Mothers and fathers: education, co-residence, and child health

This paper evaluates the causal effects of mother’s and father’s education on child-health outcomes in Zimbabwe, exploiting the exogenous variation generated by the 1980 education reform. We use four waves of Demographic and Health Surveys for Zimbabwe and estimate a simultaneous-equation model to take into account possible selection into co-residence between parents and children, endogeneity biases, and parental education sorting. Our results suggest that father’s education affects the health outcomes of under-5 children and matters more than that of the mother. These results continue to hold in a number of robustness checks. Moreover, while there is selection into co-residence with the child, this does not affect the causal effect of education on child health. Last, parental educational sorting is also shown to be important. Our findings suggest that not taking the education of both parents into account simultaneously may yield misleading conclusions.


Introduction
The factors leading to better health are as important to economists as to other researchers in social sciences and policy-makers.The lack of resources at both the governmental and individual levels has long been highlighted as the main barrier to improving health in developing countries.Poor people in low-income countries face a variety of health-related risks, with young children accounting for most of the global disease burden.Of the 55.4 million deaths in 2019, 9.3% were of children under the age of five.In Africa, this figure reached 34.8%. 1 Over 46% of all deaths in low-income countries in 2019 were caused by so-called "Group I" conditions, which cover communicable, maternal, perinatal, and nutritional conditions.This figure was 52.9% in the WHO African Region in 2019, but, by way of contrast, only 6.6% in high-income countries (World Health Organization, 2020).As such, most deaths could be avoided by adopting preventive actions such as vaccination, water filtering, breastfeeding, and the use of bed-nets (Banerjee and Duflo, 2011).Education plays a key role here via its induced increased demand for preventive actions.
Since the model of health demand developed by Grossman (1972), the educationhealth relationship has appeared in a large body of theoretical and empirical research.On average, the more-educated have better health and live longer than the less-educated (e.g., Lleras-Muney, 2005).Education not only affects adults' own health, but parental education also impacts the health of their children.
There are many channels through which education may affect health.The first is wealth: the educated are likely to have better labor-market opportunities and higher wages (e.g., Card 1999; Cutler and Lleras-Muney 2010), and so can more likely afford the cost of prevention, treatment, and private health-insurance, have better access to health care and health centers, and have less-unhealthy jobs.Second, the educated are more likely to understand the prevention messages they receive than are their less-educated counterparts (e.g., Baker et al., 2011 or de Walque 2007).Third, they have greater incentives to invest in preventive behaviors as, given that wages rise with education, their future income loss from illness is higher (as proposed by Grossman 2000 when considering cigarette consumption).Last, education helps teach discipline, compliance with rules and regulations, the exertion of effort, and the acceptance of constraints, as noted in Basu (2002).As such, education may help in the adoption of costly preventive behaviors, by making people more willing to bear non-monetary costs.Most of these mechanisms also apply to the link between parental education and child health.
Using the four waves of the Demographic and Health Surveys collected in Zimbabwe from 1994 to 2010/11, we examine the health outcomes of children aged 0-59 months born between 1990 and 2011. 2 We compare the outcomes of children with educated mothers and fathers to those with less-educated parents.
The major difficulty in making this comparison is the endogeneity of education due to the correlation between the unobservable characteristics leading to education and those leading to health investments.Two examples of these unobserved characteristics are ability and time preferences.Education and health are two indicators of human capital, and investing in education and health both entail costly investments today for an uncertain future benefit.In addition, if educated parents are in better health than are less-educated parents, child health will be affected via the intergenerational transmission of health (e.g., Bhalotra and Rawlings 2011).
A number of contributions have exploited exogenous variations in education to identify the causal relationship between education and outcomes such as employment, fertility, and health.Recent work has explored the relationship between education and health in developing countries via major school-system reforms between 1970 and 2000.Using information on reforms allows us to estimate the causal effect of education on health outcomes in a quasi-experimental setting, as it provides exogenous variation in primary-or secondary-school enrolment, the number of years of completed schooling, and the probability of dropping out of school in instrumentalvariable or regression-discontinuity analyses.Some examples of these reforms are compulsory school-enrollment (Agüero and Bharadwaj, 2014; Grépin and Bharadwaj, 2015; Günes, 2015; Silles, 2011), the rise in the school-leaving age (Albouy  and Lequien, 2009; Kemptner et al., 2011), the increase in the supply of schools (Bhalotra and Clarke, 2014; Breierova and Duflo, 2004; Silles, 2009), the provision of trained teachers (Shrestha and Shrestha, 2020), the implementation of Universal Primary Education policies (Behrman, 2015; Delesalle, 2021; Osili and Long, 2008), and changes in school fees (Chicoine, 2021; Hahn et al., 2018; Masuda and Yamauchi,  2020; Oyelere, 2010; Silles, 2009, 2011; Zenebe Gebre, 2020).
We exploit the exogenous rise in education resulting from a 1980 reform to estimate the causal effect of mother's and father's education on child health in Zimbabwe.This 1980 reform was nationwide and mostly consisted of compulsory primary schoolenrollment, the removal of primary-school fees, and automatic admission to secondary school.It affected all school-age children, and most importantly children born after 1965 as they were aged under 15 at the time of the reform and were exogenously more likely to go on to secondary schooling than were earlier cohorts.
Assuming random co-residence between parents and children in the population may also bias the estimates, and all the more so that it applies to a non-negligible share of children: only 52.7% of our survey children aged 0-59 months live with both 2 Zimbabwe is a low-income country with 16 million inhabitants and GDP per capita of 2,085.7 current international $ in PPP in 2017 (World Bank, World Development Indicators)) located in Southern Africa.The under-5 mortality rate was 86 per 1000 live births in 2010 (World Bank, World Development Indicators).Life expectancy at birth was 61 in 1985, 44 in 2002, and 51 in 2010 (World Bank, World Development  Indicators).The large fall at the end of the 1990 s reflects the country's high rate of HIV prevalence.The HIV prevalence rate in the Demographic and Health Surveys was 21.1% for women aged 15-49, and 14.5% for men in 2005 (vs.figures of 17.7 and 12.3, respectively in 2010/11).
parents.It is well-established in the literature that children growing up in single-parent households acquire less human capital, whether the parents divorced or one died (see Adda et al., 2011; Fitzsimons and Mesnard, 2014).Living with both parents, compared to living with only one or neither, is not random and might affect child health.We treat this empirically as a selection issue.One consequence of non-coresidence with both parents is that the education of the parent living elsewhere is unobserved.In our data, as in most household surveys, the questions are asked to permanent residents, and no information is recorded for those who do not currently live in the sample household.The selection equations, one for each parent, are identified using exogenous variations in community practices (e.g., the share of mothers who gave birth before being married).Our analysis of selection into co-residence provides new insights into the current literature on the education-health relationship, which has not to date taken this issue into account.Emran et al. (2018) note this source of potential bias, calling it a truncation bias due to co-residency in estimates of intergenerational mobility.
We also contribute to the literature on the respective role of mothers and fathers on child outcomes.The role of father's education has been overlooked in the current literature, with only relatively few contributions (Alderman and Headey, 2017; Apouey  and Geoffard, 2016; Breierova and Duflo, 2004; Case and Paxson, 2001; Chou et al.,  2010; De Neve and Subramanian, 2017; Lindeboom et al., 2009; Averett et al., 2005).This could reflect the common wisdom that mothers matter more than fathers for the raising of children.Another purely empirical reason is that mothers are more likely than fathers to live with their children in many countries, leading to empirical challenges when attempting to evaluate the role of fathers.Case and Paxson (2001) analyze the role of father's and mother's education and co-residence on child health in the USA, but without modeling selection into co-residence or marital sorting.
Our work also takes into account the marital education sorting of parents as an additional source of potential bias.If there is substantial correlation between the education of the two parents, the estimate of the effect of the mother's education only on child health may actually rather reflect the effect of the father's education.This source of bias is acknowledged, although not resolved, in Carneiro et al. (2013), who estimate the effect of maternal education on child outcomes.Using data from Nepal to consider the role of mother's education on child welfare, Fafchamps and Shilpi  (2014) conclude that "part of the association between female education and household outcomes is driven by marriage market matching with more educated men" (p.110).The bias may also come from unobservable characteristics (such as ability and time preferences) that drive (un)educated people to match together.Marital sorting based on education has been documented in both developed and developing countries (e.g., Azam and Djemai, 2019; Chiappori et al., 2009; Hahn et al., 2018; Van Bavel  and Klesment, 2017; Garfinkel et al., 2002).
The father's contribution has been modeled in three ways in recent research.First, the effect of the average of mother's and father's education is estimated in Breierova and  Duflo (2004).However, this does not allow us to consider differences between parents, nor to use exposure to the reform as an instrumental variable (as men are usually older than their spouses).Second, two separate models have been estimated, one controlling for mother's education and the other for father's education, as in Apouey and Geoffard  (2016), Chou et al. (2010) and De Neve and Subramanian (2017).We believe this approach to be debatable for two reasons: when there is educational marital sorting, part of the effect of mother's education may reflect that of the father, and there is no discussion of co-residence, even though the sample sizes vary from one estimation to the other.If one parent is absent because of divorce or death, the parent who lives with the child might compensate for this absence, and all the more so when (s)he is more educated and, as such, has a greater ability to adjust.Some research has explored the role of the absence of one parent on the formation of human capital, finding substantial effects.One example is Adda et al. (2011), who evaluate the long-term consequences of parental death and conclude that mothers and fathers have differential effects on child cognitive and non-cognitive skills.The third approach is to estimate the effect of both mother's and father's education in the same equation, as in Lindeboom et al.  (2009) and Alderman and Headey (2017).In the latter, the effects of maternal and paternal education are estimated even for non-biological parents, even though these might be different given the research on child fostering and step-mothers (e.g., Case  and Paxson, 2001).In this paper, we focus on the role of biological mothers and fathers and estimate their respective effects in one single equation.
The work of Grépin and Bharadwaj (2015), De Neve and Subramanian (2017), and Makate and Makate (2018) is the closest to our analysis here, as they appeal to the 1980 education reform in Zimbabwe to estimate the causal effect of parental education on child health.Grépin and Bharadwaj (2015) focus on the effect of maternal education on child mortality, and Makate and Makate (2018) on dietary practices and nutrition, while we estimate the effect of both father's and mother's education on child's current health, prenatal care, and childbirth conditions.De Neve and Subramanian (2017) consider the relationship between father's and mother's education and child malnutrition, as we do, but their estimation strategy is different from ours in a number of respects: they estimate the respective effects in separate regressions, the outcomes are different, and they take neither marital sorting nor selection into co-residence into account.De Neve and Subramanian (2017) find a negative uninstrumented correlation between both mother's and father's schooling and child nutrition outcomes (stunting, wasting, and underweight), but no evidence of a causal effect of parental schooling when schooling is instrumented by exposure to the reform.
Our results mostly confirm the existing evidence: there is a considerable correlation between both mother's and father's education and child health.We instrument education by the exposure to the 1980 reform that affected those born in 1965 or later.The instrumented effect of father's education on prenatal care, birth conditions, and vaccination continues to be positive; however, that of mother's education disappears.The same conclusion pertains when we exclude parents who were born in 1965 and 1966 (who were only partially exposed to the education reform), when we restrict the sample to parents who were born in years close to 1965, and when selection into co-residence is taken into account.While the frequently significant Inverse Mills Ratios reveal that selection affects child health, including these Inverse Mills Ratios does not affect the size and significance of the 2SLS coefficients of parental education on child's health.We also provide some supporting evidence that, while wealth and fertility might act as mediators, education directly affects child health.Last, we show that not including father's education in the regression yields a significant instrumented effect of mother's education on birth outcomes and the child sleeping under a bed net.In Zimbabwe, the effect of the mother's education is then confounded by father's education when the latter is omitted, reflecting parents' assortative matching.
The remainder of our paper is organized as follows.Section 2 presents the data, and Section 3 describes the reform and its impact on parents' education.The estimation strategy is presented in Section 4. The empirical results then appear in Section 5, and the robustness checks and extensions in Section 6. Last, Section 7 concludes.

Sample
We use household-level data from the Demographic and Health Surveys in Zimbabwe.This survey is nationally representative of households and was collected in 1994, 1999, 2005/06, and 2010/11. 3 The sampling is in two stages and is independent in each survey round.First, enumeration areas are selected based on the most recent available census.Second, a complete listing of the households living in the selected enumeration areas (also called communities here) is established in order to randomly select the sampled households, and in the latter, all women aged 15-49, whether permanent residents or visitors (who slept in the household the night before the survey), are eligible for interview.We use the data files from the household roster, the female questionnaire and, to a lesser extent, the male questionnaire.
The household roster contains the complete list of household members and, for each member, age and highest level of education.For children, the identification codes of the mother and father are reported if they live in the same household.As such, we have various types of households and family composition: we observe children who do not live with their parents (e.g., foster children) and children living with either one or both parents.By construction, if a sample mother does not live with one of her children, this child is not a household member and is not present for the collection of the anthropometric measures of height and weight.
The analysis focuses on children between 0 and 59 months old.Mothers are asked specific questions about all of the children they had over the 5 years preceding the survey as part of the female questionnaire.These questions cover prenatal care, delivery conditions, and preventive behaviors such as vaccination.We also have anthropometric measures for children in this age group.The four rounds of survey data cover 19,702 children aged 0-59 months 4 : we thus analyze young children born over the 1990 to 2011 period.However, in order to have information on the education of both parents, we restrict the sample to children who currently live with both parents (N = 10,381 children).We will discuss the potential selection bias arising from co-residence in Section 4.3 below.Mothers in this sample were born between 1916 and 1995, and  fathers between 1898 and 1993.To circumvent parental survival bias, we dropped the oldest parents from this sample (all those born before 1950). 5Our analysis sample is composed of 9365 children aged 0-59 months.
Note that couples may be observed more than once if they have more than one child aged 0-59 months at the time of the survey.These duplicates are on average more likely to concern younger and/or less-educated parents.These couples would then have greater weight in the regressions.In our analysis sample, 77% of couples have only one observed child and 23% more than one child aged 0-59 months.We thus have a total of 9365 children and 7497 mothers.Five thousand seven hundred forty-four of these have only one observed 0-59-month-old child.Our core empirical results hold when we weight the observations by the square root of the number of observations for each couple (Online Appendix Table G4).

Data description
The summary statistics for the whole sample appear in column 1 of Table 1.A full description of the variables is provided in Online Appendix Tables A1 and A2.
Over the entire sample, 50% of the children are girls, average age is 2, and 24% live in urban areas.The mother is still alive for 98% of the 0-59 month-old children living in sampled households, and the father is alive for 95%.Co-residence with the mother is 31 percentage points more likely than co-residence with the father: 85% of children live in the same household as their mother, and 54% in the same household as their father.
The summary statistics for the outcome variables appear in panel B. These can be grouped into three categories: (1) outcomes related to prenatal care and birth (a dummy for the mother having had at least four prenatal visits during her pregnancy, the child being born in a health facility, and the mother having been assisted by medical staff at birth); (2) malnutrition (dummies for stunting-too short for their age-and wastingtoo thin for their height) 6 ; and (3) preventive actions (vaccination and sleeping under a mosquito bed-net). 7ixty-nine percent of the sampled children were born in a health facility, and the birth of 68% was assisted by a skilled medical attendant.Seventy-one percent of mothers had at least four prenatal visits, and 33% of young children are stunted and 6% wasted.The average number of injections from the recommended immunization package (BCG, diphteria-pertussis-tetanus, measles, and polio) received for the sample 5 Only 100 children had mothers born before 1950, and 1004 fathers born before 1950. 6Children are stunted if their height-for-age Z-score is over two standard deviations below the reference value and wasted if their weight-for-height Z-score is over two standard deviations below the reference value. 7The use of bed-nets was not asked in the 1994 and 1999 survey waves.We do not analyze breastfeeding as 98% of children were breastfed.We are unable to estimate the effect of parental education on child mortality as it is not possible to link dead children to their fathers: the information required to do so is only recorded for children who are alive and living in the sampled households.children aged 0-59 months was 5.73 (out of 8), and 9% of sampled children slept under a bed-net the night before the survey.
Mother's and father's education appear in panel C of Table 1.Our unit of observation is the child for the parental statistics.The average years of schooling is 7.6 for mothers and 8.3 for fathers, 69% (73%) of mothers (fathers) completed primary school, and 52% (59%) had at least one year of secondary-school education.
The other control variables appear in panel D. The mothers' average age is 28.3 and that of fathers 36.2.This age difference corresponds to that often found in existing work (e.g., d'Albis et al., 2012).We also list the variables used to estimate the probability that the child lives with the father or mother.The average proportion of respondents who are separated, divorced, or widowed in the community is 15%, the proportion of women who had their first child before marriage is 20%, and the average proportion of polygamous households is 14%.
Note that the descriptive statistics for the entire sample (column 1), the sub-sample of children living with both parents (column 2), and the sub-sample of children who live with both parents and who have parents born in 1950 or later (column 3) are very similar.This suggests that our analytical sample is not overly selected.In panel C, the outcomes are very similar in columns 2 and 3, suggesting that the sample restriction to parents born after 1950 is not a major issue.

The reform
Prior to 1980, when the UK officially recognized the Independence of Zimbabwe, there were enormous inequalities in education between Whites and Blacks.For Whites, who represented 3.5% of the population, education was free and compulsory until the age of 15, and admission to secondary school was automatic after pupils passed their primary-school final exam (Dorsey, 1989).However, education was neither free nor compulsory for Blacks, who faced considerable selection at each grade.As a result, only 4% of Black pupils were in secondary school: the analogous figure was 43% for White pupils (Dorsey, 1989).There was also inequality between boys and girls.In 1975, the girl/boy ratio was 85% in primary school and 71% in secondary school (World Development Indicators, as reported in Online Appendix Table A3).
The first Black-majority government-led by the Zimbabwe African National Union (ZANU) party-came into power with Independence in 1980.Education was one of its top priorities, and the new Constitution declared education as a fundamental human right (Education Act 2004).From 1980 on, the Government launched a vast reform to raise school attendance and the education of every child (Colclough et al.,  1990).This expansion was universal, as it concerned both girls and boys and covered the whole country.The main policy changes took place in 1980 and can be summarized as follows:  1994, 1999, 2005, and 2010   Notes: Unweighted statistics.The data covers children aged 0-59 months at the time of the survey, with a maximum of 19,702 observations (for some outcomes, the number of observations varies slightly due to data availability).The sub-sample in column 2 corresponds to 0-59 month-old children living with both parents, and that in column 3 to 0-59 month-old children living with both parents, who were born in 1950 or later.Prenatal care variables (at least 4 prenatal visits, health facility birth, birth assisted by medical staff), mother's education, mother's age observed only if the mother is currently living with the child.Father's education and age observed only if the father is currently living with the child • Primary education became free and compulsory for all pupils.Given the official duration of primary education, all children would leave school with at least 7 years of education.• Admission to secondary school became automatic for all pupils, whatever their performance in the primary-school final exam.Secondary education remained paying.• Age restrictions were removed to allow older children to re-enter school.
• The government changed the school zoning system that gave Whites access to the best schools; it also introduced double-session schooling in almost all urban schools and some rural ones.
The reform took place in 1980 and was accompanied by an increase in the supply of schools and teachers in the following years.The Government reconstructed all schools that had been destroyed during the war and built new primary and secondary schools, in particular in marginalized areas and disadvantaged urban centers (Kanyongo, 2005).New teachers were recruited.In Online Appendix Table A3, World Development Indicators (World Bank) statistics show that there was a huge jump in the number of primary-school teachers between 1980 and 1985 and an even larger jump in secondaryschool teachers (from 3782 in 1980 to 19,507 in 1985).This implies that the pupil-toteacher ratio remained fairly stable at around 40 in primary schools and 28 in secondary schools.Last, government education expenditure rose sharply around the time of the reform, from 2.5% of GDP in 1980 to 12.5% in 1990.

Parental education and exposure to the reform
The reform affected children of primary-and secondary-school age.It aimed to increase access to primary education and facilitate entry to secondary schools, theoretically at age 13 as primary education lasts 7 years. 8The exposure to the reform has been used in previous analyses as it provides exogenous variation in educational attainment (Agüero and Bharadwaj, 2014; Croke et al., 2016; De Neve and Subramanian, 2017; Grépin and Bharadwaj, 2015; Makate and Makate, 2018).In all of these analyses, the cohorts born in 1967 or later are considered to be exposed as they were aged 13 or younger in 1980.The cohorts born in the 1963-1966 period are treated differently across the articles (excluded, as controls, or partially exposed). 9We consequently define all individuals who were 15 or younger in 1980 as being exposed to the Education reform, in other words, all individuals born from 1965 onwards.This definition includes individuals who were 13 or younger in 1980 (i.e., fully exposed) as well as those aged 14 and 15 in 1980, as the policy allowed over-age children to 8 Up to 1986, children started primary school at age 7 (World Development Indicators). 9Agüero and Bharadwaj (2014) and Grépin and Bharadwaj (2015) restrict their sample to those aged 9-20 in 1980.Agüero and Bharadwaj (2014) define the treatment variable as being 15 or younger in 1980.Grépin  and Bharadwaj (2015) consider women who were aged 13 and younger in 1980 to have been fully exposed to the policy, women aged 14 and 15 in 1980 to have been partially exposed, and women aged 16 or older in 1980 as the control group.Croke et al. (2016) and De Neve and Subramanian (2017) do not exclude the partially exposed.The only difference between their two definitions is that those born in 1963 appear in the "partially exposed" group in Croke et al. (2016) and in the control group in De Neve and Subramanian (2017).re-enter school (so that they were partially exposed).We will discuss the effect on our results of the inclusion of this latter group as being exposed as a robustness check.
In our sample, 89% (70%) of children have mothers (fathers) who were exposed to the reform (Table 2, panel A).Mothers exposed to the reform have on average 8.2 years of education, versus 4.8 years for those not exposed (columns 2 and 3).Seventy-six percent of the exposed mothers (37% of the non-exposed mothers) completed primary school, and 59% (18%) attended secondary school.The analogous figures for fathers were 9.4 (6.9) years of education, 85% (column 4) completed primary school (versus 59% in column 5), and 74% (38%) attended secondary school.The reform then led to around three additional years of education, with a somewhat larger effect for mothers than for fathers.Fathers were much more educated than mothers pre-reform, and this gender difference remained post-reform.
Figure 1 depicts the proportion of mothers and fathers in each birth cohort who completed primary school (Fig. 1a), who attended secondary school even without completing (Fig. 1b), and their respective years of education (Fig. 1c).The vertical line corresponds to the 1965 cohort, which was the first cohort exposed to the education reform.
There are two main features.First, as shown in Fig. 1a and b, the reform resulted in an increase in the completion of primary education and in secondary-school attendance.Years of education in Fig. 1c are also higher for those born in or after 1965.Second, educational attainment started to rise even for the cohorts born before 1965 for all three education measures (Fig. 1a-c).Even though schooling was not compulsory for this group, they may have benefited from the lifting of age restrictions for school enrollment: these cohorts were affected via easier post-1980 access to schools.
Overall, the increase in education is found for both sexes, although it is more pronounced for mothers.Fathers benefited from greater access to secondary schools, as they were already more likely to be enrolled in primary school than were mothers.
We estimate the effect of being exposed to the reform on each additional year of education.In Zimbabwe, primary education lasts for 7 years and secondary education 6 (including 2 years of lower-secondary education and 4 years of upper-secondary education), so that pupils completing both levels have 13 years of education.Figure 2 displays the effect of exposure to the 1980 reform on the probability of attaining at least a certain number of years of education, by gender, from values of 1 to 18 years. 10or both mothers and fathers, the reform had a considerable impact on primary and lower-secondary school attendance, while that for upper-secondary and tertiary school attendance is very small and insignificant for having at least 16-18 years of education.Exposure to the reform increased attendance at all primary and lower-secondary school levels.For mothers, the largest effects are for the probability of having at least 6 (+45 percentage points), 7 (+47 percentage points), and 8 (+43 percentage points) years of education, i.e., the end of primary school and the beginning of secondary education.For fathers, the largest estimated effects are for having 8, 9, and 10 years of education (+35, +33, and +35 percentage points), i.e., lower-secondary education.

Econometric specification
We estimate the joint impact of father's and mother's education on a number of childhealth outcomes.Given the way in which the Demographic and Health Surveys are collected (as described above), this is only possible when the child lives with both parents.Our empirical strategy therefore tackles three econometric issues: (i) the Fig. 2 Reform exposure and educational attainment endogeneity of father's and mother's education; (ii) marital educational sorting (i.e., homogamy); and (iii) selection into co-residence, as the sample of children who live with both parents may be non-random.

The endogeneity of education
In the child-outcome equation, father's and mother's education are likely endogenous, leading to inconsistent estimates of the impact of education on child-health outcomes.
Unobservable parental characteristics (such as time preference, ability, and intrinsic motivation) may influence their investment in both their own human capital (education) and the health of their children.In addition, parental education is correlated with parental health status, and healthy parents are more likely to have healthy children.
Not controlling for parent's own health status is then a second source of endogeneity bias.
As shown in Fig. 1, free and compulsory primary education, as well as greater access to secondary education, brought about an exogenous rise in educational attainment in Zimbabwe.Fathers and mothers born in or after 1965 (i.e., who were 15 or younger in 1980, or were not yet born) were young enough to benefit from the 1980 education reform, which substantially enlarged their schooling opportunities relative to those born earlier.The exogenous variation in education levels due to the age-specific nature of the reform can be exploited in two different ways to tackle the endogeneity of parents' education.
We can first use the regression discontinuity (RD) approach in a fuzzy design, as in Grépin and Bharadwaj (2015), with the only difference being that we have two "running variables" that partially determine mother's and father's education: the mother's and father's birth years.Using the discontinuity in the probability of attending secondary school and the average number of years of education due to the education reform for those born in 1965, as seen in Fig. 1, this would amount to implementing a double regression discontinuity approach (as in Stancanelli and Van Soest, 2012 and  Müller and Shaikh, 2018, who analyze retirement decisions within couples).However, this strategy is not suitable in our case.The RD approach provides a local estimate of the effect of education on outcomes, around the 1965 birth-year threshold, and the sample used for this estimate is restricted to observations that are close to this cut-off.However, by construction, the size of our sample is already small, and restricting it to parents born for example 10 years around the reform (which seems the largest credible bandwith for a RD approach) would lead to a sample with only 3645 observations, which is too small to provide precise estimates.More importantly, the double RD approach imposes the use of the same bandwidth for fathers and mothers, meaning that we would have to run the estimates on mothers and fathers who were both born between, say, 1955 and 1975.This would create substantial selection bias by only retaining couples of the same age.Contrary to OECD countries, where the age gap between spouses is quite low so that identical bandwidths can be used (as in Lindeboom  et al., 2009 in the UK for example), the age gap is much larger in Zimbabwe (at 7 years on average within the couple).
We therefore prefer to apply 2SLS, with two first-stage regressions: one each for mother's and father's education, using the individual exposure to the reform as the instrumental variable as follows: Here, i refers to the child (i = 1, ..., N ; N denotes the size of the analysis sample), h the household, and t the survey year.M denotes child i's mother and F the father. 11e consider two alternative dependent variables, as in previous work on the 1980 education reform.Educ M and Educ F refer to either the number of years of education of child i's mother and father, respectively, or to dummies indicating whether they attended secondary school.The continuous variable is our preferred education measure: as the reform affected attendance at both primary and secondary school, years of education pick up the full reform effect. 12 M iht (T F iht ) are dummy variables for the mother (father) being born in 1965 onwards, i.e., was 15 or younger in 1980.The direct impacts of the reform are given by β M 1 for the mother and β F 1 for the father.f (B M − 1965) (in Eq. 1) and g(B F − 1965) (in Eq. 2), where B is the parent's birth year, denote the linear trends before and after the 1965 birth-year threshold.As in Agüero and Bharadwaj (2014), these linear trends are included to capture differential trends in education for the older and younger cohorts, as suggested in Fig. 1 , and analogously for the father's g(B F − 1965).We will consider two versions of our first-stage regressions.The first does not include these linear trends, and the only excluded instrument is T M iht (T F iht ) for the mother (father).In the second, the two trends will be added to the separate first-stage equations for mothers (Eq. 1) and fathers (Eq.2).The change over time in Fig. 1 is fairly smooth for both mothers and fathers, and both pre and post the 1965 birth year, except for fathers' secondary-school attendance (in Fig. 1b).We have also explored linear-spline specifications with more than two segments: these do not improve our first-stage regressions (the coefficients are often insignificant, and the Kleibergen-Paap F-statistics are lower) and yield similar 2SLS results (see Online Appendix Table F2).
X iht is a vector of control variables that will appear in the second-stage equations (such as child sex and age), which have also to appear in the first-stage regressions for identification purposes.We also include survey-year dummies, δ t .Given our econo-metric approach, we in addition need to include other variables in these first-stage regressions: these will be described in Section 4.4, where the final model is set out.
For the instrumental variable to be valid, it has to be correlated with the observed level of education, but not with the error term of the second-stage equation (Eq. 9 below).The first correlation is discussed when presenting the results from the first-stage estimations in Sect.5.1.The second requirement is that of the exclusion restriction: the instrument should have no effect on the outcome other than through the first-stage channel.The exclusion restriction here is that having a parent being born before or after 1965 does not affect child health in any other way than via parental education.We may worry that the difference between those born before or after 1965 could reflect structural changes following Independence, in particular the health reform that was introduced in 1980.This health reform is described in Bassett et al. (1997) and Hecht et al. (1993), although there has been no formal impact evaluation of it.The main progress in the health-care sector took place between 1980 and 1985 in rural areas.This progress then stalled, mainly due a decreasing budget share devoted to health (Bassett et al., 1997). 13he health reform overall led to significantly higher vaccination, contraception use, and life expectancy, while infant mortality fell (Hecht et al., 1993).It likely improved the health of all individuals, whatever their age (Grépin and Bharadwaj,  2015).The parents in our sample were affected by this reform during a short period of time (between 1980 and 1985) and at different ages: parents treated by the education reform experienced better health care during their childhood (they were below 15 in 1980), while the non-treated parents benefited during the ages at which they were more likely to have children (they were between 16 and 30 in 1980).As such, the health reform did not specifically benefit those born before or after 1965.This can be seen in our data: when we estimate the effect of being exposed to the education reform on mother's height and her probability of being underweight at the time of the survey in a reduced-form model (Eq.1), we do not find any significant estimated coefficients (see Online Appendix Table E1).The exclusion restriction is therefore likely not to be violated.

Assortative matching
Marital educational matching may be an issue in our analysis.In the analysis sample, 86% of children whose mothers completed primary school have a father who also completed primary school; the analogous figure for attending secondary school is 82%.There is thus a substantial correlation (0.64) between mother's and father's years of education.
Note, however, that this assortative matching does not depend on exposure to the education reform, as it was already substantial for parents born before 1965.Indeed 65% of the children have parents with the same level of education (no education, primary, or at least some secondary) when their parents are both unexposed, while this figure is 72% when both parents are exposed.When estimating Eqs. 1 and 2 with a dummy for assortative matching as the dependent variable in a reduced-form approach, the effect of reform exposure is only significant for fathers (see Online Appendix Table B1).This suggests that educated men are more likely to marry educated women, as there are now more educated women on the marriage market.
If women and men with similar education tend to live with or marry each other, the unobservable characteristics that explain mothers' education (such as intrinsic motivation and time preference) may well be correlated with the unobservables that explain fathers' education.In our final model, we therefore estimate mother's and father's education (Eqs. 1 and 2) simultaneously, taking into account the correlation between the residuals (ε M iht and ε F iht ).We find positive and very significant correlations (0.56 for years of education and 0.41 for secondary-school attendance) between these residuals: fathers and mothers with similar intrinsic incentives or aspirations towards human-capital investment tend to live and have children with each other.

Selection into co-residence
Of the 19,702 sample children aged 0-59 months, 52.7% live with both parents, 13.5% with neither, 1.3% with their father only, and 32.5% with their mother only.More details on the different possible configurations appear in Online Appendix C. The percentage of children living with both parents is fairly stable over the successive survey rounds: 52.8% in 1994, 52% in 1999, 53% in 2005, and 52.7% in 2010.This relatively low percentage of children living with both parents is also found in other countries, although the figure in Zimbabwe is one of the lowest in Sub-Saharan Africa according to Pilon and Vignikin (2006). 14ppendix Table C2 shows the difference between children who co-reside with both parents and those who do not.Except for the number of injections, the difference in child-health outcomes is significant but only small in size.There is no difference in child's sex and a slight difference in age (those in the excluded sample are 0.3 years older than those in the analysis sample).However, the household characteristics are strongly significantly different: children who co-reside are much more likely to live in urban areas (32%) and in rich households (41%) than those who do not (with respective figures of 18% and 26%).We may then suspect that the levels of education will also differ between the two groups, as education is associated with urbanization and wealth.It is thus likely that the parents who do not co-reside with their children have lower (unobserved) education than do parents who co-reside with their children.
Our estimates may suffer from selection bias due to the co-residence restriction, for which we need to correct.The unit of analysis here is all children 0-59 months old living in sampled households, and selection bias is addressed via Heckman's two-step procedure. 15We estimate two probit selection equations, one each for the mother and father.Let Coresidence M iht (Coresidence F iht ) be a dummy for child i living with her mother M (father F).We have where Coresidence * M iht and Coresidence * F iht are latent variables defined as follows: As before, i indexes the child (i = 1, ..., N T , where N T denotes the size of the initial sample), h the household, and t the year of the survey.The models include the child characteristics (X iht ) from the outcome equation, as described below, and survey year fixed effects, θ t .
The estimation of these selection equations requires exclusion restrictions, i.e., variables that influence co-residence but have no direct effect on the outcome.We use community-level variables, denoted by Z iht : the proportion of sampled women who gave birth to their first child before marriage, the proportion of respondents who are currently divorced, separated or widowed, and the proportion of polygamous unions in each community. 16These community-level variables are proxies for the social norms that prevail in the community regarding household living arrangements.There are 1262 different communities in the entire sample, each of which is large enough to be distinct from the individual considered so that the norms influence the parents' behaviors and not the other way round. 17hese variables are likely to satisfy the exogeneity requirement.To illustrate, consider the proportion of women who gave birth before marriage.If a woman gives birth before marriage, it is likely that she will not live with the father of the child until she marries him.The prevalence of pregnancy before marriage across communities may depend on the way in which the communities treat mothers and children in these circumstances.Community social norms can then influence the individual's probability of having a child outside marriage and so that of co-residence with one's child.The social norms regarding living arrangements have no direct impact on child health except via the living arrangements in the family.The same arguments can be applied for the other community-level variables used as exclusion restrictions in the selection into co-residence equation.

Final specification
In our final specification, we aim to identify the causal effect of parental education on a number of child-health outcomes.We address education endogeneity via 2SLS estimation, using as an instrument the policy reform that allowed some parents to enroll and stay longer in school when they were school-aged.Selection into co-residence is addressed in a two-step Heckman selection model, and marital homogamy using correlated error terms between the fathers' and mothers' education equations.We apply the procedure described in Wooldridge (2010) to estimate a full model that takes all of these issues into account in the five-equation model below.
In Eq. 9, H iht is child health, and Educ M iht and Educ F iht are respectively the variables for mother's and father's education. 18Child health is measured by the different outcomes presented in Section 2.2. 17The number of observations used to calculate each proportion differs slightly depending on the sample.To calculate the proportion of women who gave birth before marriage, the sample is all women who had at least one child.On average, this is calculated for a sample of 14 women per cluster (median of 13, minimum 2, and maximum 47).To calculate the proportion of separated respondents, the sample is all individuals who were ever in a union, with an average of 25.7 respondents per cluster (median=24, minimum=4, and maximum=62).The proportion of polygamous unions is calculated for the sample of married women, distinguishing between monogamous and polygamous husbands.The sample used has an average of 13.9 observations per cluster (median=13, minimum=2, maximum=47). 18We are unable to include an interaction between mother's and father's education to test for complementarity between the two, as there are no children who are born to an unexposed mother and an exposed father.
The outcome equation includes a number of exogenous variables that also appear in the selection and first-stage equations: the X iht are child characteristics (age and sex), and we include survey-year dummies.The main models do not include variables such as household wealth, urban location, and dummy variables for province of residence, as these are very likely endogenous.However, we do consider them in the section that discusses the mechanisms either as the outcome variables or as additional control variables.
As described in Wooldridge (2010), we test and correct for any selection bias by adding the Inverse Mills Ratios from the Probit estimation of Eqs. 5 and 6 to both the first-stage (7 and 8) and outcome (9) equations.The two Inverse Mills Ratios are λ M and λ F , and a test for selection bias is γ M 2 = 0 and γ F 2 = 0 in (9).The sign of γ M 2 (γ F 2 ) reflects the correlation between μ M iht (μ F iht ) and ξ iht .In addition, any bias from selection into co-residence will have a direct impact on child health, but does not necessarily change the estimated coefficients on the explanatory variables in a health regression.In particular, the estimates of γ M 1 and γ F 1 may be the same with and without the correction for selection.
Equations 5 and 6 are estimated separately via Probits, and Eqs.7 to 9 are estimated simultaneously via linear-probability models.This joint estimation allows us to take into account any correlation between the error terms: ε M iht and ε F iht may be correlated due to assortative matching; ε M iht and ξ iht , as well as ε F iht and ξ iht , may also be correlated if mothers (fathers) have unobserved characteristics that influence both their choice of education and their ability to improve their child's health.We do not consider the correlation between μ M iht and ε M iht , μ F iht and ε F iht , or μ M iht , μ F iht , and ξ iht , as these error terms refer to samples of different sizes.The standard errors are clustered at the enumeration area level in all equations, as the proportions calculated at the enumeration-area level appear in the right-hand side variables in Eqs. 5 and 6.Last, selection Eqs. 5 and 6 are estimated using the whole initial sample.In our baseline analysis, Eqs. 7, 8, and 9 are estimated on the analysis sample.

First-stage results
The estimated coefficients from both first-stage Eqs. 1 and 2 are listed in Table 3. 19 For presentation purposes, the X iht coefficients are not shown. 20Panels A and B refer to different education variable: years of education in panel A and the dummy for secondary-school attendance in panel B. In both panels, columns 1 and 2 refer to the mothers' first-stage regression and columns 3 and 4 to the fathers'.In columns 1 and 3, we do not control for linear trends for the birth years before and after 1965: we impose β M 2 = 0 in Eq. 1 and β F 2 = 0 in Eq. 2. In columns 2 and 4, the additional preand post-1965 linear trends are added.
Exposure to the reform has a very large effect on educational attainment.In panel A, the average number of school years is 2.95 years higher for mothers exposed to the reform as compared to the non-exposed (column 1), with a corresponding figure of 2.35 years for fathers (column 3).This differential impact between mothers and fathers is significant at the 1% level. 21Adding the pre-and post-1965 linear trends reduces the impact of reform exposure, with a much smaller coefficient in column 2 (column 4) than in column 1 (column 3).The coefficients are, however, still significant and larger for mothers (+2.14 years for mothers; +0.92 years for fathers).
Our first-stage regressions are convincing, in that in columns 1 and 3, the Kleibergen-Paap F-statistics on excluded instruments (exposure to the reform) are not small (F = 310.3for mothers; F = 374.8for fathers).The Kleibergen-Paap F-statistics are lower when we add the pre-reform and post-reform trends to the instrumental variables in columns 2 and 4, although they are still large (116.3 for mothers and 191.3 for fathers).These conclusions remain unchanged when using the Montiel Olea and Pflueger (2013) effective F-statistic.
The same pattern is seen in panel B, where reform exposure increases secondaryschool attendance by 34 percentage points for mothers (column 1) and 33 percentage points for fathers (column 3).The inclusion of linear trends reduces both the reform's impact (+28 percentage points for mothers in column 2, +14 percentage points for fathers in column 4) and the Kleibergen-Paap F-statistic for excluded instruments.
Even though the Kleibergen-Paap F-statistics for excluded instruments are lower with the trends in the instrumental variables, we rely on these first-stage regressions in the remainder of the paper as they provide a better fit for the graphical relationship depicted in Figure 1 and allow us to control for the duration of exposure to the education reform.22

The selection-equation estimation results
The selection-equation estimation results appear in columns 1 and 2 of Table 4.The greater are the community proportions of sample women who gave birth to their first child before marriage and of sample respondents who are currently divorced, separated, or widowed, the smaller the probability that the child lives with her mother (in column 1).The same results apply for co-residence with the father (in column 2).The size of the marginal effects being larger for co-residence with the father suggests that social norms regarding pregnancy before marriage and broken unions affect the probability   that the child lives with her father more than that for the mother.The proportion of polygamous households in each community increases the probability of living with the mother and reduces that for the father.

Second-stage results
We use the analysis sample to jointly estimate the effect of father's and mother's education on a number of child outcomes.The results appear in Tables 5 and 6 for years of education and secondary-school attendance, respectively.Both tables include three estimates: OLS (panel A), 2SLS (panel B), and 2SLS correcting for selection (panel C).The results in panel C come from our preferred specification that deals with all of the estimation issues discussed above; this corresponds to the estimation of the final specification presented in Section 4.4.However, panels A and B help us to understand whether, and to what extent, our results are affected by correcting for the endogeneity of education and selection.
In Tables 5 and 6, the OLS estimates (panel A) reveal a highly significant correlation between education and all child-health outcomes, both for the mother and the father.Greater education is associated with more prenatal care and better birth conditions (i.e., a greater probability of the mother having had at least four prenatal visits, of being born in a health facility, and the birth being assisted by medical staff).Father's education, and to a lesser extent mother's education, is also associated with better nutritional outcomes (a smaller probability of stunting and wasting).Finally, in the last two columns, mother's education is associated with more preventive actions (vaccine injections and sleeping under a bed net for both education measures).
Father's education is also positively correlated with preventive actions, although not significantly so for vaccination and secondary-school attendance.
When the endogeneity of education is taken into account (panel B), mother's education is no longer significant for any education measure and child-health outcome.That the education effect on health becomes insignificant when instrumented also appears in Jürges et al. (2013), for example.On the contrary, the 2SLS point estimates of the effect of father's education remain positive and statistically significant for the three perinatal care outcomes when education is measured by secondary-school attendance and one perinatal care outcome when considering years of education.Secondaryschool attendance then seems to matter more than years of education.In Table 6, a father who attended secondary school increases the probabilities of having at least four prenatal visits by 14.4 percentage points, of being born in a health facility by 15.8 percentage points, and of having a birth assisted by medical staff by 14.5 percentage points.Father's education also affects the number of vaccinations in column 6 at the 10% level for both education measures, but no longer has an impact on nutritional status and the likelihood that the child sleeps under a bed net.
Comparing the OLS coefficients for father's education on prenatal and birth care in panel A to the 2SLS coefficients in panel B reveals that, in most cases, the latter are more positive than the former, so that the effect is larger if education is randomly distributed in the population.Only for years of education and birth in a health facility or birth assisted by medical staff (columns 2 and 3 of Table 5) are the coefficient sizes the same.Considering the effect of secondary-school attendance on these two outcomes (columns 2 and 3 of Table 6), the instrumented coefficient is larger and more positive than that from OLS, but not significantly so.The difference between the OLS and 2SLS estimates of education on having at least four prenatal visits is significant for both measures of education (column 1 of Tables 5 and 6).This estimated difference between OLS and 2SLS means that were education levels to be randomly allocated, the health gradient by education would be even larger.
Overall, our findings suggest that when endogeneity is controlled for, inequalities in child nutritional outcomes are no longer due to differences in mother's and father' education, while father's education does significantly improve prenatal care and birth conditions. 23anel B of Tables 5 and 6 also reports the correlation coefficients between the residuals of both first-stage equations from the system of equations.As noted above, we find a positive and very significant correlation: the unobserved factors behind father's and mother's education are strongly correlated (0.55 for the number of years of education, and 0.40 for secondary-school attendance).There is then considerable assortative matching between parents, as shown by both the correlation between observables (the correlation between mother's and father's years of education is 0.64) and between unobservables.
All of these conclusions continue to hold when selection into co-residence is taken into account (in panel C of Tables 5 and 6), and the two Inverse Mills Ratios are included in order to correct for any selection bias.The 2SLS point estimates in panel C are very similar to those in panel B. Therefore, even when the Inverse Mills Ratios are significant, there is only limited selection bias in the causal effect of parental education on child health due to co-residence.As such, the causal effect of parents' education on child-health outcomes is the same in the sample of children who live with both parents and those who live with only one or neither.
Our results in addition show that the mother's Inverse Mills Ratio is significant for most outcomes with the sign implying better health outcomes, so that the unobserved factors that make mothers live with their child are also associated with better birth, conditions and nutritional outcomes, and greater prevention through vaccination.The father's Inverse Mills Ratios are less significant, but when they are, they have a lessintuitive sign: fathers' unobserved characteristics that make them live with their child are associated with less health investment in our model.There are a number of potential explanations.One is related to migration: absent fathers who are migrants will not coreside with their children but may send financial resources that contribute to child health.Equally, fathers who co-reside may be in worse health than those who do not: given the intergenerational transmission of health-care use and health status, this could produce worse child-health outcomes.However, we cannot investigate these channels in more detail, as we do not observe the characteristics of non-coresident parents (which is also why the selection equation only uses instruments defined at the community level).

Robustness checks
We check the robustness of the causal results to alternative specifications of the reform's impact on education.The first-stage estimates appear in Online Appendix Table F3 and the second-stage point estimates (controlling for selection into coresidence) in Table 7.We focus on prenatal care and birth conditions, as these are the main variables for which we observe a causal effect of parental education.
We first consider the partially exposed, who are the parents born in 1965 and 1966.Robustness 1 excludes these observations, as in Agüero and Bharadwaj (2014) and Grépin and Bharadwaj (2015), while Robustness 2 considers them as not having been exposed to the reform.The point estimates are unaffected in either case: mother's education has no significant effect on prenatal care and birth outcomes, while father's education mostly significantly improves them. 24The size of the effect of father's secondary-school attendance is unchanged, increasing the probability of having four prenatal visits and an assisted birth by 11-15 percentage points.
Second, Robustness 3 includes the parents born before 1950, to see whether this age restriction lies behind our results.Our core results seem to be conservative, in that 24 The first-stage estimates are very similar to those in Table 3 (see Online Appendix Table F3).

Table 5
The impact of mother's and father's education (years of education) Father's years of education 0.018 Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey-year dummies and child sex and age.Panel C also controls for the two Inverse Mills Ratios from the two selection equations.
) denotes the correlation between the residuals of the two first-stage equations 123 Father attended secondary school 0.144 they are lower-bounds of these new coefficients.The size of the coefficients rises in columns 5 and 6, and those in columns 2 and 3 become significant.Third, Robustness 4 to 6 assess the plausibility of our exclusion restriction.We start by restricting the sample to children whose parents were born in the years around 1965.The main specification only restricted the sample to the children whose parents were born from 1950 onwards to avoid survival bias; as such, parents were born over a very wide time span. 25Restricting the sample to children of parents who were born around the pivotal year (1965) produces a more homogeneous sample of parents (as in a regression discontinuity approach), as they likely faced similar economic, social, and political environments at similar ages and were equally affected by the health reform.We use different bandwidths in Robustness 4 and 5.The bandwidths are 7 years larger for fathers than for mothers to reflect the age difference between the parents in our sample.The more-restricted bandwidth appears in Robustness 4, where the sample includes children whose mothers were born 5 years before to 5 years after 1965 and whose fathers were born up to 12 years before and 12 years after 1965.The core results are robust: the causal effect of father's secondary education remains positive and significant and that of mothers insignificant.The results are as in Table 5 for the significant causal effect of fathers' years of education on prenatal care.
To better control for the economic and social development of Zimbabwe over time, we then add a number of control variables defined at the child's year of birth: GDP per capita, life expectancy at birth, the urbanization rate, and the under-5 mortality rate (from the WDI). 26Even though these additional variables are significant, they do not change the education estimates (see Robustness 6).
Last, the exclusion restriction requires that having a parent born before or after 1965 does not affect child health other than via parental education.If this is violated, we should see better prenatal care and birth conditions even for the children of uneducated parents who were born after 1965.We therefore analyze the sub-sample of exposed and non-exposed mothers and fathers who did not complete primary education.The estimates from a reduced-form regression on this restricted sample (see Table 8) show that the exclusion restriction is likely valid: prenatal outcomes do not differ significantly between children from exposed and non-exposed parents.This is consistent with parents being born after 1965 not affecting child-health outcomes per se, at least when the parents are not educated.

The impact of mother's education only
We complement the analysis above of both mother's and father's education by looking at the impact of the former only, as this has been the focus of the literature on parental education and child health.We wish to see whether the absence of a mother's-education effect in the findings above is due to controlling for father's education.We estimate the effect of mother's education in the sample of children who live with both parents, as The sample size varies between outcomes due to data availability.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey-year dummies, child sex and age, linear trends for parent's year of birth before and after 1965, and the two Inverse Mills Ratios from the two selection equations in the main analysis, but no longer consider father's education or father's co-residence with the child.Tables 9 and 10 show the resulting estimates from OLS in panel A, 2SLS in panel B, and 2SLS with correction for selection into mother's co-residence with the child in panel C.
The education coefficient in panel A's OLS specification has the expected sign, as mother's education is associated with better health via improved prenatal care, birth conditions, child nutrition, and more preventive behaviors for both years of education (Table 9) and secondary-school attendance (Table 10).All of the estimated coefficients are significant, except that on wasting in Table 10.These OLS coefficients are very similar to those in Tables 5 and 6.
The 2SLS estimates in panel B are overall less significant.The effect of mother's education remains statistically significant for the probabilities of being born in a health facility, having a birth assisted by medical staff and sleeping under bed net, for both education measures.The same results are found in panel C, except that the causal effect of mother's years of education on the probability of sleeping under bed net is slightly reduced and becomes insignificant.
Regarding child nutrition, the findings in columns 4 and 5 in panels A and B of Tables 9 and 10 are comparable to those in De Neve and Subramanian (2017): the OLS estimates of the effect of maternal schooling on the probabilities of being stunted and wasted are negative and mostly significant, while the 2SLS estimates are always insignificant.
Overall, these results, along with those in Tables 5 and 6, suggest that if the child lives with both parents, not controlling for father's education overestimates the effect of mother's education, as the latter will capture part of the effect of father's education (especially if they have similar education).This is in line with the evidence in Fafchamps and Shilpi (2014) and Behrman and Rosenzweig (2002).Our results echo those from Behrman and Rosenzweig (2002) for child education, where there is no longer an effect of mother's education on children's schooling once father's education and the endogeneity bias are considered, whereas the effect of father's education is significantly positive.

Mechanisms
We now turn to the potential mechanisms, as parental education may affect a number of the outcomes that determine child health: these include labour-market opportunities, wealth, access to health services, urbanization, and parental choice regarding family size.
We evaluate the role of these different mediators in the effect of parental education on child health by estimating the causal effect of father and mother's education on a sequence of outcome variables and replicating the models that appear in panel B of Tables 5 and 6.Note that although we use the sample of parents observed in the analysis sample, controlling for co-residence is less justified here, as these outcome variables are not child-specific.They are observed at the mother level, the father level, or at the household level.11 first considers as mediators the ideal number of children reported by the mother and the father and the mother's age at first birth.The last row presents the mean of each variable: mothers (fathers) expect to have 4.1 (4.7) children on average, and the average age of the mothers at first birth is 19.3.The second set of mediators is related to living conditions: 34% of the households live in urban areas and 43% are in the two richest quintiles.
Columns 1-4 in Table 11 consider the role of fertility preferences and attitudes.Father's education has a significant causal effect on the ideal number of children reported by both mothers (column 1) and fathers (column 2). 27Mother's age at first birth rises with her secondary-school attendance.Mother's education significantly influences her use of modern contraception at the time of the survey in column 4: secondary-school attendance increases this use by 34 percentage points.
Columns 5-7 in Table 11 show that father's secondary-school attendance increases the probability of living in an urban area, the probability that the household is in the two richest quintiles by 16 percentage points, and the household wealth index.Part of the effects of father's education on prenatal care and birth conditions then reflects that the children live in richer households that can afford health services and in urban households where there is better access to health-care services.Our findings suggest that father's education reduces both the geographical and monetary barriers to health-care access.On the contrary, mother's education has almost no effect on these variables, except for a slight increase in the probability of belonging to the two richest quintiles from an additional year of education (panel A, Table 11).
A complementary approach is to add these mechanisms as control variables.We thus introduce controls for household's urban status, material wealth, and province of residence when estimating Eqs.5-9. 28As shown in Online Appendix Tables H1 to H3, our conclusions are unchanged when controlling for these variables, either separately (panels A to C) or simultaneously (panel D).Father's education not only affects child health indirectly through better living conditions, but also has a direct positive effect on perinatal conditions and vaccination when controlling for urban status and wealth, as the effects of father's education remain significant.This persistent effect may reflect information and allocation of resources within the household.Education may first raise fathers' awareness of the importance of prenatal care and birth conditions in child health.Given that it is the mothers who give birth, they are likely already knowledgeable about childbearing-related healthcare, no matter how educated they are.We would thus expect a larger effect for fathers than for mothers.Previous research has shown that education increases the effect of sensitization messages on health behaviors and outcomes (see de Walque (2007), for example).Second, education may affect the way in which resources are allocated within the household for a given wealth level, and educated fathers could allocate more resources to child human-capital accumulation.
(3) (4) (5) for survey year dummies.Additional covariates include parents' age categories for fertility behaviors.The unit of observation corresponds to a mother (columns 1, 3, and 4) or a father (column 2) born in or after 1950 with a child in the analysis sample, and to the corresponding households in columns 5 to 7. The sample is restricted to couples with at least one child in the analysis sample, with one observation per couple 123

Conclusion
The main results of our analysis of parental education and child health are as follows.Father's education consistently and significantly improves prenatal care, birth conditions, and vaccination, while that of the mother has no causal impact on these outcomes when controlling for the father's education.Once we control for endogeneity, child nutrition and prevention through the use of bed nets are not influenced by parental education.With respect to the education measures, secondary-school attendance is more important than years of education for child-health outcomes.Last, the unobserved characteristics of both the father and the mother that lead them to live with their child also play an important role in child-health outcomes.However, correcting for this selection does not change our parental-education estimates on the child-health outcomes; this suggests that the relationship is similar for children who live with both parents and those who live with only one or neither.
Our results overall underline the predominance of father's education in determining child health investments in Zimbabwe.The model without father's education overestimates the impact of mother's education on child health: mother's education matters less when we control for father's education.As such, the results in the existing literature without father's education may have overestimated the impact of mother's education when mothers and fathers co-reside with the child.This may reflect the assortative matching in our sample: men and women with similar observed education and intrinsic motivations or aspirations towards investment in human capital tend to live and have children together.The analysis of potential mechanisms reveals that father's education may reduce both the geographical and financial barriers to access to care and so improve prenatal care and birth conditions.The effect of father's education is not, however, entirely captured by these mechanisms.
Last, we show that education, and in particular that of the father, can help reduce inequalities in child-health outcomes in terms of prenatal care and birth conditions.These outcomes are of particular importance as they are among the main drivers of child and maternal mortality.In 2020, worldwide, 47% of children who did not reach their fifth year died within their first month of life (UNICEF). 29As education has risen in recent decades, we may hopefully see drastic improvements in child and maternal health, and a drop in the considerable burden of disease and death borne by children and pregnant women.
The research presented in this paper has important policy implications, as policies targeting fathers could have sizeable effects on their own, over and above the existing policies that focus exclusively on mothers and mothers-to-be.This conclusion holds for Zimbabwe and potentially for other low-income countries with similar characteristics.We hope that future research will build on these results to better understand the interplay between father's and mother's education in shaping child health and the role played by coresidence.

Fig. 1
Fig. 1 Mother's and father's education by birth year

Father
01.The table lists the point estimates from the analysis sample.The sample size differs between columns (1)-(2) and (3)-(4) due to data availability.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey-year dummies, as well as control variables in the second-stage equation (child sex and age).The Kleibergen-Paap and Montiel Olea and Pflueger (2013) F-statistics for excluded instruments come from the estimation of Eqs. 1 and 2. There is no correction for selection into co-residence 01. Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls

Table 2
Summary statistics -parents' exposure to the reform and education Notes: Unweighted statistics.The data covers children aged 0-59 months at the time of the survey.The analysis sample (column 1) corresponds to children aged 0-59 months living with both parents born in 1950 or later.Exposed mothers and fathers are those born in or after 1965 123

Table 4
Selection equations for mothers and fathers Authors' calculations from the Demographic and Health Surveys Notes: * p < 0.10; * * p < 0.05; * * * p < 0.01.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey-year dummies, as well as the control variables in the second-stage equation (child sex and age).The selection equations are estimated for all children present in sample households.The table lists the marginal effects.We use the observed share of children living with their mother (column 1) or father (column 2) in the sample as the cut-off to calculate the share of correctly classified predictions based on our model This table lists the point estimates from the analysis sample.The sample size varies between outcomes due to data availability.

Table 6
The impact of mother's and father's education (secondary-school attendance) This table lists the point estimates from the analysis sample.The sample size varies between outcomes due to data availability.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey-year dummies and child sex and age.Panel C also controls for the two Inverse Mills Ratios from the two selection equations.This table lists the point estimates from the analysis sample.The sample size varies between outcomes due to data availability and between robustness checks due to the corresponding sample restrictions.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey-year dummies, child sex and age, and the two Inverse Mills Ratios from the two selection equations, as in panel C of Tables

Table 8
Robustness checks-non-educated parents This table lists the 2SLS point estimates from children in the analysis sample whose parents did not complete primary school.

Table 9
The impact of mother's education (years of education) This table lists the point estimates from the analysis sample.The sample size varies between outcomes due to data availability.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey year dummies and child sex and age.Panel C also controls for the Inverse Mills Ratio from the selection equation for the child's co-residence with the mother This table lists the point estimates from the analysis sample.The sample size varies between outcomes due to data availability.Robust standard errors clustered at the enumeration area level are in parentheses.Each regression controls for survey year dummies and child sex and age.Panel C also controls for the Inverse Mills Ratio from the selection equation for the child's co-residence with the mother