Family Planning and Children's Human Capital: Experimental Evidence From Urban Malawi

Abstract

We conduct a randomized controlled trial that provides pregnant and immediate postpartum women with improved access to family planning through counseling, free transportation to a clinic, and financial reimbursement for family planning services over two years. We study the effects of our intervention on child growth and development outcomes among 1,034 children born to participating women directly before the intervention rollout. We find that children born to mothers assigned to the family planning intervention arm were 0.28–0.34 standard deviations taller for their age and 10.7–12.0 percentage points less likely to be stunted within a year of exposure to the intervention. Children born to mothers assigned to the intervention arm also scored 0.17–0.20 standard deviations higher on a caregiver-reported measure of cognitive development after two years of intervention exposure. Although the nonmeasurement of children is a challenge in our study, our estimates are robust to multiple methods of correcting for potential attrition bias. Our results are consistent with models of fertility that link couples’ fertility decisions to child health and human capital. Our results also suggest that improved access to family planning might have positive downstream effects on child health beyond contraceptive use and fertility outcomes.

Introduction

Roughly 14 million unintended pregnancies occur in sub-Saharan Africa each year, and an estimated 37% of these pregnancies are terminated (Bankole et al. 2020). For those pregnancies that result in live births, women and couples are left to care for a child that was unplanned and that they may have been unprepared or unwilling to raise (Bongaarts 2016). Although unplanned children may be welcomed by the family, they are also costly to the household (Barro and Becker 1989; Becker and Tomes 1976; Blundell et al. 1994; Robinson 1987). A mistimed birth might, therefore, affect how limited household resources and parental investments are allocated among children, with potentially significant implications for child health, human capital attainment, and longer term well-being (Adhvaryu and Nyshadham 2016; Almond and Currie 2011; Almond and Mazumder 2013; Becker and Tomes 1976).

Access to family planning and reproductive health (FP/RH) services has improved in recent decades, but contraceptive prevalence in sub-Saharan Africa (34%) is about half that of South Asia (64%) and far less than that of East Asia (84%) (United Nations Population Fund 2024). Previous studies have shown that women from low-income and disadvantaged backgrounds are one of the largest groups with an unmet need for family planning: they are sexually active and report wanting to delay or stop childbearing but are not using a contraceptive method (Bradley et al. 2012; Casterline and Sinding 2004; Westoff and Ochoa 1991). This shortfall in contraceptive prevalence among African women is partly because they may face financial and social barriers to accessing contraceptives and other FP/RH services (Haider and Sharma 2013). Therefore, improved access to FP/RH services might help avert unintended births by allowing women and couples to more effectively meet their desired family size. Moreover, contraception use also enables women to time and space future pregnancies with more certainty (Agesa and Agesa 2020; Casterline and Agyei-Mensah 2017), potentially enabling them to more effectively invest in their children's health and well-being (Gipson et al. 2008; Singh et al. 2013).

In this study, we assess the causal impact of improved access to family planning on child health and human capital outcomes using experimental evidence from a randomized controlled trial in urban Malawi. We build on previous findings on the impact of the intervention on contraceptive use and birth spacing outcomes, which has been discussed in Karra et al. (2022). Our work is motivated by models of the quantity–quality trade-off developed by Becker (1960) and later extended by Schultz (1969, 2008) and others. Most recently, Cavalcanti et al. (2021) adapted the Becker (1960) framework by modeling households’ fertility uncertainty, whereby contraception use to reduce this uncertainty would lead to increased investments in child health and human capital. In addition, we are motivated by limited evidence documenting the extent to which FP/RH services contribute to improved child health by lengthening interpregnancy intervals and promoting healthy birth spacing (Cleland et al. 2012; Conde-Agudelo et al. 2006; Fink et al. 2014; Miller and Karra 2020; Rutstein 2006). This literature has identified potential physiological channels linking family planning and interpartum spacing to birth outcomes and child health. In particular, the role of maternal nutritional depletion, which is linked to the close succession of pregnancies and lactation periods, has been proposed as a key risk factor of early-life growth faltering (Dewey and Cohen 2007; King 2003; Kozuki et al. 2013; Mayo et al. 2017; Miller 1991; Molitoris 2017). This evidence has been the basis for the development of the World Health Organization's recommendation that women wait at least 24 months after a live birth before becoming pregnant again (World Health Organization 2007).

For our field experiment, we recruited 2,143 women who were either pregnant or up to six months postpartum at baseline. Following a baseline survey, women were randomized into either intervention or control arms, and women who were assigned to the intervention arm received the following package of services over a two-year period: (1) up to six free family planning counseling sessions; (2) free transportation to a high-quality family planning clinic; and (3) financial reimbursement for family planning services received at the clinic, including for the treatment of contraceptive-related side effects. Follow-up surveys were conducted in 2017 and 2018. For our analysis, we use anthropometric data collected for children under age 6 at baseline and in the 2017 survey, along with caregiver-reported survey data on children that were collected in the 2018 survey, which measured cognitive functioning for all children under age 3.

We focus our analysis on index children¹ who were alive to be measured at baseline, resulting in a potential sample of 1,034 children. We show that children born to women who received improved access to family planning through our package of services had better health and cognitive development outcomes. In particular, children born to women assigned to the intervention group were 0.34 standard deviations (SD) taller for their age relative to children born to women assigned to the control group after one year of exposure to the intervention. Children born to women assigned to the intervention group also performed 0.23 SD better on a caregiver-reported measure of cognitive development after two years of exposure to the intervention. Although these results are promising, we do not find evidence of similar improvements in child weight or hemoglobin levels. If one believes that these improvements in early-life health and cognition could lead to improvements in longer term education and wage-earning potential, then these results lend themselves to the idea of a “demographic dividend” (Bloom et al. 2003) associated with fertility change and the provision of family planning services. Further, they suggest that family planning services might have a place in broader health campaigns and economic development strategies.

Throughout the study, anthropometric measurement rates among eligible children were low as a result of two factors. First, this study was conducted in a densely urban environment where children have relatively high freedom of mobility and were often not available at home at the time of the interview.² Second, the rate of mothers’ consent was low, perhaps partly driven by religious beliefs and mistrust. We address low measurement levels in three ways: (1) by conducting an analysis of attrition that compares differences in baseline characteristics of mothers and children by baseline characteristics and measurement status at follow-up; (2) by employing propensity score weighting and Heckman selection models (Heckman 1979) to correct for potential bias due to nonmeasurement; and (3) by presenting bounds in the tradition of Kling et al. (2007) to explore the severity with which nonmeasurement may impact our estimates. Using these three methods, we present evidence demonstrating that the high nonmeasurement rates do not bias our estimates. Nevertheless, our incomplete sample weakens our ability to make stronger causal claims throughout this study.

Relevant Literature and Contribution

The impact of fertility on child growth and development has received significant attention in several disciplines, including demography, public health, and economics. Much of the previous work in these disciplines has aimed to study the causal impact of high fertility and large family sizes on parental investments in children and has consistently shown that children from large sibling cohorts receive lower levels of investment. These studies have exploited several quasi-experimental sources of variation, including nonsingleton births (Black et al. 2005; Li et al. 2008; Marteleto and de Souza 2012; Rosenzweig and Wolpin 1980), sex composition–based fertility preferences (Kugler and Kumar 2017), and subfecundity (Bougma et al. 2015; Knodel and Wongsith 1991).

One source of exogenous variation that is of particular relevance to this body of work is a household's access to family planning services (Dang and Rogers 2016). A recent study by Mookerjee et al. (2023) used data from the National Family Health Survey for 2019–2021 in India to study the contraceptive–fertility–child health pathway by instrumenting for contraceptive use using district-level exposure to family planning messaging. Concordant with our findings, the authors found that children born to mothers who increased their contraceptive use as a result of family planning messaging were much taller for their age and biological sex.

Studies in this field have assumed that family planning services can induce human capital investments through reduced family size. The best evidence of the effect of family planning on child health outcomes beyond child survival comes from quasi-experimental evaluations of multicomponent health interventions (Miller and Singer Babiarz 2016). Analyses of the Matlab maternal and child health/family planning program in Bangladesh found positive impacts of the intervention on child height, cognitive function, and educational attainment (Barham 2012; Joshi and Schultz 2007; LeGrand and Phillips 1996). Similarly, an evaluation of health program placement in the Philippines observed a 7% increase in child height and a 12% increase in child weight from increased exposure to a family planning facility (Rosenzweig and Wolpin 1986).

Although the literature is promising, it is subject to several challenges. First, in studies that have exploited variation in access to family planning services, such as in Matlab, family planning has typically been introduced as part of a larger bundle of maternal and child health and nutrition services. As a result, it is difficult to disentangle the contribution of family planning from other program components introduced concurrently. Second, impact evaluations of improved access to family planning services are subject to concerns related to endogenous program placement. Across contexts, areas with access to family planning tend to differ systematically from those with less access.³ Finally, supply-side access to family planning services is often spatially correlated, and analyses of such programs might yield estimates that would internalize potential spillover effects and, in turn, overestimate the direct effect of improved access to family planning on outcomes.

Our approach in this study allows us to contribute to this literature in four main ways. First, by leveraging the random assignment of women to the intervention, our analysis circumvents concerns related to endogenous program placement. Second, the rollout and implementation of a pure family planning intervention allow us to directly and credibly identify the causal effect of family planning and avoid concerns over disentangling impacts in multi-intervention settings. Third, by randomly assigning our treatment at the individual level, with guidelines in place to reduce spillovers, our intervention minimizes the threats to identification posed by the spatial correlation of services. Finally, our monitoring and process evaluation strategy has provided us with rich data on program utilization and health behaviors, allowing us to test key mechanisms underpinning our results. Much of the literature proposes that family planning services might improve children's health by changing family sizes. Here, we conduct a mediation analysis motivated by Cavalcanti et al. (2021) and show that although changes in short-term fertility partially explain our results, they are not the only channel through which treatment effects are likely to operate. We show that concordant with the idea of a quality–quantity trade-off in parental preferences, changes in health investments also drive a significant portion of our results. However, much of the effect that we observe is left unexplained, which might suggest that characteristics unique to family planning services drive changes in children's outcomes independent of changes in fertility and outside traditional models of fertility and human capital.

Conceptual Framework

Much of the study of contraception, fertility, and children's outcomes has been motivated by Becker's (1960) quality–quantity model of fertility, which argues that couples face a trade-off between fertility and investments in human capital. Indeed, many of the studies that are referenced in the relevant literature section aimed to test explicitly for the existence of this trade-off. Although Becker mentioned the potential role of contraception, his model and related economic models of fertility assume that fertility is perfectly deterministic, implying that couples are either perfectly using contraceptives or have no demand for contraceptives (Becker and Lewis 1973; Becker and Tomes 1976; Robinson 1997). This assumption, in which the demand for children can be perfectly realized, is hard to reconcile with the fact that an estimated 121 million unwanted pregnancies occur in developing countries each year (Guttmacher Institute 2022).

Several models, most recently by Cavalcanti et al. (2021), have extended the Becker model of fertility to allow for stochastic realizations of a couple's underlying fertility preferences and demand for children. The defining feature and key contribution of the Cavalcanti et al. (2021) model is that couples cannot perfectly choose the number of children they have; instead, they face uncertainty in achieving their desired fertility, and this uncertainty can be mitigated through contraceptive use. Because contraceptives are costly to a couple, the model predicts that when contraceptive costs decrease or contraceptive effectiveness increases, couples will increase their level of household consumption and investments in their children, thereby improving child health and development.

Following this prediction, we expect that our intervention might encourage investments in child health by (1) lowering the realized relative price of contraceptives through financial reimbursement and free transportation and (2) improving the perceived effectiveness of contraceptives through counseling. As couples increase their contraceptive use in response to improved access to services, they might be more effective in controlling their fertility (Joshi and Schultz 2007). Couples also might become more certain of the time horizon until their next birth event, which could allow for greater human capital investments in their existing children if human capital and birth parity are substitutes in couples’ preferences. The improved certainty over the timing and spacing of birth events allows couples to commit more credibly to human capital investments in children. These investments might take the form of increased utilization of health services that present as improved vaccination status or increased uptake of care in the event of illness.⁴ Beyond direct health investments, any income effects or precautionary savings reductions that are associated with family planning services (in line with the preceding predictions) would likely improve child health outcomes indirectly through improved maternal nutrition or an improved home environment (Canning and Schultz 2012).

In the online appendix (section A), we discuss why causal channels related to “marginal children” or preceding birth intervals are unlikely to drive our observed results. Further, we validate an underlying assumption of the Cavalcanti et al. (2021) model that women are primarily using contraceptives to control their fertility (see section B, online appendix).

We also address the possibility that women utilized the intervention to seek health care services other than family planning. Our analysis reveals that women who were assigned to the intervention were approximately 10 percentage points (pp) more likely to report visiting a clinic in the year before our first-year follow-up survey and at endline. The Good Health Kauma Clinic, our partner service provider in Lilongwe, Malawi, where women were referred for family planning, offered services beyond FP/RH.⁵ However, these services were not covered as part of our intervention. Specifically, women who were assigned to the intervention arm were informed that only family planning–related services received at the Kauma Clinic were eligible for financial reimbursement. In addition, women were also informed that the taxi service would provide transportation to the Kauma Clinic only for services related to family planning. Later in the article, we discuss the results of a mediation analysis conducted to study the potential mechanisms underlying our results. Findings from this analysis provide suggestive evidence that the increase in health care use partly mediates the impact of the intervention on key outcomes; however, when we directly test the impact of transport uptake, we observe no detectable effect, suggesting that our results are not driven by reduced barriers to health care–seeking.

Study Design

Our empirical analysis is based on data from a randomized controlled trial conducted in Lilongwe, Malawi, between November 2016 and November 2018. We provide an abbreviated description of the trial; a more detailed protocol describing the study design and intervention can be found in Karra and Canning (2020).

Women who were either pregnant or immediately postpartum (had had a live birth within six months of the baseline screening) were recruited to participate in the study. Following a baseline survey that was implemented from September 2016 to January 2017, women were randomly assigned to an intervention or control arm. Women assigned to the intervention arm received a comprehensive family planning package of services over a two-year period, which included the following: (1) an information brochure and up to six counseling visits from trained family planning counselors; (2) free transportation to a high-quality private family planning clinic in Lilongwe; and (3) financial reimbursement for family planning services, including for the treatment of contraceptive-related side effects. Annual follow-up surveys were conducted with women and children under age 6 who were available in the household at the time of the interview. Data collection for the first follow-up survey began in August 2017 and was completed in February 2018. Data collection for the second follow-up survey began in August 2018 and was completed in February 2019.

In this study, we use baseline and follow-up data on children to present findings related to the intervention's impact on the subsample of children who were alive at baseline and resulted from the pregnancy or recent birth that made their mothers eligible for enrollment in the study (the index children).⁶ Among these children, we test the extent to which the family planning intervention might have impacted these early-life linear growth patterns as a result of changes in parental investment behavior.

Study Sample Eligibility

Women were recruited to participate in the baseline survey if they were:⁷

• Married;

• Currently pregnant or had given birth within the previous six months;

• Between ages 18 and 35;

• A permanent resident of Lilongwe, Malawi; and

• Not sterilized, nor had undergone a hysterectomy.

To minimize spillover effects between treated and control women, we ensure that all eligible women selected for the study were at least five households apart from one another. For women enrolled in the study, anthropometric data⁸ were collected from children who were:

• Under age 6 at baseline;

• Identified as the biological or adopted child of the woman who was enrolled in the study; and

• Present in the household at the time of the interview.

Parental consent for collecting height, weight, and hemoglobin measurements was obtained from the woman for each of her eligible children.

Sample Size and Randomization

A total of 2,143 women were enrolled in the study in 2016. Following the baseline survey, women were randomly assigned to intervention and control groups by stratified covariate balanced randomization, as proposed by Bruhn and McKenzie (2009). Women were allocated to strata based on the following baseline characteristics: number of living children, contraceptive use, age at sexual debut, level of educational attainment, work status, and their neighborhood of residence at baseline. In total, 1,026 women were assigned to the intervention arm, and 1,113 women were assigned to the control group. For additional details on the randomization protocol, see Karra et al. (2022).

For this study, we restrict the sample of children to the 1,034 index children who were already born at baseline.⁹ Among this sample, 538 were born to women assigned to the control group, and the remaining 496 children were born to women assigned to receive the family planning intervention.¹⁰Table 1 presents key descriptive statistics for children enrolled in our study at baseline and for women who had already given birth to their index child. Table 1 reveals that treatment women were slightly more likely to have ever used a contraceptive method relative to control women but that women are otherwise generally balanced across key characteristics at baseline. In addition, the table reveals no significant differences among children in the treatment group relative to the control group at baseline. Through joint significance tests, we provide additional evidence that children and women did not likely differ systematically across intervention arms at baseline.

As discussed in the Introduction, we observe high rates of nonmeasurement among children, as reflected in Table 1 by the large difference between the number of children in our sample and the number of children for whom we have anthropometric data. This nonmeasurement naturally creates a question of balance among children included in our eventual analytic sample. We provide an in-depth analysis of nonmeasurement and attrition in the Attrition Analysis section, including a balance table of the analytic sample (Table 5). At this point, it is sufficient to note that when we account for children for whom we do not observe anthropometric outcomes, the balance remains largely unchanged, and we remain unable to reject the hypothesis that characteristics are jointly balanced.

The Intervention

Women assigned to the treatment group were offered a comprehensive, multicomponent postpartum family planning package over a two-year intervention period. The intervention was designed to overcome multiple barriers to care access, including knowledge barriers and constraints to geographic and financial accessibility.

The intervention had three main components. First, women were offered up to six free family planning counseling sessions over the intervention period. During these hour-long sessions with trained counselors, women received information on a full range of contraceptive methods, their potential side effects, and the health benefits of birth spacing. Second, women were offered free transportation to the Good Health Kauma Clinic, a high-quality local service provider offering clients a comprehensive list of family planning methods and related services.¹¹ The transportation service was provided by a private taxi driver hired exclusively for the project and accompanied at all times by a female field manager to help mitigate any social stigma. Finally, women assigned to the intervention arm received up to 17,500 MKW (approximately US$25) in financial reimbursement for costs incurred for the receipt of family planning services at the Kauma Clinic. Family planning–related costs that were eligible for reimbursement included those related to the procurement of family planning methods, family planning consultations, lab test fees, and exam fees for family planning services only.¹²

Women assigned to the control arm received publicly available information on family planning methods and information about their nearest family planning clinic. These women and their children were contacted again only at follow-up.

Findings From Previous Analyses

This study is the second in a series of analyses that present findings from the randomized controlled trial. As prescribed in our pre-analysis plan and the trial protocol (Karra and Canning 2020), we identify child growth and development as secondary outcomes providing evidence of the potential causal impacts of improved access to family planning that extend beyond first-line outcomes. The trial was powered to detect effects in contraceptive use, contraceptive method mix, and short birth intervals. Elsewhere (Karra et al. 2022), we showed that women assigned to the intervention arm were 5.9 pp more likely to use contraceptives after two years of exposure to the intervention. The effect was more pronounced among women who were immediately postpartum at the time of recruitment; these women were 7.2 pp more likely to use contraception after two years of intervention exposure. Moreover, the increase in contraceptive use seems to have been driven by increased demand for long-acting reversible methods, as evidenced by a 4.6-pp increase in the use of contraceptive implants.

Although the observed impacts on contraceptive use are in line with our prior predictions, the strongest results in our previous analysis and the most relevant ones for this study are those that examine intervention impact on interbirth intervals. A survival analysis revealed that women assigned to the intervention arm were 43% less likely to have a second pregnancy within 24 months of their index birth at baseline. These results show that FP/RH services gave women greater control over their contraceptive use, impacting their likelihood of experiencing a subsequent pregnancy. Our findings from the first study suggest that the intervention's impact is likely to extend to child growth and development.

Empirical Strategy

Key Outcomes

In this study, we evaluate the impact of our intervention on four main outcomes: height-for-age z scores (HAZ), weight-for-height z scores (WHZ), weight-for-age z scores (WAZ), hemoglobin levels, and cognitive scores. Children's height-for-age, weight-for-height, and weight-for-age are measured relative to reference children taken from the WHO Multicentre Growth Reference Study (de Onis et al. 2004) and serve as long- and short-term proxies for health and nutrition, respectively. In addition to our results on height-for-age, we include results for moderate and extreme stunting. A child is considered moderately stunted if their height is more than 2 SD below that of a healthy reference child of the same age and biological sex. They are considered to be extremely stunted if their height is more than 3 SD below that of the reference child. Hemoglobin levels are used to determine children's anemia status and are measured using a HemoCue rapid diagnostic test. Finally, cognitive scores are measured using the Caregiver Reported Early Development Instruments (CREDI; McCoy et al. 2018).

In the online appendix (section D), we further discuss the measurement of these outcomes.

Intent-to-Treat Analysis

Our main results present findings from an intent-to-treat (ITT) analysis identifying the average treatment effect (ATE) on children born to mothers in the treatment group relative to the control group. We prefer an ITT analysis to a local average treatment effect (LATE) specification, which estimates the ATE for children born to mothers who utilized the program, because the LATE would likely overestimate the program's effect owing to selection into program uptake. Given that not every woman will decide to participate in the program even if such a program were ever taken to scale, an ITT specification would better justify the policy relevance of integrating family planning services into a larger campaign to ameliorate stunting and improve child health.¹³

where $Yim$ is the outcome of interest for child $i$ born to mother $m$⁠. This study presents findings on children's HAZ, stunting (a binary outcome), WHZ, WAZ, hemoglobin levels, and cognition scores. $Tm$ is an indicator variable representing the child's mother's assignment to treatment; $βT$⁠, the impact of the intervention, is our coefficient of interest; and $MOBim$ is an indicator variable for the child's birth month. $Xim$ is a vector of child characteristics measured at baseline, including biological sex and birth order. $Zm$ is a vector of maternal characteristics measured at baseline, including those used to stratify the randomization: the number of living children, contraceptive use, age at sexual debut, level of educational attainment, and work status. In addition, we control for demographic characteristics of the child's mother, including age, religion, and ethnicity. The term $χm$ represents a neighborhood fixed effect. The function $f(ageim)$ captures a flexible specification over the child's age, and the results we present are for a spline with knots at 6, 12, 18, 24, and 30 months. This specification allows our model to account for the biological changes in linear growth patterns in the early years of life (Cummins 2013). In discussing our results, we present $βT$ estimated by a naive model containing only treatment assignment, one in which we add the age-specific controls, and the fully adjusted model presented in Eq. (1). In all specifications, we cluster standard errors by mother to account for within-mother correlations among nonsingleton births.

Multiple Hypothesis Testing

We run Eq. (1) on several child health and cognitive outcomes. To correct for the testing of multiple hypotheses, we present frequentist q values adjusted for the false discovery rate associated with that estimation (Newson 2010; Storey and Tibshirani 2003). We calculate these frequentist q values using the method Simes (1986) described, calculated by estimation and sample (unadjusted vs. unadjusted and index sample vs. expanded sample). We report these q values alongside standard p values.

Attrition Adjustment

From the onset of our study, we observed high rates of nonmeasurement for anthropometric outcomes among children in our sample. At baseline, we captured anthropometric data for only 52.7% of children, providing us with a sample of 545 children. These measurement issues persisted over time, and we obtained anthropometric data for only 406 children during the first-year follow-up. Finally, during our endline survey, we had to pause our anthropometric data collection out of concern for the safety of our enumerators.¹⁴ Therefore, although we were able to collect some anthropometric data at endline, we report treatment effects using data from the more complete first-year follow-up.

Of the children who were unmeasured at first-year follow-up, 7 children died before the survey, 113 children were not at home at the time of the interview, 146 children did not have consent granted by their parents, and 111 were not measured for other reasons.^15,16Figure 1 presents a flowchart demonstrating the reasons for nonmeasurement during the first-year follow-up survey by intervention arm.

Given the high attrition rates, we cannot simply present the ITT results and interpret them as causal. High attrition rates may bias our results in two ways. First, if the likelihood of measuring children differs systematically across treatment groups, this differential nonmeasurement would introduce the possibility of omitted variable bias, threatening internal validity. In addition, the mother's or child's (un)observable characteristics might systematically determine the probability of nonmeasurement, with measured children systematically different from nonmeasured children, even when the level of attrition does not necessarily differ across treatment groups. Although this form of potential bias is less severe, it would still change the interpretation of our results. In the case where attrition is systematically determined by characteristics but does not systematically differ across groups, our external validity would be threatened, limiting our ability to make claims outside our analytic sample.

In the Attrition Analysis section, we explore the threat posed by attrition to the validity of our estimates by presenting an analysis of this attrition in both levels and characteristics. We show that although our treatment and control groups are initially balanced at baseline, suggesting that the validity of our randomization remains intact, we find evidence that unmeasured children were born to mothers who were younger, less educated, and less likely to be using contraception. Given these imbalances, we follow a large literature on attrition adjustment in randomized trials by adjusting our ITT estimates using several attrition adjustment methods described later.

Inverse Probability Weighting

In following Molina Millán and Macours (2017), we first correct for sample attrition using a propensity score weighting approach. This approach allows us to adjust for imbalances as a result of sample attrition of study women, which could be correlated with observable woman-level characteristics, such as education and age. We accompany our main ITT specification with estimates from an inverse probability weighting adjustment using the estimated propensity scores as weights. By creating the propensity scores that we use to adjust our estimates, we also create the opportunity to further characterize the observed sample attrition. Thus, in addition to presenting a balance table of characteristics among attritors and nonattritors, the Attrition Adjustment section presents the results from the selection models we use to create our propensity scores.

Heckman Selection Model

That much of the sample attrition is driven by low levels of consent for measurement might raise concerns that the attrition is correlated with unobservable characteristics that determine measurement across waves. To account for this possibility, we accompany our main ITT estimates with estimates from a Heckman selection model (Heckman 1979; Koné et al. 2019). We model missingness as a function of the enumerator assigned to interview the household under the assumption that measurement is at least partly driven by the enumerator's ability; this approach has been implemented in previous studies¹⁷ (Bärnighausen et al. 2011; Hogan et al. 2012).

The identification of our selection model rests on two assumptions. First, it must be true that measurement rates differ by enumerator. In our surveys, we enlisted 12 enumerators and observed measurement rates ranging from 76% to 27%, depending on the enumerator. To further validate this assumption, we conduct a joint test of the enumerator fixed effects used to model missingness and find that they are strongly jointly significant.

Additionally, we must assume that the enumerator assigned to a household is independent of children's outcomes. Here, we rest on the random assignment of enumerators to households by our implementing partner, Innovations for Poverty Action Malawi, implying that the exclusion restriction holds.

Bounding

Finally, a large literature has examined the extent to which attrition can be accounted for using bounding methods, which make assumptions about the potential outcomes of missing data and estimate a range of coefficients using these assumed data (Molina Millán and Macours 2017). We present bounds of the Kling–Liebman type (Kling et al. 2007), which assume that missing outcomes are within a given number of SDs from the within-intervention arm mean. Following Özler et al. (2021), we calculate bounds under two assumptions: (1) we assume missing data take the outcome within 0.1 SD of the group mean; and (2) in a more conservative case, we assume that the missing data are within 0.2 SD of the group mean.

Mechanisms: Mediation Analysis

where $Mi$ is the mediating variable. In our analysis, we utilize four mediators: birth spacing, health care use, contraceptive use, and transportation uptake. In testing for causal mechanisms, we are interested in the average causal mediation effect (ACME). Defined by $β1×γ2$⁠, the ACME represents the change in the potential outcome induced by changes in the state of the mediating variable under treatment.

To identify the ACME, our estimations must satisfy the sequential ignorability assumption from Imai et al. (2010): we must assume that conditional on treatment and covariates, our mediator is independent of our outcomes. To address potential violations of this assumption, we present the analysis with and without the set of covariates described alongside our ITT estimation. Where we find significant results in our analysis, we also present the ρ statistic from the analysis, which identifies the amount of joint variation between the mediator and outcome that would need to be explained by an omitted variable to invalidate the result (Imai et al. 2010).

Results

HAZ

To measure the effects of improved access to family planning on linear growth in children, we first report the treatment effect on HAZ.

Table 2 presents the unadjusted (columns 1 and 2) and adjusted (column 6) ITT estimates for the treatment effect on child height-for-age z scores, moderate stunting, and extreme stunting during the first year. The ITT effects are presented alongside estimates from the inverse probability weighting model (column 7), Heckman-type selection model (column 5), and Kling–Leibman-type bounds (columns 3, 4, 8, and 9). We complement these results in the online appendix (section F) by displaying nonparametric density distributions for children's height-for-age.¹⁸

The results suggest that improved access to family planning led to an increase of 0.28–0.34 SD in children's height-for-age and a decrease of 10.7–12.0 pp in the likelihood of moderate stunting.¹⁹

Findings from our models of attrition adjustment reveal that the potential impact of attrition bias on our estimates is likely to be minor. Both the inverse probability and Heckman-type²⁰ models yield coefficients that are very similar to our adjusted estimate.²¹ Meanwhile, our results are robust to the moderate version of our assumptions on the Kling–Liebman bounds. Under the more conservative assumptions, our estimates change in sign but lose statistical significance.

In the online appendix (section G), we study the potential heterogeneous effects of our intervention. We show that the treatment effects might be larger among male children, children whose parents were interested in having another child, and children with older siblings.

WHZ, WAZ, and Hemoglobin

We present estimates of the treatment effect of our intervention on children's WHZ, WAZ, and hemoglobin levels in Table 3. Our main estimates do not find evidence of a treatment effect on children's weights or hemoglobin levels. It is perhaps unsurprising that we do not observe a treatment effect of our intervention on children's WHZ or WAZ, given that we expect family planning services to improve child health in this context through increased investments in children and not through broader improvements in household resiliency to shocks or the sanitary environment in which children live. The latter would be more effective in reducing the incidence of underweight or wasting. Additionally, our observation of a negative WHZ coefficient and a positive WAZ coefficient likely reflects that children's weights are increasing (albeit not enough for us to detect an effect) but at a slower rate than children's heights, which serve as the denominator of the WHZ calculation but do not enter the WAZ calculation.

Conversely, we observe a positive but statistically insignificant estimate of the intervention's impact on hemoglobin levels. Although family planning might lower the risk of anemia in children, our model is likely underpowered in detecting these effects because of our sample size.

Cognitive Development

Table 4 presents unadjusted and adjusted estimates of the impact of our intervention on child CREDI scores and on internally standardized cognition scores.²²

We find that exposure to the family planning intervention increased CREDI scores in children by 0.17–0.20 SD. The online appendix displays the distribution of CREDI z scores by intervention arm. This distribution suggests that these mean treatment effects might be driven by a reduction in the number of children with lower scores and a lower kurtosis of the distribution, implying a more centralized distribution in the treatment group. These results suggest a lower rate of developmental delays among children, as opposed to an increase in highly positive scores, although the CREDI instrument is not specifically designed to detect such delays. Again, our attrition-adjusted results indicate that any selection bias created by our high attrition rate is likely minimal, and our estimates do not change substantively in response to the attrition adjustments that we implement.²³

We further explore the results of the intervention's impact on child cognitive development in the online appendix (section G). Table G1 shows that the treatment effects on CREDI scores might be larger among girls, children whose parents were not interested in having another child, and children with older siblings. Interestingly, these findings contrast with those subgroup findings that we present on children's height.

Attrition Analysis

Throughout this section, we adjust our results to account for threats to inference as a result of high attrition, which is a key feature of our sample. This attrition comes in two forms. First, a nonnegligible 22.8% of children were not observed at any time at the first-year follow-up. This level of attrition might be considered standard in an urban setting. Among these children, we have outcome data for only 406 of the 799 children we observe,²⁴ creating a measurement rate of only 50.8%.

To explore the threats to inference discussed alongside the empirical strategy, we compare the level of attrition by mothers’ and children's baseline characteristics by measurement status and by treatment group at the first-year follow-up. As shown in Table 5, among measured children, the pattern of balance across treatment groups remains largely unchanged, with mothers of children assigned to the treatment group reporting greater ever-use of contraception and greater current use of injectables than mothers of children assigned to the control group. However, we do not observe jointly significant differences in the baseline characteristics of children measured at the first-year follow-up. Among children who were not measured, those in the treatment group were born to slightly older mothers than those in the control group. However, much like for those children who were measured, we do not observe jointly significant differences across characteristics, providing suggestive evidence that the estimates we present are internally valid, in lieu of attrition adjustment.

Although the observed differences across treatment groups are promising for our aims of causal estimation, the differences we observe within treatment groups give us reason for pause. Within the treatment arm, we observe no statistically significant differences among baseline characteristics for children measured at the first-year follow-up versus those not measured. However, within the control group, we observe moderately sized differences in mothers’ current contraceptive use and age. Furthermore, our results suggest that the baseline characteristics of control group children who were measured at the first-year follow-up versus those who were not measured are jointly different. These differences suggest that measured children might have differed systematically from nonmeasured children, potentially regardless of their assigned intervention arm. Given the context and our field experiences with concerns over measurement, it is certainly possible that measurement refusals correlate with maternal characteristics.

As discussed in the Attrition Adjustment section, differences of the kind that we observe likely threaten the external validity of our estimates, implying that any unadjusted causal effects that we might find would not be considered unbiased estimates of the treatment effect on the study sample. We address this possibility by utilizing propensity score weighting to create sample-representative estimates of the treatment effect. Table 6 presents the results from the logit model we use to estimate these propensity scores. In addition to creating weights for our estimates, this methodology allows us to expand the investigation of our sample attrition beyond the balance table presented in Table 5.

Table 6 shows that children in the treatment group were less likely to be measured (i.e., they have lower odds) than those in the control group. We cannot, however, reject the null hypothesis that the probability of measurement is equal across intervention arms. Extending this analysis, we find little correlation between maternal and child characteristics.²⁵ Instead, across outcomes, the best predictor of measurement at follow-up is having been measured at baseline.²⁶ Taking the findings from Table 5 and Table 6 together, we note that although attrition is high, we find little evidence that it differs across groups.

Mechanisms

We present the results of our mediation analysis in Table 7. Although imprecise, our results in panel A display some evidence of the mediating effects of health care use, birth spacing, and contraceptive use on HAZ. However, our estimates are significant at the 5% level only for the unadjusted birth spacing mediation. Most other coefficients are significant at the 10% level, with contraceptive use gaining significance only in the fully adjusted model. Our sensitivity analysis suggests that the results using birth spacing as the mediator are much more robust than those using health care use or contraceptive use, suggesting that any omitted variable would need to explain 30% of the joint variation between pregnancies and z scores to invalidate our results. Taking the estimates of the greatest magnitude for each mediator, we can explain roughly one third of the adjusted treatment effect that we observe in Table 2.

We accompany the results on HAZ with mediation results for children's CREDI z scores in panel B. We find no evidence of mediating effects. Furthermore, our estimates are very close to zero relative to the treatment effects that we observe on CREDI scores. We might be able to detect effects with a larger sample, given that the point estimates for health care use are in the same direction as those from the previous mediation.²⁷ However, with the current sample, it is difficult to draw inferences on causal mechanisms from this analysis. Instead, this analysis highlights the need for further research on this topic with a larger sample and richer data on child investments.

Although this analysis is underpowered, we view these results as suggestive evidence that the underlying mechanisms of our main results at least partly corroborate the theory presented by Cavalcanti et al. (2021). The associations between the uptake of health care services, improvements in birth spacing, and children's linear growth patterns are concordant with the predictions of a model of fertility containing a quality–quantity trade-off. Additionally, the evidence linking contraceptive uptake to improved growth patterns might suggest that family planning services improve certainty over birth events, thereby influencing children's health.

In our discussion of the theoretical framework, we noted an alternative causal channel driven by the possibility that women seek services not related to family planning during visits to the clinic that are enabled by the transportation component of our intervention. In Table 7, we directly test this mechanism by estimating the ACME of transportation uptake. We find no evidence of a mediating effect on children's HAZ or CREDI scores. This finding is concordant with process data collected as part of our study showing that of the 999 women who participated in services beyond their first counseling session, only 211 utilized the transportation component.²⁸ Additionally, in our data on financial reimbursement, no women reported costs unrelated to family planning. Taken together, our process evaluation data and the results of our mediation analysis suggest that our results are not likely to be driven by women receiving non-family-planning services as part of our intervention.

Discussion

Recent developments in traditional models of fertility and human capital attainment have accounted for the uncertainty in birth parity created by a lack of access to FP/RH services. These models predict that children will likely have worse human capital outcomes when fertility is uncertain than in a counterfactual world where fertility preferences are more likely to be realized. By contrast, a decrease in the price of family planning or an increase in its effectiveness should improve human capital investments in children and their subsequent outcomes.

To test these hypotheses, we use data from a randomized controlled trial in urban Malawi that improved pregnant and postpartum women's access to FP/RH services, enhancing women's knowledge of contraceptives and decreasing the effective price of contraception. Using data on children, we find that improved access to family planning positively affects children's height—a standard marker for health and nutritional status—and cognitive development. These effects are relatively large for an intervention that did not explicitly target children. In similar work, Barham (2012) found that children exposed to the Matlab program, which included a family planning component, experienced an increase of 0.36–0.40 SD in scores on the Mini-Mental State Exam and an increase of 0.22 SD in HAZ. It is somewhat surprising that the 0.196-SD increase in CREDI scores and the 0.339-SD increase in HAZ that we observe align with the effects Barham (2012) described, in spite of differences in program design and rollout. Moreover, the Matlab program offered a more expansive suite of services in which other related interventions, including vaccination campaigns and other maternal and child health services, complemented family planning. Our identification of similar effect sizes from an exclusive family planning intervention is promising for the potential of such services.

Our results broadly support the theoretical conclusions of frameworks that highlight the links between family planning, fertility, and children's health and well-being. Furthermore, they suggest that the potential effects of family planning might accrue to downstream outcomes that are impacted by child health and cognitive development, such as schooling, employment, and labor market productivity. Finding a causal impact on educational attainment or income would substantially further the case for family planning as an effective development strategy.

Our results contribute to an extensive literature on models of fertility and the quantity–quality trade-off in fertility preferences and the demand for children. We contribute to this literature by acknowledging the uncertainty in fertility among many families and studying how changes to uncertainty affect parents’ decisions regarding their children, showing that family planning services might drive improvements in children's health and human capital. Our results imply that the consequences of a trade-off in parental preferences for birth parity and investments in children might manifest through mechanisms other than completed family size and begin to materialize before that family size is realized. Therefore, our study also contributes to a smaller and more limited evidence base on the link between family planning and child health by providing direct causal evidence of this relationship.

These results suggest potential positive impacts on health outcomes that are causally distal to those typically targeted by family planning programming. In a separate publication (Karra et al. 2022), we showed that expanded access to family planning can be effective in improving fertility and reproductive health outcomes. Our results on child health suggest that family planning might also serve a role in broader health programming and, when combined with works such as Alderman et al. (2006), suggest that family planning might be an effective intervention for promoting social and economic development more broadly. Thus, our results support the existence of a “demographic dividend” (Bloom et al. 2003) associated with the provision of family planning services, which suggests that fertility changes might eventually contribute to changes in workforce composition by way of children's improved human capital attainment, potentially promoting economic development. In this way, our findings highlight the need for a whole-of-government approach to develop coordinated multisectoral policies and programs to improve both health and economic outcomes.

Our study has several limitations. First, we observe high attrition and nonmeasurement among children in our sample. We use multiple methods to assess and overcome potential selection bias from this attrition: inverse probability weighting, Heckman-style selection models, and bounding techniques. Throughout our study, our results are comprehensively robust to these adjustments except under severe assumptions on our bounding estimates. Additionally, our results from a causal mediation analysis highlight the potential mechanisms driving our results. However, this analysis lacks the statistical power needed to make more robust inferences. Future work that more rigorously studies the pathways driving these effects is needed.

Our ability to conduct a comprehensive comparison of the impact of our intervention with similar and well-established programs, such as the Matlab program in Bangladesh, is relatively limited because of the differences in the design, implementation, and duration. For example, we find that our causal estimate on the increase in contraceptive prevalence after two years is about half that observed in the Matlab program, which found a 10-pp increase in contraceptive uptake after the first two years. However, the baseline level of contraceptive use in the Matlab sample was quite low: only 1% of women were using a contraceptive method before the 1975 rollout of the program. In contrast, baseline contraceptive prevalence in Lilongwe was significantly higher in 2016, with an estimated 58% of women using a contraceptive method (National Statistical Office and ICF 2017). As a result, our program might have been limited in its ability to improve access to family planning a priori. Despite this higher baseline prevalence, we observe significant impacts of our intervention on contraceptive prevalence and birth spacing (Karra et al. 2022). We interpret our findings as providing an estimate of a lower bound of the efficacy of our family planning intervention and expect potentially larger effects in a setting with a lower baseline prevalence.

Finally, although our intervention was designed to reduce information and cost barriers and increase access to family planning services, it did not directly address societal or partner views on family planning. Evidence on the effect of male involvement in family planning decisions in sub-Saharan Africa is mixed (Ashraf et al. 2014; Assaf and Davis 2019), and each woman assigned to the intervention could decide whether she wanted to involve her husband or partner in counseling sessions. Addressing social norms and male involvement would likely require a larger, more complex (e.g., cluster randomized, multi-arm) study design, which is beyond the scope of this study.

The case for expanding family planning programs and improving access to contraceptives is strong. Our results support this case by showing that there are likely large and positive externalities and downstream impacts associated with contraceptive use that have not been incorporated into the cost–benefit calculus of these services. Our results also validate the inclusion of family planning services in frameworks to reduce childhood stunting and improve early-life outcomes (Black et al. 2013). It is likely that improved FP/RH access and use would lead to significant short-term welfare gains for women, their children, and their families that have the potential to persist over time.

Acknowledgments

This trial was registered at the American Economic Association's Registry for randomized controlled trials on May 7, 2015 (AEARCTR-0000697), and at the Registry for International Development Impact Evaluations (RIDIE) on May 28, 2015 (RIDIE- STUDY-ID-556784ed86956). This research uses original data collected by D. Canning and M. Karra, with support from Innovations for Poverty Action (IPA) in Malawi. We thank John Hoddinott, Chris Barrett, John Cawley, Gunther Fink, Jessica Leight, and Jack Cavanaugh; seminar participants at Cornell University, Rutgers University, the University of Wisconsin–Madison, the University of Malawi, and the University of Oxford; and attendees at NEUDC, ICDE, IPC, CSAE, ASHEcon, IHEA, EPC, PAA, PACDEV, and MWIEDC for their valuable feedback and comments. We also acknowledge the dedication and support of Carly Farver, Patrick Baxter, Bagrey Ngwira, Reginald Chunda, Viola Nyirongo, Violet Chitsulo, Macdonald Salamu, and the entire Malawi Family Planning Study team. This project was supported by two grants from the Hewlett Foundation and the Program for Women's Empowerment Research at the Boston University Global Development Policy Center. Ethical approval to conduct the study was received from the Harvard University IRB (protocol number IRB16-0421) and the Malawi National Health Sciences Research Committee (protocol number 16/7/1628). The findings, interpretations, and conclusions expressed in this study are entirely those of the authors. They do not represent the views of the IPA and its affiliated organizations or those of the Executive Directors of the IPA they represent.

Data Availability

A replication package—which includes two deidentified datasets that are needed to replicate the findings for the article; five Stata do-files, which reproduce the results presented in the article and online appendix; and a Read-Me file for users—has been deposited to the Harvard Dataverse database at https://doi.org/10.7910/DVN/E0ZYL2.

Notes

References