The World Bank Economic Review, 38(1), 2024, 95–116 https://doi.org10.1093/wber/lhad033 Article Shifting Attitudes towards Domestic Violence: The Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Impact of Primary Education on Women’s Marital Outcomes in Benin Sarah Deschênes and Rozenn Hotte Abstract The paper examines the effect of a primary education program in Benin on women’s marital outcomes. The study leverages a sharp increase in the construction of schools in the 1990s to assess the causal impact of an increase in primary-school supply on primary-school attendance, employment, marital outcomes, and experience and tolerance of intimate partner violence (IPV). Using quasi-experimental geographical and historical variations in the number of schools built, the results indicate that in rural areas the school building program increased the probability of attending primary school and increased the age at marriage and at first child. It decreased the probability that women find domestic violence justified and that they experience emotional IPV. The effects are driven by women’s own increase in education rather than their husbands’. JEL classification: I25, J12 Keywords: education, marriage, intimate partner violence, gender, Sub-Saharan Africa 1. Introduction Women’s marital outcomes, such as age at marriage, age at first birth, and tolerance of intimate partner violence (IPV) are crucial indicators of women’s well-being (Raj et al. 2009; Nour 2006; Jensen and Thornton 2003). The quality of women’s marital outcomes signals the protection or vulnerability that women experience within the household, particularly in developing countries where social safety nets beyond the family are limited and where female celibacy is stigmatized. While education has been shown to delay the onset of marital and fertile life (Breierova and Duflo 2004; Basu 2002; Hahn et al. 2018), its impact on IPV and tolerance towards IPV remains unclear: though education is assumed to make women less tolerant of gender norms that conflict with their well-being (Cannonier and Mocan 2018), it may not affect all facets of women’s empowerment equally. Women may Sarah Deschênes is an Economist at the Africa Gender Innovation Lab (GIL) of the World Bank, Washington DC, USA; her email address is sdeschenes@worldbank.org. Rozenn Hotte (corresponding author) is an assistant professor at Université de Tours, Tours, France; her email address is rozenn.hotte@univ-tours.fr. The research for this article was financed by the EUR grant ANR-17-EURE-0001. The authors thank Richard Akresh, Pierre André, Luc Behaghel, Andrew Clark, Denis Cogneau, Juliette Crespin-Boucaud, Catherine Guirkinger, Rachel Heath, Wendy Janssens, Sylvie Lambert, Marion Leturcq, Alessandro Tondini, Alessandra Voena, Liam Wren-Lewis and Roberta Ziparo for their insightful comments. We thank the anonymous referees and Eric Edmonds for their suggestions, which undeniably improved the paper. A supplementary online appendix is available with this article at The World Bank Economic Review website. C 2023 International Bank for Reconstruction and Development / The World Bank. Published by Oxford University Press 96 Deschênes and Hotte benefit from improvements on some dimensions and bear a cost on others, especially given the inertia of restrictive gender norms (Erten and Keskin 2018; Guarnieri and Rainer 2021; Bobonis, González-Brenes, and Castro 2013). In this study, we examine the impact of primary-school construction on women’s level of education and marital outcomes in Benin. In the 1990s, the Beninese government accelerated the pace of primary-school construction. We combine an original data set of geolocalized primary schools and the Demographic Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 and Health Surveys (DHS). We use a difference-in-difference (DiD) strategy to compare girls who were of primary-school age at the time of the reform to girls who were too old to have benefited from it, in areas where the number of schools built was high compared to areas where the number of schools built was low (using a continuous measure of school construction). Like other large-scale education programs, school constructions in Benin did not specifically target girls, potentially resulting in a concurrent increase in men’s education that could be confounded with the effects of women’s education. This limitation is addressed by exploiting the average eight-year age gap between wives and husbands to focus on women who benefited from the policy but whose husbands did not. In addition, we tackle the issue that school placement is unlikely to be random by (a) focusing on rural areas of Benin, where we show that school placement is not correlated with baseline girls’ enrollment in primary school before the policy began (in contrast with urban areas), and (b) controlling for a potential pre-trend in primary education in regressions following Glewwe and Todd (2022). We first explore whether the policy increased women’s attendance at primary school, as increasing the number of schools may not necessarily translate into higher attendance rates. Second, we study whether the policy generated labor-market gains for women, as earning a higher income is often considered to be a key tool of women’s empowerment (Becker 1991; Manser and Brown 1979). We then investigate the impact of the program on women’s marital outcomes, particularly age at marriage, age at first birth, and tolerance of IPV. The findings suggest that improving primary-school education has positive effects on the marital out- comes of women residing in rural areas. Increased primary-school supply in Benin leads to a 15 percent rise in primary-school attendance among rural women but does not significantly lengthen years of edu- cation nor improve literacy. The policy had no significant impact on primary-school attendance in urban areas, where women were already more educated before the implementation of the school construction program. As we find that the education of the men that women marry is unaffected by the policy, the potential change in marital outcomes can be interpreted as being due to an increase in the human capital accumulation of women (though not to an increase in literacy). The additional human capital acquired through primary-school education delays the onset of mar- riage and motherhood, despite the fact that the end of primary school occurs at a younger age than the average age at marriage. Additionally, increased human capital acquired through primary education re- duces significantly the tolerance of IPV. We also find descriptive evidence consistent with a decrease in the likelihood that women experience emotional violence. The study contributes to the literature in three respects. First, it adds to the relatively scarce literature on the links between women’s education and women’s tolerance and experience of IPV on two accounts. It shows that even in cases where education does not lead to improved learning or better job outcomes, it still has the potential to enhance women’s ability to reject harmful gender norms and protect them from emotional violence, knowing that a large part of the existing literature on this question focused on contexts where labor-market outcomes improved for the treated (Erten and Keskin 2018). This finding is significant because similar policies implemented in low-income African countries have resulted in a decline in the quality of education (Mwirigi and Muthaa 2015; Niang 2014), potentially limiting the impact on women’s tolerance and experience of IPV through learning and employment. Second, the paper shows that the way tolerance and experience of IPV are affected by the school construction policy differs when women made gains in labor-market outcomes and when they did not. Erten and Keskin (2018) show in Turkey The World Bank Economic Review 97 that primary education led to higher participation in the labor market and to better job prospects for women, but also increased financial control and psychological violence against them, without promoting support for gender equality. In contrast with their results, we find (as Cannonier and Mocan (2018) in Sierra Leone) that women’s support for more gender-equal norms improved and that their experience of emotional violence decreased to a certain extent. This finding may align with the idea that policies shifting control over financial resources can potentially have unintended negative consequences for women. The Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 paper adds to the existing literature by also specifically isolating the impact of women’s own education on their marital outcomes, separately from any simultaneous change in their husbands’ education. It is a challenge the literature does not necessarily address (Cannonier and Mocan 2018; Breierova and Duflo 2004). Second, this analysis contributes to the literature by expanding the scope of outcomes usually inves- tigated in the literature on schooling and marital outcomes to spousal matching and the type of union women end up in (Osili and Long 2008; Keats 2018; Cannonier and Mocan 2018; Erten and Keskin 2018). André and Dupraz (2023) notably document that in Cameroon more-educated women are more likely to be married to a polygamous partner as they marry more educated and hence wealthier husbands. Unlike André and Dupraz (2023), we find that husbands of treated women are not more educated, yet they are less tolerant of IPV, enhancing the importance of the marriage market channel to explain the improvement in marital outcomes. Third, this paper complements the literature on the impact of secondary education on women’s marital outcomes (e.g. Hahn et al. 2018; Ozier 2018; Duflo, Dupas, and Kremer 2021; Sara and Priyanka 2023). Marriage occurs around the same time girls attend secondary school, making the influence of secondary- education programs on the timing of marriage nearly mechanical. The same however cannot be said for primary education. We show that, in our context, increasing women’s primary education is already enough to trigger lasting changes, including to marital outcomes, that are not concurrent to primary schooling. The remainder of the paper proceeds as follows. The upcoming section describes the context, educa- tion policy, and data. Following this, the identification strategy will be outlined. The subsequent section showcases the results. Robustness checks and a discussion of the results follow. Finally, the last section offers concluding remarks. 2. Context and Data 2.1. West African Education Policies in the 1990s The 1990s ushered in an era of investment in education in developing countries. In 1990, at the World Conference for Education for All in Jomtien (Thailand), 155 countries pledged to achieve universal pri- mary education for all children by 2015, a priority later reaffirmed by the international community as one of the eight Millennium Development Goals (MDGs). In Africa, the 1991 Conference of African Ministers of Education spurred financial support for education, aiming to provide free primary education and build more classrooms. Benin followed suit by increasing the number of primary schools,1 with a surge in construction from 1997 to 2003 when 1,500 new schools were founded as shown in panel A of fig. 1,2 resulting in a steady 1 Benin’s investments in infrastructure came on top of an already existing legal framework that made primary school compulsory as early as 1975. In 1990, at the time of a regime change and in a context where countries were pledging their commitment to greater access to education, Benin reasserted the compulsory nature of primary school by enshrining it in the constitution. 2 The reform was announced in 1992–1993 but, to the best of our knowledge, there are no official documents explaining why a delay exists between the announcement of the policy and the actual change in the trend in school construction that shows in the data. It may stem from potential delays in the disbursement of funds dedicated to the program or to the time required for actually building the schools. 98 Deschênes and Hotte Figure 1. School Construction and Primary-School Attendance. Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: Panel (a) of the figure presents the number of schools built in Benin since 1980. Panel (b) of the figure shows the share of women and men who attended primary school, by birth cohort in Benin. The World Bank Economic Review 99 rise in enrollment that increased from 722,000 to 911,000 pupils over the same period as illustrated in table S2.1 in the supplementary online appendix. The growth was particularly notable for girls, as their education had previously lagged behind that of boys: in 1990, 27 percent of girls attended primary school, whereas 52 percent of boys attended primary school. As shown in panel B of fig. 1, the share of women who attended primary school increased for women aged 12 or younger (born after 1984) when the policy started. Owing to factors such as late entry into school and grade repetition, it is not surprising that girls Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 as old as 12 when the reform was implemented benefited from it, even though they were beyond the official primary-school age of 6 years old. 2.2. Data 2.2.1. School Construction Data We use an original administrative database on school construction in Benin that provides the number of schools built per year all over Benin between 1980 and 2005.3 The school data are geocoded based on the school name, which contains the name of the town or village where it was built for nearly every public school. 2.2.2. Demographic and Health Surveys We use two waves of the DHS for Benin, collected in 2011 and 2017. The DHS collect harmonized information on women aged 15–49 years and provide the geolocation of its survey clusters. The identification strategy relies on the birth year of women to determine whether they were of school age at the time schools were built, which makes age a crucial variable. Demographers (A’Hearn, Baten, and Crayen 2009; Lyons-Amos and Stones 2017) have long emphasized that in contexts like ours, where people do not necessarily know their age well, survey respondents tend to give an age that ends in 0 or 5 or that corresponds to a social milestone like being 18 at the time of the survey. This leads to age-heaping patterns that are visible in the data, as shown in fig. S1.1 in the supplementary online appendix, which displays the distribution of year of birth in the full sample. Age-heaping patterns tend to make any cohort-study graph look more jagged, often with a periodic pattern of 5 years, than those usually produced in papers investigating other contexts. This is a limitation inherent to the age data used in this study, but despite adding noise to the estimation, it does not prevent us from providing meaningful causal estimates of the impact of the policy; aggregating women in age groups to define treated and control cohorts smooths the artificial irregularities in age patterns (in a way that cannot be done when looking at the effect of the policy year of birth by year of birth). To assess the impact of the school construction policy, we investigate first the following educational outcomes: whether the individual has attended primary school, the number of years of education, and whether she has been to secondary school. We further document the impact on literacy using a dummy variable that takes the value 1 if the woman has an education higher than secondary education, or if she can read the whole or part of a sentence when assessed by the DHS enumerator. Regarding labor-market outcomes, DHS data provide information on whether the woman is working at the time of the survey, and for women who work, in which sector they are working. A measure of migration can also be built with the second wave of the data (DHS 2017) as we know how long women have been living in their current place of residence. Based on this information, we compute a binary variable indicating whether the respondent arrived in her current place of residence after 8 years old, i.e. after being potentially exposed to school construction in her locality of origin. Information collected in all the DHS includes women’s marital status, age at first marriage, and age at first birth, all of which are used as marital outcomes at or near the time of marriage. 3 We thank Pierre André (CY Cergy Paris Université-THEMA) for sharing the data. 100 Deschênes and Hotte Two other dimensions of women’s marital outcomes are also examined: women’s tolerance of IPV and women’s experience of IPV. The DHS ask respondents whether they find it justifiable for a husband to beat his wife if she goes out without telling her husband, neglects the children, argues with him, refuses to have sex, or burns the food. These variables are used as our main outcomes of interest as they have been shown to be relevant proxies for women’s empowerment and well-being (Kishor and Subaiya 2008). To limit the risk of overrejection of the null hypothesis due to multiple inference, women’s binary responses Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 to the five different scenarios are aggregated in an Anderson index (Anderson 2008), which is a weighted average of the normalized individual outcomes. The index is built so that a positive direction indicates that women’s tolerance of IPV is receding (i.e. it is a “better outcome”). In the 2017–18 DHS, a subsample of ever-partnered women are asked about their experience of IPV. For safety reasons, one eligible woman per household is randomly selected to answer the IPV module. It notably provides measures of emotional and physical violence. 2.2.3. Matching the DHS and the School Construction Data The school construction data set and the DHS data sets are matched by projecting the locations of the schools and the DHS clusters onto a map. We then counted the number of public primary schools open in a 10 km buffer around the DHS cluster of a respondent when she was of school age. Choosing a 10 km buffer is relevant because the DHS program randomly displaces the latitude and longitude of the survey clusters to maintain the confidentiality of respondents. Survey clusters are moved by 0 to 2 km in urban areas and by 0 to 5 km in rural areas, with 1 percent of them being moved by up to 10 km. A 10 km buffer allows us to have a measure of exposure to primary schooling that is sufficiently granular, while also limiting the random error in measurement induced by the displacement. It is also worth noting that, in the case of Benin, clusters were randomly displaced, yet maintained within their actual municipality. To account for population density, the number of schools available in a 10 km buffer around a DHS cluster is divided by the number of children who were of school age in the locality according to the 2003 census. Finally, the obtained ratio is multiplied by 1,000. Figure 2 displays the number of schools built between 1997 and 2003 for 1,000 children in the municipality in a 10 km buffer around each DHS cluster. 2.3. Determinants of School Placement The placement of newly built schools is unlikely to be random and may correlate with our outcomes of interest. To the best of our knowledge, no official documents detail the drivers of the policy; therefore, we rely on the data to identify the rationale for the placement of schools. In this section, the correlates of the intensity of the program are investigated. We defer the discussion of the impact of the findings on the validity of the empirical strategy to the next section. Tables 1 and 2 show that the program’s intensity and determinants in cities appear to have been dif- ferent from in the countryside, though both urban and rural areas benefited from the school construction program. First, the surge in school construction relative to the initial stock of schools in 1996, just before the program began, was stronger in rural areas than in urban areas. The penultimate line in table 1 shows that the difference in the program’s intensity in urban and rural areas is both economically and statistically significant.4 Second, the correlates of school construction also differ across rural and urban areas. As shown in the last two columns of table 2, the correlation between female attendance before the program and treatment intensity is three times higher in urban compared to rural areas. In rural areas, there seems to be no significant correlation between female attendance at primary school and school placement, which suggests that the allocation of schools is credibly orthogonal to the outcome “attending primary school.” This result is consistent with the fact that primary-school attendance of girls was initially low and rather 4 In this analysis, we exclude the economic capital Cotonou. The World Bank Economic Review 101 Figure 2. Number of Schools Built between 1997 and 2003 by Clusters. Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Note: The figure presents the number of schools built by clusters between 1997 and 2003, for 1000 children in the municipality. Source: PASEC (Programme d’analyse des systèmes éducatifs de la Confémen) data on school construction in Benin and Demographic and Health Surveys Benin 2011 and 2017–2018. Table 1. Number of Schools Built Variables Urban Rural Diff. Number of schools in the cluster in 1996 2.52 1.96 0.56∗∗∗ (0.00) Number of schools built in the cluster between 1997 and 2003 18.89 12.55 6.33∗∗∗ (0.00) Number of schools built in the cluster between 1997 and 2003 for 1,000 children 1.08 0.91 0.16∗∗∗ (0.01) Number of schools built between 1997 and 2003/stock in 1996 0.55 0.67 −0.13∗∗∗ (0.00) Number of clusters 413 719 1,132 Source: Demographic and Health Surveys Benin 2011 and 2017 and PASEC (Programme d’analyse des systèmes éducatifs de la Confémen). Note: The table presents the differences in mean of school allocations between 1997 and 2003, according to the status of the cluster (in a rural or urban area). We look at the stock of schools available in 1996 in the cluster, before the policy, and at the number of schools built between 1997 and 2003, in absolute terms and in relation to the already available stock. Sample: DHS clusters. Cotonou is excluded. Significance levels are denoted as follows: ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01. undifferentiated in rural areas: 16 percent of girls and women aged 12 and more and living in rural areas had attended primary school at baseline, compared to 35 percent for women living in urban areas. Table 2 shows that the number of schools built by cluster is positively correlated with the share of Fon and Adja, which are the major ethnic groups in Benin (the Fon represent 37 percent of the population and the Adja 15 percent). It is not surprising, since people from these ethnic groups live more in the south 102 Deschênes and Hotte Table 2. Correlates of Allocation of Schools between 1997 and 2003 Number of schools Number of schools for 1,000 children Urban Rural Urban Rural Number of children in the municipality (thousand) 0.836∗∗∗ 0.280∗∗∗ −0.020∗∗∗ −0.032∗∗∗ (0.07) (0.07) (0.01) (0.01) Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Female primary attendance average 5.989∗∗∗ −2.955∗ 0.372∗∗ −0.168 (2.19) (1.61) (0.15) (0.12) Share of Fon 17.918∗∗∗ 11.858∗∗∗ 1.282∗∗∗ 0.874∗∗∗ (2.42) (1.50) (0.17) (0.11) Share of Adja 20.346∗∗∗ 17.548∗∗∗ 1.492∗∗∗ 1.198∗∗∗ (2.78) (1.61) (0.20) (0.12) Share of Yoruba 5.880∗∗ 2.231 0.218 0.110 (2.59) (1.72) (0.18) (0.13) Share of Christians −1.781 −1.442 −0.050 0.003 (2.50) (1.37) (0.18) (0.10) Share of Muslims 1.217 −0.363 0.300 0.140 (2.75) (1.71) (0.19) (0.13) Number of clusters 405 700 405 700 R2 0.48 0.28 0.27 0.26 F 45.15 34.13 18.33 30.39 Source: Demographic and Health Surveys Benin 2011 and 2017 and PASEC (Programme d’analyse des systèmes éducatifs de la Confémen). Note: Sample: DHS clusters. Cotonou is excluded. Significance levels are denoted as follows: ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01. where more schools were built. We defer the discussion about how it may affect the identification strategy to the upcoming section. 3. Empirical Strategy 3.1. Difference in Difference We use a difference in difference (DiD) to identify the causal impact of the rise in school construction on the outcomes of interest. We exploit the fact that women’s exposure to the policy varies according to their birth cohort and municipality of residence. Primary school starts at 6 years old in Benin, but early or late entry in school is a common phenomenon, and so is grade repetition. As a result, it cannot be excluded that women pre- and post- the official primary- school age may have partially benefited from school construction. With that in mind, the first specification defines the exposed cohort as women aged 4 to 8 years in 1997 and the untreated cohort as women aged 13 to 17 years when the program began (women who were too old to benefit from school openings).5 Late entry into primary school and grade repetition may lead to an attenuation bias as some women in the control cohort may have been exposed to the education program. The second source of variation used is the number of schools built between 1997 and 2003 within a 10 km radius around each DHS cluster of residence of women. The DHS does not provide information on women’s location when they were of primary-school age (nor on their place of birth), so we use as a proxy their place of residence at the time of the survey. The implications of this approximation are discussed below. The following model is estimated: yimcg = a0 + βc + θ ∗ Ng + δ ∗ Ng ∗ TREATi + αm + ηXi + γ Zmc + εimcg, (1) 5 A UNESCO report published in 2014 (Equipe nationale du Bénin and de Dakar 2014, p. 81) establishes that among children attending the first year of primary school in 2009–2010, 92 percent of them were between 5 and 8 years old. The World Bank Economic Review 103 where yimcg is the outcome of interest for the woman i residing in municipality m and cluster g and born in year c, a0 is a constant, α m is a municipality of residence fixed effect,6 β c is a coefficient capturing birth cohort fixed effects, and Ng is the number of schools built between 1997 and 2003 in a 10 km radius around a woman’s DHS cluster of residence. This variable can be understood as the intensity of the program in cluster g. The model also includes the variable TREATi , a dummy variable equal to 1 if the woman was born between 1989 and 1993 (meaning that the woman was between 4 and 8 in 1997). Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 It is equal to 0 if she was born between 1980 and 1984 (meaning that the woman was between 13 and 17 in 1997). The variable Xi is a set of individual controls and includes religion and ethno-linguistic group. We control for municipality-specific year effects (Zmc ), for the density of school-age children, and for the average of school attendance before the program began to avoid confounding treatment effects with the impact of the density of school-age children. As we are using several waves of DHS, we control for age effects by introducing the variables age and age2 in the model. Standard errors are clustered at the DHS cluster level. Second-stage least squares estimates are not presented because the exclusion restriction may be vio- lated. It would be the case for instance if school construction spurred changes in the norms on age at marriage or on tolerance of domestic violence without these changes being caused by a girl’s own educa- tion. 3.1.1. Analysis by cohort In the section describing the results, we present the effect of the policy on the outcomes of interest per age at the time the policy was implemented, which is tantamount to studying the policy’s effect on a given cohort. The results shown are yielded by the following specification: 21 yimcg = a0 + βc + θ ∗ Ng + δa ∗ (Ng ∗ via ) + αm + ηXi + γ Zmc + εimcg, (2) a=2 which contains variables previously used in equation (1), to which we add via , a dummy indicating whether individual i was age a in 1997, and Xi which includes the individual’s religion, ethnicity, and the squared age. Standard errors are also clustered at the DHS cluster level. 3.1.2. Synthetic panel approach Women in the treated group are not all married because they are younger at the time of the survey. In this case, using ordinary least squares to assess the impact of school construction on the age at marriage and age at first birth can bias the result, because it is only available for already-married women. The selection bias thus introduced may be all the more problematic if the average ages of entry into marriage are different between high-treatment and low-treatment areas. Following the literature, we use a linear probability model on a data structure modified as follows: there is one observation by woman and by age (in year) starting from age 8, since there is no marriage and birth before this age. The outcome (marriage or first birth) takes the value 0 if the woman is not married (or has not given birth yet) at the age considered. It takes the value 1 at the age when the woman gets married (or gives birth for the first time). In the subsequent year, the woman leaves the sample. For women who are still not married, the outcome takes the value 0 for each age, until the age they are at the time of the survey. The same control variables as in equation (1) are included, except for the variables age and age2 , which are replaced by the age for the observation in question and not at the time of the survey. Standard errors remained clustered at the DHS cluster level. 6 We do not apply a DHS cluster fixed effect because the number of observations in each cluster ranges from 7 to 42 at an average of 23, which we deem to be too few. 104 Deschênes and Hotte Figure 3. Primary-School Attendance by High-/Low-Intensity Regions and Birth Cohorts in Rural Areas. Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Source: Demographic and Health Surveys Benin 2011 and 2017. Women born between 1974 and 1995 residing in rural areas. Note: Panel A: The figure represents the level of primary-school attendance by high-/low-intensity areas and birth cohorts smoothed with a kernel-weighted local polynomial. Panel B: The figure represents the level of the index of tolerance of domestic violence by high-/low-intensity areas and birth cohorts smoothed with a kernel-weighted local polynomial. The index is built using the methodology of Anderson (2008). 3.2. Addressing Threats to Validity For the DiD to yield a valid causal estimate of the impact of school construction on the outcomes of interest, the parallel trends assumption has to hold. It requires that, absent the surge in school construction, the increase in women having attended primary school (and women’s marital outcomes) would not have systematically differed between treated and control areas. A first major threat to the validity of the parallel trend assumption is that the decision to build schools at a given place is not random, but in fact that one or several drivers of school construction implementation may affect treated and control cohorts differentially over time, causing us to confound the effect of school construction and the effect of the said driver. We assess how likely it is by showing the trend in primary- school enrollment and tolerance of IPV as a function of the birth year of respondents in areas where the intensity of the program was high and in areas where the intensity of the program was low. DHS clusters are split between “high-intensity” zones, which are defined as clusters that received more than the median number of schools built, and “low-intensity” zones, which are defined as clusters that received fewer than the median number of schools built. As shown in the section describing the results, there is a significant impact of school construction on primary education in rural areas only. For this reason (and for the sake of brevity), we display the graphs for rural areas only. Panel A of fig. 3 provides evidence that the impact of school construction is unlikely to be confounded with any cohort-varying confounders, as the gap between the high-intensity and low-intensity areas is relatively stable across cohorts up until the exposed cohorts for primary-school attendance. We grant that panel B of fig. 3 shows that the gap between high- and low-intensity areas for the index of tolerance The World Bank Economic Review 105 of domestic violence does not appear as stable as the one for primary education, which is a concern we directly address later in this section.7 The last part of the second section showed that school placement was correlated with some pre- expansion characteristics; in urban areas, the intensity of the treatment correlates with the initial atten- dance rate of girls, whereas it does not in rural areas. To account for that, we control for the interaction between cohort of birth dummies and the initial attendance rate at the municipality level in our main Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 regression.8 In both urban and rural areas, school placement is correlated with the share of Fon and Adja in the DHS cluster. Additional tables in the supplementary online appendix show that the results are robust to controlling for a potential differential trend in school demand between areas where different ethnic groups are more concentrated. The identification assumption would also be violated if they omitted time-varying and regional specific effects correlated with school construction, such as other governmental programs initiated at the same time.9 To our knowledge, no other contemporaneous program was implemented at the same time. This is not surprising, since education had been identified as a priority and funding was limited. Furthermore, since we are exploiting the geographical variation in schools construction at a very granular level, other potential campaigns are unlikely to be a credible confounder. To further assess the credibility of the parallel trends assumption, we also check whether there is ev- idence of a pre-trend in the outcomes of interest by using placebo cohorts. Equation (1) is estimated on two cohorts of women who were too old to have benefited from the policy; we compare women aged 13 to 17 years in 1997 to women aged 21 to 26 years in 1997 and show the results in all our tables . We also plot the impact of the policy on each cohort of birth of women in cohort-study graphs using equation (2). All these tests should account for time-varying confounders. However, as panel B of fig. 3 was not displaying as stable a gap as for primary education, we go a step further and directly account for a potential pre-trend in the outcomes of interest by comparing the DiD estimator yielded by equation (1) with the estimator of (Glewwe and Todd 2022, Chapter 12, p. 183), which allows us to dispense with the parallel trends assumption provided that three periods of data are available. We adapt this insight and directly control for differential pre-trends using the following model, which uses a level specification rather than a differentiated one: yimcg = a0 + β Timec + φ TREATEDi + π Timec ∗ Ng + θ ∗ Ng + δ ∗ Ng ∗ TREATEDi + αm + ηXi + γ Zmc + εimcg, (3) with Timec a variable taking the value 0 for individuals born between 1971 and 1976 (period t0 ), the value 1 for women born between 1980 and 1984 (period t ), and the value 2 for women born between 1989 and 1993 (period t ). The variable TREATEDi takes the value 1 for the women born between 1989 and 1993 and 0 for women born between 1971 and 1976 or between 1980 and 1984. The first two periods (t0 and t ) are used to estimate separate time trends for participants (π ) and nonparticipants (β ). The variable δ , which captures the deviations from that time trend in the third period for the participants, is an estimate of the program impact (after allowing for time-period-specific shocks that affect both groups in the same way with φ ). Estimates yielded by equation (3) are shown in all the tables . 3.2.3. Migration Finally, another severe threat to the validity of the identifying strategy is migration between areas with different levels of education at baseline. As the DHS does not provide information on the place where 7 We do not present here the same graph for the age at marriage due to the right-censorship of the variable. 8 As suggested by Duflo (2001), it also allows us to ensure that our estimates do not capture a simple reversal to the mean for the primary attendance rate (and therefore a difference in pre-trends). 9 In order to encourage parents to enroll girls in primary school, fee waivers were decided for them in 1993 but the measure was made effective in 2006 (Gastineau, Gnele, and Mizochounnou 2015). 106 Deschênes and Hotte women lived when they were of school age, we proxy the place where women went to primary school using women’s residence at the time of the survey. Beyond the measurement error that it introduces, if migration in and out of the place of birth is endogenous to the treatment or the outcomes of interest, the impact of migration may be confounded with the impact of school construction. First, it is worth noting that, according to the 2013 census, migration is limited as only 18 percent of women born between 1989 and 1993 in rural areas have migrated between municipalities.10 Second, we Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 used migration as an outcome in the results section and found that school construction did not affect the probability of migrating: more specifically, it does not impact the probability of arriving in the cluster of residence after 8 years old. Third, in the robustness checks, we demonstrate that patterns of migration in treated and control areas would have to be very specific to explain our results. The discussion is the basis for a bounding exercise whose output suggests that migration is unlikely to be driving our results. 3.2.4. A potential confounder: The education of boys The policy was not designed to specifically target girls, and boys could also have benefited from school construction. It would be a confounder if the change in marital outcome is in fact the result of an increase in the education of boys rather than that of girls. We investigate this risk and find no evidence that boys were affected by the policy.11 This absence of change in the trend of boys’ education can be explained by their already greater access to schooling before (and even after) the reform. A 2002 World Bank report on education in Benin12 estimated the gender gap in access to primary school to be 22 percentage points in rural areas (86 percent for boys versus 64 percent for girls). What needs to be specifically ruled out is an increase in the education of the men susceptible to becoming the husbands of treated women.13 As the mean difference in age between partners in Benin is 8 years, the average husband was not affected by the reform because he was too old to have benefited from it. The youngest women in our sample could be the exception, but only 6 percent of the husbands of treated women in rural areas were young enough at the time of the policy (born in 1989 or after) to have benefited from it, making it unlikely that they are driving our results. This absence of any impact on boys’ and husbands’ primary-school attendance means that any potential benefits to various marital life aspects occur as a result of the human capital acquired by girls in primary school. 4. Results 4.1. School Attendance and Literacy All the tables in this section are divided into panel A, which shows the estimates yielded by equation (1), panel B, which displays the estimation of equation (1) on placebo cohorts, and panel C, which provides the estimation of equation (3) which directly controls for a potential pre-trend in the outcomes. 10 Ideally, we would have liked to match the location of schools with the women’s places of birth and check whether our results on primary-school attendance are consistent with the census data. However, Beninese census data are not precisely geolocalized and we are not able to perform this test. We are nevertheless aware that doing so would introduce another measurement error, as women did not necessarily attend primary school in the municipality where they were born. Furthermore, the two sets of data are not comparable. For instance, the share of women attending primary school is 10 percentage points lower in the census compared to DHS. 11 The table is available upon request. 12 World Bank Country Status Report: “The Beninese Education System, Performance and Room for Improvement for the Education Policy,” 2002. 13 Here we refer to the risk that potential effects on age at marriage and on tolerance of IPV could be originally linked to an increase in men’s but not women’s education. Note that we do not exclude the possibility that an increase in the husband’s level of education could also explain the results as a channel but not as a confounding effect. However, in this case, the increase in the husband’s education results from the increase in women’s education. The World Bank Economic Review 107 Table 3. Education Outcomes All Urban Rural Number of Number of Number of Attendance years Attendance years Attendance years Literacy (1) (2) (3) (4) (5) (6) (7) Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Panel A: Interest experiment Number of schools 0.003 0.273∗ 0.052+ 0.727∗∗ −0.021 −0.069 0.008 (0.02) (0.15) (0.03) (0.38) (0.02) (0.14) (0.02) Number of schools ∗ treat 0.015 0.088 −0.006 −0.015 0.037∗∗∗ 0.163 0.013 (0.01) (0.11) (0.02) (0.19) (0.01) (0.12) (0.01) Mean dep. var. 0.22 1.39 0.34 2.35 0.15 0.83 0.11 N 9,142 9,142 3,455 3,455 5,687 5,687 5,671 R2 0.26 0.28 0.28 0.28 0.22 0.22 0.16 Panel B: Placebo experiment Number of schools ∗ placebo −0.003 0.019 0.003 −0.021 −0.006 0.025 0.007 (0.01) (0.09) (0.02) (0.17) (0.01) (0.09) (0.01) Mean dep. var. 0.19 1.03 0.32 1.87 0.12 0.59 0.08 N 7,947 7,947 2,830 2,830 5,117 5,117 5,103 R2 0.23 0.23 0.29 0.26 0.11 0.11 0.08 Panel C: With pre-trend controls Number of schools ∗ treat 0.023 0.134 −0.010 0.048 0.051∗∗ 0.217 0.021 (0.02) (0.17) (0.03) (0.28) (0.02) (0.18) (0.02) N 12,838 12,838 4,727 4,727 8,111 8,111 8,090 R2 0.26 0.29 0.28 0.29 0.21 0.22 0.16 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: In columns (1), (3), and (5), the dependent variable is having attended primary school. In columns (2), (4), and (6), the dependent variable is the number of years of education. In the last column, the dependent column is a variable indicating whether the respondent is literate. Panels A and B present the results of the double difference model. Panel C presents the results of the specification with the inclusion of the pre-trends. We control by the ethnicity and the religion of the woman. Sample: Women aged 15–49 years. Significance levels are denoted as follows: +p < 0.15, ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01. As shown in columns (1) and (2) of panel A of table 3, there is no significant effect of the policy on women’s attendance at primary school, nor on the number of years of education. Pooling urban and rural areas masks heterogeneity in the impact of the policy; if columns (3) and (4) suggest that the policy had no impact in urban areas, columns (5) and (6) indicate that building schools increased primary-school attendance among school-age girls in rural areas: on average, one school built per 1,000 children in a 10 km radius around a cluster in a municipality increased the probability of primary-school enrollment by 3.7 percentage points in rural areas for the cohort treated.14 The placebo test in panel B shows that earlier cohorts were unaffected by the policy, as coefficients are not significant and of a low magnitude. The estimate of the impact of the program that directly control for pre-trends in panel C is consistent with the initial results, though slightly higher at 5.1 percentage points, which may indicate a slight negative pre-existing change in the primary education trend that would play down the magnitude of the effect of the policy measured with equation (1). The number of years of education is not significantly affected by the program as shown in column (6) of table 3, nor is secondary education (see table S2.2 in the supplementary online appendix). It indicates that the program mainly affected the extensive margin of primary education. Column (7) of table 3 shows that literacy remains unchanged, eliminating this channel to explain improvements in marital well-being. Figure 4 singles out the cohorts that were most affected by the program and shows the coefficients 14 When a child born in 1982 was 10 years old, there were on average 1.2 schools per thousand children. For a 10-year-old child born in 1992, there were on average 1.9 schools per thousand children. 108 Deschênes and Hotte Figure 4. Effect of the Treatment on School Attendance by Birth Cohort in a Context of Strong Age Heaping. Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: The figure presents the coefficients of the interaction of respondent’s age in 1997 and the number of schools built between 1997 and 2003 in the region of residence in equation (2). The dependent variable is having attended primary school. Sample: Rural women aged 15–49 years. identified by equation (2). The figure provides visual confirmation that girls in rural areas aged 4 to 10 in 1997 benefited from the program, and it further suggests that the younger they were in 1997, the more intense the effect of school construction on primary-school attendance. The periodic inverted-U pattern of five years found throughout the curve is characteristic of age heaping, as already described in the section presenting the context and data : every five years, one point is lower than the others. This same inverted-U pattern was already visible in fig. 1. It explains that the point estimate for women who were 17 in 1997 is negative and significant, which is also consistent with the estimate from equation (3) being higher than the estimate from equation (1). Since the paper investigates the education-induced improvements in women’s well-being, the analysis from this point forward will focus on women residing in rural areas at the time they were surveyed. Bearing in mind that we capture effects only in rural areas and no effects in urban areas (where growth may be higher), this suggests that it is unlikely that a change in growth trend drives our results. 4.2. Labor-Market Outcomes and Migration This section investigates whether the education policy generated gains in the labor market that could improve women’s marital outcomes. The education reform appears to have decreased the likelihood that women were employed at the time of the survey by 5 percent compared to the baseline level (table 4).15 Among women who were employed at the time of the survey, treated women were less likely to work in sales16 (a decrease of 21 percent compared to the mean in the control group) and more likely to work in the services sector17 (a significant increase of 15 percent). Women are also less susceptible to work for cash (column (5) of table 4). The DHS data do not provide enough data on occupation for us to provide further insights into the reasons why treated respondents exposed are less likely to be employed. It is possible that treated women 15 We reran the analysis on women who did not give birth in the 12 months prior to the survey to check whether they may influence these results. The results are the same. 16 Working in sales includes street vendors, shop owners (albeit less than 5 percent), and fruit and vegetable sellers. 17 Working in services notably includes hairdressers, cleaners, and hospitality. The World Bank Economic Review 109 Table 4. Labor-Market Outcomes and Migration Currently working Works in agriculture In sales In services Works for cash Migration (1) (2) (3) (4) (5) (6) Panel A: Interest experiment Number of schools 0.053∗∗∗ −0.047∗∗ 0.017 0.034∗ 0.048∗∗ −0.017 Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 (0.01) (0.02) (0.02) (0.02) (0.02) (0.04) Number of schools ∗ treat −0.042∗∗∗ 0.014 −0.068∗∗∗ 0.022+ −0.029∗∗ −0.044 (0.01) (0.01) (0.02) (0.01) (0.02) (0.04) Mean dep. var. 0.78 0.34 0.32 0.19 0.68 0.41 N 5,687 4,245 4,245 4,245 4,207 2,495 R2 0.17 0.24 0.11 0.10 0.20 0.20 Panel B: Placebo experiment Number of schools ∗ placebo 0.008 0.007 −0.001 0.013 −0.006 0.035 (0.01) (0.01) (0.02) (0.01) (0.01) (0.04) Mean dep. var. 0.81 0.38 0.30 0.20 0.65 0.37 N 5,117 4,150 4,150 4,150 4,076 1,729 R2 0.20 0.24 0.14 0.10 0.21 0.25 Panel C: With pre-trend controls Number of schools ∗ treat −0.054∗∗∗ 0.006 −0.064∗∗ 0.002 −0.045∗∗ −0.083 (0.02) (0.02) (0.03) (0.03) (0.02) (0.07) N 8,111 6,245 6,245 6,245 6,181 3,225 R2 0.17 0.23 0.11 0.09 0.19 0.20 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: The dependent variable in column (1) is a binary variable equal to 1 if the respondent was working at the time of the survey. The dependent variables in columns (2), (3), and (4) are binary variables equal to 1 if the respondent works in agriculture, in sales, or in services (only for currently working women). The dependent variable in column (5) is a binary variable taking the value 1 if the woman works for cash (only for currently working women). The dependent variable in the last column is a binary variable equal to 1 if the respondent has migrated after the age of 8 years (available only for the 2017 wave). The specifications include municipality dummies, year of birth dummies, and interactions between the year of birth dummy and the number of children in the district of residence in 1993. We control for ethnicity, religion, age, and age squared. Sample: Rural women aged 15–49 years. Significance levels are denoted as follows: +p < 0.15, ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01. are less inclined to work because they may have married into wealthier families and, as a result, do not need to work (Cameron, Malcolm Dowling, and Worswick 2001). The program may also have influenced the mobility of the more educated individuals by opening up work opportunities in urban areas. Column (6) of table 4 indicates that it is not the case; the program did not have a significant impact on the probability of migration after the age of 8. This suggests that migration behaviors are not affected by the reform, greatly reducing potential concerns that our estimates may be biased by selective migration driven by school opportunities. 4.3. Marital Outcomes 4.3.1. Marriage Characteristics at the Time of the Union This section focuses on whether building schools improved women’s probability of being married before 15 years old (child marriage) and of delaying the age at marriage and the age at first child. The dependent variable in column (1) of table 5 is the probability of being married as a child. In columns (2) and (3), the results of the estimates obtained using the synthetic panel approach are displayed. The dependent variables are dummy variables that, for each age of a respondent, switch to 1 the year she gets married for the first time or has a child, or remain 0 otherwise. A negative sign means that the outcome is delayed, which we consider to be an improvement. For instance, the negative coefficient in column (2) means that the year women marry occurs less early among the treated compared to the control cohorts. The coefficient can be interpreted as a dependent variable dummy would be, in percentage point change. Lastly, the dependent variable in column (4) is a continuous variable measuring the age gap in years 110 Deschênes and Hotte Table 5. Marriage Characteristics Child marriage Marriage First birth Age gap Education gap (1) (2) (3) (4) (5) Panel A: Interest experiment Number of schools 0.013 0.008∗∗∗ 0.008∗∗∗ 0.204 0.037∗∗ Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 (0.01) (0.00) (0.00) (0.29) (0.02) Number of schools ∗ treat 0.009 −0.009∗∗∗ −0.007∗∗∗ −0.316 0.002 (0.01) (0.00) (0.00) (0.26) (0.02) Mean dep. var. 0.17 0.09 0.08 8.19 0.26 N 5,687 64,734 70,001 4,818 4,735 R2 0.05 0.08 0.09 0.06 0.11 Panel B: Placebo experiment Number of schools ∗ placebo −0.009 0.003 0.005∗∗ 0.334 0.041∗∗∗ (0.01) (0.00) (0.00) (0.27) (0.01) Mean dep. var. 0.17 0.08 0.07 8.61 0.25 N 5,117 61,843 66,752 4,741 4,723 R2 0.04 0.07 0.08 0.07 0.12 Panel C: With pre-trend controls Number of schools ∗ treat 0.017 −0.011∗∗∗ −0.012∗∗∗ −0.641+ −0.048∗ (0.02) (0.00) (0.00) (0.43) (0.03) N 8,111 95,337 102,831 7,017 6,958 R2 0.04 0.07 0.09 0.05 0.11 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: The dependent variable in column (1) is a binary variable equal to 1 if the woman was married before 15 years old (available for the whole sample). The dependent variable in column (2) is a binary variable equal to 1 the year the respondent got married. The dependent variable in column (3) is a binary variable equal to 1 the year the woman had her first child. The dependent variable in column (4) is the age gap between spouses measured in years (available for married women at the time of the survey). The dependent variable in column (5) is a dummy equal to 1 if the husband is more educated than the wife, 0 otherwise (available for married women at the time of the survey). All specifications include municipality dummies, year of birth dummies, and interactions between the year of birth dummy and the number of children in the district of residence in 1993. We control for ethnicity, religion, age, and age squared. Sample: Women residing in rural areas. Significance levels are denoted as follows: +p < 0.15, ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01. between husband and wife, and the dependent variable in (5) is a dummy variable equal to 1 if the husband is more educated than the wife, and 0 otherwise. The policy did not affect the likelihood of early marriage as shown in column (1) of table 5, indicating that the pool of women who are susceptible to being married at primary-school age remained unchanged. However, columns (2) and (3) provide evidence that building schools reduced the probability of marriage and childbirth. At a given age, on average, it reduced the probability of being married by 0.9 percentage points (a decrease of 10 percent compared to the control group) and of giving birth for the first time by 0.7 percentage points. For age at first birth, the placebo in panel B is significant, capturing a difference in trend before the program started, albeit in the opposite direction to the main effect. Once the pre-trend in age at first birth is accounted for, in column (3) of panel C, the magnitude of the effect is slightly higher at 1.2 percentage points. Since child marriage remained unaffected, it implies that the link between primary education and marriage is not simply a substitution effect, where girls marry later because they are attending school at an age when they were previously already married. Another important aspect of the marital conditions is the characteristics of the chosen spouse, which could also be influenced by the program. Ideally, we would have liked to have data on all potential (un- realized) matches to investigate this aspect. The available data allows us to examine some characteristics of the actual matches for married women at the time of the survey. It is worth noting that the reform is relatively recent, and fewer women were married at the time of the survey in the treated cohorts com- pared to the control cohorts: 20.3 percent of treated women had never been in a union, compared to 1.45 percent of women in the control group. Treated women who were already married are likely to have been The World Bank Economic Review 111 Table 6. Polygamy, Tolerance and Experience of IPV Polygamy Emotional violence Physical violence Condemning violence index (1) (2) (3) (4) Panel A: Interest experiment Number of schools 0.019 0.045 −0.079+ −0.056+ Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 (0.02) (0.06) (0.05) (0.04) Number of schools ∗ treat 0.011 −0.077+ 0.056 0.057∗∗∗ (0.01) (0.05) (0.04) (0.02) Mean dep. var. 0.25 0.39 0.26 0.03 N 4,771 899 899 5,687 R2 0.06 0.21 0.14 0.13 Panel B: Placebo experiment Number of schools ∗ placebo 0.005 0.050 −0.019 −0.028 (0.02) (0.09) (0.09) (0.02) Mean dep. var. 0.27 0.41 0.23 0.09 N 4,681 662 662 5,117 R2 0.04 0.24 0.23 0.12 Panel C: With pre-trend controls Number of schools ∗ treat 0.004 −0.113 0.088 0.088∗∗ (0.03) (0.13) (0.13) (0.04) N 6,938 1,183 1,183 8,111 R2 0.04 0.17 0.13 0.12 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: The dependent variable in column (1) is a binary variable equal to 1 if the woman is married to a polygamous husband. The dependent variable in column (2) is a dummy taking the value 1 if the respondent experienced emotional violence. The dependent variable in column (3) is a dummy taking the value 1 if the respondent experienced physical violence. The dependent variable in column (4) is an Anderson index of tolerance of IPV, with reverted sign, meaning an index of condemnation of intimate partner violence (IPV). Sample: Women residing in rural areas. Significance levels are denoted as follows: +p < 0.15, ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01. selected in a particular way, as well as their husbands. Therefore, the analysis of the characteristics of the husbands may be biased in a direction that is difficult to anticipate. Columns (4) and (5) in panel A of table 5 shows that the education policy did not change the age gap between husband and wife among married women nor the education gap. The coefficient in column (5) of panel B captures a positive pre-trend in the education gap that goes in the opposite direction to the effect captured by the coefficients shown in columns (4) and (5) of panel C, obtained with specification (3), which directly controls for a pre-trend in the outcome variable. Using specification (3), we find that the education policy had a small impact on the age gap between partners that it decreased by 0.6 year or 0.08 percent of the baseline level (significant at the 10 percent level). As shown in column (5), the probability that men are more educated than their wife decreased by 5.4 percentage points (18 percent of the baseline level). The very modest change in the age gap and the relatively more substantial decrease in the education gap are consistent with women marrying men with similar characteristics as those they used to marry before the policy; since women are less likely to be uneducated, the education gap reduces mechanically. 4.3.2. Polygamy, Attitude towards IPV, and Experience of IPV We now investigate whether the education policy affected the probability of being in a polygamous union, the experience of domestic violence, and the tolerance of domestic violence. The dependent variable in column (1) of table 6 is a dummy variable equal to 1 if a woman is married to a polygamous partner. In column (2), it is a dummy variable equal to 1 if the respondent has experienced emotional violence. In column (3), the dependent variable is a dummy variable equal to 1 if the respondent has experienced physical violence. In column (4), it is an index of tolerance of domestic violence built using the method 112 Deschênes and Hotte Figure 5. Effect of the Treatment on the Intimate Parner Violence Index. Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 Source: Demographic and Health Surveys Benin 2011 and 2017. Note: The figure presents the coefficients of the interaction of the respondent’s age in 1997 and the number of schools built between 1997 and 2003 in the region of residence in equation (2). The dependent variable is a standardized index built using Anderson (2008). Sample: Rural women aged 15–49 years. by Anderson (2008). The scale is reversed so that a positive sign of the index suggests a positive outcome (experience of physical IPV and tolerance of IPV are decreasing). In contrast to the context studied by André and Dupraz (2023), the program seems not to have changed the probability of being in a polygamous union (table 6). Using the subsample of respondents who answered the DHS module on domestic violence in the DHS 2017–2018 survey wave, we find that the education reform decreased by 7.7 percentage points the expe- rience of emotional violence, which represents a decrease of 6 percent compared to the level of IPV in the control group (column (2) of table 6). The result is marginally significant at the 15 percent level and is not robust to directly controlling for pre-trend in column (1) of panel C (though it may be underpowered). The education policy did not significantly alter the experience of physical IPV. The estimate displayed in column (4) of panel A of table 6 indicates that the policy increased women’s likelihood of condemning domestic violence: the index of tolerance of IPV increased by 0.057 item (mean- ing that the tolerance of IPV decreased). Results are consistent with the estimation that directly controls for a pre-trend in column (4) of panel C. The magnitude of the coefficient in column (4) of panel C is larger as it accounts for a pre-trend that slightly goes in the opposite direction to the main effect. The effect of the treatment on each birth cohort is displayed in fig. 5. The figure illustrates that a change in trend occurs for the younger cohorts. The impact is noisier than for the access to primary school. These results may indicate that (a) education modified gender norms and relaxed the expectation around women’s behavior in the household, (b) increased education changed women’s perceptions of husbands’ alleged right to use physical violence to police their behavior, or (c) both phenomena occurred simultaneously. These three potential changes would mean that access to schooling can foster a process of awareness around the gender norms that curtail a woman’s ability to oppose a behavior that threatens their physical integrity. One could argue that the effects are driven by a social desirability bias. Even if it were the case, it would still be a signal that gender norms are becoming more progressive; if women worry that they may appear conservative to the enumerator, it suggests an underlying awareness that the prevailing norm is shifting away from tolerating domestic violence. The World Bank Economic Review 113 5. Robustness and Discussion 5.1. Migration To further allay concerns that selective migration may be driving our results, additional tests to those mentioned in the section that describes the empirical strategy are performed. Since we only know where women currently reside and not where they were educated, the results on education could be upwardly Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 biased if areas where the intensity of the program was high (low) attracted educated (uneducated) migrant women coming from areas where the intensity of the program was low (high). Likewise, the results on tolerance of domestic violence would be upwardly biased if areas where the intensity of the program was high (low) attracted progressive (conservative) migrant women coming from areas where the intensity of the program was low (high). Bounds of the estimate of school construction on tolerance of IPV using a worst-case/best-case sce- nario are first provided. The 2013 census is used to compute the share of women who have moved to high-intensity rural municipalities from either an urban area or a low-intensity area.18 According to our calculations, among the treated women who have migrated to high-intensity areas, 7 percent of them come from either an urban area or a low-intensity area. Among the treated women who have migrated to low-intensity rural areas, 2 percent of them come from either an urban area or a high-intensity area.19 In the worst (best) case, a scenario is simulated where the entirety of the 2 percent of the migrant women residing in low-intensity areas and who come from high-intensity areas are given the most conservative (progressive) score of tolerance of IPV, and the entirety of the 7 percent migrant women residing in high- intensity areas and who come from low-intensity areas are given the most progressive (conservative) score of tolerance of IPV. Table S2.3 in the supplementary online appendix shows that the bounds for the effect are tight and significant, which is to be expected as the specific patterns of migration that may lead to confound the effect of migration and the effect of school construction are limited. A simulation exercise is also performed whose outcome can be shown in fig. S1.2in the supplementary online appendix and that shows how strong migration in high- and low-intensity areas has to be to make the worst-case (lower) bound of the estimate non-significant. Figure S1.2 shows that under the worst-case scenario, there is no value of our estimate that becomes insignificant along the curve of the actual level of in-migration to low-intensity areas from high-intensity areas (at 0.02 along the green square-shaped markers). Along the curve of the actual level of in-migration to high-intensity areas from low-intensity areas (at 0.07 along the brown triangle-shaped markers), in-migration of treated women to low-intensity areas has to be twice the actual level for our estimates to become non-significant under the worst-case scenario. 5.2. Discussion The results show that increasing access to primary school improved some facets of women’s empower- ment; women delay marriage and motherhood and are less likely to condone domestic violence. Some results may point to a decrease in the actual experience of emotional violence but the results are only marginally significant. The disconnection between women condoning IPV and the actual experience of IPV (also found in other contexts, e.g. Erten and Keskin (2018)) confirm that changes in women’s toler- ance do not necessarily lead to changes in behavior. It could also be consistent with the program shifting the perception of what domestic violence is, without changing the level of violence experienced. Overall, even though married women among the youngest cohorts may be selected, which warrants caution in the interpretation, the results consistently point in the direction that the change in tolerance of 18 Women moving to high (low) intensity municipalities from a high (low) intensity municipalities are not a concern since they are likely to have been educated in areas where the intensity of the program was similar to the one where they are residing. 19 These computations are based on the census, which only provides information on the municipality of birth and of current residence: computations are therefore based on inter-municipality migrations (municipalities being larger than DHS clusters). 114 Deschênes and Hotte IPV primarily stems from women’s own exposure to more schools. The potential channels of change are here further discussed. Among the channels usually highlighted in the literature, we are able to discuss three: matching with a “better” husband in the marriage market, improved labor-market outcomes for women, and human capital acquired in school, broadly understood as the stock of knowledge, skills, and other personal characteristics embodied in people that helps them to be productive. In table S2.4 in the supplementary online appendix, the results highlight that for a subset of married Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 women, the policy reduced their husbands’ tolerance of domestic violence. Interestingly, these men were not directly affected by the policy due to their age. This suggests that the policy may have created broader changes in gender norms or that the husbands may have been influenced by their wives. Another possibil- ity is that women affected by the policy are marrying men who are less approving of domestic violence, even though these men are not more educated themselves (as shown in the section describing the results, the education gap with the partner decreases mechanically because women are more likely to have at- tended primary school, but the education level of their partner stays the same). Results are consistent with women’s marital outcomes being improved through a betterment of their position in the marriage market. Having access to resources outside the household through the labor market or improving outside options do not seem to be channels holding much weight in improving women’s marital outcomes in this study.20 It is consistent with the literature showing that similar policies have brought limited returns to the labor market for beneficiaries (Oyelere 2010), credibly linked to a concurrent decrease in school quality. It suggests that in this context, improvements in women’s empowerment are unlikely to be driven by higher access to financial resources and that it has an impact on the type of violence they are exposed to. In Erten and Keskin (2018) and Bobonis, González-Brenes, and Castro (2013), women’s increased access to financial resources (through the labor market or through a cash transfer) notably led to more psychological violence. In this study, we show that when this channel is likely to be muted, other facets of women’s empowerment improve and women seem to escape unintended consequences related to tensions within the household for control over financial resources. In spite of a lack of improvement of their literacy, it cannot be ruled out that women may have picked up skills, know-how, or formed networks among their peers at school that may have improved their human capital in a way that was conducive of an improvement in empowerment. The current unavailability of data constrains the understanding of the way women’s human capital may have changed. Studying the dimensions of human capital beyond learning that may boost women’s empowerment could be a fruitful avenue for future research. 6. Conclusion In this paper we show that in rural areas women who benefited from school openings delayed the onset of marital and fertile life and were less likely to find domestic violence justified. Evidence is provided that the changes in marital outcomes were caused by women’s own exposure to school construction and not by their husbands’. The paper contributes to the discussion on whether education may unevenly improve various aspects of women’s empowerment and our results suggest that (a) education policies that did not change women’s access to resources through the labor market may still be able to improve women’s empowerment, and that (b) because women’s access to financial resources seems to have remained unchanged in this context, 20 We acknowledge that the policy may have increased women’s bargaining power in the labor market, potentially pro- viding them with increased opportunities without necessarily requiring them to actually work. For instance, the policy might have made the threat of divorce more credible for women who had better work options available if they needed them. However, considering the context and the fact that the policy did not have an impact on literacy, we believe that the likelihood of this scenario is not very high. The World Bank Economic Review 115 unintended negative consequences of education policies, like an increase in psychological violence and a tightening of the control exerted by the husband (Erten and Keskin 2018), did not materialize. The findings suggest that education policies can make women better off, even though labor-market outcomes do not improve, by notably bettering their position in the marriage market. This paper stands out as one of the few that focus specifically on the effects of 1990s mass education programs on women’s well-being within the household in a West African French-speaking country, where Downloaded from https://academic.oup.com/wber/article/38/1/95/7457025 by Joint Bank/Fund Library user on 02 February 2024 the level of baseline education was lower than in the countries that have garnered more attention from researchers so far. 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