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. Author manuscript; available in PMC: 2026 Mar 17.
Published in final edited form as: Alcohol Alcohol. 2025 Nov 16;61(1):agaf076. doi: 10.1093/alcalc/agaf076

Mandatory warning signs for alcohol use during pregnancy and birth and infant outcomes in southern United States: a quasi-experimental study

Sarah CM Roberts 1,*, Alex Schulte 1, Sarah Raifman 1, Guodong Liu 2, Claudia Zaugg 1, Meenakshi S Subbaraman 3
PMCID: PMC12990223  NIHMSID: NIHMS2145934  PMID: 41317082

Abstract

Introduction:

Policies mandating posting of signs warning of the risks of alcohol consumption during pregnancy (MWS-alcohol-pregnancy) are common in the United States Previous research suggests these policies are ineffective and relate to increased adverse infant and maternal outcomes. Research about MWS-alcohol-pregnancy using quasi-experiments is needed.

Materials and Methods:

This study uses Vital Statistics birth certificate data and commercial insurance claims data from Merative MarketScan® and policy data from NIAAA’s Alcohol Policy Information System. We systematically selected a treatment (Texas) and comparison (Florida) state for a quasi-experimental examination of effects of an MWS-alcohol-pregnancy policy going into effect in 2007. Difference-in-difference models compared changes in birthweight, low-birthweight, and infant injuries consistent with maltreatment from pre- to post-policy change between the treatment and comparison state.

Results:

Mean birthweight decreased 4.06 g more from pre- to post-periods in the treatment as compared to the comparison (average treatment effect on the treated [ATET] −4.06, 95% CI −7.02, −1.09) state. The difference in the pre- to post-policy change in low-birthweight in the treatment relative to the comparison state was not statistically significant (ATET .0 pp, 95% CI −.0, .0). The pre- to post-policy change in infant maltreatment was .5 percentage points greater in the treatment relative to the comparison state (ATET .5 pp, 95% CI .2, .8).

Conclusions:

The MWS-alcohol-pregnancy policy was associated with lower birthweight and more infant maltreatment. This study provides further evidence that MWS-alcohol-pregnancy policies are mostly ineffective and possibly harmful.

Keywords: alcohol use, alcohol warning sign policy, pregnancy, infant outcomes, quasi-experimental study

Introduction

While the United States has mandated that alcohol beverage containers include a label warning of the risks of drinking during pregnancy since 1989 (Hilton and Kaskutas 1991), national policy does not cover requirements about posting of signs warning about risks. Instead, decisions about whether to mandate posting signs warning about risks of alcohol consumption during pregnancy (MWS-alcohol-pregnancy) in places where alcohol is sold are left to individual states. MWS-alcohol-pregnancy policies are common in the United States, with half of United States having such a policy in 2024, most of which went into effect in the 1980s and 1990s (NIAAA 2024). MWS-alcohol-pregnancy policies presume warning signs alert people to risks of drinking during pregnancy, which influence pregnant people to stop or limit consumption and therefore reduce adverse effects of drinking during pregnancy.

While early studies suggested MWS-alcohol-pregnancy policies might reduce drinking during pregnancy and related adverse health effects, more recent studies suggest otherwise (Cil 2017, Subbaraman et al. 2018, Roberts et al. 2019, Berglas et al. 2023, Roberts et al. 2023a). One study examining effects of introducing the alcohol warning label (which includes a pregnancy-focused warning) to beverage containers throughout the United States in 1989 found it was associated with a small reduction in drinking during pregnancy, although not among the heaviest drinkers or people who had given birth previously (Hankin et al. 1993, Hankin et al. 1996). Other research has focused on state-level MWS-alcohol-pregnancy policies. A 2017 study did not find associations between MWS-alcohol-pregnancy policies and low-birthweight or preterm births, although did find reductions in very-low-birthweight and very-preterm births associated with the policy (Cil 2017). This study focused on MWS-alcohol-pregnancy in isolation and did not consider them in the context of other policies targeting alcohol use during pregnancy. More recent research examining relationships between nine state-level policies focused on alcohol use during pregnancy (including MWS-alcohol-pregnancy policies) found that while MWS-alcohol-pregnancy policies are associated with reduced self-reported binge drinking during pregnancy, they are not associated with any drinking or heavy drinking during pregnancy or with infant morbidities related to maternal alcohol consumption during pregnancy (Roberts et al. 2019, Roberts et al. 2023a). Instead, this research found that MWS-alcohol-pregnancy policies relate to increased low-birthweight and preterm births, increased infant injuries consistent with maltreatment, increased severe maternal morbidities, less prenatal care, and less substance use disorder treatment utilization among pregnant people (Subbaraman et al. 2018, Subbaraman and Roberts 2019, Berglas et al. 2023, Roberts et al. 2023a). Overall, the research suggests MWS-alcohol-pregnancy policies are mostly not associated with reduced drinking during pregnancy and instead relate to increased adverse maternal and infant outcomes and decreased prenatal care and treatment. These findings suggest MWS-alcohol-pregnancy policies may create stigma regarding drinking during pregnancy and thus lead people who drink during pregnancy to avoid healthcare and treatment, resulting in worse health outcomes. Research on similar warning signs policies focused on cannabis use during pregnancy, if applied to MWS-alcohol-pregnancy policies, support the possibility that the mandatory signs relate to increased stigma (Roberts et al. 2023b, Gould et al. 2025) and also suggest another possibility, that people may not believe the information in warning signs (Roberts et al. 2023b).

There is current policy attention to whether individual states in the United States should mandate signs warning of health risks caused by alcohol consumption in general (Rosen 2024), which is bringing renewed attention to MWS-alcohol-pregnancy and relevant research evidence. The existing research suggests findings regarding adverse effects of MWS-alcohol-pregnancy are mostly consistent across data sources and outcomes and are consistent with similar research regarding MWS-cannabis-pregnancy (Subbaraman et al. 2018, Roberts et al. 2019, Roberts et al. 2022, Berglas et al. 2023, Roberts et al. 2023a, Roberts et al. 2023b). Yet, most quantitative research to date has examined multiple MWS-alcohol-pregnancy policy changes across multiple states with effective dates staggered over long periods of time in the context of multiple other policy changes focusing on alcohol use during pregnancy. Research focusing narrowly on a single MWS-alcohol-policy change in a single state over a shorter time frame using quasi-experimental methods can complement the existing research and provide additional evidence that can inform evidence-based policy moving forward.

Materials and Methods

Overview of study design

This quasi-experimental study examined the relationship between adopting a MWS-alcohol-pregnancy policy and birth and infant outcomes, using outcome data from Vital Statistics records and commercial insurance claims. To identify a single policy change to examine, we systematically identified a state that had a MWS-alcohol pregnancy policy go into effect at a time that did not co-commence with another related policy change and a comparison state. We then used a difference-in-differences (DID) approach to compare changes in outcomes from before to after the policy change in the treatment state to changes in the comparison state.

State selection

We first identified a treatment state that adopted an MWS-alcohol-pregnancy policy and where there were sufficient years of outcome data available in each outcome data source before and after the policy change. As the earliest year of data was 2005 in the commercial insurance dataset and we wanted to avoid possible confounding with the COVID-19 pandemic onset, we were limited to finding a policy change between 2007–2017. Only Texas (1 September 2007) and Utah (1 July 2010) adopted an MWS-alcohol-pregnancy policy during that timeframe. Most other states adopted MWS-alcohol-pregnancy policies in the 1980s and 1990s (NIAAA 2024). We then investigated whether Texas or Utah adopted MWS-alcohol-pregnancy policies within one year of other policy changes that might be associated with study outcomes. Other policy changes included: (i) other pregnancy-specific alcohol policies; (ii) pregnancy-specific drug policies; (iii) general population alcohol policies (e.g. gas and grocery store sales, taxes, government monopoly control); (iv) recreational cannabis legalization; and (v) general population tobacco policies (e.g. tobacco taxes). The Texas and Utah MWS-alcohol-pregnancy policies did not co-commence with any of the first four policy types. Both states, however, increased tobacco taxes; in Texas, this change occurred eight months before its MWS-alcohol-pregnancy policy went into effect; in Utah, this change occurred the same date the MWS-alcohol-pregnancy policy went into effect. For this reason, combined with Utah’s small population and atypical alcohol environment (Erickson et al. 2014), we selected Texas. As previous research has found relationships between tobacco tax policy changes and birth outcomes (Adams et al. 2012, Hawkins et al. 2014), we conducted sensitivity analyses (described below) that account for Texas’s tobacco tax increase. Texas’s MWS-alcohol-pregnancy policy required all businesses with on-premise alcohol consumption permits in Texas to display warning signs on restroom doors informing the public that drinking alcohol during pregnancy can cause birth defects and other harms to a baby, and recommended that people who are pregnant or are trying to become pregnant abstain from alcohol (Texas Alcoholic Beverage Code 2007, Tex. Admin. Code 2023).

To select a comparison state, we first identified states that, through when the research was conducted, had not adopted a MWS-alcohol-pregnancy policy. From that subset, we identified states geographically close to Texas that did not have any of the five policy change types (listed above) within one year of Texas’s MWS-alcohol-pregnancy policy change. Florida, Alabama, and Virginia met these criteria. We focused on Florida due to it being more similar to Texas in population size (17 and 22 million people, respectively), state politics (both had Republican governments), and demographics (61% white, 15% Black, 20% Hispanic in Florida and 48% white, 11% Black, 36% Hispanic in Texas) than the other two possible states (for Alabama and Virginia: 4 million and 7 million; divided governments; and 69% white, 26% Black, 2% Hispanic and 68% white, 19% Black, 6% Hispanic) (U.S. Census Bureau 2006, Flood et al. 2025, National Conference of State Legislatures 2025). While state-specific information about alcohol consumption during pregnancy is not available, binge drinking among adult females was also similar across Florida (6.2%) and Texas (7.2%) in 2004 (Centers for Disease Control and Prevention 2023).

Data sources

We obtained outcome data from the United States National Center for Health Statistics Vital Statistics System birth certificate data (National Center for Health Statistics 2024) and Merative MarketScan®, a longitudinal commercial insurance claims database, with birth outcome data from birth certificates and infant outcome data from Marketscan (Truven Health Analytics 2017). We obtained pregnancy-specific alcohol and drug policy data and data on cannabis legalization from NIAAA’s Alcohol Policy Information System (APIS) (NIAAA 2024), general population alcohol policies from the National Beverage Control Association Survey Database, APIS, Liquor handbooks, the Wine Institute, and original legal research (The International Culinary Schools at The Art Institutes 2010, Blanchette et al. 2020, National Alcohol Beverage Control Association 2024, NIAAA 2024), and tobacco policies from the Centers for Disease Control and Prevention and the American Nonsmokers Rights Foundation (Centers for Disease Control and Prevention 2021, American Nonsmokers’ Rights Foundation 2024).

The Vital Statistics sample included singleton births to residents of Texas and Florida with estimated dates of conception between September 2004 and August 2010 (three years before and three years after policy change). We included only singletons because multiples have different birthweight and gestation curves (Alexander et al. 1998). Individual-level birth outcomes included birthweight (continuous, 299–4455 grams, excluding implausible birthweights (Talge et al. 2014)), low-birthweight (dichotomous, <2500 grams), gestation (continuous, 21–45 weeks), and preterm birth (dichotomous, <37 weeks gestation). Potential individual-level covariates (all categorical) included: maternal age, parity, education, marital status, and race/ethnicity.

The MarketScan sample was a cohort of birthing person-infant dyads where the birthing person resided in Texas or Florida and had an estimated date of conception between March 2005 and August 2010 (two and a half years before and three years after policy change). The MarketScan sample begins in March 2005 because of criteria we used for developing the original MarketScan study cohort (Roberts et al. 2023a), which included the birthing person having been continuously enrolled for a full year before delivery. As MarketScan data are available beginning in 2005, we only included people who gave birth in 2006 or later. Full inclusion criteria were: female beneficiaries aged 25–50 who gave birth to a singleton at least 280 days after a previous birth, had been continuously enrolled one year before and one year after delivery, and could be matched under the same household with an infant who had at least one claim within the first month after delivery and was continuously enrolled for one year after birth (Roberts et al. 2023a). Birthing people aged <25 years were excluded because more than 70% could not be matched with an infant.

Infant outcomes were coded based on ICD-9 diagnosis codes and were dichotomous, coded as 1 if they had and 0 if they did not have one or more diagnoses in their first year. Infant injuries consistent with maltreatment was defined as an infant, within their first year after birth, having a claim for one or more injuries that previous research found to have positive predictive values >50% for maltreatment (e.g. abusive head trauma; rib fractures) (Syed et al. 2021). Infant morbidities related to maternal alcohol consumption was defined as an infant, within their first year after birth, having one or more morbidities previous literature has identified as being related to maternal alcohol use during pregnancy (e.g. lobulated, fused and horseshoe kidney; interruption of aortic arch and other congenital malformations of aorta) (O’leary et al. 2013). Potential individual-level covariates (both categorical) included birthing person’s age and health status, measured by the Elixhauser Comoridity Index (Elixhauser et al. 1998).

We merged policy and outcome data based on the estimated month of conception, meaning we considered the post-period to include people who became pregnant during the month the treatment state’s MWS-alcohol-pregnancy policy went into effect or later.

Statistical analysis

We used DID to compare changes in outcomes from pre- to post-periods in the treatment (Texas) as compared to comparison (Florida) state. We used multivariable linear regressions for each outcome, because linear regression coefficients are directly interpretable in terms of probabilities and nonlinear models such as logit and probit are unsuitable in the presence of interaction terms or fixed effects (Beck 2018, Gomila 2021). Models included indicators for state, policy period, and time (in quarters), an interaction between indicators for state and post-policy implementation (the average treatment effect on the treated or ATET), and relevant individual-level covariates. Among measured individual-level covariates, we tested for differential pre- to post-policy compositional changes between states and included in the model covariates that differentially changed. Robust standard errors were clustered by state.

A key assumption necessary to draw causal inferences from DID models is that outcome trends would have been the same in treatment and comparison states in the post-period absent the policy change. This counterfactual is inherently untestable. In practice, we test if pre-policy outcome trends were parallel in treatment and comparison states and assume trends would have remained parallel in the post-period, absent the policy change in the treatment state. We used post-estimation commands to visualize and test the parallel trends assumption, and report findings only for outcomes that met the assumption.

We conducted several sensitivity analyses, again testing the parallel trends assumption in each case. To assess whether associations may have been confounded by the increased tobacco tax in the treatment state, we estimated a DID model controlling for state-level per capita cigarette consumption (PCCC), which is the hypothesized mechanism through which tobacco tax policy affects birth outcomes. We also ran models moving the effective date of the policy forward by 6 months, which accounts for possible delays in policy implementation, business compliance, and/or consumer behavior change. We also used an alternative comparison state (Georgia), which has had an MWS-alcohol-pregnancy policy in place since 1986 (NIAAA 2024). Assuming that effects of Georgia’s policy had been realized by the start of our study period (almost 20 years later), we would expect Georgia’s birth and infant outcomes would remain stable over the study period and that Texas’s outcomes would change from pre- to post-policy time periods.

We considered p-values less than .05 statistically significant. Analyses were conducted in Stata 18. The University of California San Francisco IRB considered this de-identified data study exempt, and the Penn State IRB did not consider this study human subjects research.

Results

Sample description

Table 1 includes unadjusted outcomes as well as the sample size for pre- and post-periods in each state. Descriptively, mean birthweight was 3251 g pre- and 3244 g post-policy in treatment state (Texas) and 3252 g pre-and 3247 g post-policy in comparison state (Florida); low-birthweight was 6.7% both pre- and post-policy in Texas and 7.0% both pre- and post-policy in Florida. Mean gestation was 38.5 weeks pre- and post-policy in Texas, and 38.6 weeks pre- and post-policy in Florida; preterm birth was 12.1% pre- and 11.5% post-policy in Texas and 12.2% pre- and 12.0% post-policy in Florida. The proportion experiencing infant injuries was 1.4% pre- and 1.8% post-policy in Texas and 1.5% both pre- and post-policy periods in Florida. Infant morbidities was 2.9% pre- and 3.0% post-policy in Texas and 2.8% pre- and 3.4% post-policy in Florida.

Table 1.

Birth and infant outcomes in Texas and Florida before and after Texas’ Mandatory Warning Signs for alcohol use during pregnancy policy in September 2007.

Texas
 Florida
Pre-period Post-period Pre-period Post-period
Birth outcomesa,b
Total N 1,165,907 1,144,210 684,366 635,803
Birthweight mean g (SD) 3251 (533) 3244 (529) 3252 (545) 3247 (545)
Low birthweight % (n) 6.7 (78,420) 6.7 (76,746) 7.0 (47,839) 7.0 (44,702)
Gestation mean wks (SD) 38.5 (2.3) 38.5 (2.3) 38.6 (2.5) 38.6 (2.5)
Pre-term birth % (n) 12.1 (140,652) 11.5 (131,190) 12.2 (83,799) 12.0 (76,048)
Infant outcomesb,c
Total N 29,611 39,712 7600 14,363
Infant injuries % (n) 1.4 (410) 1.8 (701) 1.5 (117) 1.5 (210)
Infant morbidities % (n) 2.9 (852) 3.0 (1183) 2.8 (209) 3.4 (491)
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a

Pre-period is September 2004 to August 2007.

b

Post-period is September 2007 to August 2010.

c

Pre-period is March 2005 to August 2007.

Difference-in-difference results

Table 2 shows parallel trends assumption test results for main and sensitivity analyses. For main analyses, the parallel trends assumption was met for birthweight, low-birthweight, and infant injuries, but not for gestation, preterm birth, or infant morbidities.

Table 2.

Checks of whether parallel trends assumption was met for main analysis and each sensitivity analysis Texas’s MWS-alcohol-pregnancy policy as compared to Florida.

Sensitivity analyses
Main models Controlling for PCCC 6 month lag Georgia (which had policy entire time) as comparison state
parallel trends P-value parallel trends P-value parallel trends P-value parallel trends P-value
Birthweight .104 .121 .819 .022a
Low-birthweight .106 .107 .039a .039a
Gestation .012a .002a .005a .024a
Preterm birth .032a .034a .007a .094
Infant injuries .089 .060 .125 .337
Infant morbidities .044a .079 .228 .254
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Bold indicates meets parallel trends assumption (P > .05). Ns for each model vary slightly, depending on missingness for the variables, n = 3 592 942 for birthweight, n = 3 629 221 for low-birthweight, n = 3 614 245 for gestation, n = 3 630 047 for preterm birth. Infant maltreatment and morbidities each include n = 91 286. Models include individual-level covariates with a significant compositional change, quarter fixed effects, and robust standard errors clustered at the state level.

a

indicates P < .05.

Table 3 and Fig. 1 show results for main analyses. The decline in mean birthweight was differential by state, with an additional −4.06 g decline from the pre- to post-periods in the treatment as compared to the comparison state (ATET −4.06, 95% CI −7.02, −1.09). The difference in pre- to post-policy changes in low-birthweight across states was not statistically significant (ATET .0 pp 95% CI −.0, .0). Changes in infant injuries from pre- to post-policy were differential by state, with a .5 percentage-point greater change in the treatment pre-to-post policy relative to the comparison state (ATET .5 pp 95% CI .2, .8).

Table 3.

DID models, ATET of Texas’s MWS-alcohol-pregnancy policy as compared to comparison states main models and sensitivity analyses

Main models
 Sensitivity analyses
Controlling for PCCC
 6 month lag
 Georgia (which had policy entire time) as comparison state
ATET 95% CI P-value ATET 95% CI P-value ATET (95% CI) P-value ATET 95% CI P-value
Birthweight −4.055 −7.024, −1.087 .037 −3.779 −10.244, 2.696 .085 −4.808 −6.993, −2.624 0.023 - - -
Low-birthweight 0.000 −0.000, .000 .103 −0.000 −0.000, .000 .284 - - - - - -
Gestation - - - - - - - - - - - -
Preterm birth - - - - - - - - - −0.003 −0.005, −.001 .033
Infant injuries 0.005 0.002, .008 .030 0.006 −0.003, .016 .060 0.007 0.007, .007 .002 0.003 0.001, .004 .029
Infant morbidities - - - −0.004 −0.008, .000 .079 −0.004 −0.006, −.002 .022 −0.003 −0.006, −.000 .045
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Ns for each model vary slightly, depending on missingness for the variables, n = 3 592 942 for birthweight, n = 3 629 221 for low-birthweight. Infant maltreatment includes n = 91 286. - parallel trends assumption not met (see Table 2). Models include individual-level covariates with a significant compositional change, quarter fixed effects, and robust standard errors clustered at the state level.

Figure 1.

Figure 1

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DID main models examining changes in outcomes from before to after Texas’s MWS-alcohol-pregnancy policy in Texas and comparison state (Florida)

Sensitivity analyses

The parallel trends assumption was met in each sensitivity analysis for infant injuries and infant morbidities, in both the controlling for PCCC and 6-month lag sensitivity analyses for birthweight, in only the controlling for PCCC sensitivity analysis for low birthweight, and in only the comparison with Georgia sensitivity analysis for preterm birth (Table 2).

Table 3 and Fig. 2 show sensitivity analysis results. Findings for infant injuries were consistent across all sensitivity analyses, with the exception of slight shifts in point estimate and p-value shifting from less than .05 in main analyses to .060 in the sensitivity analysis controlling for PCCC. Findings for birthweight were consistent across sensitivity analyses for which the parallel trends assumption was met (PCCC and 6-month lag), again with slight shifts in point estimates and with p-value shifting from less than .05 in main analyses to .085 in the sensitivity analysis controlling for PCCC. Findings for low birthweight were consistent across the one sensitivity analysis for which the parallel trends assumption was met.

Figure 2.

Figure 2

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Sensitivity analyses

For infant morbidities, the ATET was not statistically significant at a P < .05 level in the PCCC sensitivity analysis, although had a similar P-value of .079 to birthweight and infant injuries. In the 6-month lag sensitivity analysis, changes in infant morbidities were differential by state, with infant morbidities increasing by .4 percentage points less from pre- to post-periods in the treatment relative to comparison state (ATET −.4 pp, 95% CI −.6, −.2, Fig. 2), with the graph suggesting that prevalence remained steady in the treatment state while increasing in the comparison state. The increase in infant morbidities was .3 percentage-points less from pre- to post-periods in Texas relative to Georgia (ATET −.3 pp, 95% CI −.6, −.0), with the graph suggesting prevalence remained relatively steady in the treatment state while increasing in the comparison state.

When using Georgia as the comparison, the decrease in preterm birth was .3 percentage-points more from pre- to post-period in the treatment relative to the comparison state (ATET −.3 pp, 95% CI −.4, −.1 preterm birth).

Discussion

In findings from our main analyses that met the key assumption for DID analysis, this study found that having an MWS-alcohol-pregnancy policy go into effect was robustly associated with decreased birthweight and increased infant injuries and no significant changes in other outcomes. These findings are inconsistent with the presumption that MWS-alcohol-pregnancy policies deter pregnant individuals from drinking and thereby improve birth and infant outcomes. These findings instead support previous research about MWS-alcohol-pregnancy policies that has also found increased adverse birth outcomes and infant injuries associated with MWS-alcohol-pregnancy policies using different study designs (Subbaraman and Roberts 2019, Roberts et al. 2023a). Having consistent findings across study designs strengthens confidence in the findings.

It is worth noting, though, that some findings from sensitivity analyses suggest that having the MWS-alcohol-pregnancy policy go into effect in Texas may have related to a less steep increase in infant morbidities than was occurring in comparison states.

It is also worth noting that the finding regarding infant injuries consistent with maltreatment was robust across sensitivity analyses. While research about the association between drinking during pregnancy and subsequent infant maltreatment is not conclusive (Austin et al. 2022), research consistently indicates that parental or caregiver drinking is associated with increased risk of child maltreatment and injury-related hospitalizations (Brummer et al. 2021, Leung et al. 2025). Combined with other research that suggests that MWS-alcohol-pregnancy policies relate to care avoidance (Subbaraman et al. 2018, Roberts et al. 2023a) these findings suggest that, when exposed to MWS-alcohol-pregnancy policies, people who drink alcohol during pregnancy may avoid care and thus be less likely to reduce drinking during pregnancy or more likely to resume drinking soon after pregnancy, thereby increasing the risk of an infant exposed to parental alcohol consumption and thus injury.

While the idea that MWS-alcohol-pregnancy policies could contribute to increased adverse health effects may seem counterintuitive, these findings are consistent with findings for MWS-cannabis-pregnancy (Roberts et al. 2022). They are also consistent with a recent systematic review on effects of alcohol warning labels on beverage containers that concluded that there was only low certainty that warning labels reduced consumption during pregnancy (Zuckermann et al. 2024) and a recent study in Chile that found pregnancy-specific alcohol warning labels may be less effective than alcohol warning labels focused on cancer risk for the general population (Schwartz et al. 2024). Research about tobacco warnings grounded in psychological theories of reactance offers a possible explanation. This research conceptualized reactance as an ‘emotional and cognitive resistance to a warning, characterized by (i) a perceived threat to one’s freedom, (ii) anger, and (iii) counterarguments against the warning such as denial or derogation’ (p. 737) (Hall et al. 2016). This study found that reactance to tobacco warnings was associated with lower perceived effectiveness of the warnings and ability to motivate people to quit smoking and was associated with greater avoidance of warnings. Thus, when warnings lead to reactance, this can weaken their intended effects. The research regarding MWS-cannabis-pregnancy was not informed by this theory. Yet, findings that pregnant people who used cannabis and lived in a state with MWS-cannabis-pregnancy believed that cannabis use during pregnancy was safer than pregnant people who used cannabis and lived in a state without MWS-cannabis-pregnancy are consistent with this theory as are findings that pregnant people who use cannabis do not think that there is currently strong enough scientific evidence on the adverse effects of using cannabis during pregnancy to justify MWS-cannabis-pregnancy (Roberts et al. 2023b, Gould et al. 2025). It is not clear whether findings from the research related to MWS-cannabis-pregnancy will generalize to MWS-alcohol-pregnancy, given differences in how established the evidence base is regarding effects of cannabis versus alcohol use during pregnancy (e.g. (O’leary and Bower 2012, Lo et al. 2025)), and different broader policy contexts. Thus, future research should examine whether MWS-alcohol-pregnancy might be operating similarly to MWS-cannabis-pregnancy, and also explore other possible explanations such as whether MWS-alcohol-pregnancy relate to increased stigma or fear.

It is also important to note that the policy change occurred eight months after Texas increased their tobacco tax, which means the tobacco tax change could have affected findings, especially if tax increase effects are delayed. However, as we would expect tobacco tax increases to increase birthweight, our estimate for the effect of the policy on decreased birthweight might be an underestimate of the true effect. In our sensitivity analysis adjusting for PCCC as a proxy for the tax change, effect magnitudes are similar, although findings are no longer statistically significant at a P < .05 level. This statistical significance change may be due to collinearity at the state-level between state, time, and cigarette consumption, thereby reducing power. It is also possible that the analyses with the tobacco tax policy represent the true effects of the MWS-alcohol-pregnancy policy, i.e. that there is not an adverse association of the MWS-alcohol-pregnancy policy with birthweight, and instead reflect the broader literature that finds benefits on birth outcomes associated with increased tobacco taxes (Hawkins et al. 2014, Hawkins et al. 2025).

This study has limitations that are important to consider. First, the policy in Texas is slightly different than many other MWS-alcohol-pregnancy policies in that the signs are required to be posted only on-premise alcohol consumption venues and not also in off-premise consumption venues (NIAAA 2024). If people respond differently to MWS-alcohol-pregnancy in on-premises venues versus off-premise venues, or pregnant people are more or less likely to be exposed to signs in one venue type, this might mean findings do not generalize. However, of states in the United States with MWS-alcohol-pregnancy policies, only one state has an off-premise only policy, indicating the on-premise requirement is typical even if the on-premise only requirement is a-typical. Second, the claims data have some limitations with respect to generalizability, as we had to exclude birthing people younger than 26 from analyses and the data only includes those with commercial insurance. Third, while the decreased birthweight finding is mostly robust across sensitivity analyses, the actual effect size is small. In the context of other studies that have found increases in low birthweight associated with MWS-alcohol-pregnancy policies across all United States over time (Subbaraman and Roberts 2019), though, one might view this small change in average birthweight in this study of one state as a signal of possible adverse public health effects. It is also similar in magnitude other recent studies of population-level effects of substance use policy, e.g. (Hawkins et al. 2025). Fourth, while we used a systematic approach to identify a policy change that did not co-commence with other substance use policy changes, there may have been other relevant unmeasured changes during the study period, which could be biasing findings. Fifth, only people exposed to the MWS-alcohol-pregnancy policy for their entire pregnancy are included in the treated group, which means the pre-period in the treatment state includes some people who were exposed to the policy for only some of their pregnancies. If we assume any effect of the policy was similar regardless of the proportion of pregnancy spent exposed, this would mean some Texas residents who conceived in the pre-period were mis-categorized as unexposed, which would bias effects towards the null.

Conclusion

Having a MWS-alcohol-pregnancy policy go into effect was associated with lower birthweight and more infant maltreatment. This study provides further evidence that MWS-alcohol-pregnancy policies are mostly ineffective and possibly harmful.

Acknowledgements

This work was supported by the United States National Institute on Alcohol Abuse and Alcoholism at the National Institutes of Health [Grant 2R01AA023267]. The content is solely the responsibility of the authors and does not necessarily represent the official views of the National Institutes of Health.

Footnotes

Competing interests

M.S.S. has received funding and travel support from the National Alcohol Beverage Control Association.

Data availability

Alcohol and Drug Pregnancy Policy data are publicly available through APIS. Both the Vital Statistics and insurance claims datasets are available to researchers via a data use agreement; per the terms of the agreements, the authors do not have permission to share the data.

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Associated Data

This section collects any data citations, data availability statements, or supplementary materials included in this article.

Data Availability Statement

Alcohol and Drug Pregnancy Policy data are publicly available through APIS. Both the Vital Statistics and insurance claims datasets are available to researchers via a data use agreement; per the terms of the agreements, the authors do not have permission to share the data.

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