which men use IPV instrumentally to assert dominance as women’s bargaining position improves. This framework helps explain why ELIIP exacerbated IPV while CWLP did not: since men and women benefited roughly equally from CWLP, the program was less likely to shift relative bargaining power within the household, and thus less likely to threaten men’s status. We argue (but cannot definitively prove) that the two programs’ disparate effects on IPV are plausibly a function of these discrepancies in program design. But even if the differential effects are instead a function of contextual (or other) differences, our results are clearly consistent with theories of instrumental violence, and clearly inconsistent with theories of expressive violence, stress, and exposure.
From a more practical perspective, our results suggest that policy makers may face a trade-off when designing women’s economic empowerment programs. On the one hand, women’s economic empowerment may require designing interventions that exclusively or disproportionately benefit female participants. This is especially likely to be true in contexts where patriarchal norms remain deeply entrenched. On the other hand, interventions that exclusively or disproportionately benefit women may provoke ‘male backlash’ (Erten and Keskin Reference Erten and Keskin2021; Field et al. Reference Field, Pande, Rigol, Schaner and Troyer Moore2021) and, ultimately, IPV. This, too, is especially likely to be true in settings with strong patriarchal norms (Angelucci and Heath Reference Angelucci and Heath2020), where IPV may be more culturally accepted.
Of course, our study is not without limitations. First, although IPV is usually defined to encompass sexual abuse, we did not measure this outcome in either country due to cultural sensitivities and corresponding ethical concerns. Moreover, while we measured psychological abuse and economic coercion identically in the two countries, we measured physical violence differently. We did this to mitigate ethical concerns among our Egyptian implementing partners about asking detailed questions about physical violence. It is possible that we would have detected an increase in physical violence in Egypt in the short term if we had measured it in a more disaggregated way, but we cannot be sure. Second, we did not conduct a baseline survey in either country. Fortunately, this will not bias our treatment effect estimates, though it limits our ability to assess balance along baseline covariates. (We report balance tests using covariates that are either time-invariant or unlikely to be affected by treatment in SI Section F.)
Third, both ELIIP and CWLP prioritized recruiting youths, though only ELIIP imposed a specific quota for the percentage of youths in its workforce. While in SI Section N.5 we find little to no evidence of treatment effect heterogeneity by age in either country, this focus on youths may somewhat limit the generalizability of our findings, as older and younger participants (and their spouses) may respond differently to women’s economic empowerment (Blaydes et al. Reference Blaydes, Gengler and Lari2024). Fourth, we measured employment and income among female survey respondents’ spouses in Egypt but not Tunisia. This limits our ability to test whether CWLP indeed benefited women and their spouses roughly equally. We substantiate our interpretation of CWLP as a weaker shock to women’s bargaining power in SI Section M, and show in SI Section N.3 that ELIIP in Egypt did not increase employment or savings among female survey respondents’ spouses. Nonetheless, the lack of data on spouses’ employment and income in Tunisia is a limitation of our study.
Importantly, we do not interpret our results to imply that women’s economic empowerment should simply be abandoned. Indeed, our evaluation of CWLP suggests it is possible to improve women’s economic and psychological welfare without exacerbating IPV, even in a highly patriarchal context. But in some cases these programs may need to be accompanied by efforts to improve the welfare of men as well, especially in settings where unemployment is perennially high. These programs could also be combined with other mechanisms to change attitudes and behaviors related to IPV – for example, counseling to improve communication and relationship skills between intimate partners (Karakurt et al. Reference Karakurt, Whiting, van Esch, Bolen and Calabrese2016), or mass media campaigns to encourage reporting of abuse (Green et al. Reference Green, Wilke and Cooper2020). To our knowledge, no previous study has tested whether women’s employment programs are more effective, or generate fewer adverse unintended consequences, when combined with mechanisms of this sort. Testing this possibility should be a priority for future policy making and research.
Supplementary material
Supplementary material for this article can be found at https://doi.org/10.1017/S0007123425100902.
Data availability statement
Replication data for this article can be found in Harvard Dataverse at https://doi.org/10.7910/DVN/DDVFCL.
Acknowledgements
For their helpful feedback we thank Lucy Martin and colleagues and participants at numerous seminars and conferences, including the Brown University Security Seminar, the Duke University Political Economy and Political Institutions Speakers Series, the University of Arizona Law & Conflict Seminar, and the Stanford University Comparative Politics Seminar. We also thank Diego Angel-Urdinola, Fotini Christia, Raphael Cottin, Claudia Eger, Thiemo Fetzer, Chad Hazlett, Jacobus de Hoop, and Furio Rosati for their contributions to the research designs and/or pre-analysis plans for the two studies. Aanchal Bagga, Amani Diallo, Carlos Guastavino, Sophia Janssens, and Gabriela Sagun provided excellent research assistance.
We are also grateful to our project and survey implementing partners and their teams, namely the Micro, Small and Medium Enterprises Development Agency (MSMEDA) and El-Zanaty & Associates for the Egypt study and the Ministry of Vocational Training and Employment’s National Observatory of Employment and Skills (ONEQ by its French acronym) and BJKA Consulting for the Tunisia study. Partners in Egypt and Tunisia were supported by outstanding Field Coordinators, Brooke Hill and Samir Ben Zineb, respectively. Finally, we express our deepest gratitude to all households and individuals that participated in our surveys. This research would have not been possible without their collaboration. We gratefully acknowledge financial support from the World Bank through the Jobs Multi-Donors Trust Fund (Jobs MDTF), the Umbrella Facility for Gender Equality (UFGE), the MNA Gender Innovation Lab (MNAGIL), and the i2i Multi-Donors Trust Fund (i2i). The views expressed in this paper are those of the authors alone and do not represent in any way the views or official position of the aforementioned organizations.
Financial support
This work was supported by the World Bank through the Jobs Multi-Donors Trust Fund (Jobs MDTF), the Umbrella Facility for Gender Equality (UFGE), the MNA Gender Innovation Lab (MNAGIL), and the i2i Multi-Donors Trust Fund (i2i).
Competing interests
None to disclose.
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