PRELIMINARY AND INCOMPLETE – PLEASE DO NOT CITE

New Evidence on Minimum Drinking Age Laws, Pregnancy and Birth Outcomes Alan Barreca Department of Economics Tulane University 206 Tilton Hall New Orleans, LA [email protected] Marianne E. Page Department of Economics University of California Davis One Shields Avenue Davis, CA [email protected] March 2012 Abstract Do restrictive alcohol policies affect birth outcomes? In this paper we re-evaluate the relationship between minimum drinking age laws and infant health outcomes by examining the sensitivity of current findings to the inclusion of additional, and economically significant, controls. We also implement a new differences-in-differences design that compares differences in health across infants whose mothers who turned 21 during vs. after pregnancy, to differences in health across infants whose mothers turned 20 during the same stages of pregnancy. Our estimates provide little support for the hypothesis that alcohol policies affect birth outcomes.

We would like to thank seminar participants at UC Merced for their comments. We gratefully acknowledge funding support from National Institutes of Health (R01AA017990-01). We are solely responsible for the views expressed in the article. Barreca is an Assistant Professor at Tulane University and can be contacted at [email protected]. Page is a Professor at University of California, Davis and can be contacted at [email protected].

I. Introduction Do restrictive alcohol policies affect birth outcomes? Several studies have found evidence that minimum drinking age laws affect the amount of alcohol young women consume and their probability of engaging in risky sexual activity.1 Taken together with evidence on the negative correlation between prenatal alcohol consumption and birth defects2, it would seem that the answer to the question must be Yes. Yet surprisingly little is known about whether laws that limit young adults’ consumption of alcohol improve birth outcomes. The answer to this question is important since a substantial portion of young adults drink alcohol. Carpenter and Dobkin (2009), for example, find that a third of young adults drink heavily, and Fertig and Watson (2009) find that approximately 33% of pregnant women between the ages of 18 and 22 consume alcohol. Given the mounting evidence that health, even at the very beginning of life, affects markers of later socioeconomic success (Almond and Currie, 2010), MLDA laws may be an important tool for improving children’s life chances.3 The goal of this paper is to test whether alcohol policies affect birth outcomes. To date, the most convincing research design that has been used to estimate causal effects on birth outcomes exploits cross-state changes in U.S. minimum legal drinking age (MLDA) laws that occurred during the 1970s and 1980s. Prior to the 1970s, most states maintained a legal drinking age (MLDA) of 21, but during the early 1970s a number of states reduced their MLDA, and in many states the new drinking age was as low as 18. A subsequent rise in the number of alcohol related fatalities induced the majority of these states to raise their minimum drinking age to 21 again during the 1970s and 1980s. With the passage of the Uniform Drinking Act, all states had adopted an MLDA of 21 by 1988.4 Using this policy variation, Fertig and Watson (2009) (hereafter FW) find that, among young mothers, lenient drinking laws are associated with higher rates of low birthweight and 1

See, for example, Cook and Mare (2002); Cooper (2002); Grossman and Markowitz (2002); Kaestner (2000); Kaestner and Joyce (2000); Markowitz et. al. (2005); Rashad and Kaestner (2004); Rees et. al. (2001); and Sen (2002). 2 A non-exhaustive list of recent studies includes Albertsen et al., 2004; Berkowitz et. al, 1982; Jaddoe et al, 2007; Kesmodel et. al, 2000; McDonald, et. al, 1992; Mills et. al, 1984; Shu et. al, 1995; Whitehead and Lipscomb, 2003; Windham et. al, 1995. 3 In doing so, they may also substantially reduce medical costs. Almond, Chay and Lee (2005), for example, estimate that increasing the birthweight of singleton births that are below 2500 grams, until they met the low birthweight threshold would produce an average cost savings of $10,000 per child. 4 Although the law mandating a MLDA of 21 was passed in 1984, the law was not enforced until late in 1986. The law withheld a portion of a state's Federal highway funds if the state did not enact a MLDA of 21 by October 1, 1986. (Distilled Spirit Council of the United States 1996)

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premature birth. They note that this result is partly due to selection effects. In particular, they find that a lower drinking age is associated with lower levels of education among births to white mothers and the absence of paternal information on the birth certificates associated with black mothers. This selection effect is also documented by Dee (2001), who finds that increasing the MLDA to age 21 reduced childbearing rates among black teens by roughly 6 percent, but had no statistically significant effect on whites. As Dee notes, however, there are limitations to using changes in the MLDA to identify causal effects; namely, factors underlying the policy changes may not be completely eliminated even when using state level changes in the MLDA. States that initially had low MLDAs and were required to raise the MLDA to 21 when the Uniform Drinking Act was passed in 1984, are arguably different from states that consistently maintained an MLDA of 21. The speed with which states complied with changes in the federal MLDA during the late 1980s is also likely nonrandom. In this study, we explore the robustness of FW’s findings to the inclusion of an alternative set of controls that better address the endogeneity of the MLDA changes and possible omitted variables bias. We show that there is no consistently meaningful relationship between the MLDA laws and birth outcomes once key control variables, i.e. age specific time trends and state-by-age fixed effects, are included. We also make note of the fact that 12 states consistently maintained a MLDA of 21 during our sample period,7 and we document the importance of our preferred control variables by examining their economic and statistical significance in these 12 “placebo” states. The control variables turn out to have predictive power in the states where MLDA laws did not change, which suggests that previous evidence on the relationship between MLDA laws and birth outcomes is likely driven by omitted variables. We also introduce a complementary difference-in-differences estimation strategy that does not rely on policy changes for identification. For this analysis, we use restricted data on the universe of births that occurred in California between 1989 and 2004. This research design compares differences in birth outcomes across two samples of births: births to mothers who turn 20 sometime within a year of conceiving (the control group), and births to mothers who turn 21 7

These 12 states include: Arkansas, California, Indiana, Kentucky, Missouri, Nevada, New Mexico, North Dakota, Oregon, Pennsylvania, Utah, and Washington. Note that many of these states are geographically clustered. For example, California, Oregon, Nevada, and Washington, and are thus less likely to be affected by MLDA law changes in treated states.

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within a year of conceiving (the treatment group). Within each sample, we group births according to the four-week bin during which the mother experienced a birthday, and take first differences in birth outcomes between those whose mothers turned 20(21) in a given 4-week bin and those whose mothers turned 20(21) in a post-partum bin (i.e. weeks 45-48). We then estimate the impact of gaining legal access to alcohol by estimating a “second difference” that compares the differences across the treatment and control groups. One advantage of this difference-in-difference identification strategy is that we can test whether there are non-linear effects associated with gaining access to alcohol during particular stages of pregnancy. For example, it may be that gaining access to alcohol is particularly harmful during the first 8 weeks (or so) of pregnancy. 8 Convincing human studies on the impact of prenatal alcohol exposure are hard to come by, but animal studies suggest that prenatal exposure to “teratogens”, or foreign substances like alcohol, matter most during the early part of pregnancy (Tough et al. 2006). In addition, some women do not realize they are pregnant during the early weeks of pregnancy, which might lead to risky behaviors (e.g. binge drinking) that they might have avoided had they been cognizant of the pregnancy (Kesmodel 2001; Tough et al. 2006). Alcohol consumption might also lead to negative selection (or culling) during the early part of pregnancy, something we can test by examining impacts on the fraction of births that are female since male fetuses are less likely to survive in utero health shocks. Our D-in-D approach allows us to explicitly examine whether access to alcohol during this period matters differently than access at later stages. Further, the women in our D-in-D sample could not legally drink prior to conception, which helps mitigate alcohol-related selection into pregnancy. Similar to the analysis using policy changes, however, our difference-in-difference identification strategy yields, at best, weak evidence that pregnant mothers’ legal access to alcohol affects their infants’ health outcomes. Most of the relevant coefficient estimates are not statistically distinguishable from zero.10 In cases where they are both economically and statistically significant, other aspects of the analysis produce red flags. One might be concerned that our lack of evidence results from measurement error in mothers’ reports of their estimated date of last menses; we dismiss this concern by dropping mothers who have a date of menses that 8

As a matter of language, it is common to count weeks as the time from the last menses. The actual conception usually occurs 14 days after the last menses (Niebyl and Simpson 2001). 10 Point estimates are sometimes large but too imprecisely estimated to be able to reject the null hypothesis of no effect.

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is most likely to be measured with error. Furthermore, we find some evidence of “flattening” in the age-outcome profile among women who turn 21 during pregnancy (compared to women who turn 20), suggesting our estimates are biased away from zero by positive selection. Thus, our estimates may be upper bound estimates of the true causal effects. Taken as a whole, our analyses provide little support for the hypothesis that alcohol policies affect birth outcomes. However, we cannot rule out the possibility that alcohol consumption during pregnancy has a detrimental effect on infant health. It may be that young mothers find non-legal ways of obtaining alcohol and that the laws have little impact on their drinking behavior. Alternatively, MLDA laws may affect maternal consumption of alcohol and subsequently affect infant health in ways that cannot be observed in existing data. At the same time, Armstrong (2003) makes a compelling case that, given the quality of existing research, Americans may have jumped too quickly to the conclusion that consumption of alcohol during pregnancy in any amount has devastating consequences. Although the relationship between alcohol access and infant outcomes is intuitive, our research indicates that the causal link is far from established. In the next section we provide background on minimum legal drinking age laws. Sections II and III describe our data and empirical methodologies. Our results are described in Section IV, with further interpretation and conclusions in Section V. II. Data The data on MLDA laws come from the Distilled Spirits Council of the United States. We have information on the month and year that the MLDAs changed for each state, between 1978 and 1988. We match the MLDA data with birth outcome data by mother's estimated age at conception and the month the child was conceived.11 Treatment is assigned based on whether the mother's age was greater than or equal to the MLDA in her state of residence at the time her child was conceived. Figure 1 illustrates the changes in the MLDA between 1977 and 1989. For example, the number of states with a MLDA of 21 increased from 12 in 1977 to 23 in 1985, and 51 (including the District of Columbia) by 1988.

11

Following Fertig and Watson, we assume that the mother’s age at conception was one year less than her age at birth for all gestational lengths over 26 weeks.

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The birth-outcome data used in our state-year MLDA analyses come from the National Center for Health Statistics (NCHS) public-use Natality Files. The NCHS data are derived from information reported on birth certificates and include the near universe of all U.S. births that occurred in the 1970s and 1980s.12 With respect to birth outcomes, the NCHS data have information on the child's gender, birth weight, length of gestation, presence of congenital anomalies, and five-minute APGAR score. Birth weight and APGAR score are commonly used indicators of infant health at birth and have been linked to a number of long-term outcomes (e.g. Black, Devereux and Salvanes, 2007; Behrman and Rosenzweig, 2004; Oreopolous and Stabile, 2008).13 14 In addition, we construct dichotomous indicator variables for whether the child's birth weight is below 2500 grams ("low birth weight") and whether the length of gestation was under 37 weeks ("premature birth"). We include the fraction of births that are female as a dependent variable because evolutionary theory suggests that males are more sensitive than females to in utero health shocks (Trivers and Willard, 1973) and because several recent studies have found evidence that stressors during pregnancy affect the probability of bearing a male child (Cagnacci et al., 2004; Almond et. al., 2007; Nilsson, 2008; Sanders and Stoecker, 2011). To discern whether the mother was of legal drinking age during her pregnancy, we rely on information in the NCHS data on the mother’s age, the mother's state of residence, and the month of the child's birth. A limitation of the data is that we observe the mother's age (in whole years) at the time of child's birth but not at the time of conception so we cannot tell whether the mother was the same age during the majority of her pregnancy. To be consistent with previous research, we assume the mother's age at conception is one year less than her age at the child's birth.15 We assume a mother is eligible to drink if her age at conception is at or above the MLDA in her state of residence. Our NCHS analyses are restricted to mothers who are between 14 and 24 years of age at the time of conception and are U.S. residents.16 Women over the age of 21 are legally able to drink throughout the entire period under study, so the MLDA laws should not causally affect 12

The vast majority of states reported 100-percent samples. The remaining states report 50-percent samples. APGAR scores are on a 10-point scale based on five categories of infant health. 14 We are the first to explore the effects of changing MLDA laws on infants’ APGAR score. The Vital Statistics began collecting APGAR scores in 1978 but at that time they were only reported in 38 states. The number of states reporting the APGAR score increased gradually through 1989 when it was reported in 47 states. 15 For gestational lengths less than 26 weeks, we assme the mother’s age at delivery and conception are equal. 16 Note that we assign treatment based on the state of residence to avoid contamination of our estimates by endogenous short-term migration responses that are correlated with the MLDA. 13

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these women (assuming there are no intertemporal effects or spillovers.) As such, changes in the health outcomes of infants born to these women can be used to control for within-state changes in birth outcomes that may be spuriously correlated with MLDA changes, or for any effects of the MLDA that are common to all age groups. For example, the MLDA policy changes may be endogenous to the changes in health conditions that affect infants born to women of all ages. For our difference-in-differences analyses we need information on mother’s exact date of birth, which is not available in the NCHS public-use Natality Files, but is available from the California Department of Public Health’s (CDPH) restricted-use Birth Cohort Files and Birth Statistical Master Files. These files contain information that is provided on birth certificates for all births that took place in California between 1989 and 2004. These data have information on all of the birth outcomes mentioned above except for the APGAR score, which is not reported. We can infer the exact age of the mother at any point during her pregnancy because we have the mother's exact date of birth, the child's exact date of birth, and the date of the mother’s last menses. Importantly, these data are linked to infant mortality records so we can estimate impacts on the probability the child died within one year of birth. We restrict our sample to births among mothers who were themselves born in California, and for whom last normal menses is reported.17 An advantage of these datasets is that they include information on several million births. Our NCHS sample has over 19 million births to women ages 14-24, and our CDPH samples have close to 300 thousand observations for those mothers who were between 19 and 20 at the time of conception. Most human studies on the relationship between maternal alcohol consumption and fetal health rely on data with only a few hundred to a few thousand observations. Both datasets include information on mother’s race and education, which allows us to test for effects on the composition of women who give birth. Summary statistics for our samples of births are presented in Table 1 and Table 2. III. Estimation Approach A. MLDA Law Changes Our first identification strategy exploits variation in the MLDA laws across states and over time. Because the MLDA laws vary across states, years and cohorts we conduct our

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We restrict our sample to mothers who were born in California because we do not want our estimates to reflect migration, in the unlikely event that women migrate in anticipation of turning 21.

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analyses at the state-year-age cohort level. We begin by estimating the following regression via ordinary least squares: (1) Yast = !1 MLDA18st + !2 MLDA18st * age14-17ast + !3 MLDA18st * age18-20ast + "s + #t + $a + %s * t + &cst where Yast is an average outcome for infants born to mothers of age a residing in state s at the time of conception t,18 MLDA18st is an indicator for whether the drinking age in the mother’s state of residence s was 18 at time t, MLDA18st is interacted with age14-17ast and age18-20ast to allow the effects of the MLDA to vary for mothers who were 14 to 17 and 18 to 20 years old, respectively, "s are state fixed effects; #t are year-month fixed effects; $a are age fixed effects; and %s * t are state-specific linear time trends. The inclusion of state specific time trends allows us to account for the possibility that variation in the MLDA is correlated with unobserved factors that vary by state and year that might affect infant health. To account for the possibility that the error term & is correlated within states, we cluster our standard error estimates at the state level. We focus on whether the state had an MLDA of 18 in order to be consistent with the existing literature. Dee (2001) shows that an indicator for whether the state has an MLDA of 18 sufficiently captures the variation in youth’s drinking behavior, and FW also adopt this approach. We have run similar models where we replace the MLDA18 dummy and its interactions with indicators for whether the mother could legally drink at the time of conception. These models produce similar, though smaller, estimated relationships. One interpretation of the smaller estimates is that, in addition to providing legal access to alcohol for those 18 and over, an MLDA of 18 also provides women under the age 18 greater access to alcohol, possibly through their 18year-old peers. An implication of this is that women under age 18 cannot serve as a reliable control group. Women who are over 21 can arguably serve as an adequate control group, however, since the MLDA varies between 18 and 21.19 Equation (1) is qualitatively similar to the model to that FW use and produces very similar estimates.20 After estimating equation (1) we systematically add two important sets of

18

The month the mother conceived the child can be inferred by using publicly available information on length of gestation; in the cases where gestation is not reported, we assume gestation began 40 weeks prior to the date of the child's birth. 19 There is some possibility that exposure to an MLDA of 18 has long-term effects on fertility decisions and birth outcomes, which would potentially bias our results downward. 20 FW rely on individual level data and control for infant sex and plurality. We disagree with controlling for these characteristics since they are potentially endogenous to changes in the MLDA.

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controls that have not been presented in previous studies.21 First, we add age-specific linear trends. The inclusion of these trends allows us to account for the possibility that the estimated ! coefficients are capturing a convergence in birth outcomes among mothers of different ages over time. Second, we also include state-specific age fixed effects. This allows us to control for the possibility that within state differences in birth outcomes between mothers of different ages are correlated with states’ MLDA policies. This might be the case if states differ in the extent to which they protect teenagers, or the extent to which they regulate teenagers’ behavior. We show that including these controls substantively affects the estimated impact of alcohol access on birth outcomes. B. Difference-in-Differences Analysis Our second identification strategy relies on restricted CDPH natality data covering births that occurred in California between 1989 and 2004, a period when the MLDA was fixed at 21 in California and all other states. We exploit the fact that the CDPH data have information on the child’s date of birth, the mother’s date of birth, and the date of the mother’s last menses, to set up a difference-in-differences (D-in-D) style identification strategy. Specifically, we compare: a) the difference in birth outcomes among women who turned 21 during pregnancy to birth outcomes among women who turned 21 just after giving birth to b) the difference in birth outcomes among women who turned 20 during their pregnancy to birth outcomes among women who turned 20 just after giving birth. This approach has several nice features. First, it allows us to estimate the impact of the MLDA law in a more current context---the MLDA has been 21 for over two decades. Second, it allows us to estimate the impact of gaining access to alcohol at different points during pregnancy. Third, none of the women in our sample had legal access to alcohol before they turned 21, which mitigates the possibility of alcohol-consumptionrelated selection into fertility. In order to implement this identification strategy we create two samples. The first sample consists of births to mothers who were 19 at the time of their last menses, and the second sample consists of births to mothers who were 20 at the time of their last menses. The first group is our control group, and the second group is our treatment group. As a starting point, we take each

21

FW discuss the robustness of their results to the inclusion of the age-specific trends, but this robustness check is not presented in the published manuscript.

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sample and group the observations according to the four-week period during which the mother experienced a birthday. We assign an indicator variable for each 4-week period and run the following regressions: (2) Yiat = DUM21ia + 't (t WEEKt+ 't !t (WEEKt * DUM21ai) + ) Xiat + &it where Y is a measure of health (birthweight, gestation, etc.) for an infant born to mother i, who was age a and experienced a birthday in trimester t. DUM21 is an indicator variable that identifies whether the mother was 20 years old at the time of her last menses (and subsequently turned 21). The inclusion of this variable helps control for the fact that infants born to 20 year olds are healthier, on average, than infants born to 19 year olds. WEEKt is a vector of 11 dummy variables that indicate whether the mother turned 20 (21) during one of 11 four-week bins (1-4, 5-8, …, 41-44). X is a vector of controls including year-month (of last menses) fixed effects and county fixed effects.22 We cluster our standard error estimates&) on the county of residence in order to account for the possibility, however small, that some counties have policies or norms that have differential effects on women of different ages. Our omitted category is infants whose mothers experienced a birthday during weeks 4548, which is nearly always postpartum. As Appendix Figure A1 illustrates, only 2 percent of all pregnancies ever reach 45 weeks. Further, given less than 25% of pregnancies ever reach 41 weeks, we can use the ! estimate on weeks 41-44 as a useful placebo check. Note that our control group does not include births to women who have a birthday in weeks 49-52 of the pregnancy since these women are likely to have had a birthday just prior to conception, which might affect the composition of mothers in our sample. If the types of mothers who conceive just after their birthday are different from those who conceive at other times, then including births to these women may affect the magnitude of the estimates and their interpretation.23 Thus, ( captures the first difference between the outcomes of infants whose mothers experienced a birthday in the four-week-bin t, and infants whose mothers experienced a birthday in the postpartum period (i.e. weeks 45-48). The coefficient vector ! reflects the impact of turning 21 at different stages of the pregnancy. After accounting for fixed differences in birth outcomes to women who conceived at age 19 and age 20, we assume that the counterfactual outcome for women who turned 21 during 22

The inclusion of these controls does not affect the point estimates or the precision of said point estimates. The results of regression discontinuity analyses not shown (but available from the authors), indicate notable increases in fertility right after a woman’s birthday. 23

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period t of their pregnancy would have been equivalent to turning 20 during the same period. The detrimental effect of alcohol on fetal development has been difficult to pinpoint and there are several reasons one might expect any or all of the coefficients to be important. Much of the medical literature suggests that exposure to teratrogens, like alcohol, is most harmful during days 31 and 71, or when the heart and central nervous system are developing (Niebyl and Simpson 2007). Further, we might expect drinking intensity to be greatest during the early part of pregnancy, roughly weeks 3 through 8, when women may not know they are pregnant (Kesmodel 2001; Tough et al. 2006). This suggests that the magnitude of the coefficient on weeks 5-8, in particular, may dominate the magnitude of the other coefficients. On the other hand, some animal studies suggest that the third trimester is a particularly important period for brain development (Marcussen et al. 1994). It is also the period associated with the largest weight gain. If calories from alcohol are substituted for calories containing more nutrition, then access to alcohol during the third trimester might be more important. Previous studies (e.g. Almond et. al, 2010; Painter et. al, 2005) have found that nutritional shocks during the third trimester have the largest impact on birthweight. In sum, pinpointing the detrimental effect of alcohol with respect to a specific period of gestation remains an open and important research endeavor. While our estimates can address this question to a certain extent, it should be noted that our treatment captures the effects of gaining access to alcohol from at a given point in the pregnancy onwards. Thus, distinguishing from an acute episode of drinking and the cumulative effects of drinking throughout pregnancy is impossible. The D-in-D analyses are an excellent complement to analyses based on state-year policy changes because of the different assumptions that are necessary for clean identification. Using state/year variation in MLDAs relies (perhaps questionably) on the assumption that policy changes are exogenous. On the other hand, underlying the D-in-D analyses are functional form assumptions regarding the relationship between mother’s age and infant health.24 Both identification strategies are susceptible to error-in-variables bias. In the case of the D-in-D strategy measurement error problems may result if a significant number of women inaccurately report the date of their last menses. When we use state-year level policy changes we only have

24

We examine the robustness of our estimates to a variety of alternative assumptions about this relationship.

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information on the mother’s age at the time of the birth and are forced to make some assumptions about her age at conception. The two empirical approaches also pick up different local average treatment effects. The D-in-D design identifies the effect of maternal alcohol consumption on infants whose mothers are close to their 21rst birthday, whereas using variation in state level MLDA’s over time identifies the effect on infants born to mothers who are significantly younger. One might expect the impact of alcohol access to differ across these two groups. For example, the same amount of alcohol may affect babies born to teenage girls differently than babies born to older mothers because of other differences in maternal health. Infants born to young mothers tend to be less healthy than other infants so they may be more susceptible to the impacts of alcohol. Older women may also be less likely to drink (or less likely to drink heavily) during pregnancy than younger women, regardless of legality, because they are either better informed or more responsible. Finally, it is important to keep in mind that our two approaches use data from different locations and time periods: our NCHS analyses are based on the 11 years of data covering all births between 1978 and 1988, whereas our CDPH analyses are based on all births that took place in California between 1989 and 2004. If there are differences in the impact of MLDA laws on maternal consumption across states or over time then this could also generate differences in the local average treatment effects. IV. Results A. Estimates based on State/Year Variation in MLDA Laws Table 3 presents the estimated impact of the MLDA laws using variation in these laws across states and over time. We present results for three specifications: the first specification includes dummy variables that control for state of birth, month and year of birth, and mother’s age, along with state-specific time trends. This specification is nearly identical to that used by FW and produces estimates that are nearly identical.25 The second specification adds an agespecific linear trend to the set of control variables. And our third specification adds state by age interactions. We present the estimates for all races (Panel A), white mothers only (Panel B), and black mother only (Panel C).

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For example, the three key coefficients in Panel A column (1) are -0.18, 0.49, and 0.24. FW’s analogous coefficients are -0.17, 0.50, and 0.26, respectively.

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The pattern across the specifications is striking. When age trends and state*age interactions are omitted from the regression, we find that lower legal drinking ages are associated with worse birth outcomes for both the affected group, and among women who are younger than the MLDA. The coefficient estimates suggest that among 18-20 year old mothers an MLDA of 18 increases the probability of low birthweight, relative to 21-24 year olds, by 0.24 percentage points. The probability of a premature birth also increases by 0.16 percentage points. To put these estimates into perspective, about 8 percent of infants born to 18-20 year old mothers are born weighing less than 2500 grams, and about 12 percent are born before 37 weeks. The estimates, therefore, appear to be economically as well as statistically significant. Note, however, that the estimated impact of the MLDA on births to the older age group is also substantive, and in the opposite direction. Among women 21-24 years old, who are too old to be materially affected by a change in the minimum legal drinking age26, an MLDA of 18 is associated with a 0.18 percentage point lower probability of having a low birthweight, and a 0.26 percentage point lower probability of a premature birth. If the state minimum drinking age were truly exogenous we would expect these estimated coefficients to be near zero. The fact that these coefficient estimates are opposite in sign to the estimated impacts on younger mothers, together with the fact that the fraction of states with an MLDA of 18 was declining over this period, suggests that the estimated effects among younger women may be biased by differential trends across age groups. In order to investigate this possibility, we add age-specific trends to the regression, and display the results in columns 2 and 5. Including age trends cuts the estimated MLDA coefficients dramatically, and substantively reduces their statistical significance. Columns 3 and 6 show what happens when we add state*age interactions: the estimated coefficients fall even further, and when the dependent variable is an indicator for premature birth the estimated coefficient on the MLDA is no longer statistically different from zero. FW acknowledge that adding age trends reduces the estimated impact of the MLDA laws but they argue that omitting these trends is reasonable given the strong degree of colinearity between the trends and the MLDAs. Their argument is that the addition of age specific time trends absorbs important identifying variation in the MLDA laws. In general, we find that the standard error does increase with the addition of the age-specific time trends, although only 26

It is possible that 21-24 year olds may have been affected by the MLDA law change earlier in life.

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slightly. For example, the standard error on “MLDA is 18 x mother is 14-17” for the low birthweight outcome goes from 0.157 to 0.183 (columns 1 and 2, respectively). However, when both age-specific trends and state-by-age fixed effects are included, the standard error estimates are actually smaller. In the previous example, the standard error is now 0.080 (column 3). Thus, we can rule out the possibility that our model is absorbing a substantial portion of the identifying variation. More plausibly, the estimates in columns 1 and 4 are being identified from: (a) changes in birth outcomes over time that differentially affect mothers of different ages, and (b) differential age-outcome profiles for treated and untreated states. Figure 2 begins to investigate possibility (a) by plotting differences in outcomes between 14-17 years olds and 21-24 year olds over time, separately for states that did (“treatment states”), and did not (“placebo states”), experience changes in their MLDA laws between 1978 and 1988. As Panel A.1 in Figure 2 illustrates, relative to infants born to 21-24-year-old mothers, there are notable decrease in low birthweight rates born to 14-17 year old mothers over time. Panel B.1 illustrates that 18-20 year olds have also had improved outcomes, relative to 21-24 year olds, over time. Also, 14-17 year olds and 18-20 year olds, respectively, saw an improvement in pre-term delivery rates relative to 21-24 year olds (Panels A.2 and B.2.) Again, the convergence in pre-term delivery rates is apparent in both the “treatment” and “placebo” states, which strongly suggests that the patterns are driven by factors that are unrelated to the changes in the MLDA. These illustrations suggest that failing to control for age-specific trends will result in overstating the benefits of the MLDA changes. Figure 3 tests the possibility that treated and control states have differential age-outcome profiles. Panel A illustrates that younger ages had worse birth outcomes compared to older ages in 1978. However, younger mothers were relatively worse off in treated states compared to control states. Panel B demonstrates that the younger age groups are were still worse off in 1988 in treated states. Thus, failing to control for state-by-age fixed effects would lead to an overestimate of the effects of an MLDA of 18 on birth outcomes. Table 4 shows the relationship between alcohol policies and all of the other birth outcomes that we are able to observe in the NCHS files, once we include the full set of control variables. When the full spectra of outcomes are considered, we cannot reject the hypothesis that higher MLDAs have no impact on birth outcomes. Nearly all of the coefficient estimates on the MLDA interactions are small and statistically insignificant when our preferred controls are

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included. The patterns are similar for both white and black births. An exception to this pattern is that an MLDA of 18 is associated with a higher fraction of births that are female among the 1820 year old group, especially for the sample of black mothers (Panel C). Taken with the fact that we see a statistically significant decrease in the probability of an Apgar score less than or equal to 5, the female results may be indicative of higher rates of fetal deaths, based on the TriversWillard hypothesis, and positive selection. Previous studies have also found evidence that MLDA laws affect selection into motherhood, particularly among blacks (FW, 2009; Dee, 2001). Table 5 explores this possibility in the presence of age specific trends and state*age fixed effects. The coefficients on MLDA is 18 x mother is 14-17 suggest that an MLDA of 18 increases the fraction of births to black mothers by 0.8 percentage points, decreases the fraction of women without a high-school degree by 0.2 percentage points, and the fraction of births to where the father’s information is missing by 1.1 percentage points. The estimated relationships for mothers 18-20 is qualitatively similar, but smaller in magnitude. Although only the estimate on the probability the mother is black is statistically significant, on the whole these estimates suggest that an MLDA of 18 increases the fraction of births to more economically disadvantaged groups. Further, these results are in accordance with Dee (2001), who finds that less restrictive MLDAs increased childbearing among blacks. All of this suggests that our estimates are potentially biased towards finding negative effects of a MLDA of 18, which is contrary to our finding that a MLDA of 18 has no observable impact on birth outcomes. B. Difference-in-Difference Results We further investigate the relationship between MLDA laws and infant health outcomes by employing the D-in-D design described in Section IV.B. Figure 4 shows the ! coefficients and 95% confidence intervals that are produced when we estimate equation (2). The full set of coefficient and standard error estimates are available in Appendix Table A.1. Each panel of Figure 4 focuses on a different outcome, and presents the impact of turning 21 during each of the four-week bins.

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Very few of the estimated coefficients are statistically different from zero.27 We find no statistically significant evidence that turning 21 during pregnancy affects the probability of being born prematurely, the probability of having abnormal conditions, or the probability of being female. The analyses produce weak evidence that turning 21 during weeks 13-16 affects birthweight outcomes but these are the only coefficient estimates that are statistically different from zero at conventional levels. Importantly, we do not observe any sharp change in outcomes during the first trimester or during weeks 5-8, when we might expect turning 21 to have the largest effects. Even though we have been able to harness a sample that includes some 270,000 observations, the confidence intervals are too large to reject the null hypothesis. At first glance there does appear to be evidence that the probability of dying within the first year is adversely affected by changes in mothers’ access to alcohol. The estimated impacts of turning 21 on infant mortality are positive, statistically different from zero and of substantive magnitude: representing an increase of approximately 3-4 deaths per 1000 births. Across the full sample, about 8 out of every 1000 infants die within the first year of life, so the magnitude of these estimates is non-trivial. Notice, however, that these large effects are present even for mothers who turned 21 during weeks 41-44 of their pregnancy. This is surprising because over 75 percent of the mothers in our sample have already given birth by week 41. Thus, if legal access to alcohol was driving the estimated effects on infant mortality, we would expect the coefficient estimate associated with weeks 41-44 to be smaller than the estimates that are associated with turning 21 earlier. This suggests that the estimated coefficients are driven by some unobservable variable or noise that is affecting the control group (weeks 45-48). The key identifying assumption with the difference-in-difference identification strategy is that in the absence of alcohol access, the age-outcome profiles would have been the same for women in our treatment and control groups. Equation (2) includes an age intercept (DUM21), but otherwise we assume that in the absence of access to alcohol, the “return” to experiencing a birthday during weeks 1-4, 5-8 etc. would be the same for mothers turning 20 and mothers turning 21. If the returns to maternal age are increasing at a decreasing rate, then our estimates will be biased upward. We have conducted a number of “specification checks” where we saturate the model with parametric controls for maternal age but the general pattern of results is 27

We have run our regressions separately by race and find no notable differences between whites and blacks with respect to the patterns of the estimates. For brevity, we do not report those estimates here but they are available from the authors upon request.

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consistent.30 As a further robustness check, we have also re-estimated equation (2) replacing our control group with infants born to women whose last menses was at age 21 (and who thus turned 22 during or just after pregnancy). An advantage of this control group is that the marginal impact of mother’s age is likely to be smaller than among mothers who conceive at age 19.31 Nevertheless, the pattern of results is similar: in cases where we see statistically significant impacts during weeks 1-40, the estimates on weeks 41-44 are of similar magnitude, which calls into question the causal interpretation of the other estimates (See Appendix Table A.2).32 As in the MLDA analyses, we also explore the possibility that differential selection into motherhood drives our lack of evidence in support of the hypothesis that legal access to alcohol has spillover effects onto infant health. Figure 5 summarizes the results of six regression analyses that replace the dependent variables in equation (2) with indicator variables summarizing the mother’s race or ethnicity, her level of education, and whether information about the father is missing from the child’s birth certificate. The figures show some evidence of selection, mostly with regards to maternal education. Specifically, compared to mothers experiencing a birthday postpartum, mothers who turn 21 during the first eight to twelve weeks of pregnancy are relatively less likely to have completed some college compared to mothers who turn 20 during the same point in the pregnancy. The direction of selection, however, likely biases our estimates towards finding an effect of alcohol access on infant health. This suggests that the difference-in-difference estimates are likely overestimates of the true impact on health outcomes. On the other hand, one reason that we may have failed to detect strong evidence that MLDA laws affect infant health is that the regressor of interest is measured with error. For example, some mothers may be unable to recall the date of her last menses at time of delivery. Where recall at delivery is not an issue, the initial determination of the date of last menses still may be an issue (Kramer et. al, 1989; Rossavik and Fishburne, 1989). In terms of our research design, this will cause us to incorrectly ascertain the week of gestation during which the mother’s birthday occurred, and bias our estimates towards zero. Figure 6 lends weight to this concern. There is substantive heaping in the number of births associated with a day-of-month of last menses is a multiple of 5, when the true dates are presumably evenly distributed throughout the 30

31

Results available from the authors upon request.

A disadvantage of this control group is that the mothers were able to drink legally throughout their pregnancies. 32

Results available from the authors upon request.

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month. In order to address this concern, we have rerun our regression analyses dropping all births where the day of last menses is at a heap, or where gestational lengths are implausibly large (i.e. greater than 44 weeks). The results of this exercise are presented in Appendix Figure A.3 and are similar to our main estimates. V. Conclusion The results from previous research imply that raising the MLDA would lead to better birth outcomes among young mothers. The analyses presented in this paper suggest that such a conclusion may be premature. Using two different types of estimation strategies, we find little evidence to support the hypothesis that MLDA laws affect fetal health. We show that after controlling for age specific time trends and cross state variation in the maternal age gradient, there is little correlation between higher MLDAs and birth outcomes. Alternative identification strategies that harness variation across maternal birthdates rather than state/year policy variation also yield little evidence of MLDA effects, although statistical imprecision precludes ruling out meaningful effect sizes. It is important to note that our results do not necessarily imply that prenatal exposure to maternal alcohol consumption has no effect on birth outcomes. There are at least two reasons that this should be stressed. First, our design focuses on the effects of MLDA policies, not alcohol consumption. It could be that MLDA laws have little effect on the drinking behavior of pregnant women. Previous studies have shown that barriers to alcohol do substantively affect drinking among young women (e.g. Carpenter and Dobkin, 2009) but to our knowledge no study has looked at how they affect the drinking behavior of pregnant women in a quasi-experimental framework. It is also important to keep in mind that although we do not find evidence that MLDA laws affect birth outcomes, some of our point estimates are actually quite large. For example, a back of the envelope calculation using the estimated effect of turning 21 during weeks 5-8 on the probability of being a low birthweight baby, together with Carpenter and Dobkin’s (2009) estimate of the impact of turning 21 on women’s drinking behavior, implies that the additional exposure to alcohol experienced by the fetus as a result of the change in its mother’s drinking behavior increases the probability of being below 2500 grams by 60 percentage points.37 The 37

Our calculation is based on the following: the coefficient on the probability of low birth weight is approximately

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imprecision with which our coefficients are estimated is also consistent with effect sizes that are equal to zero, however. It might also be that MLDA laws affect mothers’ drinking behavior, but that for most infants the effects of in-utero exposure to alcohol are more evident later in childhood. The infant health information that is available on birth certificates is collected within hours (or, more usually, minutes) of a child’s birth and represent only a tiny fraction of the child outcomes that might be affected. Using a natural experiment in Sweden, Nilsson (2008) finds large long-term impacts as a result of changes in alcohol policies. Further research is needed to assess the full impact of these laws on children’s development. The main conclusion that we draw from this series of empirical analyses is that, contrary to the results that are emphasized in the existing literature, the impact of MLDA laws on infant health is still unknown. Our findings resonate with Armstrong (2003) who argues that, given the quality of existing research, Americans may have jumped too quickly to the conclusion that consumption of alcohol during pregnancy in any amount has devastating consequences. Although the relationship between alcohol access and infant outcomes is intuitive, our research indicates that the causal link is far from established.

0.006, or a 0.6 percentage point increase. Using a regression discontinuity approach, Carpenter and Dobkin (2009) estimate that women turning 21 increase the proportion of days that they drink by 3.1 percentage points, and the proportion of days that they binge drink by 1.2 percentage points. If we assume that when pregnant women turn 21 that the probability of drinking increases by 1 percentage point then the additional exposure to alcohol experienced by the fetus increases his/her probability of being low birthweight by (0.006/0.01) =60 percentage points. The statistical imprecision and conjecture regarding drinking behavior of pregnant women in our sample preclude making strong predictions, however.

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Table 1: Summary of means, by mother’s race National Natality Data, 1978-1989 Women aged 14 and 24 at time of conception

Birthweight Birthweight < 2500g Gestation Gestation < 37 weeks Apgar score (5 min) Apgar