ESSAYS IN THE ECONOMICS OF REPRODUCTIVE HEALTH By Graham Gardner A DISSERTATION Submitted to Michigan State University in partial fulfillment of the requirements for the degree of Economics—Doctor of Philosophy 2023 ABSTRACT This dissertation is composed of three chapters detailing the health and fertility effects of restricted access to abortion in the United States. Chapter 1: The Maternal and Infant Health Consequences of Restricted Access to Abortion in the United States Since the recent US Supreme Court decision in Dobbs v. Jackson Women’s Health Organization, people across the country have experienced large sudden changes in their access to abortion care. In this paper, I look to the history of abortion access in the United States to inform predictions for this new future. I study the effects of targeted regulations on abortion providers (TRAP laws) on a variety of maternal and infant health outcomes, using variation in the timing of policy adoption across states and a direct measure of the distance to an abortion provider. I implement difference- in-differences techniques across outcomes from restricted-use microdata on the universe of US births and national survey data from the Behavioral Risk Factor Surveillance System. I find that TRAP laws lead to 11-16% increased rates of hypertensive disorders of pregnancy, and I provide suggestive evidence that these health effects may not be isolated to the period of pregnancy and birth. Additionally, I find evidence that TRAP laws widen existing disparities in adverse infant health outcomes across parental race and education. These results demonstrate the potentially wide-ranging health effects of restricting access to abortion. Chapter 2: Notification vs Consent: The Differential Effects of Parental Involvement Laws on Teen Abortion US state legislation requiring parental involvement in the abortion decision of a minor has grown in prevalence since its origin in the 1970s. Today, 36 states impose a parental involvement requirement on their residents below the age of 18. These laws come in two primary categories: parental notification and parental consent. Though much research estimates the effects of these policies, limited evidence exists regarding any differential impact between parental notification and parental consent. This paper uses the synthetic control method to determine if the increased marginal cost of an abortion imposed by a parental consent statute affects the abortion rate and birth rate for minors relative to parental notification. Results indicate no evidence of a marginal effect of parental consent laws on the abortion/birth rate of minors overall, suggesting that the additional cost of a parental consent law may be small. Chapter 3: The Effects of Restricted Abortion Access on IUDs, Contraceptive Implants, and Vasectomies: Evidence from Texas (with Cara Haughey and Brad Crowe) Abortion and contraception are often considered to be substitutes, such that an increase in the cost of abortion will increase the demand for contraception. Although the effects of restricted abortion access are wide-reaching and often studied, we know little about the influence of abortion access on the take-up of contraception. In this paper, we exploit the timing of passage of House Bill 2 (HB2) in Texas, a regulation on abortion providers that shut down over half of all abortion clinics in the state. Using administrative outpatient records from Texas, we identify the effects of HB2 on the timing and take-up of intrauterine devices (IUDs), contraceptive implants, and vasectomies using difference-in-differences methods. We find suggestive evidence that expectations of limited abortion access significantly increase the take-up of IUDs, with no substantial evidence of an effect for the incidence of implants or vasectomies. These early findings support the hypothesis that abortion and contraception are substitutes, but the lack of evidence to indicate an effect of HB2 on the incidence of vasectomies suggests that partners may not internalize the cost of abortion in their contraceptive choices. TABLE OF CONTENTS CHAPTER 1 THE MATERNAL AND INFANT HEALTH CONSEQUENCES OF RESTRICTED ACCESS TO ABORTION IN THE UNITED STATES . . 1 CHAPTER 2 NOTIFICATION VS CONSENT: THE DIFFERENTIAL EFFECTS OF PARENTAL INVOLVEMENT LAWS ON TEEN ABORTION . . . . 38 CHAPTER 3 THE EFFECTS OF RESTRICTED ABORTION ACCESS ON IUDS, CONTRACEPTIVE IMPLANTS, AND VASECTOMIES: EVIDENCE FROM TEXAS . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 59 BIBLIOGRAPHY . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 75 APPENDIX A CHAPTER 1 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . 81 APPENDIX B CHAPTER 2 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . . . 84 iv CHAPTER 1 THE MATERNAL AND INFANT HEALTH CONSEQUENCES OF RESTRICTED ACCESS TO ABORTION IN THE UNITED STATES 1.1 Introduction On June 24, 2022 the abortion landscape in the United States changed dramatically. The Supreme Court of the United States issued their ruling on Dobbs v. Jackson Women’s Health Organization, holding that the Constitution does not confer a right to abortion and reversing the existing precedents set by Roe and Casey. Thirteen1 states now restrict abortion in all or almost-all circumstances. Georgia restricts abortion after six weeks gestation, effectively prohibiting nearly all abortions. Indiana, Iowa, North Dakota, Montana, Ohio, South Carolina, Utah, and Wyoming currently have abortion bans that are temporarily blocked by state courts (Times, 2022) As a result of these recent policy changes, people all over the country with the capacity to become pregnant experience large and sudden increases to their travel distance to an abortion provider. In this paper, I look to the history of restrictive abortion legislation in the United States to inform predictions for the new world post-Dobbs. I estimate the effects of state-level targeted regulations on abortion providers (TRAP laws) on maternal and infant health outcomes using restricted-use Vital Statistics Natality data. The adoption of TRAP laws serves as a relevant natural experiment for understanding the effect of Dobbs because these supply-side regulations often burden clinics to the point of closure and substantially increase the travel distance to a provider. In this way, they can be considered a microcosm of the current abortion environment. In a restrictive abortion environment, people with the capacity to become pregnant may change their contraceptive and sexual behavior to avoid pregnancy, and this incentive may be particularly strong if they expect the pregnancy to be at a high risk for complications. At the same time, conditional on pregnancy, the additional cost of an abortion may prevent people who are pregnant from accessing the procedure, resulting in a greater number of pregnancies carried to term. Those who would otherwise seek an abortion but are prevented from accessing the procedure may have a 1 At the time of writing, these states are: Alabama, Arkansas, Idaho, Kentucky, Louisiana, Mississippi, Missouri, Oklahoma, South Dakota, Tennessee, Texas, West Virginia, and Wisconsin. 1 higher risk of pregnancy/birth complications due to the selection into abortion. So, abortion access impacts health outcomes through a compositional change in the population of people carrying a pregnancy to term, and the theoretical predictions of their effects are ambiguous. Health outcomes may improve on average if a large number of high-risk pregnancies are avoided. However, if the cost of abortion results in more high-risk pregnancies carried to term, health outcomes will worsen on average. Then, the average effect of TRAP laws on maternal and infant health outcomes is largely an empirical question. I exploit the timing of TRAP laws at the state level and use the Borusyak et al. (2021) difference- in-differences estimator to identify causal effects of restrictive abortion legislation on average rates of adverse health outcomes among birthing people2 and infants that are robust to heterogeneity across treated units and time. I find that TRAP laws increase state-level rates of hypertensive disorders of pregnancy by 11-16%. These effects are stable across alternative TRAP policy codings from Austin and Harper (2019) and Jones and Pineda-Torres (2021), and robust to controlling for a variety of reproductive health policy indicators and including region-year fixed effects. I complement this analysis relying on policy variation in abortion laws by directly measuring the effect of increasing travel distance to a provider. I use a panel of abortion provider distance at the county-month level compiled by Myers (2021b) and a fixed effects design including county fixed effects, time fixed effects, and a state time trend to measure the effect of increasing travel distance to a provider on county-level rates of adverse health outcomes. I find that increasing the distance to the nearest abortion provider by 100 miles increases county-level rates of pregnancy- associated hypertension and chronic hypertension by 8.7% and 16% respectively. And, this larger travel distance increases rates of diabetes and gestational diabetes by 10.3% and 8.6%. Maternal and infant health effects are particularly relevant in the US context. Age-adjusted rates of hypertensive disorders of pregnancy nearly doubled in the US between 2007 and 2019, and significant disparities exist across racial/ethnic groups and region. These conditions are a leading cause of pregnancy-associated mortality, and a major contributor to the current maternal health 2 Throughout the paper, “birthing people" refers to people with the capacity to become pregnant. 2 crisis in the United States (Cameron et al., 2022; Declercq and Zephyrin, 2020; MacDorman et al., 2021). Although rates of infant low birthweight and preterm birth are relatively stable over time, disparities between racial groups persist, with Black infants experiencing substantially higher rates of premature birth and low birthweight relative to white infants (Pollock et al., 2021; Gupta and Froeb, 2020). I implement a triple-difference procedure to explore how these laws affect the disparities in adverse outcomes across demographic groups demonstrated to be more impacted by family planning access. I find that TRAP laws increase the gap in premature birth and low birthweight between Black and white infants by 3-6%, and these laws increase the gap in premature birth between infants born to people with a high school diploma or less and those born to college-goers by 19.5%. This is the first study to describe the causal effects of any modern restrictive abortion policies in the United States on the health status of birthing people who carry to term and infants using administrative Vital Statistics Natality data. We know that restricted abortion access tends to decrease abortion rates and increase birth rates (Jones and Pineda-Torres, 2021; Myers, 2021a,b; Myers and Ladd, 2020; Lindo et al., 2019) but relatively little about how abortion access affects other outcomes. I contribute foremost to the literature surrounding effects of abortion access on outcomes for birthing people beyond abortion and birth rates. Most of this evidence is dedicated to socioeconomic outcomes (Jones and Pineda-Torres, 2021; Brooks and Zohar, 2022; González et al., 2020; Mølland, 2016; Bloom et al., 2009) and the limited evidence on health outcomes focuses almost exclusively on maternal mortality. Vilda et al. (2021) use a pooled cross-section of data on maternal mortality and state abortion policies to estimate that states with a greater number of abortion restrictions have higher rates of maternal mortality. However, their estimates do not have a direct causal interpretation. Hawkins et al. (2020) use standard difference-in-differences to assess the effect of a large panel of state-level policy decision on maternal mortality, finding that gestational limit laws increase the risk of maternal mortality by 38%, a surprisingly large estimate given the fact that these laws apply only to people seeking abortion after twenty weeks gestation 3 when relatively few abortion occur. Hawkins et al. (2020) also study the passage of two TRAP laws, but find null effects. Notably, the timing of gestational limit laws may be correlated with other TRAP or demand-side abortion policies (mandatory waiting periods, parental involvement laws, etc.) in a way that is not accounted for in their research design. In a current working paper Farin et al. (2021) use difference-in-differences to estimate the effect of legalized abortion leading up to and at the time of Roe v. Wade on maternal mortality, finding a significant reduction in non-white mortality of 30-40%. The limited causal evidence on abortion and mortality outside of the US is consistent with this finding. Clarke and Mülrad (2021) estimate significant declines in maternal morbidity and abortion-related morbidity following abortion legalization in Mexico. The closest existing work to this paper comes from The Turnaway Study, an analysis of being denied a wanted abortion by seeking it after the 20 week gestational limit. In this study of over 1,000 women, Ralph et al. (2019) find that women who are denied a wanted abortion are more likely to report chronic pain and lower overall health within five years relative to those who receive their abortion in the second trimester. The authors find no significant results in the five year rates of gestational diabetes, gestational hypertension, or non-gestational hypertension between these two groups in this small sample of individuals who seek an abortion around 20 weeks gestation. I make my primary contribution here, by estimating effects on maternal health beyond mortality using national data on the universe of US births. In addition, I analyze a natural experiment that is closely tied to the current state of abortion access, and I move beyond policy variation by directly measuring the effect of increasing provider distance. Another closely connected literature studies the effects of abortion access on infants. A sizeable portion of this literature considers the effects of expanded abortion access around the time of Roe on infant mortality and infant health at birth, finding that abortion access is correlated with improvements in infant low birthweight and mortality (Gruber et al., 1999; Joyce and Grossman, 1990; Joyce, 1987; Corman and Grossman, 1985; Grossman and Jacobowitz, 1981). Two recent papers measure the association between modern abortion restrictions and adverse infant health outcomes. Redd et al. (2022) use a state-level abortion restrictiveness index and a multivariate 4 logistic regression model to measure associations between restrictive environments and infant preterm birth and low birthweight. They find that national associations between abortion laws and these outcomes are not statistically significant, but there is some heterogeneity in effects across regions. Pabayo et al. (2020) also use a multivariate logistic model and a panel of state-level abortion laws including several demand-side policies and Medicaid funding restrictions, finding that infants born in states with more restrictions have higher odds of mortality. I provide the first causal evidence on the effects of modern abortion restrictions on infant health at birth in the United States. The paper proceeds as follows: in Section 2, I describe the policy environment and categorize TRAP laws using two possible policy codings. In Section 3, I present a conceptual framework that describes the selection into abortion and potential pathways for treatment effects. In Section 4, I describe the data, estimation, and results for measuring the effects of TRAP laws on Vital Statistics Natality outcomes. In Section 5, I provide suggestive evidence regarding the potential for these effects to persist beyond the time surrounding pregnancy and birth. In Section 6, I summarize and conclude. 1.2 TRAP Laws TRAP laws are a catch-all term to describe supply-side interventions in the market for abortion. These laws restrict where an abortion can be performed, under what conditions, and who can perform them. The treatment effects of TRAP laws come from the closure of clinics that cannot meet the requirements, either by shutting their doors or ceasing to provide abortion care. Several recent papers study the effects of TRAP laws in a national or state-specific setting. In Texas and Pennsylvania, studies find that these laws increase the travel distance to a provider, reduce abortion rates, and increase birth rates (Lindo and Pineda-Torres, 2021; Kelly, 2020; Fischer et al., 2018; Quast et al., 2017). The only national evidence regarding the effects of TRAP laws comes from Jones and Pineda-Torres (2021). The authors use a difference-in-differences methodology, exploiting state-level policy variation in TRAP laws over time, to study the effects of being exposed to a TRAP law as a teenager on fertility and future socioeconomic outcomes. The find that birth 5 rates increase for Black teens and that Black women exposed to TRAP laws as a teenager are less likely to attend and complete college. Because TRAP laws are a broad category of legislation with variation in their nature and stringency, classifying a state as “treated" by a TRAP law is a complicated endeavor. To meet this challenge, I consider two possible TRAP law codings from the literature. I begin with the first published longitudinal database on TRAP laws published by Austin and Harper (2019). In this paper, the authors catalog supply-side regulations on abortion providers from 1973 to 2017, dividing them into three broad categories: Ambulatory Surgical Center (ASC) Requirements ASC laws require that abortion facilities in the state adhere to the regulations placed on ambula- tory surgical centers. These often involve building codes and personnel guidelines. Some of these burdens include regulations on the width of doorways and hallways, access to medical equipment appropriate for an ASC that may not apply to abortion care, and staffing requirements. Meeting these requirements is often expensive, forcing providers to either purchase equipment and make renovations to the facility or shut down their abortion services. Admitting Privileges Some TRAP laws require a facility providing abortion services to have a clearly defined rela- tionship with a nearby hospital. One type of these is an admitting privilege requirement. These laws specify that one or all physicians providing abortion care must have admitting privileges at a hospital that often must be within a certain radius of the abortion facility. This burden may be difficult for rural abortion clinics without a hospital in the proximity radius defined by the TRAP law. Admitting privilege requirements were declared unconstitutional by the Supreme Court in 2016 in Whole Women’s Health v. Hellerstedt, but the laws were enforced for many years leading up to that decision. And, the Whole Women’s Health decision was recently superseded by Dobbs, meaning these laws are back on the table for state legislatures. Transfer Agreements Transfer agreement laws are another example of legislation that requires an explicit clinic- 6 hospital relationship. These laws specify that facilities providing abortion services must have a written agreement in place at a nearby hospital to transfer patients in the event of complications or an emergency. Transfer agreements are commonly a component of ASC requirements but can be part of separate legislation. Although transfer agreements are generally easier to acquire than admitting privileges, the burdens of the two laws are similar when there are proximity issues or public relations complications with the nearest hospital. In addition, I use the TRAP law coding from Jones and Pineda-Torres (2021). This coding is similar to Austin and Harper (2019) with a few notable differences. First, Jones and Pineda-Torres define slightly different TRAP law categories: transfer agreements, admitting privileges, building regulations, and distance requirements. Essentially, this coding more closely identifies features of the TRAP law by considering building regulations separately from ASC requirements and distance to the nearest hospital regulations that are not a part of transfer agreements and admitting privilege requirements. Also, the authors implement a stringency requirement for TRAP treatment. In some cases, TRAP laws that may fall into one of these four categories are not considered strong enough to classify a state as “treated." A primary example is laws that apply only to providers of second trimester abortions. Since only ten percent of abortions take place in the second trimester, these restrictions likely do not have large effects on abortion access. Table 1.1 summarizes the treatment timing for various TRAP laws by Austin and Harper (2019) and Jones and Pineda-Torres (2021). 1.3 Conceptual Framework To describe behaviors and outcomes under restrictive abortion environments, I expand on the predictions from a model of abortion and selection by Ananat et al. (2009). In their model, the authors consider decisions around pregnancy, abortion, and birth in the context of increased access to abortion care and make theoretical predictions about the effects of abortion access on infant health outcomes. I extend their logic by considering the effect of restricted access to abortion on maternal health outcomes. In this model, a person makes decisions about pregnancy and abortion sequentially. The decision to become pregnant depends on the expected benefits and costs of childbirth, and people choose to 7 Table 1.1 TRAP Law Treatment Timing Austin and Harper (2019) Jones and Pineda-Torres (2021) State ASC Transfer Admit Building Reg Distance Req Transfer Admit AL 1997 AK Pre-1990 Pre-1990 Pre-1990 AZ 2000 2000 2012 2000 AR 1999 CT Pre-1990 FL 2016 2016 GA Pre-1990 Pre-1990 Pre-1990 IL Pre-1990 Pre-1990 Pre-1990 IN Pre-1990 Pre-1990 2011 2006 2006 KY 1998 1998 LA 2014 2015 2014 MD 2012 2012 MI 1999 1999 2012 2012 MS 2005 2013 MO 2007 2007 Pre-1990 Pre-1990 2005 Pre-1990 NC 1994 ND 2014 2013 2013 NE 2001 2001 2001 OH 1999 1999 2015 2006 PA 2012 2012 2012 2012 Pre-1990 Pre-1990 RI Pre-1990 2002 SC 1996 1996 1996 1996 1996 SD 2006 2016 TN 2015 2015 2015 2015 2015 2012 TX 2004 2013 2009 2013 UT 1998 1998 2011 2011 2011 2011 VA 2012 2012 2013 WI Pre-1990 Pre-1990 Pre-1990 Notes: A description of the timing for each state treated under the policy codings from Austin and Harper (2019) and Jones and Pineda-Torres (2021). 8 get pregnant3 as long as the marginal benefit outweighs the marginal cost. Once pregnant, a person may receive new information regarding the benefits and costs to birth and can use this information in their decision to receive an abortion. The choice to receive an abortion depends again on the marginal benefits and marginal cost for the procedure. I assume (as in the original model) that children’s outcomes are directly related to the benefits of giving birth, where births that result from wanted pregnancies have better outcomes than births from unwanted pregnancies. Based on the evidence that people seeking abortion report that a concern for their health is a component of their reasoning, I make an additional assumption not explicitly specified in Ananat et al. (2009) that the health of the pregnant person is directly linked to the payoff from giving birth (Foster et al., 2018). Then, abortion access potentially affects maternal and infant health outcomes by entering the decision both to become pregnant and to receive an abortion conditional on pregnancy. In a restrictive abortion environment, fewer people become pregnant because the risk of receiving negative information following the pregnancy is more costly given the reduced access to abortion. By assumption, those on this margin expect with higher probability that the birth will involve some risk to their individual health status or the health of the infant. By preventing these at-risk births through the channel of reduced pregnancy, abortion restrictions will improve average maternal and infant outcomes of births, all else equal. In addition, restricted access to abortion affects the abortion decision among people who become pregnant by increasing the marginal cost of the procedure. This additional cost increases the number of births, and I follow the logic of the original model and refer to these new births that result from restricted abortion access as “marginal births.” Because of the assumed direct relationship between health expectations and the payoff of birth, the marginal births have lower-than-average outcomes. So, the inclusion of these marginal births will decrease the average maternal and infant outcomes of births, all else equal. Consider the potential effect of restricted abortion access on pregnancy-associated hypertension 3 Given evidence that nearly half of all pregnancies in the US are unintended, it may seem unusual to consider the first stage in this model to be the decision to become pregnant. It is worth noting that the logic and conclusions of the theoretical model are identical if the first stage is instead modeled as a decision around contraceptive and sexual behavior with various probabilities of pregnancy. 9 presented in Figure 1.1a. Let 𝑋0 and 𝑌0 be the number of births and the number of cases of pregnancy-associated hypertension respectively, assuming no change in abortion access. Then, the 𝑌0 counterfactual rate of hypertension (denoted Rate of Hypertension0 ) is equivalent to 𝑋0 . Suppose that an abortion restriction is passed, and further assume that people do not include the extra cost to abortion in their pregnancy decision. So, in this scenario, there are no pregnancies avoided due to the increased marginal cost of an abortion, and the presence of marginal births drives maternal health effects entirely. Following the restriction, the number of births increases to 𝑋1 and the number of hypertension cases to 𝑌1 . The new rate of hypertension under restricted abortion access 𝑌1 𝑌1 −𝑌0 is measured 𝑋1 and depends on the rate of hypertension among marginal births, 𝑋1 −𝑋0 . In Figure 1.1b, consider the same scenario but allow people to avoid pregnancy following a restrictive abortion law. Then, two competing effects on the number of births are included in the model. First, the number of births decreases from 𝑋0 to 𝑋−1 and the cases of hypertension decreases from 𝑌0 to 𝑌−1 as higher-risk individuals avoid pregnancy due to the high cost of abortion. Then, conditional on pregnancy, more people give birth as a result of the abortion restriction, increasing the number of births from 𝑋−1 to 𝑋1 and the number of hypertension cases from 𝑌−1 to 𝑌1 . The rate 𝑌1 −𝑌−1 of hypertension among the marginal births is 𝑋1 −𝑋 −1 . In this paper, I identify the changes in the average rates of adverse maternal and infant health outcomes following a restrictive abortion policy. So, coefficients that I estimate represent (Rate of Hypertension1 - Rate of Hypertension0 ). While I do not estimate the rates of adverse health outcomes among the marginal births, my estimates are informative of their direction and magnitude. Observing an increase in the rate of hypertension following a restrictive abortion law implies that the rate of hypertension among marginal births is higher than Rate of Hypertension0 . Outside of this observation, I do not make further comments on the rate of adverse health outcomes among marginal births. Using only birth records, this rate can not be calculated or bounded in any way that is informative. Note that the scenarios pictures in Figure 1.1a and Figure 1.1b involve the same average treatment effect of the policy on the rate of hypertension while having very different rates among the marginal births. 10 Figure 1.1 Visual Model of Treatment Effects (a) A Model of Hypertension and Marginal Births (b) A Model of Hypertension, Marginal Births, and Avoided Pregnancies 11 The most notable feature of this model of abortion and selection is that health effects from abortion access are not dependent on observing a change in the number of births. Because of the competing responses of pregnancy avoidance and the increased probability of birth conditional on pregnancy, health effects may be explained by the changing composition of people giving birth in states with restricted access to abortion with or without evidence that the number of births changes in response to an abortion policy. 1.4 TRAP Laws and Pregnancy/Birth Outcomes 1.4.1 Data To identify the effect of these abortion policies on state-level rates of adverse health outcomes among people giving birth and infants, I use restricted All-County Natality files provided by the National Center for Health Statistics (NCHS, 2022). The files contain the universe of birth records in the United States from 1990 to 2017. Birth records include a rich set of demographic characteristics, indicators for the health status of the birthing person, indicators for adverse health outcomes associated with pregnancy, and various characteristics of the health of the infant at birth. Table 1.2 presents summary statistics for these data. Over the time period, the average birthing person is 27.41 years old. Half of all birthing people are white, and 80% have at least a high school diploma. Average gestational age for infants at birth is 38.95 weeks, and average birthweight is almost 3300 grams. Eight percent of infants born are low birthweight and twelve percent are born premature. Beginning in 2003, US states adopted the revised standard birth certificate differentially over time. To address any potential confounding associated with this rollout adoption, I consider only health outcomes measures for birthing people and infants that are reported consistently across both the revised and unrevised certificate. The outcomes are: pregnancy-associated hypertension, chronic hypertension, diabetes4, infant birthweight, gestational age at birth, and five-minute AP- GAR score. The selected maternal health outcomes are relatively rare: five percent of births involve 4 The 2003 revised certificate makes a distinction between diabetes and gestational diabetes. Even though gestational diabetes info is only available in the revised certificate, I include that health outcome in my analysis for comparison. 12 Table 1.2 Summary Statistics - NCHS Number of Variable Mean S.D. Observations Mother’s Age (years) 27.41 6.09 112,863,754 Mother’s Race 111,674,714 Non-Hispanic White 0.50 Non-Hispanic Black 0.16 Hispanic 0.28 Other 0.05 Mother’s Education 81,749,166 0-8 years 0.06 9-11 years 0.15 12 years 0.32 13-15 years 0.23 16+ years 0.25 Gestational Age (weeks) 38.95 4.07 112,148,648 Premature Birth (<37 weeks) 0.12 0.32 112,148,648 Birthweight (grams) 3297.66 618.70 112,803,275 Low Birthweight (<2500 grams) 0.08 0.27 112,803,275 Five Minute Apgar Score 8.87 0.80 97,742,540 Number of Prenatal Visits 11.14 2.07 109,214,623 Chronic Hypertension 0.01 0.10 111,676,723 Pregnancy-Associated Hypertension 0.04 0.20 111,676,723 Diabetes 0.04 0.20 111,167,704 Gestational Diabetes 0.05 0.22 41,005,843 gestational diabetes, four percent involve pregnancy-associated hypertension and diabetes, and only one percent involve chronic hypertension. Pregnancy-associated and chronic hypertension are differentiated by the timing of diagnosis. Hypertension diagnosed prior to 20 weeks gestation is denoted chronic hypertension, while hy- pertension diagnosed after 20 weeks gestation is pregnancy-associated hypertension. An APGAR score is a quick summary measure of infant health after birth. Infant health is ranked in five categories (Appearance Pulse Grimace Activity and Respiration) on a scale from 0 to 2. So, these scores range from 0 to 10, with higher scores generally indicating healthier infants. Figure 1.2 provides a summary of the data over time by comparing trends in states that never receive treatment and states that pass at least one TRAP law over the study period. If TRAP laws are associated with higher rates of adverse health outcomes, then I expect to observe a widening gap between eventually-treated and never-treated states over time as more TRAP laws are passed. This 13 trend is present in the rates of hypertensive disorders of pregnancy. The gap in the rate of chronic hypertension between treated and untreated states begins to widen in the early 2000s, and widens considerably for the rest of the study period — rates were nearly indistinguishable in 2000, but by 2017 treated states have a 33% higher rate of chronic hypertension. For pregnancy-associated hypertension, the gap between treated and untreated states widens in the mid-2000s but narrows toward the end of the period. Infant health outcomes premature birth and low birthweight have a significant gap throughout, but the gap widens by the end of the period. Treated states have a 10% higher rate of premature birth in 1990 and a 20% higher rate in 2017. A similar pattern exists for the rates of infant low birthweight. For maternal metabolic outcomes diabetes and gestational diabetes, the raw trends do not indicate a strong association with TRAP laws. 1.4.2 Estimation To measure effects from abortion access on outcomes related to pregnancy and birth, I exploit the variation in state-level policies over time. So, I estimate the average treatment effect on the treated (ATT) using difference-in-differences methods. I begin with the standard two-way fixed effects (TWFE) specification for analysis: 𝑌𝑖𝑠𝑡 = 𝛼𝑠 + 𝛿𝑡 + 𝛽𝑝 𝑠𝑡 + 𝜖𝑖𝑠𝑡 (1) where 𝑌𝑖𝑠𝑡 is the outcome of interest, 𝛼𝑠 and 𝛿𝑡 are state and time fixed effects respectively, and 𝑝 𝑠𝑡 is a simple policy indicator taking value 1 if a state 𝑠 has the policy being considered in year 𝑡 and 0 otherwise. In an ideal setting, coefficient 𝛽 identifies the ATT. TWFE under staggered intervention timing imposes a homogeneity assumption. This assumption requires that treatment effects are homogeneous across units/time, otherwise the estimate of the ATT is biased by the “forbidden comparison" between newly treated units and previously treated units (Goodman- Bacon, 2021). The heavily staggered nature of treatment in Table 1.1 demonstrates the importance of considering the bias introduced by a violated homogeneity assumption. States likely experience heterogeneous responses to restrictive abortion legislation, and treat- ment effects are likely larger closer to the time of the policy change, when the “shock" occurs. 14 Figure 1.2 Abortion Restrictions and Birth Outcomes, 1990-2017 15 If this is the case, TWFE estimates for average treatment effects are attenuated. For this reason, the preferred specification is the Borusyak, Jaravel, and Spiess (2021) imputation estimator (BJS), which relaxes the homogeneity assumption. The BJS estimation of the ATT is computed in a three-step process. In the first step, fixed effects are estimated according to equation (1) using only the set of untreated observations to impute potential outcomes 𝑌𝑖𝑠𝑡 (0) = 𝛼ˆ 𝑠 + 𝛿ˆ𝑡 . I delay treatment timing by a year from the policy change, because these likely include the birth records of those who first responded to the TRAP law. Next, treatment effect 𝜏𝑖𝑠𝑡 is defined to be the difference between observed and potential outcomes in a treated state 𝑠 at time 𝑡. Finally, treatment effects are aggregated together according to weights 𝑤 𝑖𝑠𝑡 . In my context, all treatment effects are weighted equally such that 𝜏𝑤 is the simple average. 𝜏𝑖𝑠𝑡 = 𝐸 [𝑌𝑖𝑠𝑡 − 𝑌𝑖𝑠𝑡 (0)] (2) ∑︁ 𝜏𝑤 = 𝑤 𝑖𝑠𝑡 𝜏𝑖𝑠𝑡 (3) 𝑖𝑠𝑡 Although the BJS estimator is robust to arbitrary heterogeneity across treated units and time, there are still a number of potential challenges to the identification of true treatment effects. The first is that while state fixed effects allow for static differences across states, there may be a concern that states in the treatment and control group differ in time varying ways that affect their trends in adverse birth outcomes and chronic conditions. To address this, I estimate and test for parallel pre-trends using the method outlined in Borusyak, Jaravel, and Spiess (2021). Here, a separate OLS regression similar to a traditional event study is performed using untreated observations only: 5 ∑︁ 𝑌𝑖𝑠𝑡 = 𝛼𝑠 + 𝛿𝑡 + 𝛾 𝑘 1(𝑡𝑖𝑚𝑖𝑛𝑔𝑠 − 𝑡 = 𝑘) + 𝜖𝑖𝑠𝑡 (4) 𝑘=1 where 𝑡𝑖𝑚𝑖𝑛𝑔𝑠 indicates the year that state 𝑠 was treated by a policy change. Coefficients from this regression can be plotted alongside the previously estimated set of treatment effects in order to present a picture that can be interpreted in a similar manner to an event study. The parallel trends asumption is evaluated by estimating 𝛾ˆ 𝑘 and testing 𝛾 = 0 using an F test. 16 Table 1.3 BJS Parallel Trends Assumption F Test F-stat p-value df PA Hypertension 1.258 0.299 43 Chronic Hypertension 0.956 0.455 43 Diabetes 5.269 0.001 43 Gestational Diabetes 3.394 0.013 37 Low Birthweight 1.398 0.244 43 Premature Birth 1.678 0.160 43 APGAR Score 1.384 0.249 43 Notes: Results from testing 𝛾 = 0 from equation (4) by an F test. Figure 1.3 and Table 1.3 demonstrate that for most pregnancy and birth outcomes, the parallel trends assumption for TRAP laws is satisfied. Exceptions are the metabolic outcomes, diabetes and gestational diabetes. These outcomes are only differentiated after the 2003 revision to the standard birth certificate, and the parallel trends violation could be a product of the staggered adoption of the revised certificate. I present results for these outcomes in the next section, but I consider the treatment effect estimates uninformative because of this parallel trend violation. A second identification challenge is the passage of concurrent reproductive health policies in treatment and control states. I check to see if results are robust to the inclusion of controls for various reproductive health and family planning state-level policies compiled by Myers and Ladd (2020) and Myers (2021b). I augment equation (1) to include controls for the following indicators: access to over-the-counter emergency contraception, Medicaid expansions for pregnant people, an insurance mandate for private providers to cover prescription contraception, and a one-trip and two-trip mandatory waiting period for abortion services. Results, presented in the next section, indicate that effects are robust to the inclusion of these policies in the specification. Because TRAP laws are heavily sorted into states in the South and Midwest, there may be a concern that effects are confounded by concurrent regional differences in maternal and infant health trends. To assuage this concern, I repeat the difference-in-differences analysis with the inclusion of region-year fixed effects. Results, presented in the appendix, suggest that estimates are robust to the inclusion of these regional effects. 17 Figure 1.3 BJS Event Studies - TRAP Laws (Vital Stats) 18 Table 1.4 Difference-in-Differences Results (Vital Statistics) TWFE BJS A&H (2019) A&H (2019) A&H (2019) J&P (2021) w/policy controls (1) (2) (3) (4) PA Hypertension 0.0021 0.0046∗∗∗ 0.0050∗∗∗ 0.0033∗∗∗ (mean = 0.0403) [0.002] [0.001] [0.001] [0.001] Chronic Hypertension 0.0010 0.0016∗∗ 0.0010 0.0023∗∗∗ (mean = 0.0105) [0.001] [0.001] [0.001] [0.001] Diabetes −0.0032∗ -0.0018 -0.0007 -0.0008 (mean = 0.0403) [0.002] [0.002] [0.002] [0.001] Gestational Diabetes −0.0040∗ −0.0146∗∗∗ −0.0094∗∗∗ −0.0050∗∗∗ (mean = 0.0504) [0.002] [0.002] [0.0003] [0.001] Low Birthweight 0.0013 0.0004 0.0006 0.0010∗ (mean = 0.0778) [0.001] [0.001] [0.001] [0.0005] Premature Birth 0.0019 0.0014 0.0024∗ 0.0043∗∗ (mean = 0.1159) [0.002] [0.002] [0.001] [0.002] 5-Minute APGAR Score 0.0085 0.0316∗∗ 0.0649∗∗∗ 0.0697∗∗ (mean = 8.87) [0.016] [0.013] [0.017] [0.009] Notes: Results from TWFE and BJS difference-in-differences analysis. Column (2) uses the TRAP policy coding from Austin and Harper (2019), Column (3) uses the Austin and Harper (2019) coding along with a set of reproductive health policy controls, and Column (4) uses the alternative policy coding from Jones and Pineda-Torres (2021). In each specification, standard erros are clustered at the state level. ∗ 𝑝 < 0.1, ∗∗ 𝑝 < 0.05, ∗∗∗ 𝑝 < 0.01. 1.4.3 Results Difference-in-Differences Table 1.4 presents results from the difference-in-differences analysis with various specifications. Column 1 presents the TWFE results for comparison, and columns 2-4 present the BJS results for the Austin and Harper (2019) coding, the Jones and Pineda-Torres (2021) coding, and the inclusion of reproductive health policy controls. Treatment effect estimates are meaningfully different between TWFE and BJS methods, suggesting that treatment is likely not homogeneous across units/time. The primary specification the BJS method using the Austin and Harper (2019) TRAP treatment designation presented in column (2) of Table 1.4. I use this policy coding as the primary 19 specification because it defines TRAP treatment more broadly without the stringency requirement of Jones and Pineda-Torres (2021), and therefore it should produce more conservative estimates of the average treatment effects. With the exception of the APGAR score, outcome variables are binary indicators such that coefficients can be interpreted as percentage point changes in the rate of adverse health outcomes in a state following TRAP policy implementation. Coefficients on the APGAR score represent raw changes in the five-minute APGAR score ranging from zero to ten. For reference, I provide the sample mean of the health outcomes under their label on the left side of the table. So, the coefficient of pregnancy-associated hypertension in column (2) of 0.0046 means that the rate of pregnancy- associated hypertension among birthing people in states that passed a TRAP law increased by 0.46 percentage points on average following the policy change, and this is a 11.5% increase from the sample mean of 0.04. Results from Table 1.4 indicate that TRAP laws increase state-level rates of hypertensive disorders of pregnancy, increasing the rate of pregnancy-associated hypertension by 11.5% and the rate of chronic hypertension by 16% and establishing a causal link between abortion access and the maternal health crisis in the United States. These results are robust to the inclusion of reproductive health policy controls in column (3) and an alternative TRAP policy coding from column (4). There is not enough evidence to suggest that TRAP laws increase the risk of premature birth and low birthweight among infants — coefficients are positive but small and not statistically significant in the primary specification. Effects on premature birth are only meaningfully larger and statistically significant using the policy coding from Jones and Pineda-Torres (2021) in column (4). The counterintuitive negative effect of TRAP laws on metabolic outcomes is likely a product of the violated parallel trend assumption. In Figure 1.3, it appears that treatment effects for diabetes and gestational diabetes increase following a TRAP law, but the differential trends in the pre- treatment period result in coefficients that are negative. I argue that this parallel trend violation is a result of the staggered adoption of the revised birth certificate. If the timing of adoption of the revised certificate is correlated with lower rates of adverse maternal health outcomes, this may 20 explain the differential trend leading up to the passage of a TRAP law. Since all other outcomes are reported consistently across the revised and unrevised birth certificate, the issue is isolated and the violation of the parallel trends assumption for metabolic outcomes does not limit the credibility of the research design for other results. In addition, I address this issue later by measuring the effect of travel distance to an abortion provider at the county level using a research design that is not confounded by the adoption of the revised certificate. The coefficients in Table 1.4 also suggest that infant APGAR scores rise as a result of TRAP laws, implying that the laws result in healthier infants being born on average. While this result is theoretically possible, it stands in contrast to the maternal health results. It would be unusual to observe a policy decrease the average maternal health while increasing average infant health because maternal and infant health at birth are intricately connected. One possible explanation for the positive coefficients on the APGAR score is the limited variance of the scores within the data. While scores are reported on a 0-10 scale, 82% of infants in the sample have an APGAR score of 9. This low variance contributes to a low standard error of my estimate, leading to a coefficient that is statistically significant but not economically significant — a 0.0316 increase in APGAR score is 0.36 percent increase from the sample mean. Heterogeneity and Health Disparities Much of the literature surrounding abortion access establishes that the effects of abortion laws are often heterogeneous across race/socioeconomic status (Jones and Pineda-Torres, 2021; Myers, 2021a; Kelly, 2020; Clarke and Mülrad, 2021; Farin et al., 2021). To determine if there exists significant heterogeneity in the burdens of TRAP laws, I estimate effects by the birthing person’s race and education in Table 1.5. For nearly5 all outcomes, treatment effects are larger for Black birthing people at equivalent levels of education. This indicates that Black birthing people likely experience a larger burden from the passage of a TRAP law, consistent with existing evidence in the literature. For people with a high school diploma, TRAP laws increase the rate of chronic hypertension for Black birthing 5 The singular exception is the effect of TRAP laws on pregnancy associated hypertension among those with some college education. Here the treatment effect is slightly larger for white birthing people. 21 Table 1.5 Diff-in-Diff by Subgroup PA Hypertension Chronic Hypertension Premature Birth Low Birthwt White, college 0.0050∗∗∗ 0.0019∗∗ 0.0039∗∗ 0.0027∗∗ (n = 36,328,911) [0.0012] [0.0010] [0.0017] [0.0011] White, HS 0.0036∗∗ 0.0018∗ 0.0036 0.0014 (n = 12,078,283) [0.0017] [0.0009] [0.0022] [0.0014] White, 30 miles following HB2. This definition of treatment results in 117 treated counties and 137 control counties. Figure 3.3 indicates that the incidence of LARC and vasectomies rose substantially during the study period in control counties. This may be indicative of general trends in contraceptive behavior within Texas and could also be associated with the policy change. If people respond to expectations of limited abortion access, they may substitute toward long-acting forms of contraception even if they do not experience the loss of an abortion provider as a result of the TRAP law. We do not consider this potential bias overly concerning, as it attenuates our treatment effects and results in plausibly conservative estimates of the effect of HB2 on contraceptive behavior in treated counties. 67 Treated counties experience a sharper increase in the number of IUD insertions leading up to the time of the policy change. The trend peaks in the first few months following the introduction and passage of HB2 and then declines back to pre-treatment levels roughly one year after. Contraceptive implant insertions also increase in treated counties around the time of the policy change, but at a lower rate than in the control group. This may suggest that individuals responding to the policy change are more likely to seek an IUD rather than a contraceptive implant. Interestingly, the incidence of vasectomy is stable and near zero in treated counties across the study period even though the rate of vasectomies steadily increases in control counties. Because vasectomies do not appear to be a common method of contraception in treated counties, the policy change may not be effective at influencing behavior on this margin. In the next section, we formalize analysis of the descriptive trends between the treatment and control group using an event-study design. 3.4 Methods and Results We rely on an event-study design to estimate the effects of restrictive abortion policies on LARC and vasectomy take-up. Contentious policy proposals, such as those governing access to abortion, often receive media attention before formal bills are debated in legislative houses. Forward-looking agents may use their perception of expected future abortion access in their contraceptive decisions. The dynamic specification in Equation (1) permits the observation of these anticipation effects. Because the data contain discrete counts of LARC and vasectomy incidence occasionally equal to zero, we employ a Poisson model that takes the form: 𝐸 [𝑌𝑐𝑡 |𝛼𝑐 , 𝛿𝑡 , 𝛽𝑥 𝑐𝑡 , Σ9𝑘=−9𝜆 𝑘 1(𝑡 = 𝑘)] = 𝑒𝑥 𝑝(𝛼𝑐 + 𝛿𝑡 + 𝛽𝑥 𝑐𝑡 + Σ9𝑘=−9𝜆 𝑘 1(𝑡 = 𝑘)) (1) where 𝑌𝑐𝑡 is the number of IUDs, contraceptive implants, or vasectomies in county 𝑐 at quarter- year 𝑡, 𝛼𝑐 and 𝛿𝑡 are county and quarter-year fixed effects respectively. Here, 𝑘 indexes the coefficients 𝜆 according to the time relative to the original introduction of HB2 as Senate Bill 5 in 2013 quarter 2. We include controls 𝑥 𝑐𝑡 for the total number of outpatient discharge records for county 𝑐 in quarter-year 𝑡 to account for changing overall healthcare utilization across counties over 68 Figure 3.4 Poisson Event Studies time. Figure 3.4 presents the Poisson event-study plots of 𝜆 𝑘 for each contraceptive method along with the 90% confidence intervals. For IUD insertions, the event plot reveals that trends are parallel between treatment and control counties leading up to three quarters prior to the introduction of HB2. In the two quarters leading up to HB2, IUD insertions increased significantly in treated counties. Notably, this time of anticipation effects occurs immediately following the 2012 state elections in Texas and during the eight-third legislative session, where multiple restrictive abortion bills are introduced that ultimately fail. At this time, news articles circulated around Texas detailing the strong anti-abortion stance of the legislature and the governor, which may contribute to the increases in IUDs prior to the introduction of HB2. Treated counties have a higher rate of IUD insertion until one year following the policy change, at which point trends return close to pre- 69 treatment levels. Ultimately, IUD insertions increase by an average of 0.6163 cases per county in quarters immediately surrounding the introduction of the policy change. This value is small in magnitude but meaningful. The mean number of IUD insertions in the entire outpatient data is 1.59 per county-quarter. Among counties with any IUD insertion, the mean is 9.62 insertions per quarter. Results in Figure 3.4 for contraceptive implants and vasectomies do not indicate the same changes in contraception behavior. For contraceptive implants, the parallel trend assumption may be in question due to the large outlier in the Poisson coefficient 𝜆 in late 2011, and the coefficients are roughly zero otherwise throughout the study period. In the event plot for vasectomies, trends are parallel leading up to the time of the policy, but there is not strong evidence of an effect for treated counties after the introduction of HB2. The results do indicate a small negative effect in 2014, and this may be explained by the stable trend in vasectomies in treated counties compared to the general increase among the control group in Figure 3.3. One limitation of our data is that we can only see LARC insertions and vasectomies in hospital- based outpatient and ASC settings. Therefore, we are concerned that the observed trends are mechanically driven by changes in reproductive healthcare in Texas during this time period. In 2012, Texas made changes to its Women’s Health Program (WHP) to exclude sexual health clinics that are affiliated with or make referrals to abortion providers from receiving Medicaid reimbursement. In addition, many abortion clinics that also provide family planning services may have been closed due to the implementation of HB2 in mid-2013. Both policies could cause people to switch from care in independent clinics toward hospital-owned facilities, resulting in a false conclusion that take-up of these contraceptive methods increased in the state overall. We make two efforts to explore the possibility that these mechanisms confound our estimates. 3.4.1 Medicaid Recipients The decision to exclude family planning clinics from receiving reimbursement from the WHP could drive Medicaid recipients from independent family planning clinics (such as Planned Par- 3 This value comes from transformation of the Poisson model coefficients where log(Yk | policy) - log(Yk | no policy) = 𝜆 𝑘 . 70 Figure 3.5 Trends and Event Study, Non-Medicaid IUD Insertions enthood affiliates) toward hospital-based outpatient facilities. If this facility shift occurs primarily in our group of counties treated by HB2, it would result in increases in LARC in our data that we falsely attribute to restricted abortion access. Fischer et al. (2018) show that there is little correlation between increased distance to an abortion provider following HB2 and restricted access to publicly funded family planning clinics after the change to the WHP. So, we do not expect that the effects we observe in Figure 3.4 are heavily driven by funding restrictions. To be sure, we repeat the event study analysis for IUD insertions in Equation (1) excluding Medicaid recipients from our sample. Figure 3.5 shows that excluding Medicaid recipients does not fundamentally shift the trends between treatment and control counties or the event plot, therefore providing evidence that Medicaid recipients are not driving changes in IUD insertion around the timing of HB2. This supports a conclusion that the changes to the Texas Women’s Health Program are unlikely to cause the increases in IUD insertions we observe for counties that experience increased distance to an abortion provider following the TRAP law. 3.4.2 Other Services Policies like HB2 that target abortion clinics may lead to consequences for other family planning services. When abortion clinics close, access to all other services provided by the clinic also decreases. In the Myers (2021b) data describing the distance to an abortion provider, “closures" 71 Figure 3.6 Trends in General Gynecologist Visits in Texas indicate facilities that shut down or simply stopped providing abortion care. Facilities that continue to operate without providing abortions would not influence the access to contraceptive care for residents of that county. On the other hand, complete facility closures may result in a mechanical increase in LARC incidence when the population served by that facility seeks contraceptive care elsewhere. While this response is a consequence of the TRAP law, it is not necessarily related to abortion access. Therefore, this behavior may be confounding our central research question. We explore the possibility that people in areas experiencing facility closures shift their care to a hospital-owned facility or ASC in our data by observing trends in other reproductive health services unrelated to contraception. In Figure 3.6, we plot the average trend and the trends by treatment status for general gynecologist visits over the study period. If people are making a fundamental shift in their facility for care, we would expect to see corresponding increases in visits to the gynecologist after clinic closures due to HB2, concentrated in treated counties. Trends demonstrate that the overall incidence of general gynecologist visits did increase over the study period, but this increase occurs almost exclusively in the control group. Among treated counties, the incidence of gynecologist visits is stable. So, it does not appear that there is evidence to suggest that residents of counties affected by HB2 systematically shift to receive healthcare in hospital-owned an ASC facilities. 72 3.5 Conclusion In this paper, we measure the effect of restricted abortion access in Texas on the incidence of hospital-based long-acting reversible contraception and vasectomies. For identification, we exploit the within-state geographic variation in the distance to a nearest abortion provider following the 2013 passage of House Bill 2, a TRAP law that shut down over half of all abortion clinics in Texas. We find that counties with an increase in their travel distance to an abortion provider greater than 30 miles experience an average increase of 0.616 IUD insertions per quarter around the time of the policy change. Overall, this amounts to roughly 432 additional IUD insertions during our sample period, representing 5.15% of total hospital-based IUD cases between 2011 and 2015. We do not find evidence that counties affected by HB2 experience increases in the take-up of contraceptive implants or vasectomies. Our data on outpatient procedures includes only discharge records for LARC and vasectomies that occurred in a hospital-owned facility or ambulatory surgical center. As such, our results may be biased by changes in the location of care resulting from these policies. However, we do not believe this is the case and we make efforts to argue that the public policy environment in Texas did not significantly shift the location of care in the state from independent clinics toward hospital- owned facilities. Our results are robust to the exclusion of Medicaid recipients from the sample — a population that experienced reduced access to contraceptive care in publicly funded clinics after changes to the reimbursement structure for the state Women’s Health Program in 2012. In addition, we do not find evidence that counties affected by the abortion clinic closures following HB2 increased the number of hospital-based general gynecologist visits, supporting a conclusion that these counties did not make large changes in their location of reproductive healthcare during the study period. Ultimately, we find that increasing the cost of abortion through travel distance increases the demand for IUD insertions. To our knowledge, our study is the first in the United States to provide empirical evidence supporting the hypothesis that abortion and IUDs are substitutes. We also explore the potential for this substitutability to extend to vasectomies, a long-acting contraception 73 method used by people without the capacity to become pregnant themselves. We find that the incidence of vasectomies does not significantly increase in counties treated by the policy change, suggesting that the additional cost of abortion may not pass through to partners. Our study has a few key limitations. When presented with new information, people may respond to changes in their expectation of abortion access in the future, regardless of realized restrictions in access. In this way, people across the entire state of Texas may be influenced by the media surrounding abortion access during the eighty-third legislative session, and therefore defining a treatment group to only include counties affected by abortion clinic closures may be too narrow. So, we consider our treatment effects to be conservative estimates of changing contraceptive behavior. Additionally, we only measure the effects of abortion access on a subset of contraceptive options. While 65.3% of US reproductive-age women report using contraception, only 10.4% report using long-acting reversible contraception (Daniels and Abma, 2020). LARC is the third most common contraceptive method among women, behind sterilization (18.1%) and the pill (14%). More research is necessary to determine the influence of abortion access on the take-up of contraception, broadly. Finally, our study relies on variation in abortion access in a single US state. 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American Journal of Public Health. apalike 80 APPENDIX A CHAPTER 1 APPENDIX Supplemental Analysis Diff-in-Diff with Region-Year Fixed Effects To ensure that treatment effects are not driven by concurrent regional changes in rates of adverse maternal and infant health outcomes, I separate US states into four regions (Northeast, South, Midwest, West) according to the Census Bureau regions and divisions of the United States, and I repeat the BJS difference-in-differences analysis described in Table 1.4 with the inclusion of region-year fixed effects. So, the imputation step is now: 𝑌𝑖𝑠𝑡 (0) = 𝛼ˆ 𝑠 + 𝛿ˆ𝑡 + 𝛾ˆ𝑟∗𝑡 where 𝛾ˆ𝑟∗𝑡 represents the region-year fixed effects. Average treatment effects are then calculated according to equation (2) and (3). There are no material changes to the difference-in-difference estimates and interpretations after including these additional fixed effects. Figure A1 and Table A1 present the BJS event study graphs and results from the F test described in Section 4. Table A2 presents the ATT estimates from the BJS difference-in-differences specification using the Austin and Harper (2019) policy coding. Table A.1 BJS Parallel Trends Assumption F Test (Regional FEs Included) F-stat p-value df PA Hypertension 1.780 0.138 42 Chronic Hypertension 2.000 0.098 42 Diabetes 1.514 0.206 42 Gestational Diabetes 2.911 0.026 36 Low Birthweight 0.847 0.524 42 Premature Birth 1.225 0.314 42 APGAR Score 1.251 0.303 42 81 Figure A.1 BJS Event Studies - TRAP Laws (Region FEs Included) 82 Table A.2 BJS Difference-in-Differences Results (Regional FEs Included) PA Chronic Gestational Premature Low APGAR Diabetes Hypertension Hypertension Diabetes Birth Birthweight Score TRAP Law 0.0042∗∗∗ 0.0010 -0.0008 −0.0097∗∗∗ 0.0013 0.0013∗ 0.0487∗∗∗ [0.001] [0.001] [0.002] [0.0005] [0.001] [0.001] [0.012] N 95654017 95654017 95654017 30995668 96695485 96695485 81645928 83 APPENDIX B CHAPTER 2 APPENDIX Data Sources Demographics Surveillance, Epidemiology, and End Results (SEER) Program Populations (1969-2018), Na- tional Cancer Institute, DCCPS, Surveillance Research Program, released December 2019. CDC Abortion Data Koonin LM, Smith JC, Strauss MRLT Abortion Surveillance – United States, 1995. MMWR Surveillance Summ 1998;47(SS-2):31-68. Koonin LM, Strauss LT, Chrisman CE et al. Abortion Surveillance – United States, 1996. MMWR Surveillance Summ 1999;48(SS04):1-42 Koonin LM, Strauss LT, Chrisman CE et al. Abortion Surveillance – United States, 1997. MMWR Surveillance Summ 2000;49(SS11):1-44 Herndon J, Strauss LT, Whitehead S et al. Abortion Surveillance – United States, 1998. MMWR Surveillance Summ 2002;51(SS03):1-32 Elam-Evans LD, Strauss LT, Herndon J et al. Abortion Surveillance – United States, 1999. MMWR Surveillance Summ 2002;51(SS09):1-28 Elam-Evans LD, Strauss LT, Herndon J et al. Abortion Surveillance – United States 2000. MMWR Surveillance Summ 2003;52(SS12):1-32 Strauss LT, Herndon J, Chang J et al. Abortion Surveillance – United States 2001. MMWR Surveillance Summ 2004;53(SS09):1-32 Strauss LT, Herndon J, Chang J et al. Abortion Surveillance – United States 2002. MMWR Surveillance Summ 2005;54(SS07):1-31 Strauss LT, Gamble SB, Parker WY et al. Abortion Surveillance – United States 2003. MMWR Surveillance Summ 2006;55(SS11):1-32 Strauss LT, Gamble SB, Parker WY et al. Abortion Surveillance – United States 2004. MMWR 84 Surveillance Summ 2007;56(SS09):1-33 Gamble SB, Strauss LT, Parker WY et al. Abortion Surveillance – United States 2005. MMWR Surveillance Summ 2008;57(SS13):1-32 Pazol K, Gamble SB, Parker WY et al. Abortion Surveillance – United States 2006. MMWR Surveillance Summ 2009;58(SS08):1-35 Pazol K, Zane SB, Parker WY et al. Abortion Surveillance – United States 2007. MMWR Surveillance Summ 2011;60(SS01):1-39 Pazol K, Zane SB, Parker WY et al. Abortion Surveillance – United States 2008. MMWR Surveillance Summ 2011;60(SS15):1-41 Pazol K, Creanga AA, Zane SB et al. Abortion Surveillance – United States 2009. MMWR Surveillance Summ 2012;61(SS08):1-44 Pazol K, Creanga AA, Burley KD et al. Abortion Surveillance – United States 2010. MMWR Surveillance Summ 2013;62(SS08):1-44 Pazol K, Creanga AA, Burley KD et al. Abortion Surveillance – United States 2011. MMWR Surveillance Summ 2014;63(SS11):1-41 Pazol K, Creanga AA, Jamieson DJ Abortion Surveillance – United States 2012. MMWR Surveillance Summ 2015;64(SS10):1-40 Jatlaoui TC, Ewing A, Mandel MG et al. Abortion Surveillance – United States 2013. MMWR Surveillance Summ 2016;65(SS12):1-44 Jatlaoui TC, Shah J, Mandel MG et al. Abortion Surveillance – United States 2014. MMWR Surveillance Summ 2017;66(SS25):1-48 Jatlaoui TC, Boutot ME, Mandel MG et al. Abortion Surveillance – United States 2015. MMWR Surveillance Summ 2018;67(SS13):1-45 Jatlaoui TC, Eckhaus L, Mandel MG et al. Abortion Surveillance – United States 2016. MMWR Surveillance Summ 2019;68(SS11):1-41 ITOP Data Arkansas Department of Health Statistics. (2000-2016) Induced Abortions. 85 Georgia Department of Public Health Online Analytical Statistical Information System. (1995- 2016). Induced Termination of Pregnancy. https://oasis.state.ga.us/oasis/webquery/qryITOP.aspx Iowa Department of Health. (2005-2016). Vital Statistics: Termination of Pregnancy Data. https://idph.iowa.gov/health-statistics/data Minnesota Department of Health. (2009-2016). Reports to the Legislature: Induced Abortions in Minnesota. https://www.health.state.mn.us/data/mchs/pubs/abrpt/abrpt.html South Dakota De- partment of Health. (2008-2016). Vital Statistics: Induced Abortion. https://doh.sd.gov/statistics/ Utah Office of Vital Records and Statistics. (1998-2016). Utah’s Vital statistics: Abortions. https://digitallibrary.utah.gov/awweb/main.jsp Synthetic Control Details Arkansas Figure B.1 Synthetic Control for the Abortion Rate of Minors - Arkansas 86 Table B.1 Arkansas - Synthetic Control Group for Abortion Rate of Minors State Weight MI 0.146 NE 0.028 NM 0.085 OR 0.038 WI 0.704 Figure B.2 Synthetic Control for the Birth Rate of Minors - Arkansas Table B.2 Arkansas - Synthetic Control Group for Birth Rate of Minors State Weight AL 0.478 CA 0.116 NM 0.352 WY 0.054 87 Texas Figure B.3 Synthetic Control for the Abortion Rate of Minors - Texas Table B.3 Texas - Synthetic Control Group for Abortion Rate of Minors State Weight State Weight AL 0.02 NC 0.019 GA 0.033 NE 0.028 IA 0.027 NJ 0.031 IL 0.018 NM 0.024 IN 0.025 NV 0.014 KS 0.018 NY 0.01 MA 0.088 OR 0.04 ME 0.019 SC 0.025 MI 0.037 SD 0.037 MN 0.025 TN 0.024 MO 0.051 WA 0.018 MS 0.32 WI 0.025 MT 0.023 88 Figure B.4 Synthetic Control for the Birth Rate of Minors - Texas Table B.4 Texas - Synthetic Control Group for Birth Rate of Minors State Weight MS 0.319 NM 0.681 89 Virginia Figure B.5 Synthetic Control for the Abortion Rate of Minors - Virginia Table B.5 Virginia - Synthetic Control Group for Abortion Rate of Minors State Weight AL 0.484 MS 0.078 NE 0.029 OR 0.33 WI 0.079 90 Figure B.6 Synthetic Control for the Birth Rate of Minors - Virginia Table B.6 Virginia - Synthetic Control Group for Birth Rate of Minors State Weight State Weight AL 0.005 MT 0.005 CA 0.01 NC 0.007 CO 0.005 ND 0.021 DE 0.111 NE 0.154 GA 0.007 NJ 0.016 IL 0.01 NM 0.007 IN 0.008 NV 0.007 KS 0.06 NY 0.016 KY 0.007 OR 0.011 LA 0.007 PA 0.011 MA 0.019 RI 0.236 MD 0.009 SC 0.006 ME 0.013 SD 0.009 MI 0.011 VT 0.066 MN 0.011 WA 0.009 MO 0.007 WI 0.046 MS 0.004 WY 0.068 91 Ohio Figure B.7 Synthetic Control for the Abortion Rate of Minors - Ohio Table B.7 Ohio - Synthetic Control Group for Abortion Rate of Minors State Weight State Weight AL 0.007 NC 0.006 GA 0.065 NE 0.005 IL 0.007 NJ 0.022 IN 0.007 NM 0.189 KS 0.011 NV 0.017 MA 0.01 NY 0.118 ME 0.008 OR 0.005 MI 0.023 SC 0.006 MN 0.012 SD 0.037 MO 0.007 WA 0.009 MS 0.275 WI 0.015 MT 0.14 92 Figure B.8 Synthetic Control for the Birth Rate of Minors - Ohio Table B.8 Ohio - Synthetic Control Group for Birth Rate of Minors State Weight ME 0.078 MI 0.112 MS 0.125 ND 0.204 OR 0.187 RI 0.04 SC 0.158 SD 0.096 93 Kansas Figure B.9 Synthetic Control for the Birth Rate of Minors - Kansas Table B.9 Kansas - Synthetic Control Group for Abortion Rate of Minors State Weight MN 0.249 NV 0.606 SC 0.013 WA 0.132 94 Figure B.10 Synthetic Control for the Birth Rate of Minors - Kansas Table B.10 Kansas - Synthetic Control Group for Birth Rate of Minors State Weight MS 0.073 ND 0.333 NM 0.054 WV 0.243 WY 0.296 95 Nebraska Figure B.11 Synthetic Control for the Abortion Rate of Minors - Nebraska Table B.11 Nebraska - Synthetic Control Group for Abortion Rate of Minors State Weight KY 0.025 MS 0.157 MT 0.128 WI 0.427 WV 0.263 96 Figure B.12 Synthetic Control for the Birth Rate of Minors - Nebraska Table B.12 Nebraska - Synthetic Control Group for Birth Rate of Minors State Weight KY 0.025 MS 0.157 MT 0.128 WI 0.427 WV 0.263 97