Abstract
Community Health Centers (CHCs) deliver primary care to underserved populations by locating sliding-scale clinics in disadvantaged areas. We investigate how this policy affected infant health using the rollout of CHCs and a flexible event-study framework with Vital Statistics natality data. We find that maternal access to CHCs improves infant health outcomes within seven years after their introduction. Treatment-on-the-treated estimates show a 25- to 42-gram increase in birth weight and a 9–16 percent reduction in the likelihood of low birth weight. These improvements can be explained by increased access to early prenatal care and reductions in maternal smoking.
I. Introduction
Health disparities across socioeconomic groups are an important concern to policymakers because they start at birth and persist throughout one’s lifetime. To reduce these disparities, the federal government has invested in demand- and supply-side policies that serve low-income populations, including pregnant women and young children. Demand-side policies to address gaps in nutrition and access to health insurance include Food Stamps, the Special Supplemental Nutrition Program for Women, Infants, and Children (WIC), and Medicaid. One of the critical supply-side policies that directly delivers primary care is Community Health Centers (CHCs). There is a large body of causal evidence that documents the effects of nutrition and health insurance programs on health outcomes across the life cycle (Almond, Hoynes, and Schanzenbach 2011; Almond, Currie, and Duque 2018; Bailey et al. 2024; Hoynes, Page, and Stevens 2011; Currie and Gruber 1996; East et al. 2023), but the evidence is limited on the causal effects of the delivery of primary care services at scale on health outcomes (Bailey and Goodman-Bacon 2015).
This paper provides the first causal analysis of the effects of the introduction of the CHC program on infant health with evidence of potential mechanisms. Established as part of the War on Poverty (WOP), CHCs have provided both primary and preventive care to medically underserved communities since 1965. While CHCs do not specifically target their services to pregnant women, a majority of them provide prenatal and postpartum care as well as voluntary family services (Goldman and Grossman 1988). Indeed, women of childbearing age are the second-most common users of CHCs, representing around 30 percent of users by mid-1980s (Rosenbaum 1986).1 To understand how the increased availability of these primary care services affected infant health, we analyze birth weight and the incidence of low birth weight as our main outcomes, both of which are commonly used as proxies for health at birth. Individuals who are healthier at birth are more likely to be healthier adults, with improved educational and labor market outcomes (for example, Almond, Currie, and Duque 2018; Currie 2011; Black, Devereux, and Salvanes 2007).
Our main outcome data are from Vital Statistics birth records between 1968 and 1988 (Kose, O’Keefe, and Rosales-Rueda 2024). This data set provides rich information on infant health and maternal characteristics, including the county of residence, age, race, and, in some states and years, marital status and educational attainment. For the rollout of CHCs, we extend data on the introduction of CHCs between 1965 and 1980 compiled by Bailey and Goodman-Bacon (2015) using the Federal Assistance Awards Data System (FAADS) from the US Census Bureau until 1988.2 Combining the outcome data with the introduction of CHCs, we assign the treatment based on birth year and county of residence at birth. We also explore the effect of CHCs separately by maternal characteristics to assess whether the impacts are stronger for low-socioeconomic-status women, who are more likely to use CHC services. To analyze the potential mechanisms, we use data from the 1979 National Longitudinal Survey of Youth (NLSY79) and the Survey of Health Services Utilization and Expenditures (SHSUE) in addition to the Vital Statistics.
Our empirical strategy uses a difference-in-differences design that exploits geographic and time variation in the introduction of CHCs. We use the robust difference-in-differences estimation strategy introduced by Sun and Abraham (2021) after diagnosing the presence of treatment effect heterogeneity associated with the standard two-way fixed effects approach (de Chaisemartin and D’Haultfœuille 2020). We first present our estimates using static difference-in-differences and then dynamic event-study models. To limit concerns about potential endogeneity of program placement, our preferred specification follows previous WOP studies and controls for county-of-birth fixed effects and 1960 county characteristics interacted with flexible trends (Bailey and Goodman-Bacon 2015; Almond, Hoynes, and Schanzenbach 2011; Bailey et al. 2024; Bailey, Sun, and Timpe 2021). Moreover, we show that the trends in outcomes are not statistically different between treated and control counties before the introduction of CHCs.
Our results show that the introduction of CHCs led to significant improvements in infant health. We find that maternal exposure to CHCs increased average birth weight by 3–6 grams (≈0.09 percent of the mean) and reduced the incidence of low birth weight by 1 percent. These intent-to-treat (ITT) estimates reflect the average effect for the whole population in a county. Scaling the ITT effects by approximate CHC participation rates among pregnant women (between 6.4 percent and 10.7 percent) implies that the average treatment effect on the treated (TOT) is between 25 and 42 grams for birth weight and between 9 percent and 16 percent for low birth weight. While the type and targeting of other interventions are different, these effect sizes are comparable to other TOT estimates of policy interventions on infant health, including Food Stamps and WIC (Almond, Hoynes, and Schanzenbach 2011; Hoynes, Page, and Stevens 2011). The TOT effect implies that the benefits to infants of maternal exposure to a CHC are roughly three times the program’s costs per user.3
Based on the target population of CHCs, we expect the impacts to be concentrated among low-socioeconomic-status mothers. Indeed, we find that CHCs’ impacts on infant health are stronger for low-educated mothers.4 Moreover, our findings are robust to including or excluding various control variables; alternative fixed effects, trends, and timing measures; and alternative methods robust to treatment effect heterogeneity (Borusyak, Jaravel, and Spiess 2024; Gardner 2021). Lastly, we show that these effects are not driven by fertility responses or changes in the composition of women giving birth.
To explain potential mechanisms underlying the effects on infant health, we show that CHCs’ introduction improved access to prenatal care, in particular in the first trimester. In addition, we find that mothers exposed to CHCs before their child’s birth experienced a large, statistically significant reduction in smoking during pregnancy.5 This finding is critical because smoking is one of the primary risk factors for intrauterine growth restrictions, which leads to smaller infants (Kabir et al. 2013; Reeves and Bernstein 2008). Moreover, maternal smoking is negatively related to access to prenatal care—women with reduced access to prenatal care, especially early in pregnancy, are more likely to report using tobacco (Evans and Lien 2005). Additionally, we provide evidence that childbearing-age women without a high school degree living in areas with a CHC were more likely to have a regular source of healthcare, pointing to improved pre-conception health as another potential mechanism.
Our paper contributes to several strands of literature. In the CHC literature, the best available causal evidence of the effects of the CHC program comes from Bailey and Goodman-Bacon (2015), who study the effect of the rollout of CHCs from 1965–1974 on adult mortality (age 50 plus). They find significant reductions in age-adjusted adult mortality rates up to 15 years after CHCs’ introduction. We contribute to this literature by studying another important group of beneficiaries of CHCs: pregnant women. We provide new causal evidence that CHCs improved several markers of birth outcomes up to seven years after their introduction. To understand the potential mechanisms underlying the long-run effects on infant health outcomes, we use various data sources that allow us to examine the maternal and infant experiences following CHCs’ introduction. This is important because understanding mechanisms can also inform the design of policies that are more effective.
Prior CHC literature provides descriptive evidence that these centers may improve infant birth outcomes. For example, Goldman and Grossman (1988) use cross-sectional analyses and find that an increase in the number of CHCs in the 1970s was associated with reductions in infant mortality rates in exposed counties, with larger effects for Black infants than white infants. Studies that analyze more recent CHC expansions find positive (for example, Shi et al. 2004a,b) or null (Gourevitch and Hatfield 2022) associations between primary care availability and infant health outcomes. We build on this work by leveraging the rollout of CHCs using modern panel data techniques to control for nonrandom assignment and reduce endogeneity bias.
Additionally, our study contributes to the literature that shows that WOP programs have been effective in improving outcomes for individuals who were exposed to the programs’ introduction (for example, Bailey et al. 2024; Bailey, Sun, and Timpe 2021; Barr and Gibbs 2022; Currie and Gruber 1996; East et al. 2023; Goodman-Bacon 2018, 2021b; Hoynes, Schanzenbach, and Almond 2016; Ludwig and Miller 2007). While these studies have examined human capital investments related to early childhood education, nutrition, and health insurance, we study health investments related to the direct provision of primary care services that improved prenatal care access. Interestingly, the magnitudes of our effects on birth outcomes are similar to those from Food Stamps, WIC, and Medicaid, which suggests that different types of policies that promote different investments can generate similar effects.
Lastly, our work is related to the broader literature on the effects of healthcare access, particularly prenatal care, on child health outcomes. Previous studies have examined the effects of prenatal care access through health insurance on infant health and later-in-life outcomes (Currie and Gruber 1996; Miller and Wherry 2019, 2022). Other related work has analyzed the health impacts of disruptions in access from strikes and hospital closures (Evans and Lien 2005; Fischer, Royer, and White 2022). Complementing these studies, our work shows that expanding access to primary healthcare services, including prenatal care, through a supply-side intervention improves health at birth, providing children with a strong start in life. The US setting in the 1970s, with limited access to health services and growing health insurance coverage, is relevant for similar contexts today in low- and middle-income countries (Wüst 2022), thus informing potential impacts of similar community-based health delivery programs.
In Section II, we provide background information about CHCs’ introduction and evidence on the exogeneity assumption. Section III describes our data sources, and Section IV introduces the empirical methodology followed by the results in Section V. In Sections VI and VII, we present potential testable mechanisms and the robustness of our results. Section VIII concludes.
II. The Community Health Center Program
A. Background
The CHC program was established with the passage of the Economic Opportunity Act in 1964, which also created the Community Action Program (CAP) as part of the Office of Economic Opportunity (OEO) (Wolfe 2013). Focusing on a community empowerment approach, CHCs (known originally as Neighborhood Health Centers) provide primary and preventive health services, as well as referrals to hospitals if additional care is needed (Erickson 2013). Access to services is based on residence only, and the population they serve includes low-income families, the uninsured, migrants, and homeless people (Levitan 1969).
The first CHCs were established in 1965 in Boston, Massachusetts, and Mound Bayou, Mississippi. The initial phase of grants funded CHCs mainly in urban areas with high concentrations of poverty. By August 1968, 32 centers were operating, and 75 percent of them were in urban areas (Levitan 1969). By the early 1970s, the federal government had funded more than 100 centers through the OEO grants (Erickson 2013). However, federal involvement in supporting the provision of health services declined during Richard Nixon’s presidency, and the OEO was dismantled. By 1974, grants were awarded through the regional Department of Health, Education, and Welfare offices rather than through the federal government (Erickson 2013). Due to disagreements in the administration, the program was stagnant during this time, and the number of CHCs only increased slightly in the first half of the 1970s (Figure 1, Panel A).
Timing of CHC Adoption and Geographic Variation
Notes: We compile data on CHC timing from Bailey and Goodman-Bacon (2015) for years 1965–1980 and FAADS for years 1981–1988.
In 1975, despite a lack of support from the Ford administration, Congress formalized the CHC program. This legislation required organizations receiving CHC grants to serve medically underserved areas, which were defined based on the percentage of the population below the federal poverty line, the infant mortality rate, the percentage of the population over 65, and the primary care physician to population ratio (Wolfe 2013). This new legislation shifted the focus and funding of CHCs toward rural areas. Between 1975 and 1980, during the Ford and Carter administrations, the number of counties with a CHC increased significantly, and by 1980, 622 counties had at least one CHC.
In the early 1980s, the Reagan administration showed opposition to the CHC program. Reagan eliminated all categorical health service grants and created five block grants where CHCs became part of a primary care block grant via the 1981 Omnibus Budget Reconciliation Act (Erickson 2013). From 1984 to 1986, Congress continuously rejected a health center block grant that would be administered by states, and the CHC program remained federally funded. In 1986, because of overwhelming congressional support, Reagan signed the Health Services Amendments Act of 1986 that repealed the primary care block grant, authorized funding for CHCs as categorical grants through FY 1988, and increased state involvement in the program. During the 1980s, the creation of CHCs increased slightly (Erickson 2013). Between 1981 and 1988, CHCs were introduced in 111 counties, and by 1988, 733 counties in total had at least one CHC (Figure 1, Panel A).
Our analysis spans up to 1988 because, in 1989, Congress created the federally qualified health centers (FQHC). This new designation changed the centers’ funding structure: block grants were responsible for a smaller portion of CHC budgets while Medicaid and Medicare reimbursements became the dominant source of revenue (Wolfe 2013).
B. CHC Services and Population Served
CHCs were designed to comprehensively serve the health needs of individuals living in medically underserved and poor areas. They focus on providing primary and preventive health services, as well as health education, and some also have in-house pharmacies to ensure patients can access necessary medication. In cases where more specialized or acute care is needed, practitioners at CHCs can refer patients to local hospitals (Wolfe 2013).
CHCs are staffed by multidisciplinary teams of clinical personnel, including general practitioners, internists, OB/GYNs, pediatricians, nurses, and nurse practitioners/physician assistants (Dievier and Giovannini 1998). While children make up the majority of patients, women of childbearing age are the second largest group, representing 28.6 percent of users (Rosenbaum 1986). Consequently, prenatal care is an important part of the primary care services provided by CHCs. Obstetrics patients account for the second-most patient days and number of admissions (National Association of Community Health Centers 1984). Around 85 percent of CHCs provide prenatal care, serving more than 200,000 pregnant women per year by the end of our study period (Witwer 1990).
Evidence from national-level surveys indicates that CHCs were an important source of prenatal care during our study period. Online Appendix Figure A.1 shows the percentage of women who reported receiving prenatal care at a “clinic” in the first four cycles of the National Survey of Family Growth (NSFG). In the 1973 and 1976 cycles, all types of clinics were grouped together. Starting in 1982, the clinic category was broken into more detailed categories, including CHCs specifically. Overall, approximately 80 percent of pregnant women received care from a private practitioner (US Institute of Medicine 1989). But for the 20 percent of women who could not access these sources, CHCs and other public clinics have been an important source of prenatal care. The largest increase in the use of clinics in Online Appendix Figure A.1 occurred between the 1976 and 1982 waves of the NSFG. This corresponds to the largest increase in the number of counties with CHCs, which also occurred in the late 1970s. This is suggestive evidence that pregnant women received primary care services from CHCs during the rollout period we analyze.
Consistent with the goal of providing primary care to underserved populations, most CHC patients’ family income was below the poverty level. According to a 1984 survey of CHC users, 60.8 percent had family incomes at or below the poverty line, while only 13.7 percent had an income above 200 percent of the poverty level. Their patients also had relatively low levels of education: 45.4 percent reported one to eight years of education, and 39.3 percent reported nine to 12 years. Only 15 percent reported more than a high school education (National Association of Community Health Centers 1984). While we cannot observe income in our outcome data, we examine the effects separately by maternal education, as we expect stronger effects for low-educated mothers.
C. The Rollout of CHCs Between 1965 and 1988
From 1965 to 1980, CHCs’ introduction year at the county level comes from data collected by Bailey and Goodman-Bacon (2015). From 1965 to 1974, they use multiple sources of information, including the National Archives Community Action Program, Public Health Services Reports, and OEO reports. From 1975 to 1980, they use data from the National Archives Federal Outlays files. By 1980, CHCs were established in 622 counties (Figure 1, Panel A).
Because our analyses cover the years between 1968 and 1988, we supplement the rollout compiled by Bailey and Goodman-Bacon (2015) by extending it up to 1988. We use data from the FAADS to identify the counties of organizations awarded grants related to CHCs. These data allow us to identify the introduction of CHCs in 111 additional counties between 1981 and 1988 (Figure 1, Panel A).
Figure 1, Panel B depicts the rollout of CHCs across counties over time. The map clearly illustrates that there is considerable variation across both time and states. This map also shows the presence of significant within-state variation in the establishment of CHCs. This variation is useful for our analysis as it allows us to include state-by-year fixed effects, which absorb time-varying changes in state policies, such as Medicaid expansions, access to contraception, and others that may be correlated with CHCs’ rollout. We show this specification as part of our robustness checks in Section VII.
As discussed above, the initial funding introduced CHCs in more urban areas, and after 1975, it shifted to establishing centers in more rural counties. Online Appendix Table A.1 presents 1960 characteristics of counties that received CHCs between 1965 and 1988. Counties where CHCs were established between 1965 and 1974 have 58–76 percent of their population in urban areas. For counties that received CHCs after 1975, the urban population drops to 36 percent. Consistent with this, counties that introduced CHCs in the initial phases of funding had lower poverty rates (as measured by the share of families with incomes below $3,000, the 1960 poverty line for a family of four) than counties that introduced CHCs after 1975 or did not receive CHCs between 1965 and 1988. Early CHC counties were also more educated, more affluent and had a larger number of physicians per capita in 1960. These observed differences and the potential for unobservable time-invariant county characteristics correlated with establishing CHCs during this period motivate us to include county fixed effects in our analyses.
Our identification strategy requires that the timing of CHCs’ introduction is exogenous after conditioning on covariates. The previous discussion suggests that counties with certain characteristics were more likely to receive CHCs in the earlier phases. This potential systematic variation in CHCs’ introduction could contaminate our estimates of the CHCs’ impacts if those characteristics are associated with differential trends in our outcomes of interest. To provide evidence on this assumption, we test whether 1960 county characteristics (pre-program) predict the timing of a county’s CHC opening in Table 1, following a similar approach used by other WOP studies (Hoynes and Schanzenbach 2009; Bailey 2012; Bailey et al. 2024).6,7 Columns 1–3 focus on all the counties that adopted CHCs between 1965 and 1988. They show that counties that are more urban, more nonwhite, have a higher number of MDs per capita, and have a larger fraction of poor families implemented CHCs earlier. Furthermore, counties with a larger fraction of educated adults introduced CHCs later. Some of these associations are no longer significant when we include state fixed effects (Column 3), except for urban and nonwhite percentages, as well as MDs per capita, which are consistent with the political economy of the program (Wolfe 2013).
Determinants of CHCs Rollout Between 1965 and 1988
Because the Vital Statistics data start in 1968, we do not observe pre-treatment outcomes for counties that adopted a CHC before 1969 and do not include them in the analyses.8 Columns 4–6 present models for our analytical sample. For this sample, urbanicity, the nonwhite share of the population, and the supply of physicians are associated with a CHC opening earlier. However, the quantitative importance of these predictors is smaller than for the full set of counties (in Columns 1–3), and most of the variation remains unexplained (as illustrated by the low R-squared between 0.06 and 0.32). This benefits our identification strategy, as there is no strong evidence of endogeneity in the timing of CHCs. However, unobservables may still be a concern. To ameliorate this issue, our preferred specification includes interactions of significant 1960 pre-treatment county characteristics with flexible time trends to control for differential trends across counties that could be spuriously correlated with CHCs’ effects.9
III. Data
Data on birth outcomes are from Vital Statistics birth records from 1968–1988. These data are coded from individual birth records and represent either a 50 percent or 100 percent sample of births occurring in each state.10 We follow prior literature and process these data by expanding them in the 50 percent sampled states by two (Almond, Hoynes, and Schanzenbach 2011). Our primary outcomes of interest are birth weight and if the infant is considered low birth weight (birth weight <2,500 grams).
To better understand the effects and explore mechanisms, we examine several additional outcomes from the birth certificate: if the infant was classified as having a very low birth weight (birth weight <1,500 grams), the gestational age of the infant, if the infant was small for gestational age,11 and whether the infant was born prematurely (before 37 weeks of gestation). We also examine if the mother received any prenatal care during pregnancy and if prenatal care began in her first trimester.
The birth certificate data include additional information on the mother’s age, race, and, in some states and years, marital status and educational attainment. We restrict the sample to White and Black women ages 15–39 at the time of the birth.12 The data are collapsed into cells due to computational intensity.13 To preserve our ability to use fixed effects to control for socioeconomic and demographic factors, cells are defined by county, mother’s age group (15–19, 20–24,…, 35–39), mother’s race (Black or white), mother’s marital status (unmarried, married, missing), mother’s education (less than high school, high school, more than high school, missing), parity (first, second, third, fourth, fifth or more birth), and year.
We combine these data with the CHCs’ rollout and county-level characteristics. These include county-level transfers per capita, hospital beds per capita (Bailey and Goodman-Bacon 2015), and the white and nonwhite share of women and children receiving Aid to Families with Dependent Children (AFDC) at the state level as a proxy for Medicaid access compiled by Goodman-Bacon (2018). We also include information on the rollout of contemporaneous policies including Food Stamps from Almond, Hoynes, and Schanzenbach (2011), family planning programs from Bailey (2012), and WIC.14
IV. Research Design
A. Empirical Strategy
We exploit time and geographic variation in the rollout of CHCs to estimate the causal effect of access to primary healthcare services on birth outcomes using the method from Sun and Abraham (2021). Our first specification is a “static” difference-in-differences (DD), where we compare the infant health outcomes for children born in a county with a CHC and without a CHC before and after the program’s introduction. Formally, we estimate the following equation at the cell level:
1where Yijt is the birth outcome of infants whose mothers are in cell i, born in county j and year t. Cells are defined by parity and mother’s age, race, marital status, and educational attainment.15 CHCjt is an indicator equal to one if a child is exposed to a CHC based on their county and year of birth.
Mit contains a constant and cell-level sociodemographic characteristics, such as mother’s education, marital status, race, and age. As male infants are, on average, heavier at birth (Lehre, Laake, and Sexton 2013), we also control for the portion of births in the cell that is male.16 Xjt includes time-varying county and state characteristics that could confound the effect of CHCs: county-level transfers per capita, hospital beds per capita, the rollout of Food Stamps, WIC and family planning programs, and the white and nonwhite share of women and children using AFDC at the state level as a proxy for Medicaid access.
θj represent county fixed effects that absorb time-invariant characteristics that could be correlated with the CHCs’ rollout, and δt represent year fixed effects that capture time-varying national changes.17 Additionally, in our preferred specification, we include C1960 * γt: the interaction of significant 1960 county characteristics with year fixed effects. Those characteristics are the share of the nonwhite population, MDs per capita, and the share of the population in urban areas in terciles to capture high, medium, and low urbanicity (Table 1). Regressions are weighted by the number of births in the cell, and standard errors are clustered at the county level. The coefficient of interest is τ, which measures the effect of CHC exposure and is identified from changes in birth outcomes between births exposed and nonexposed to a CHC before and after the rollout.
To examine dynamic treatment effects, we estimate the following event-study specification:
2where Dj is a binary treatment variable equal to one if the county ever receives a CHC grant. Indicator variables 1(t − Tj* = 1) capture the time relative to CHC’s implementation year, Tj*, for observations in counties that ever received the program, and are zero in all periods for counties without a CHC. Observations eight years or more before CHC’s establishment are captured by the dummy, 1(t − Tj* ≤ −8). Similarly, observations eight years or more after CHC’s introduction are captured by the dummy 1(t − Tj* ≥ −8).18 Relative periods between −7 and +7 are grouped in two-year bins for precision. Relative period −1 is always excluded.
τl are the coefficients of interest, which show how the selected outcome evolves over relative time (l) after a CHC opens (relative to the year prior to CHC introduction). πl show the pre-treatment changes in birth outcomes in eventually treated counties relative to never-treated counties; these coefficients are expected to be small and statistically insignificant if birth outcomes in CHC and never-CHC counties trended similarly before the program’s introduction.
Considering recent developments in econometrics (Goodman-Bacon 2021a), we use the method from Sun and Abraham (2021) instead of the more traditional two-way fixed effects (TWFE) method to estimate our specifications. TWFE may produce biased coefficients in staggered designs, such as the rollout used in this paper, if the treatment effects are not homogeneous (Goodman-Bacon 2021a). We perform two tests to understand if treatment effect heterogeneity is a concern in our setting. First, we perform a diagnostic test proposed by de Chaisemartin and D’Haultfœuille (2020). In summary, we find evidence the TWFE estimator may be biased due to treatment effect heterogeneity over time and by county and individual socio-demographic characteristics (Online Appendix Table B.1). Second, we perform a test proposed by Sun and Abraham (2021). We find evidence that variation from other relative time periods is biasing the TWFE event-study coefficients (Online Appendix Figure B.1). Because we find evidence of treatment effect heterogeneity in our setting, we use a robust estimation method introduced by Sun and Abraham (2021) to estimate the effects of a CHC on infant health.19 Online Appendix B contains a more complete discussion of both these tests and of treatment effect heterogeneity in our setting.
The Sun and Abraham (2021) estimation procedure consists of three steps. First, the procedure identifies the cohort-specific average treatment effect on the treated in relative time period (l) for the cohort who received the intervention at time e (CATTe,l) using a saturated regression that interacts relative time dummies with cohort dummies (excluding indicators for the comparison group). From this regression, the CATTe,l estimator, 
, is a DD estimator of the following form:20
3where 
corresponds to the CHC’s implementation year for a given observation (cell) i, which is determined by the county j. s corresponds to the excluded relative time pre-periods, which for the case of the dynamic estimation is relative period −1. C includes the control cohorts, which are counties without a CHC in our setting. In words, 
captures the differences in average outcomes between the treated cohort (e) and the never-treated control group (C) relative to the excluded time period (−1).21
The second step creates the weights by calculating the sample shares of each cohort in each relative time period. The final step computes the interaction-weighted estimator of the aggregated event-study coefficients (for each relative time period) by taking the weighted average of estimates of 
from step one using the weights from step two. This procedure calculates the treatment effect heterogeneity robust event-study estimates of the dynamic effects of CHCs on birth outcomes (Sun and Abraham 2021).
B. Identification Assumptions and Internal Validity Checks
The validity of our research design relies on the assumption that the timing of CHCs’ introduction across counties is uncorrelated with other county time-varying determinants of our outcomes of interest. We assess and address threats to identification in several ways.
First, we discussed the potential endogeneity of CHC placement by estimating the role of 1960 pre-program characteristics in predicting CHC rollout in Section II.C. We showed that although the quantitative importance of these predictors is small, counties with a larger share of doctors per capita and those with a greater fraction of the population that was urban and nonwhite implemented CHCs earlier. Therefore, our preferred specification controls for interactions of these pre-program county characteristics with flexible time trends. This implies that our empirical strategy relies on the exogeneity of the timing of CHCs’ introduction after controlling for covariates. Importantly, our conclusions do not depend on the inclusion of these covariates, and our preferred estimates are very similar to those from the baseline specification that only includes county and year fixed effects and demographic controls, as we show in the next section.
Second, we test whether CHCs’ presence is correlated with time-varying county characteristics (Pei, Pischke, and Schwandt 2019; Bailey et al. 2024). Table 2 presents static estimates of the coefficient of the presence of CHCs in a county from a model similar to the one depicted in Equation 1 using the listed county characteristics as the dependent variable. We find that CHC exposure has no association with health characteristics, such as hospitals per capita and Medicaid transfers per capita, or with economic characteristics. We also find no relationship between CHCs and the availability of Food Stamps and family planning programs. We do find a statistically significant positive association between CHCs and WIC presence, suggesting a potential confounder. To address this concern, we perform several robustness checks as explained in Section VII and show that our results are unlikely to be driven by WIC presence.
Balance Test: Correlations Between CHC Exposure, Time-Varying County Characteristics, and Other Programs Between 1965 and 1988
Third, the lack of pre-trends in the event-study specification provides evidence of the validity of the parallel trends assumption. We find that those coefficients are small and statistically insignificant. Lastly, Section VII presents additional robustness checks (such as alternative timing measures, fixed effects, and trends, among others) that support the validity of our empirical strategy.
V. Main Results
A. Full Sample
In this subsection, we present estimates from both static and dynamic difference-in-differences models for birth weight (in grams) and the incidence of low birth weight (less than 2,500 grams) using the estimation method developed by Sun and Abraham (2021). We start with our baseline specification, which includes county and year fixed effects and demographic controls (Table 3 and Online Appendix Table A.2, Columns 1 and 4). We then add time-varying state and county controls (Columns 2 and 5) and 1960 county variables interacted with year fixed effects (Columns 3 and 6). While it is reassuring that our results are not sensitive to model specification, our preferred specification is the one that includes time-varying state and county controls as well as 1960 significant determinants interacted with flexible trends.
Static Effect of CHCs on Infant Health—Main Outcomes, Full Sample
Table 3 presents the results using a static difference-in-differences design where we find that CHCs’ introduction improved infant health outcomes. The results for birth weight indicate that CHCs led to a small increase in birth weight of 3–6 grams. Relative to the pre-period mean of 3,300 grams, our preferred specification in Column 3 implies a 0.09 percent increase in average birth weight. Turning to the incidence of low birth weight, we also find that there was a reduction of 0.09 percentage points with exposure to a CHC during pregnancy. Relative to the mean, this corresponds to a 1 percent decrease. Online Appendix Table A.3 shows our main results using individual-level data. The coefficients and standard errors are almost identical to those reported using cell-level data.
Figure 2 presents the event-study coefficients that capture dynamic effects before the introduction of CHCs (−7 to −2 years) and after the introduction (0–7 years) using bins to increase statistical precision (Bailey and Goodman-Bacon 2015).22 Importantly, for our empirical strategy, the coefficients in the periods before the introduction of CHCs are small and do not show statistical evidence of differential trends in infant health outcomes, which confirms the parallel trends assumption. In the post-period, we see a sharp increase in birth weight that persists in the long run. For low birth weight, we see a gradual reduction that attenuates in the longer run.
Effect of CHCs on Infant Health—Main Outcomes, Full Sample
Notes: This figure plots the estimated coefficients and 95 percent confidence intervals obtained from event-study specification using the methods introduced in Sun and Abraham (2021). The outcome data are from the Vital Statistics Natality Files that cover the years between 1968 and 1988. We compile data on CHC timing from Bailey and Goodman-Bacon (2015) for years 1965–1980 and FAADS for years 1981–1988. The analysis is run using data at the cell level. All regressions include county and year fixed effects and individual demographic controls. Standard errors are clustered at the county level. For more details about the estimation, see Equation 2 in Section IV.
Overall, the magnitudes of these ITT effects are small on the full population; however, recall that most pregnant women do not receive care at a CHC. Our ITT estimates on birth weight and low birth weight are within the ranges of those found by other WOP programs.23 For example, Almond, Hoynes, and Schanzenbach (2011) find that the Food Stamp program’s introduction increased birth weight by around 2 grams for white infants and 4.3 grams for Black infants while reducing the likelihood of low birth weight by 1 percent and 1.3 percent for white infants and Black infants, respectively. For WIC, Hoynes, Page, and Stevens (2011) estimate that its rollout increased birth weight between 2.3 and 2.7 grams.24
B. Translating ITT Effects into TOT Estimates
To translate the ITT estimates into average TOT effects, we need information on the fraction of births to women who used CHC services during pregnancy in the 1970s and 1980s. To approximate that information, we gather a range of statistics based on historical reports and survey data. Witwer (1990) states that CHCs and migrant health centers served “an estimated 213,000 pregnant women per year.” From the Vital Statistics data, we calculate that there were 3.3 million births per year, on average, between 1968 and 1988. Combining these two statistics, we estimate that approximately 6.4 percent of pregnant women were served by CHCs per year. If we use the total births in counties that had a CHC by 1988 (1.98 million), we get a CHC participation rate of 10.7 percent. Using these two alternative potential participation rates to scale our ITT estimates gives an estimated TOT effect for birth weight between 25 and 42 grams and for low birth weight between 0.8 and 1.4 percentage points (9 percent and 16 percent of the mean).
Alternatively, the 1982 and 1988 National Survey of Family Growth (NSFG) asked specifically about prenatal care use at CHCs. Approximately 5.2 percent of pregnant respondents reported receiving care at a CHC. However, survey respondents tend to underreport their use of public programs, and Bound, Brown, and Mathiowetz (2001) document that for clinic visits, survey responses agree with provider records as little as 39 percent of the time. Adjusting for underreporting, the CHC participation rate could be as high as 13 percent. Using both the unadjusted and adjusted CHC participation rates, we get an estimated TOT effect on birth weight between 21 and 52 grams. For low birth weight, these participation rates imply a TOT effect between 8 percent and 20 percent.
It is reassuring that the two alternative approaches yield similar ranges of average TOT effects. Furthermore, these effect sizes are comparable to other TOT estimates of policy interventions on infant health, including Food Stamps and WIC (Almond, Hoynes, and Schanzenbach 2011; Hoynes, Page, and Stevens 2011), as summarized in Online Appendix Table A.4.25 Regarding other health policies, such as access to health insurance, during the dramatic Medicaid expansions to pregnant women in the 1980s, Currie and Gruber (1996) find that a 30 percentage point increase in eligibility was associated with a reduction of 1.9 percent in low birth weight. Overall, the similarity of the effects of demand-side policies and supply programs like the CHC is interesting since the first set of policies promotes different types of health investments, and some are more targeted than CHCs. For example, WIC specifically promotes nutrition investments for low-income pregnant women and infants, whereas CHCs provide primary healthcare access in underserved areas for populations of all ages. While there is a large body of causal evidence that shows the significant impacts of targeted programs on infant health, we show that less-targeted policies can have similar effects on health outcomes at birth.
C. Heterogeneity
1. Mother’s education
Based on the population served by CHCs, we expect the impacts to be concentrated among low-socioeconomic-status families. Using information available on maternal education in the Vital Statistics data, Figure 3 presents the results on infant health separately for mothers with less than high school, high school, and greater than high school education.26 As expected, the results are stronger for infants whose mothers had less than a high school education, particularly for low birth weight. However, the effect sizes are not statistically different across the subsamples.
Effect of CHCs on Infant Health—By Mothers’ Education
Notes: This figure plots the estimated coefficients and 95 percent confidence intervals obtained from event-study specification using the methods introduced in Sun and Abraham (2021). The outcome data are from the Vital Statistics Natality Files that cover the years between 1968 and 1988. We compile data on CHC timing from Bailey and Goodman-Bacon (2015) for years 1965–1980 and FAADS for years 1981–1988. The analysis is run using data at the cell level. For this analysis, we restrict our sample to 36 states that include complete information about maternal education following Kearney and Levine (2007). All regressions include county and year fixed effects, individual demographic controls, time-varying county controls, and 1960 determinants trends. Standard errors are clustered at the county level. For more details about the estimation, see Equation 2 in Section IV.
Our findings in Online Appendix Table A.5 suggest that among women with less than high school education, following CHCs’ introduction, there is a sharp increase in birth weight and a gradual reduction in the fraction of low-birth-weight births. The average birth weight increases by 7 grams, while the incidence of low birth weight decreases by 0.2 percentage points. While the overall effect size on birth weight is small, the reduction in the incidence of low birth weight is 1.9 percent relative to the mean. The magnitude of the overall effect for the low-educated sample is similar in size to the effects of Food Stamp access in high-poverty counties (Almond, Hoynes, and Schanzenbach 2011) and WIC access to low-educated mothers (Hoynes, Page, and Stevens 2011).
2. Other maternal characteristics
Next, in Online Appendix Figure A.2, we explore treatment effect heterogeneity by maternal race (Panels A and B) and age groups (Panels C and D) for our main outcomes. On average, Black mothers are more likely to have a low-birth-weight child and more preterm births than white mothers (Aizer and Currie 2014). These disparities persist through adulthood and are associated with later-life health and human capital accumulation (Currie 2011). We hypothesize that CHCs may play a role in closing the health disparities between Black and white infants. Panels A and B present our infant health results separately for all mothers, white, and Black mothers, using our preferred specification. These results show that the effects of CHCs on birth weight and low birth weight are greater for Black infants than white infants in the short run (up to three years after CHCs’ introduction). However, the effects dissipate quickly after three years for Black infants.
Similarly, teenage mothers are more likely to have low socioeconomic status, experience a low birth weight delivery, and have complications during birth (Geronimus and Korenman 1993). It may be that a CHC’s arrival to a county provides easy access to healthcare during early pregnancy for teenage mothers and improves infant health outcomes for this group. Panels C and D of Online Appendix Figure A.2 present the results on infant health outcomes separately for all mothers, teenage mothers, mothers who are ages 20–29 and 30–39, using our preferred specification. We show that infants of teenage mothers benefit from a CHC’s introduction slightly more than other infants. However, these effects among the subgroups are not statistically different from one another.
VI. Other Outcomes and Potential Mechanisms
A. CHCs and Other Birth Outcomes, Prenatal Care, and Maternal Behaviors
We also examine other birth outcomes in Figure 4 and Online Appendix Table A.6, including an indicator for very low birth weight (<1,500 grams), gestation in weeks, small for gestational age (below the tenth percentile of birth weight for gestational age), and an indicator for a premature birth (<37 weeks gestation). Online Appendix Table A.6, Column 1 shows that exposure to a CHC reduced the probability of very low birth weight by 1.4 percent of the mean, a small effect that we detect in the static model, which is noisier in the dynamic specification (Figure 4, Panel A).
Effect of CHCs on Other Birth Outcomes and Mechanisms
Notes: This figure plots the estimated coefficients and 95 percent confidence intervals obtained from event-study specification using the methods introduced in Sun and Abraham (2021). The outcome data are from the Vital Statistics Natality Files that cover the years between 1968 and 1988. We compile data on CHC timing from Bailey and Goodman-Bacon (2015) for years 1965–1980 and FAADS for years 1981–1988. The analysis is run using data at the cell level. All regressions include county, year fixed effects, individual demographic controls, time-varying county controls, and 1960 determinants trends. Standard errors are clustered at the county level. For more details about the estimation, see Equation 2 in Section IV. Online Appendix Table A.6 presents the point estimates and standard errors on the underlying regression results that produce the figure.
In addition, birth weight is partly determined by gestational length (Kramer 1987a,b). While we do not find significant effects on average gestational age, we do find that CHCs reduced the probability of an infant being small for their gestational age by 1.3 percent (Online Appendix Table A.6, Column 3). The effects are concentrated between two and seven years after a CHC opening (Figure 4, Panel C). Additionally, we see evidence of a decrease in the likelihood of preterm delivery by around 1.2 percent between Years 0 to 5 post-CHC introduction (Figure 4, Panel D). Due to infants’ increased vulnerability, preterm birth is one of the leading causes of infant mortality. While we do not find evidence of CHCs’ effects on infant mortality (Online Appendix Figure A.3), this finding is still relevant since preterm births are costly. In 2005, each preterm birth led to increased costs of more than $50,000 (US Institute of Medicine 2007).
Regarding the mechanisms underlying CHCs’ effects on birth outcomes, prenatal care is one of the main services provided by these centers (Goldman and Grossman 1988). Access to and use of prenatal care have been linked to the length of gestation and birth weight (Rosenzweig and Schultz 1983; Abrevaya and Dahl 2008; Corman, Dave, and Reichman 2019). We find a very small positive effect of CHCs using the static estimation (0.26 percent as shown in Online Appendix Table A.6, Column 5, relative to a baseline rate of 98 percent). However, this result should be taken with caution as the event-study analysis depicted in Figure 4, Panel E reveals the presence of pre-trends in the likelihood of attending prenatal care.27
In this context, a more relevant dimension of prenatal care is its timing. Online Appendix Table A.6, Column 6 shows that the introduction of CHCs led to a 1.3 percent increase in the probability of receiving prenatal care during the first trimester relative to the mean. Figure 4, Panel F presents that the effect is immediate and only grows stronger throughout the post-period. During the first prenatal visit, the provider gathers information about the patient’s health history, asks about alcohol and tobacco use, screens for conditions that could lead to complications, and counsels her on nutrition and health behaviors. This early screening can help prevent serious complications later in the pregnancy (National Institutes of Health 2017). Additionally, early prenatal care can be thought of as an information treatment (Bersak and Sonchak-Ardan 2022). Receiving this information earlier allows women to engage in positive health behaviors for a larger fraction of their pregnancies, making early initiation of prenatal care especially important for later outcomes.
At that time, birth certificates did not report information on maternal health behaviors during pregnancy. Therefore, we turn to the NLSY79 to understand how access to a CHC affected women’s behaviors during pregnancy. For each pregnancy, women were asked if they used alcohol or tobacco during the pregnancy. In this setting, a pregnancy is considered treated if the child was born after a CHC opened in the county of birth. The effects were estimated using our preferred specification for pregnancies that occurred by 1988. Given the much smaller sample of the NLSY79, we only estimate static effects.
In Table 4, Columns 1 and 3, we provide suggestive evidence that CHCs’ introduction led to mothers reducing their alcohol use during pregnancy. This table also shows that access to a CHC before a child’s birth significantly reduces the probability of the mother reporting smoking during her pregnancy by four percentage points, or 11 percent of the mean (Column 2). The decline is larger if we consider a sample of mothers with less than high school education, who are more likely to use CHCs (Column 4). CHCs can plausibly influence maternal smoking since around 85 percent of the centers provided health education as part of prenatal and perinatal services in our study period, and around 70 percent specifically provided smoking cessation services (HHS Office of Inspector General 1992). While the reduction in tobacco use we estimate is significant, it is about one-fifth of the size of ITT estimates of interventions that exclusively focus on prenatal smoking (Sexton and Hebel 1984).
Effect of CHCs on Substance Use in Pregnancy
The reduction in maternal smoking during pregnancy following CHCs’ introduction is consistent with the birth weight results. Smoking is the primary risk factor for intrauterine growth restrictions, which leads to smaller infants (Kabir et al. 2013; Reeves and Bernstein 2008). Nationally, tobacco use during pregnancy accounts for 20 percent to 30 percent of low-birth-weight births (Ricketts, Murray, and Schwalberg 2005). Although prenatal smoking has declined since our study period, it remains one of the most prevalent causes of poor infant outcomes and deaths (Dietz et al. 2010). Tobacco use remains more common for some demographic groups. For example, 22 percent of mothers with less than a high school education in nonmetropolitan areas reported tobacco use during pregnancy in 2019 (Centers for Disease Control and Prevention, National Center for Health Statistics 2019).
In addition, maternal smoking is negatively related to access to prenatal care; women with reduced access to prenatal care, especially early in pregnancy, are more likely to report smoking during pregnancy (Evans and Lien 2005). Reducing maternal smoking may be a primary mechanism through which improved access to care from a CHC could lead to better infant outcomes. For example, oxygen delivery to the fetus improves immediately upon stopping smoking, leading to improved fetal growth rates. Therefore, quitting earlier relative to later improves the in utero environment for a longer portion of pregnancy (Centers for Disease Control and Prevention 2017).
Taken together, we find suggestive evidence that the introduction of CHCs improved additional markers of health at birth. We show that early access to prenatal care and smoking cessation are plausible mechanisms.
B. CHCs and Women’s Access to Healthcare
As discussed in Section II.B, national-level surveys show that clinics, including CHCs, were important sources of prenatal care, and their use grew as the CHC program expanded. However, we are unable to observe if a woman lives near a CHC in the NSFG surveys. To investigate if living in an area with a CHC changes healthcare utilization, we use data from the 1963 and 1970 SHSUE to investigate if being near a CHC increased women’s access to healthcare. The SHSUE is a nationally representative survey of healthcare use with data from 1963, before the CHC program began, and the same areas were sampled again for the 1970 wave (post-introduction of CHCs). The SHSUE survey is the best information about healthcare access with geocoded data available during our study period.28
First, we identify the counties that make up the primary sampling units (PSUs) of the SHSUE. Some PSUs contain more than one county. In those cases, we consider women treated if any county in their PSU had a CHC by 1970. While we cannot specifically analyze pregnant women in these data, we limit the sample to women ages 15–39, which matches the ages of mothers in our Vital Statistics sample. We estimate the following difference-in-differences linear probability model:
4where i is an individual and t is the survey year. Yit is whether the woman has a regular source of care or, for those with a regular source of care, if the source of care is a clinic, a category that explicitly includes CHCs in 1970. The equation includes an indicator for whether the woman lives in an area that receives a CHC by 1970, an indicator for the 1970 wave, and an interaction term, whose coefficient is reported in Table 5. Xit is a set of controls for age, marital status, race, and the same urban categories as used in the main regressions. Standard errors are clustered at the PSU level. Given the educational distribution of CHC users and the stronger effects for mothers without a high school degree discussed in Sections II.B and V.C, we perform this analysis for the full sample and separately for women without a high school degree.
Effect of CHCs on Women’s Healthcare Access
Table 5 shows that the opening of a CHC improved healthcare access for women without high school degrees. Those living in an area with a CHC by 1970 were significantly more likely to report having a regular source of care. This is an 11 percent increase relative to the mean. Much of this increase seems to be driven by increased use of clinics—the coefficient in Column 4 represents almost a 100 percent increase in the portion of women reporting a clinic as their regular source of care. Individuals with a regular source of care are more likely to receive preventive care and less likely to delay visits for specific conditions. Having a regular source of care is more strongly predictive for these outcomes than having health insurance (Sox et al. 1998).
This pattern is consistent with our results on early prenatal care. Women who already have a provider will find it easier to start prenatal care early in their pregnancies. In addition to prenatal care, this result points to another potential mechanism for the observed improvements in infant health: pre-conception health. Regular access to healthcare may lead to general improvements in the health of childbearing-age women. Women who are healthier before pregnancy are more likely to carry to term and have healthier infants (Stephenson et al. 2018).
VII. Composition, Sensitivity, and Robustness
A. Composition
Beyond the direct effect on infant health, access to healthcare through a CHC may have indirect effects on the health of observed infants if women respond to CHC access by changing their fertility patterns. This is plausible considering access to contraception was increasing throughout this time period (Myers 2017) and CHCs provide reproductive health services including family planning (Wolfe 2013). If more disadvantaged women responded to these services by having fewer children, then our results may be biased. However, in Table 6, we see no evidence of changes to fertility: when measured by the birth rate or the natural log of the total number of births, there is no measurable change in overall fertility.
Effect of CHCs on Maternal Composition
Table 6 also shows no effect on marital status, parity, maternal age, or the percentage of teen births. In CHC-exposed areas, women giving birth may be slightly more likely to be Black. This effect is not significant in the static analysis but is statistically different from zero up to five years following a CHC’s introduction. Given that Black women are more likely to have adverse birth outcomes, any potential bias from this shift in maternal composition works against our finding of infant health improvements. Additionally, this effect may be evidence of reductions in miscarriages and stillbirths for Black women, important health outcomes that we cannot directly measure in our data. Lack of prenatal care, especially early prenatal care, and maternal smoking are known risk factors for these events and likely contribute to racial disparities in miscarriage and stillbirth rates (Hogue and Silver 2011). If CHCs are improving access to early prenatal care and reducing maternal smoking, as we report in Section VI, these mechanisms may also improve fetal health.
B. Sensitivity Using Alternative Specifications
Our results are robust to alternative specifications, which are presented in Figure 5. These results in table form are available in Online Appendix Tables A.7 and A.8. The results for birth weight and low birth weight in this figure follow the same pattern. The square reproduces our preferred specification, which includes demographic and time-varying county characteristics, as well as flexible trends for 1960 county determinants. Next, we estimate this specification using a TWFE model (triangle). The effect is no longer statistically significant, and there is some evidence of a pre-trend. However, as discussed above, we present evidence of potential treatment effect heterogeneity, and we use the Sun and Abraham (2021) procedure to address the bias from using earlier-treated units as a comparison for later-treated units. We consider this evidence in favor of our estimation method choice. Next, we add state-by-year fixed effects (circle), which reduce the magnitude of the static effect but show similar dynamic effects as our preferred specification. Finally, the estimate represented by the diamond redefines the timing of the intervention to be relative to the time of conception. Conception timing is calculated using the gestational age at birth; in our study period, this information is missing for 21.3 percent of the sample. The static effect using this timing is very similar to our preferred specification. However, the dynamic effects are noisier and attenuated, potentially due to the decreased sample size.
Effect of CHCs on Infant Health, Alternative Specifications
Notes: This figure plots the estimated coefficients and 95 percent confidence intervals obtained from event-study specification using the methods introduced in Sun and Abraham (2021), except for the estimates labeled “TWFE,” which use two-way fixed effects. The outcome data are from the Vital Statistics Natality Files that cover the years between 1968 and 1988. All regressions include county, year fixed effects, individual demographic controls, time-varying county controls, and 1960 determinants trends. Standard errors are clustered at the county level. For more details about the estimations, see Equation 2 and Section VII.
Additionally, in Online Appendix Tables A.7 and A.8 in Column 5, we reproduce our results using the urbanicity controls from Bailey and Goodman-Bacon (2015). While we prefer the data-driven urban-tercile trend described in Section IV, our estimates are not sensitive to this choice. Finally, in Column 6, we rerun our preferred specification without controlling for access to WIC. The results with and without controlling for the WIC rollout are very similar. We include a detailed discussion on WIC in the next section.
C. Additional Robustness
1. Randomized inference
Beyond the sensitivity checks, we perform a randomization test to ensure the effects we report could not have been the result of random chance. We compute the static policy effect from 1,000 permutations of the treatment, holding the distribution of rollout dates constant. The distribution of coefficients from these permutations are reported in Online Appendix Figure A.4. For both birth weight and the incidence of low birth weight, the blue histogram represents the distribution of the randomized coefficients and the red line represents the estimated effect. For both outcomes, the estimated effect of the CHC is well into the tail of the distribution of randomized coefficients.
2. Placebo treatment timing
In a similar spirit, we want to be sure the dynamic results we report are not the result of unrelated trends in areas that receive a CHC. To test this, we reestimate the CHC effects with a change in the treatment timing. Instead of using the actual year a CHC opened, we assign the treatment timing to be four years earlier than the truth. If our results are driven by spurious trends in areas that received a CHC, these trends will now be picked up by the regression as the treatment effect. Because this requires additional years of pre-period information, we can only include treated counties that received a CHC in 1977 or later in this robustness check. Online Appendix Figure A.5 presents these results and shows no observable effect of an artificially early CHC arrival on average birth weight or the incidence of low birth weight. In all three versions of the specification, the “treatment effect” is flat, statistically insignificant, smaller in magnitude, and opposite signed than the true treatment effects we find.
3. Event-time balanced panel
Another concern may be that the panel of treated counties is unbalanced in event time. Given the timing of CHC rollout and the years for which Vital Statistics data are available, creating a balanced sample requires reducing the number of counties in the analysis, estimating fewer pre- and post-periods, or both. Figure 6 presents results for a balanced sample that only includes counties that received their first CHC between 1970 and 1981.29 The effects of CHC exposure on the balanced panel are very similar to the effects we find using the full set of available data. We prefer to use all available data in our main specification, but this gives us confidence that our findings on the effects of CHCs on infant health are not driven by changes in the composition of counties across event time.
Effect of CHCs on Infant Health, Balanced Sample
Notes: This figure plots the estimated coefficients and 95 percent confidence intervals obtained from event-study specification using the methods introduced in Sun and Abraham (2021). These results exclude counties that received a CHC before 1970 or after 1981 in order to create a balanced panel. The outcome data are from the Vital Statistics Natality Files that cover the years between 1968 and 1988. All regressions include county and year fixed effects and individual demographic controls. Standard errors are clustered at the county level. For more details about the estimations, see Equation 2 and Section VII.
4. Alternative CHC timing
The focus of this study is to analyze the effect of CHC exposure for the first 20 years after the program’s introduction. In Online Appendix Figure A.6, we examine whether the benefit of CHCs for infant health is still observable when considering exposure to either the earliest adopters or over a shorter time frame (similar to the preferred specifications in Bailey and Goodman-Bacon 2015). To check this, we estimate two variations of our preferred specification: first, for counties that received the CHC grant before 1975 (green circle), and second, for counties that adopted CHCs by 1980 using the Vital Statistics data up to 1980 (blue diamond). Our main specification is reproduced for comparison purposes (red square). While the point estimates are generally larger in magnitude for the early adopters, there is significant overlap across all three estimations, and all three support our conclusion that the introduction of the CHC program leads to improvements in infant health.
5. WIC exposure as a potential confounder
As discussed earlier, we found empirical evidence that CHCs’ rollout is correlated with WIC presence, which could confound our results. To address this concern, we perform various robustness checks. First, we reestimate our results, focusing on the CHC rollout before WIC’s first year of implementation in 1974. If the effects of CHC on infant health were confounded by exposure to WIC, we should not see evidence of CHC impacts for counties that adopted a CHC before 1975. Online Appendix Figure A.6 suggests that the estimates are slightly larger if we restrict the sample to counties that adopted a CHC before 1975 (see estimates in green). Second, our results are not sensitive to including WIC exposure as a control variable (see Column 6 of Online Appendix Tables A.7 and A.8). While our preferred specification includes WIC exposure as a control variable, our results are almost identical without including WIC exposure (Online Appendix Figure A.7). Third, as an additional robustness check, we present estimates that drop counties that were early adopters of WIC (program adoption between 1974 and 1977). Online Appendix Figure A.8 shows that our results are not sensitive to this exclusion. Overall, the evidence outlined reassures that our results are not driven by WIC presence in a county.
6. Alternative difference-in-differences methods
Lastly, we check if our main results estimated using the Sun and Abraham procedure are robust to using alternative methods that address treatment effect heterogeneity. Online Appendix Figure A.9 presents estimations using the imputation method from Borusyak, Jaravel, and Spiess (2024),30 and Online Appendix Figure A.10 shows estimates using the two-stage difference-in-differences procedure from Gardner (2021). Overall, we corroborate our findings of (i) no pre-program differential trends in infant health outcomes as coefficients for the periods before the introduction of CHCs are small and not statistically different from zero, and (ii) a sharp increase in birth weight and a gradual decline in the likelihood of low birth weight post-CHC introduction. In sum, our main findings are robust to using other recently developed methods to address treatment effect heterogeneity.
VIII. Conclusion
Reducing children’s health disparities across socioeconomic groups is an important policy goal given the long-run consequences of poor health (Currie 2011). The introduction of the CHC program provides an opportunity to understand how the direct provision of healthcare in medically underserved areas affects infant health. By leveraging the rollout of CHCs in a flexible difference-in-differences empirical framework, we show that infants born to mothers with access to a CHC in their county were significantly healthier at birth as measured by birth weight. On average, the introduction of CHCs increased birth weight by 3–6 grams and reduced the incidence of low birth weight by 1 percent of the mean. These ITT effects translate into TOT effects between 25 and 42 grams for birth weight and between 9 percent and 16 percent for low birth weight. The magnitudes of these impacts are comparable to those from the other WOP programs, including Food Stamps and WIC.
To examine potential mechanisms, we use the information available in the Vital Statistics and auxiliary data from the NLSY79 and the SHSUE. We identify early prenatal care use and smoking cessation as potential mechanisms behind the CHCs improvements in health at birth. Also, we show evidence of improvements in pre-conception healthcare for low-educated childbearing-age women as another mechanism.
To assess the social benefits of the CHCs through improvements in health at birth, we calculate a back-of-the-envelope benefit-to-cost ratio using our TOT estimates. Black, Devereux, and Salvanes (2007) estimate that a 10 percent increase in birth weight is associated with a 1 percent increase in earnings. Our estimates imply that CHCs increase birth weight by approximately 1 percent, which translates into a 0.1 percent increase in earnings.31 Using the lifetime earnings reported in Currie, Mueller-Smith, and Rossin-Slater (2022) of $520,753 (measured in 2017 dollars), we calculate the benefits per participant to be around $520. On the cost side, the total CHC program cost was around $850 million (measured in 2017 dollars) per year throughout the 1980s while serving around five million patients per year (Bailey and Goodman-Bacon 2015; National Association of Community Health Centers 2015), which corresponds to a cost of $170 per patient.
We calculate a benefit-to-cost ratio of 3.06, implying that every dollar spent on the CHC program generates a $3 benefit through improvements to infant health. This estimated benefit-to-cost ratio is a lower bound, as previous work has shown CHCs also improve health outcomes for other groups (Bailey and Goodman-Bacon 2015). Our work shows that interventions that do not specifically target mothers and infants, but instead focus on increasing access to healthcare, can improve health outcomes for the next generation.
Acknowledgments
The authors thank Liz Cascio, Eric Chyn, Janet Currie, Hilary Hoynes, Jason Lindo, and Lucie Schmidt for their helpful feedback, as well as seminar and session participants at the American Economic Association Annual Meetings, NBER Health Economics Program Meeting, Southern Economic Association Meetings, University of South Carolina, Columbia Women’s Applied Micro seminar, Dickinson College, Furman University, University of North Carolina Greensboro, Carolina Regional Empirical Economics Day, Liberal Arts Colleges Public and Labor Conference, the Global Labor Organization virtual seminar, and the Society of Labor Economists Annual Meeting. They gratefully acknowledge support from the Eunice Kennedy Shriver National Institute of Child Health & Human Development of the National Institutes of Health under Award Number R01HD093898. The findings, conclusions, views, and opinions are solely those of the authors and do not necessarily represent the views of the National Institutes of Health. Data and programs for replication are available in ICPSR (https://doi.org/10.3886/E207041V1). The replication files do not include the NLSY data, which are available for researchers by request through the Bureau of Labor Statistics, or the SHSUE data, which are available through ICPSR and NORC.
Footnotes
↵1. The first-most common group of users are children under the age of 14 (36 percent of the users).
↵2. Our analysis spans up to 1988 because, in 1989, the federally qualified health centers (FQHC) were created by Congress. With the new designation, the financing and reimbursement options changed in response to low Medicaid reimbursement rates paid in some states (Wolfe 2013).
↵3. This ratio is a lower bound because we assume that CHCs only benefit infants in our calculation. However, previous research has shown CHCs’ benefits to other age groups (Bailey and Goodman-Bacon 2015). Additional details on this calculation are in Section VIII.
↵4. One caveat with this analysis is that parental education information is available for only 36 states, which we discuss further in Section V.C.
↵5. We also provide suggestive evidence that CHCs’ introduction led to mothers reducing their alcohol use during pregnancy.
↵6. The dependent variable is the year of CHCs’ introduction expressed as an index equal to one beginning in 1965.
↵7. The results, presented in Table 1, include models with and without state fixed effects, both unweighted and weighted by county population in 1960.
↵8. Only 39 counties introduced CHCs by 1968.
↵9. A similar approach has been used by other studies on the impact of WOP programs, such as Food Stamps (Almond, Hoynes, and Schanzenbach 2011).
↵10. Vital Statistics micro data are available starting in 1968, and county identifiers are publicly available through 1988. In state-years with a 50 percent sample, the technical documentation describes a stratified random sample (National Center for Health Statistics 1982). Additionally, in 1989, the federally qualified health centers (FQHC) were created by Congress. This new designation changed the financing and reimbursement options, creating a natural end to the rollout period (Wolfe 2013).
↵11. “Small for gestational age” is defined as being in the bottom 10 percent in birth weight of all infants born at the same gestational age in the same year.
↵12. In the early years of the Vital Statistics, races other than white or Black are often coded simply as “other,” so we cannot track births to women of other races consistently throughout the sample period.
↵13. Our results are not sensitive to this choice. Online Appendix Table A.3 shows our main results using individual-level data. The coefficients and standard errors are almost identical to those reported using cell-level data.
↵14. The WIC rollout data correspond to Hoynes, Page, and Stevens (2011), supplemented by ongoing work with National Archives documents by Bitler et al. (2024).
↵15. For marital status and education, we include a category for missing information. Due to computational intensity, all results presented are estimated at the cell level; the results are almost identical when we perform our analyses at the individual level, as discussed in Section V.A.
↵16. It is worth noting that we do not find evidence that the birth cohort sex ratio is affected by exposure to CHCs.
↵17. We show robustness to adding state-by-year fixed effects in Section VII.
↵18. Following similar recent studies (for example, East et al. 2023; Bailey et al. 2024), these binned endpoints are not reported in the figures because they are estimated using a very imbalanced sample of counties (we observe only a small subset of counties with a CHC eight years before and eight years after).
↵19. Our results are consistent if we use other treatment effect heterogeneity robust estimators, which we show in Section VII.
↵20. EN abbreviates the symbol
, where i denotes the unit of observation which in our case is the cell level.↵21. The calculation is similar for the static DD estimation, but in that case, there are only two relative-time bins: one with all the pre-periods and the other with all the post-periods. The first is omitted due to collinearity, similar to the omission of −1 in the dynamic estimation, and serves as the comparison point for the differences in average outcomes.
↵22. Online Appendix Table A.2 presents the coefficients and the standard errors on the underlying regression results that produce the figure. The last column of Online Appendix Table A.2 reports the number of treated counties in each bin for our event years (the years relative to the introduction of CHC). For each bin, we have at least 605 treated counties, and the number of never-treated counties that we use as our comparison group is 2332.
↵23. We summarize these point estimates in Online Appendix Table A.4.
↵24. Bitler et al. (2024) find that exposure to WIC rollout decreased the likelihood of low birth weight, especially for minority populations.
↵25. We acknowledge that our estimated participation rates may be measured with error, leading to either higher or lower TOT estimates. Our approach represents our best attempt given the information available.
↵26. Following Kearney and Levine (2007), we restrict our sample to 36 states that include complete information about maternal education. The states with missing information on maternal education are AL, AR, CA, CT, DE, DC, FL, GA, ID, MD, NM, OR, PA, TX, and WA.
↵27. It is worth noting that the baseline fraction of pregnant women who received prenatal care is very high, and the magnitudes of the differential trends are not sizable.
↵28. In 1980, the National Medical Care Utilization and Expenditure Survey was administered. This data set is available at ICPSR, but it does not contain county information. According to correspondence with the Centers for Disease Control and Prevention and the Agency for Healthcare Research and Quality, the geographic identifiers for this survey are no longer available. Therefore, we are unable to use the 1980 survey in our analysis.
↵29. These results are available in table form in Online Appendix Table A.9.
↵30. It is worth noting that the method in Borusyak, Jaravel, and Spiess (2024) does not allow binning of periods. Thus, the figures present the results for single years relative to the opening of a CHC (in contrast, our main specifications use two-year bins to increase precision).
↵31. The effect sizes are 0.76 percent when we use the lower bound TOT estimates (=25/3300) and 1.27 percent when we use our upper bound estimate of 42 grams (=42/3300).
- Received June 2023.
- Accepted April 2024.
This open access article is distributed under the terms of the CC-BY-NC-ND license (https://creativecommons.org/licenses/by-nc-nd/4.0) and is freely available online at: https://jhr.uwpress.org.
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