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DID EARLY TWENTIETH-CENTURY ALCOHOL PROHIBITION AFFECT MORTALITY?

MARC T. LAW and MINDY S. MARKS∗

We investigate the contemporaneous mortality consequences of alcohol prohibition laws introduced in America between 1900 and 1920. We improve on existing studies by constructing a time-varying measure of prohibition at the state level that corrects for the timing of prohibition enforcement and accounts for the presence of dry counties. Using summary indices that aggregate alcohol-related mortality due to disease and poor decisions, we find that prohibition significantly reduced mortality rates. These findings are corroborated with an area-level analysis that exploits data on deaths in urban areas that were wet prior to statewide or federal prohibition and nonurban areas that were partially dry. (JEL I18, N4, K2)

I. INTRODUCTION

Public policies aimed at curbing alcohol consumption have been an important feature of the American regulatory landscape since the nineteenth century. By and large, the lit- erature suggests that current alcohol control policies pursued in the United States and elsewhere — for instance, minimum drinking age laws, taxes on alcohol beverages, and anti- alcohol campaigns — have had positive health and safety effects.1 In stark contrast, it is often argued that national prohibition of alcohol from 1920 to 1933 — the largest alcohol-control quasi-experiment ever conducted in American history — was a policy disaster. Thornton (1991, 8), for instance, reviews the data and litera- ture on the effects of national prohibition and concludes that it “failed to improve health and

∗Earlier versions of this paper were presented at the University of Manitoba, the International Workshop on the Analysis of Institutions at Xiamen University, and Vanderbilt University. We are grateful to Emily Beam, Lee Benham, Cheryl Long, the editor, and two anonymous referees for their comments and suggestions. Law: Full Professor, Department of Economics, University

of Vermont, Burlington, VT 05405, Phone 802-656-0240, Fax 802-656-8405, E-mail [email protected]

Marks: Associate Professor, Department of Economics, Northeastern University, Boston, MA 02115, Phone 617-373-2882, Fax 617-373-3640, E-mail [email protected]

1. See, for instance, Cheeson, Harrison, and Kassler (2000), Cook and Moore (2002), Fertig and Watson (2009), Carpenter and Dobkin (2009, 2011), and Bhattacharya, Gath- mann, and Miller 2013.

virtue in America.” More recent studies that take advantage of variation arising from state and federal prohibition statutes enacted during the early decades of the twentieth century reach ambiguous conclusions regarding the health and safety impacts of alcohol prohibition.2 Given that alcohol prohibition is still a widely used pol- icy worldwide — for instance, alcohol sales are restricted in most of the Middle East as well as parts of Africa and South Asia, and there are still dry counties in the United States — it is important to resolve the question of how prohibition affects health and safety.

On the one hand, it seems reasonable to think that prohibition should have positive effects on health and safety. Banning the sale or production of alcohol should reduce its consumption by more than the imposition of alcohol taxes or minimum drinking age laws. While there is some evidence that low to moderate levels of alcohol consump- tion may be beneficial, it is widely agreed that, beyond a small amount, the health and safety dan- gers of alcohol are an increasing function of the quantity consumed (National Institutes of Health 2000). Policies that have large negative effects

2. See Miron (1999), Dills and Miron (2004), Dills, Jacobson, and Miron (2005), Owens (2011), Depew, Edwards, and Owens (2013), Evans et al. (2016), and Livingstone 2016.

ABBREVIATIONS

GDP: Gross Domestic Product

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Economic Inquiry (ISSN 0095-2583) Vol. 58, No. 2, April 2020, 680 – 697

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on consumption should therefore have large posi- tive effects on health and safety if the initial level of alcohol consumption is high. This may have been especially true in United States at the turn of the twentieth century, a setting where alco- hol abuse was a serious social menace, the health risks of excessive alcohol consumption were not well understood, and high transportation costs made evasion of local prohibition laws costly (Okrent 2011). On the other hand, it is possible that the positive effects of prohibition on health and safety were mitigated if not even reversed if the prohibition laws were poorly enforced; if pro- hibition, by creating black markets, gave rise to organized crime and greater violence; or if pro- hibition resulted in a substitution away from beer and wine and into stronger and more dangerous forms of alcohol (Edwards and Howe 2015).

In this study, we shed light on this puzzle by examining the impact of local, state and federal prohibition exposure between 1900 and 1920 on a wide range of alcohol-related mortality out- comes. We improve on the existing literature in three main ways. First, we construct a more accurate measure of exposure to prohibition that (1) accounts for gaps between the dates when state prohibition laws were enacted and when they became effective and (2) adjusts for the fact that within many states, local governments enacted and repealed county-level alcohol prohi- bition ordinances prior to the adoption of state or federal prohibition. This should reduce measure- ment error in prohibition exposure that may have biased previous regression estimates toward zero.

Second, we scoured the United States Mor- tality Statistics for a wider range of state-level mortality outcomes than previously investigated by this literature.3 Specifically, we gathered data on deaths due to “alcoholism,” cirrho- sis, other liver diseases, circulatory disease, ulcers, diseases of the stomach, peritonitis, infant mortality, suicides, accidents, homicides, and syphilis — essentially any mortality outcome reported consistently in the Mortality Statistics that might be plausibly related to excessive alco- hol consumption, either through its direct effect on disease or through its indirect effect on human behavior. This all-inclusive approach gives us a more comprehensive picture of the impact of prohibition on health and safety outcomes.

Third, to provide a closer match between pro- hibition exposure and alcohol-related mortality

3. Unfortunately, county-level data on mortality out- comes was not collected during this period.

outcomes, we collected data on exposure to pro- hibition and a limited set of alcohol-related death rates for urban and nonurban areas within states. Specifically, we gathered annual data from 1910 to 1920 on cause-specific mortality rates and pro- hibition for 23 urban areas and 12 nonurban areas located within 12 states. This allows us to com- pare the differential impact of the passage of state or federal prohibition on cities that were wet and nonurban areas in the same state that were already partially dry. With this approach, we can include state-by-year fixed effects that absorb any time- varying state-specific factors that may bias esti- mates that rely on state-level variation.

Using state-level data, we estimate a continu- ous treatment difference-in-differences model of the impact of prohibition on mortality outcomes. We find that early twentieth-century prohibition laws had sizeable negative impacts on mortal- ity. We show that the magnitude and precision of our results is sensitive to how prohibition is mea- sured. Our main findings are robust to the inclu- sion of state-specific trends. Importantly, while we find that prohibition reduced mortality due to alcohol-related causes, we find no relation- ship between prohibition and causes of death that are not alcohol related. Finally, using data on urban and nonurban areas within states reinforce the conclusion that prohibition reduced alcohol- related sources of mortality. Accordingly, the evi- dence accumulated suggests that early twentieth- century prohibition laws had salutary effects on health and safety.

II. HISTORICAL BACKGROUND

The temperance movement and its efforts to secure government policies to reduce the availability of alcoholic beverages have a long and well-documented history (see Okrent 2011 for a recent overview). From the mid-nineteenth century onward, temperance campaigners — coalescing under the banners of the Anti-Saloon League and, later, the Women’s Christian Temperance Union — lobbied against brewers, alcohol manufacturers, and saloon owners to secure local (municipal and county), state, and national laws that made it illegal to sell and/or manufacture alcohol. During the early 1900s, temperance campaigners were success- ful in securing prohibition ordinances at the city or county level that proved quite durable, some even to the present day. The number of dry counties in wet states increased from 162 in 1900, to 772 in 1905, and reached 1,030

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TABLE 1 Prohibition among Registration States

Year Statewide

Prohibition Enacted

Date Statewide

Prohibition Became Effective

Share of State Population in a Dry County in Year Prior to

State or Federal Prohibition

Year State Enters the

Registration Area

California 0.302 1906 Colorado 1914 January 1, 1916 0.574 1906 Connecticut 0 1900 Delaware 0.340 1919 Florida 1918 January 1, 1919 n/a 1919 Illinois 0.237 1918 Indiana 1917 April 1, 1918 0.612 1900 Kansas Pre-1900 n/a 1914 Kentucky 1919 January 1, 1920 0.728 1911 Louisiana 0.395 1918 Massachusetts 0.059 1900 Maryland 0.337 1906 Maine Pre-1900 n/a 1900 Michigan 1916 April 30, 1918 0.369 1900 Minnesota 0.670 1911 Missouri 0.445 1911 Mississippi 1908 December 1, 1908 n/a 1919 Montana 1916 January 1, 1919 0 1910 North Carolina 1908 January 1, 1909 n/a 1910 Nebraska 1916 May 1, 1917 n/a 1920 New Hampshire Pre-1900, 1917a May 1, 1918 0.198 1900 New Jersey 0 1900 New York 0.028 1900 Ohio 1918 May 27, 1919 0.062 1909 Oregon 1914 January 1, 1916 n/a 1918 Pennsylvania 0.267 1906 Rhode Island 0.071 1900 South Carolina 1915 January 1, 1916 n/a 1916 South Dakota 1916 July 1, 1917 n/a 1906 – 1909b

Tennessee 1909 July 1, 1909 n/a 1917 Utah 1917 August 1, 1918 0.450 1910 Virginia 1914 November 1, 1916 0.740 1913 Vermont 0.519 1900 Washington 1914 January 1, 1916 0.032 1908 Wisconsin 0.007 1908

aNew Hampshire repealed prohibition before 1900 and enacted it again in 1917. bSouth Dakota entered the registration area in 1906 and exited in 1909. Source: See Appendix for details.

by 1910. State-level prohibition soon followed beginning with Georgia and Oklahoma in 1907. The movement’s ultimate objective — national prohibition that banned the production, sale, and distribution of alcohol throughout the United States — was obtained in 1920 with the pas- sage of the Eighteenth Amendment to the US Constitution and the Volstead Act. While many factors, including the Progressive movement and the rise of women’s suffrage, contributed to the timing of national prohibition, the passage of the Sixteenth Amendment in 1913, which created the federal income tax and reduced the national government’s reliance on liquor tax revenues, was undoubtedly critical (Okrent 2011).

Table 1 presents data on the timing of pro- hibition laws for the 35 states that were within the Mortality Statistics’ registration area between 1900 and 1920. For each of these states we report the year in which its prohibition law was enacted, the date at which its prohibition law became effective, and the year in which the state entered the Mortality Statistics registra- tion area. Additionally, because many states con- tained numerous dry counties prior to state or federal prohibition, we also display an estimate of the share of a state’s population that lived in a dry county in the year before state or federal prohibition was enacted (see section A1 for more information on the construction of this estimate).

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For most states, there was a time lag of at least 1 year between the adoption of a statewide pro- hibition statute and the date it became effective. Additionally, for many Americans, exposure to prohibition was a fact of life even before state and federal governments became involved in banning the production and sale of alcoholic beverages. For instance, in Kentucky, Virginia, and Min- nesota, more two-thirds of the population lived in a dry county prior to the passage of statewide or federal prohibition.

III. LITERATURE REVIEW

The dangers of excessive alcohol consumption for public health and safety are well documented. Heavy drinking is associated with an increased risk of liver disease, circulatory disease, high blood pressure, diseases like pancreatitis, peri- tonitis, gastritis and ulcers, and infant mortality (for an overview see Rehm 2011). Additionally, by adversely affecting decision-making, alco- hol abuse correlates with an increased incidence of suicides, accidents, homicides, and sexually transmitted illnesses (Bates 1918; Brown and Todd Jewell 1996; Chatterji et al. 2004; Gyimah- Brempong 2001; Wasserman 1989).

A large literature examines the effects of contemporary alcohol control policies like alco- hol taxes, minimum drinking age regulations, county-level prohibitions, and anti-alcohol cam- paigns. Taking advantage of state-level varia- tion in alcohol tax rates, Cheeson, Harrison, and Kassler (2000) find that higher alcohol taxes reduce gonorrhea and syphilis rates. Carpen- ter and Dobkin (2009, 2011) show that higher state-level minimum drinking age laws reduce mortality rates due to motor vehicle accidents, alcohol-related deaths, and suicides. Fertig and Watson (2009) and Barreca and Page (2015) estimate that increases in minimum drinking age laws reduce the incidence of adverse birth outcomes among young mothers. Bhattacharya, Gathmann, and Miller (2013), take advantage of cross-region variation in the intensity of Gor- bachev’s 1985 – 1988 anti-alcohol campaign and find that it disproportionately reduced mortality in regions where the campaign was more intense. Wasserman, Varnik, and Eklund (1994, 1998) also find that the Gorbachev anti-alcohol cam- paign reduced the incidence of suicide.

Not all studies, however, find that current alcohol control policies have positive effects on safety. For instance, Conlin, Dickert-Conlin, and Pepper (2005) find that counties in Texas that

prohibit alcohol have higher mortality rates due to increased use of illicit drugs. Baughman et al. (2001) find that prohibiting the sale of beer and wine at the county level increases automobile fatalities. The health and safety impacts of min- imum drinking age laws are also ambiguous, with some studies showing no impact on pedes- trian deaths, drowings, or crime (Howland et al. 1998; Joksch and Jones 1993; Jones, Pieper, and Robertson 1992). Accordingly, while the bulk of the evidence suggests that alcohol control laws have positive effects on health and safety (see Cook and Moore 2002 for a survey), this conclu- sion is not uniformly supported in the literature.

Ambiguous evidence also emerges from the body of scholarship that examines the health effects of state and federal alcohol prohibition statutes adopted during the late nineteenth and early twentieth centuries. Dills and Miron (2004), taking advantage of cross-state variation in the timing of state-level prohibition as well as the adoption and repeal of national prohibition, find that state-level prohibition had no effect on cir- rhosis death rates but federal prohibition tem- porarily reduced them by 10% – 20%. Depew, Edwards, and Owens (2013) estimate that state- level prohibition reduced infant mortality rates due to external causes (violence, neglect, and accidents) but not due to internal causes (sick- ness or congenital disorders). Jacks, Pendakur, and Shigeoka (2017) look at the repeal of national prohibition in 1933 on county-level infant mortal- ity, using as a control the fact that some counties remained dry in the post-prohibition period, and find that repeal resulted in an increase in infant mortality rates.4

The findings of studies that examine the impact of early prohibition on public safety outcomes are also ambiguous. Miron (1999), using national time series data, argues that federal prohibition increased homicides. Exploit- ing cross-state variation in the passage and repeal of state-level prohibition laws, Owens (2011) finds that prohibition had no impact on state-level homicide rates. Employing a similar source of variation but using city-level homicide data, Livingstone (2016) finds that prohibition decreased homicide rates but only for a 3-year

4. Evans et al. (2016) examine the long-run impact of in utero exposure to state-level prohibition on adult educational attainment, obesity and height using data on World War II recruits and find that individuals who were born after state- level prohibition was enacted attained more education and were less likely to be obese but were no taller than their preprohibition counterparts.

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period, after which homicides returned to their preprohibition levels. Finally, Bodenhorn (2016) takes advantage of cross-county differences in the enforcement of South Carolina’s 1893 prohibition statute and finds that in counties that enforced the law more vigorously, prohibition increased the homicide rate by 30% – 60%.

We believe that measurement error in expo- sure to prohibition contributes to the ambigu- ity in the estimates of the impact of prohibi- tion on health and safety outcomes. One source of measurement error arises because of gaps between the dates in which state-level prohibi- tion laws were enacted and the dates when they became effective. Much of the literature that exploits state-level variation in the adoption of prohibition uses the year in which prohibition is enacted as the start date of prohibition expo- sure. However, as shown in Table 1, for most states, there was a time lag, in some instances of 2-years’ duration, between when statewide pro- hibition was enacted and when it took effect. The approach taken by this literature will there- fore include in its measure of prohibition some state-years where statewide prohibition was not yet enforced. Mismeasurement of a dichotomous independent variable invariably leads to attenu- ation bias (Aigner 1973). Second, none of these studies account for the fact that prior to state or federal prohibition, a growing number of locali- ties were already dry. During this period, many localities enacted and repealed county-level pro- hibition ordinances. Accordingly, the prohibition exposure variable used by these studies, which is coded as 0 in all years prior to the adoption of state-level prohibition, will underestimate the true reach of prohibition prior to statewide prohi- bition, and miss important temporal variation as well.5

Additionally, we improve on the literature by examining the impact of prohibition exposure on a larger set of mortality outcomes. Most studies of early prohibition only focus on a few narrowly defined mortality outcomes. There are several advantages to examining the impact of prohibition on a larger number of mortality

5. Some studies account for the fact that statewide prohi- bition varied in terms of strictness (see, for instance, Owens 2011). In all states that enacted prohibition, commercial sales of alcohol were prohibited. However, in only a handful of states — sometimes called “bone-dry” states — it was illegal to import alcohol from out of state. We are unable to use vari- ation in bone-dry status because we do not know whether county ordinances were bone dry or not and we only have usable variation in bone-dry status for four states in our sam- ple (Colorado, Montana, Utah, and Washington).

outcomes. First, the Mortality Statistics include data on some mortality outcomes (for instance, deaths due to “alcoholism”) that should be related to excessive drinking but have not yet been investigated. Examining a broader range of mortality outcomes will yield a more com- prehensive picture of the effects of prohibition. Second, in an environment where statistical power is a challenge, it is helpful to look at a broad range of outcomes. As shown by Kling, Liebman, and Katz (2007) individual mortality outcomes that are marginally significant may aggregate into an index that is statistically sig- nificant if the effects work in the same direction. Following Kling, Liebman, and Katz (2007), Anderson (2008), and Hoynes, Schanzenbach, and Almond (2016), we sum the z-scores of indi- vidual mortality outcomes into two standardized mortality indices. Because excessive alcohol consumption may contribute to mortality either directly through a disease (for instance, cirrho- sis) or indirectly through poor decision-making (suicide or venereal disease), we construct a disease-mortality index and a poor decisions mortality index.

The use of summary indices has two addi- tional benefits. First, by aggregating mortality outcomes, we protect ourselves from multiple hypothesis testing bias (i.e., finding statistically significant results simply because we are con- sidering more outcomes). This is because the likelihood of a false positive does not increase as more outcomes are added to the index. Sec- ond, aggregation helps account for the possibil- ity that causes of death were misclassified in the Mortality Statistics. For instance, cirrhosis deaths could have been coded as deaths due to some other liver disease. Similarly, heart fail- ure caused by excessive drinking, a condition known as alcoholic cardiomyopathy, might have been classified as death due to circulatory dis- ease or simply as “alcoholism.” The extant lit- erature, by only looking at narrowly defined mortality categories, may therefore be under- counting the true alcohol-related mortality rate and consequently underestimating prohibition’s impact.

IV. DATA

Our primary data source for health and safety outcomes is the Census Bureau’s Mortality Statistics (for more details see section A2). Pub- lished annually, the Mortality Statistics contain comprehensive data on cause-specific mortality

LAW & MARKS: PROHIBITION AND MORTALITY 685

at the state level, and, for a more limited set of mortality outcomes, at the city-level. For our primary analysis, we gathered state-level mortality data for each year from 1900 to 1920 on all (mutually exclusive) reported causes of deaths that might be related to excessive alcohol use, either directly through disease or indirectly through behavior. This included deaths due to alcoholism, cirrhosis, other diseases of the liver, peritonitis, ulcers, other diseases of the stomach, homicides, and syphilis, which we inputted directly from the Mortality Statistics tables. We also have state-level data on deaths due to cir- culatory disease, accidents, suicides, deaths due to all causes, and infant mortality deaths from Miller (2006). Accidents include deaths due to fractures and dislocations, burns and scalds, heat and sunstroke, cold and freezing, lighting, drowning, inhalation of poisonous gases, acci- dental poisonings, accidental gunshot wounds, injuries by machinery, injuries in mines and quarries, railroad accidents, streetcar accidents, injuries by vehicles and horses. We normalized each mortality outcome by total state-year pop- ulation to obtain cause specific mortality rates (per 100,000).

We subtracted all alcohol related mortality rates from the total mortality rate to obtain a mea- sure of all nonalcohol-related deaths. Our result- ing state-year panel data set is incomplete and unbalanced because not all states were within in the Mortality Statistics registration area during this period, and those that were within the reg- istration area joined in different years.

Using these cause-specific mortality rates, we computed two summary indices that aggregate mortality due to disease (alcoholism, circulatory disease, cirrhosis, liver diseases, infant mortal- ity, peritonitis, ulcers, and diseases of the stom- ach) and deaths due to poor decisions (accidents, homicides, suicides, and syphilis).6 These sum- mary indices are computed as the unweighted sum of the z-scores for each of the individual mor- tality rates within each index. Kling, Liebman, and Katz (2007) suggest calculating the z-scores by subtracting the control group mean and divid- ing by the control group standard deviation. Since we have a quasi-experimental design, the con- trol group in our setting consists of state-years

6. We include infant mortality in the disease index because excessive drinking during pregnancy can cause deaths due to fetal alcohol syndrome. However, it is also pos- sible that access to alcohol harms infants through an environ- mental or behavioral channel, for instance, due to neglect or abuse, or the reallocation of household resources away from childcare.

in which no prohibition laws were in place (i.e., wet state-years). As a result, for control group state-years, the mean incidence of a given cause of mortality is normalized to equal 0 and to have a standard deviation equal to 1.

Specifically, the indices were constructed as follows. Let Mdst denote the mortality rate from cause d in state s in year t. Let 𝜇dw and 𝜎dw denote the mean and standard deviation of the same cause-specific mortality rate in wet state- years. The z-score for mortality cause d in state s in year t is defined as:

(1) Zdst = (Mdst − μdw)∕σdw where Zdst tells us, in standard deviation units, how much a given cause of death varies relative to the mean in wet state-years. After computing Zdst for each cause of death, we summed Zdst across all alcohol-related diseases to obtain the disease index and we summed Zdst across all causes of death that are related to poor decision-making to construct the poor decisions index. Accordingly, each cause of death receives equal weight within each index.7

Aggregation using these indices has the ben- efit of increasing statistical power if the effect of prohibition goes in the same direction across multiple causes of death. Suppose that in a given state-year, prohibition is associated with one dis- ease in the index increasing by one standard devi- ation and another falling by one standard devi- ation. In this case, the index will equal 0 and, in a regression with the index as the dependent variable, the coefficient on prohibition exposure will be statistically indistinguishable from zero. However, if both diseases fall by 1 standard devi- ation, then the index will take a value of −2 standard deviation units. The index will therefore become larger in magnitude and the estimated coefficient on prohibition exposure is more likely to attain statistical significance if prohibition

7. One could also aggregate by summing the mortality rates. A shortcoming of this approach is that it places greater weight on those causes of death that are more common. As shown in Table 2, some alcohol-related causes of death are much more common than others. For instance, in wet state-years, the mean infant mortality rate was 21 times the mean cirrhosis mortality rate (300 deaths per 100,000 vs. 14 deaths per 100,000). Suppose cirrhosis deaths were to fall by 50% (an approximately two SD decrease) and infant mortality rates were to rise by 5% (0.29 SDs). If we were to aggregate by summing mortality rates, it would appear that prohibition increased mortality. By constructing our indices using z-scores, we avoid this problem. With z-scores we allow a 1 standard deviation change to count the same across all causes of death, regardless of the widely varying underlying incidence of each cause of death.

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reduces mortality across numerous causes of death.

Our measure of prohibition coverage is the fraction of a state’s population that lives in a dry area in each year.8 For years prior to the date at which state or federal prohibition became effective, this variable is measured as the share of a state’s population that lives in a dry county. To estimate this share, we combined Sechrist’s (2012) county-year data on whether a county had a local prohibition ordinance with county-level population counts collected from the decennial U.S. Censuses, linearly interpolated for non- census years. We collected data on the year that statewide prohibition became effective from Pickett, Wilson, and Smith (1917) and the National Association of Distillers and Wholesale Dealers (1918), updated and cross-checked by searching the websites of historical societies. Our exposure to prohibition variable is coded as a 1 in the year that state or federal prohibition became effective. If state prohibition became effective mid-year, we pro-rate by the fraction of the year in which state prohibition was effective, adjusting for county-level prohibition exposure from the previous year.9

As noted earlier, our measure of prohibition coverage differs from the literature because (1) we account for county-level exposure prior to state or federal prohibition; and (2) we use the date that state prohibition became effective rather than the date in which state prohibition was adopted. Figure 1 shows three different measures of prohibition exposure for the states in the registration area. The first measure, Statewide_Dry_Enacted, nei- ther accounts for county-level exposure nor adjusts for the date that prohibition became effective. This variable is used by the existing

8. It is important to note that this approach implicitly assumes that local, state, and national prohibition have the same effect as long as they increase the share of the population exposed to prohibition by the same increment. If enforcement varied by level of government then this assumption may be unwarranted. However, the direction of bias is unclear. Local and state laws may have had a smaller effect than federal pro- hibition if they could be easily evaded by purchasing alcohol in nearby wet areas. On the other hand, it is possible that state and local authorities were more committed to enforcement than federal authorities. Accordingly, it is unclear whether we have under or over-estimated the impact of prohibition.

9. Sechrist (2012) did not collect data on county-level prohibition after a state-level prohibition law is enacted. Accordingly, in cases where there is more than 1-year gap between the date in which statewide prohibition is enacted and the date it becomes effective, we use information on county-level prohibition from the year prior to the enactment of statewide prohibition.

literature to measure prohibition. The second, Statewide_Dry_Effective, adjusts for the date that statewide prohibition became effective but does not account for prior county-level prohibition. The third, Share_Dry, is our pre- ferred measure that accounts for both sources of measurement error. As shown in the figure, Statewide_Dry_Enacted, the variable used by the literature, underestimates prohibition coverage by failing to account for county-level prohibition and overestimates prohibition coverage by using the enactment date rather than effective date.

For control variables, we followed the litera- ture and gathered state-year data from the decen- nial population censuses linearly interpolated for noncensus years on urbanization, the share of the population that was non-White, the share that was foreign born, the share that was female, the share that was between 15 and 25 years of age, the share that was at least 65 years old, and the illit- eracy rate. We collected data on the share of the population that was Catholic from the Censuses of Religious Bodies for 1890, 1906, 1916, and 1926, linearly interpolated for missing years. As noted by Lewis (2008) and Owens (2011), states that adopted prohibition were rural, heavily con- centrated in the south and the west, had fewer immigrants, and had disproportionately evangeli- cal protestant populations. We also gathered data on state-level women’s suffrage since the liter- ature also suggests that the women’s suffrage movement influenced the timing of prohibition.

Table 2 presents the summary statistics sep- arately for three groups: “dry” state-years (i.e., state-years where either state or federal pro- hibition was in effect), “semi-dry” state-years (i.e., state-years where there is only county- level prohibition), and “wet” state-years (i.e., state-years where there is no prohibition what- soever). Of the total number of state-years in our sample (N = 405), 23% are dry, 44% are semi-dry, and 32% are wet. Prohibition expo- sure was substantial in state-years where there was only county-level prohibition: in semi-dry state-years, the mean prohibition exposure is 0.23. For every alcohol-related disease mortal- ity outcome except ulcers and diseases of the stomach, mortality rates are lower in dry state- years than those in semi-dry state-years, and lower in semi-dry state-years than those in wet- state-years. For instance, death rates due to cir- rhosis are 14.3 per 100,000 in wet state-years, 11.9 per 100,000 in semi-dry state-years, and 6.8 per 100,000 in dry state-years. The disease index that aggregates over these mortality rates,

LAW & MARKS: PROHIBITION AND MORTALITY 687

FIGURE 1 Prohibition Exposure in the Registration Area

Note: Statewide_Dry_Enacted neither accounts for county-level exposure nor adjusts for the date that prohibition became effective. Statewide_Dry_Effective adjusts for the date that statewide prohibition became effective but does not account for prior county-level prohibition. Share_Dry accounts for both sources of measurement error.

reinforces this conclusion. Mortality rates due to alcohol-related diseases were 3.89 standard deviation units smaller in semi-dry state years than in wet state-years, and 8.67 standard devia- tion units smaller in dry state-years than in wet state-years. Greater prohibition exposure there- fore appears to be correlated with better alcohol- related disease mortality outcomes. For mortality rates due to poor decisions, the evidence is more mixed. Deaths rates due to accidents fall as a state-years become drier, but not death rates due to homicides, suicides, or syphilis. Impor- tantly, mortality rates from all other causes of death (not alcohol related) are similar across dry, semi-dry, and wet state-years, which suggests that overall health is uncorrelated with prohibi- tion coverage. The share of the population that was female, between 15 and 25 years old, and at least 65 years old was nearly identical across dry, semi-dry, and wet state years. Consistent with the literature, we find that drier state-years have smaller populations, are less urbanized, have smaller non-White population shares, smaller

Catholic population shares, smaller foreign-born population shares, and are more likely to have female suffrage. It will be therefore important to control for these factors in our regression analysis.

V. EMPIRICAL FRAMEWORK AND REGRESSION RESULTS

To determine the impact of prohibition laws on mortality rates, we estimated the following continuous treatment difference-in-differences regression model: (2)

Mdst = βShare Dryst + Xstδ + γs + λt + ϵdst

The dependent variable in this regression, Mdst is the mortality rate from cause d per 100,000 people in state s in year t. We estimated this regression separately for eight different disease- specific mortality rates related to chronic alco- hol consumption and for four causes of death that may be due to poor decision making brought

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TABLE 2 Descriptive Statistics for Dry State Years, Semi-Dry State Years, and Wet State Years, 1900 – 1920

Dry Semi-Dry Wet

Mean SD Mean SD Mean SD

Share_Dry 1 0.23 0.23 0 Alcoholism 1.33 0.98 4.53 2.06 6.16 2.02 Circulatory 141.45 40.89 153.54 34.63 166.16 35.22 Cirrhosis 6.82 1.94 11.88 2.98 14.3 3.48 Infant mortality 211.91 61.61 237.3 58.78 301.19 52.72 Liver 4.89 1.72 5.11 1.52 5.42 1.65 Peritonitis 2.75 2.56 3.38 2.71 5.86 3.77 Stomach 10.91 6.02 12.41 5.46 9.64 4.62 Ulcers 3.51 0.9 3.87 0.94 3.49 0.87 Disease index −8.67 3.69 −3.89 3.51 0 3.87

Accidents 73.34 12.9 85.08 14.69 90.37 17.13 Homicides 6.68 4.34 6.8 4.86 3.43 2.27 Suicides 10.54 3.6 14.92 5.19 14.25 3.28 Syphilis 8.08 3.62 7.42 2.86 4.53 1.81 Decision index 1.06 3.06 2.59 3.72 0 3.05

All other causes 909.19 191.55 902.05 179.39 938.11 144.61

Catholic 0.15 0.10 0.19 0.08 0.25 0.07 Foreign born 0.13 0.09 0.17 0.08 0.26 0.06 Illiteracy 0.06 0.05 0.05 0.02 0.05 0.01 Nonwhite 0.10 0.15 0.04 0.05 0.02 0.01 Suffrage 0.60 0.49 0.20 0.4 0.02 0.15 Urban 0.48 0.20 0.58 0.17 0.70 0.15 Female 0.49 0.01 0.49 0.01 0.49 0.01 Young 0.18 0.01 0.18 0.01 0.19 0.01 Old 0.05 0.01 0.05 0.01 0.05 0.01

Population (in millions) 3.14 2.74 4.65 2.78 4.96 3.16 N 95 180 130

Notes: Cause-specific mortality variables are measured as deaths per 100,000 population. The disease and decision indices are summary indices constructed as the unweighted average of the z-statistics for each mortality rate within the index. Share_Dry, catholic, foreign born, illiteracy, urban, nonwhite, female, young, and old are measured as fractions of state population. Suffrage is an indicator variable equal to 1 if a state has enacted female suffrage in a given state year and 0 otherwise. A state-year is defined as “Dry” if Share_Dry is equal 1 (i.e., if statewide or federal prohibition is in place), “Wet” if Share_Dry is equal to 0, and “Semi-Dry” if Share_Dry is greater than 0 but less than 1.

about by excessive drinking. We also estimate this regression using the alcohol-related disease index and poor decisions index as the depen- dent variable.

Our treatment variable, Share_Dryst is the share of the population of state s that lives in a dry county in year t. This measure of prohibition corrects for the two sources of measurement error discussed earlier. Share_Dryst is a time-varying continuous variable that falls within the interval [0, 1]. Accordingly, the coefficient 𝛽 will capture the mortality effect of a state switching from com- pletely “wet” to completely “dry.”

The regressions include a fixed effect for each state (𝛾s) to remove time-invariant dif- ferences among the states as well as a fixed effect for each year (𝜆t) to absorb year to year variation in mortality. Despite the continuous

nature of our treatment variable, this formu- lation retains the basic features of a standard difference-in-differences model. Xst is a vector of state-year controls. To probe the robustness of our difference-in-differences identification framework, in some specifications we also include state-specific time trends among the regressors in Xst. Finally, 𝜖dst is an error term. Under the assumption that that 𝜖dst is uncorre- lated with prohibition exposure, the regression model will yield unbiased estimates of 𝛽.10

10. Some studies of prohibition use population-weighted regressions (Depew et al. (2013); Owens 2011). When we use population weights the point estimates are slightly smaller. For instance, for the disease index, the coefficient on Share_Dry is −2.144 (SE of 0.516) when we weight by pop- ulation and −2.735 (SE of 0.842) when we do not weight. A full set of results is available upon request.

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TABLE 3 Impact of Early Prohibition on Disease Outcomes, 1900 – 1920

Panel A: Results Using Share_Dry to measure prohibition exposure

Alcoholism Circulatory

Disease Cirrhosis Infant

Mortality Liver

Diseases Peritonitis Stomach Diseases Ulcers

Disease Index

Share_Dry −2.648*** −6.587* −0.644 −11.71 −0.178 0.011 −1.366 −0.406** −2.735*** (0.822) (3.69) (0.445) (8.149) (0.275) (0.429) (1.075) (0.192) (0.842)

N 405 405 405 405 405 405 405 405 405 R2 .833 .966 .901 .95 .796 .897 .884 .688 .917

Panel B: Results Using Statewide_Dry_Enacted to measure prohibition exposure

Alcoholism Circulatory

Disease Cirrhosis Infant

Mortality Liver

Diseases Peritonitis Stomach Diseases Ulcers

Disease Index

Statewide_Dry_ −0.361 −4.723* −0.009 −2.549 0.008 −0.203 −0.312 −0.200 −0.705 Enacted (0.482) (2.602) (0.330) (6.398) (0.186) (0.293) (0.975) (0.156) (0.640) N 405 405 405 405 405 405 405 405 405 R2 .812 .966 .900 .949 .796 .898 .882 .686 .910

Panel C: Results Using Share_Dry to measure prohibition exposure and including state-specific trends

Alcoholism Circulatory

Disease Cirrhosis Infant

Mortality Liver

Diseases Peritonitis Stomach Diseases Ulcers

Disease Index

Share_Dry −2.833** −6.868** −1.251*** −7.622 −0.227 0.279 −0.410 −0.744** −3.072*** (1.124) (3.325) (0.338) (6.435) (0.341) (0.539) (0.637) (0.336) (0.938)

N 405 405 405 405 405 405 405 405 405 R2 .859 .981 .930 .972 .817 .925 .940 .713 .940

Notes: Each column represents a separate regression. State and year fixed effects are included in each regression, as well as state-year controls for the literacy rate, the urbanization rate, the non-White share of the population, the share of the population that is catholic, an indicator variable for whether a state has women’s suffrage in effect, the foreign-born share of the population, the share that was female, the share that was young, and the share that was old. Share_Dry is our preferred measure of prohibition exposure. Statewide_Dry_Enacted is the binary measure of prohibition used by the literature. The units of all dependent variables except the disease index are deaths per 100,000. The disease index is the unweighted sum of the z-scores for each of the individual mortality rates. Robust standard errors clustered by state are reported in parentheses.

*denotes statistical significance at the 10% level; **denotes statistical significance at the 5% level; ***denotes statistical significance at the 1% level.

Panel A of Table 3 displays our estimates of the impact of prohibition exposure on mortality rates due to diseases that are alcohol related. Standard errors, clustered at the state-level, are reported in parentheses.11 The coefficient on the treatment variable is negative for seven out of eight of the mortality rates. We find that if a state switched from being entirely wet to entirely dry, there would be 2.65 fewer deaths per 100,000 for alcoholism, 6.59 fewer deaths per 100,000 from circulatory disease, and 0.41

11. Abadie et al. (2017) suggest that clustering at the state level may not be appropriate in settings like ours. Accord- ingly, we have estimated all of our regressions using robust but not clustered standard errors. Perhaps unsurprisingly, we find that the impact of prohibition becomes statistically sig- nificant for more causes of death when we do not cluster the standard errors. For instance, when we use Share_Dry as the treatment variable but do not include state-specific trends, we find that prohibition had a negative and statistically signifi- cant impact on deaths due to infant mortality and stomach diseases, in addition to alcoholism, circulatory disease, ulcers, and the disease index. A full set of results is available from the authors.

fewer deaths per 100,000 for ulcers. These are economically significant magnitudes given that among wet state-years the mean death rates from alcoholism, circulatory disease, and ulcers are 6.16 per 100,000, 166 per 100,000, and 3.49 per 100,000, respectively. The estimates of the impact of prohibition exposure on the other causes of death are not precisely estimated; this may be because, for each the illnesses apart from alcoholism and cirrhosis, excessive drinking is one of many potential contributors. Additionally, for some diseases, the impact of prohibition may only become apparent over time. The fact that the coefficient on the treatment variable in most of these regressions is negative, however, suggests that it may be possible to improve statistical power by aggregating these outcomes. When we use the disease index as the depen- dent variable, the coefficient on prohibition exposure is large, negative and statistically significant, which indicates that prohibition laws were effective in reducing alcohol-related

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disease mortality rates overall. By construction, the mean value of the index is zero in entirely wet state-years. The estimate therefore tells us that switching from entirely wet to entirely dry reduced alcohol disease-related mortality by 2.74 standard deviation units relative to entirely wet state-years. Given that the standard deviation of the alcohol disease mortality index across all state-years is 4.65, this is an economically significant magnitude.

Panel B of Table 3 shows coefficient estimates obtained if we follow the approach taken by the literature and use the year that statewide prohibi- tion was enacted instead of effective and ignore county-level laws to measure prohibition expo- sure. We refer to this binary measure of state-level prohibition exposure as Statewide_Dry_Enacted. Using this measure, we obtain much weaker results, consistent with bias due to measurement error.12 For six of the eight mortality outcomes, the magnitude of the coefficients falls by more than 50% and we only obtain statistical signif- icance for circulatory disease (only at the 10% level). For two of the causes of death (liver dis- eases and peritonitis), the coefficient on the pro- hibition variable changes sign. Importantly, when we use the disease index as the dependent vari- able, we find no relationship between the litera- ture’s measure of prohibition and alcohol-related disease mortality.

The states in our sample likely differ along many margins for which we are unable to con- trol and that might be independently correlated with changes in mortality rates and prohibition exposure. For instance, it is possible that states that with rising per capita incomes had falling alcohol-related mortality rates, and that these states were more likely to adopt prohibition. Given that we have variation over time within

12. Correctly measuring the timing of statewide prohi- bition has a larger impact on the coefficient estimates than including county-level variation. For instance, when the dis- ease index is the dependent variable, the coefficient on pro- hibition falls to −2.11 but remains statistically significant if county-level variation is ignored but timing is coded cor- rectly. On the other hand, the coefficient falls to −1.01 and loses statistical significance if we retain county-level variation but miscode the timing of statewide prohibition. For deaths due to alcoholism and circulatory disease, the coefficient on prohibition falls to −2.27 and −6.36 but remains statistically significant if we code the timing of statewide prohibition cor- rectly but ignore county-level variation. If we include county- level variation but incorrectly code the timing of statewide prohibition the coefficient on prohibition exposure for these two outcomes falls to −0.56 and −5.36, respectively, and nei- ther coefficient is statistically significant. A similar pattern of results is found when we investigate mortality due to poor decisions. See Tables S1 and S2 for the full results.

a state we can include a linear time trend for each state to control for this possible source of bias. With the inclusion of state-specific trends, the regressions will now estimate the impact of prohibition exposure on deviations to trends in cause-specific mortality rates.

The inclusion of state-specific trends rein- forces our main findings (see Panel C of Table 3). In seven cases, the coefficient on prohibition exposure is negative, with four (alcoholism, cir- rhosis, circulatory disease, and ulcers) obtain- ing statistical significance. The estimates are also economically significant. For instance, switch- ing from entirely wet to entirely dry is predicted to reduce deaths due to alcoholism by 2.83 per 100,000 while the mean death rate from this cause is 6.16 per 100,000. The disease index increases slightly in magnitude and remains eco- nomically significant. The findings reported in Panel C therefore suggest that increasing prohibi- tion exposure was not concentrated in states with falling alcohol-related death rates.

The first four columns of Table 4 report regression results for causes of death associated with poor decision-making brought on by exces- sive drinking. As shown in Panel A, using our preferred measure of prohibition (Share_Dry), we find that all four mortality rates are negatively correlated with prohibition exposure with the impact statistically significant for homicides and accidents. The point estimates indicate that statewide prohibition reduced deaths due to accidents and homicides by 8.16 per 100,000 and 1.43 per 100,000 respectively. As a comparison, the mean death rates from accidents and homi- cides in wet state-years were 90.37 per 100,000 and 3.43 per 100,000, respectively. When we aggregate the four mortality outcomes into a poor-decisions mortality index, as shown in the second to last column, the coefficient on prohi- bition exposure is negative and large, providing support for the claim that prohibition reduced the mortality consequences of poor decision-making due to excessive drinking. Compared with wet state-years, the estimates suggest that prohibition reduced deaths due to poor decisions by 1.83 standard deviation units, an economically signif- icant magnitude when compared to the standard deviation of the poor decisions index, which is 3.67 across all state-years.

In the last column of the panel we report the coefficient on prohibition exposure when we use the mortality rate due to all nonalcohol-related causes as the dependent variable. This regression provides us with a falsification test. One might be

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TABLE 4 Impact of Early Prohibition on Mortality Due to Poor Decisions and all Other Causes, 1900 – 1920

Panel A: Results using Share_Dry to measure prohibition exposure

Accidents Homicides Suicides Syphilis Decisions Index All Other Causes

Share_Dry −8.156** −1.426** −1.695 −0.378 −1.828** −12.61 (3.867) (0.623) (1.05) (0.462) (0.837) (33.97)

N 404 405 405 405 405 405 R2 .855 .935 .915 .896 .927 .88

Panel B: Results Using Statewide_Dry_Enacted to Measure Prohibition Exposure

Accidents Homicides Suicides Syphilis Decisions Index All Other Causes

Statewide_Dry_ 0.041 −0.206 −0.523 −0.042 −0.269 11.670 Enacted (3.747) (0.518) (0.685) (0.435) (0.639) (24.94) N 404 405 405 405 405 405 R2 .850 .931 .912 .896 .922 .881

Panel C: Results Using Share_Dry and Including State-Specific Trends

Accidents Homicides Suicides Syphilis Decisions Index All Other Causes

Share_Dry −10.580* −1.941** −2.360** −0.247 −2.329** −47.06 (5.478) (0.750) (1.136) (0.450) (1.033) (38.46)

N 404 405 405 405 405 405 R2 .883 .952 .935 .942 .951 .916

Notes: Each column is a separate regression. State and year fixed effects are included in each regression, as well as state-year controls for the literacy rate, the urbanization rate, the non-White share of the population, the share of the population that is Catholic, an indicator variable for whether a state has women’s suffrage in effect, the foreign-born share of the population, the female share, the share that was young, and the share that was old. Share_Dry is our preferred measure of prohibition exposure. Statewide_Dry_Enacted is the binary measure of prohibition used by the literature. The units of all dependent variables except the decisions index are deaths per 100,000. The decisions index is the unweighted sum of the z-scores for each of the individual mortality rates. All other causes are defined as total mortality rate minus the death rate from all 12 alcohol-related causes of death. Robust standard errors clustered by state are reported in parentheses.

*denotes statistical significance at the 10% level; **denotes statistical significance at the 5% level; ***denotes statistical significance at the 1% level.

concerned that our estimates are simply capturing an overall improvement in mortality that occurs in states that enact state or local prohibition laws. For instance, improvements in economic conditions may reduce the need to rely on alcohol tax revenues (and therefore facilitate the adoption of prohibition) while at the same time contribute to declining mortality rates. In this case, we may be falsely attributing declining mortality that is due to better economic conditions to increased prohibition exposure. As shown in the table, how- ever, the coefficient on prohibition exposure in this regression is small relative to the mean mor- tality rate from nonalcohol-related causes and not precisely estimated. There is therefore no relationship between the share of the population exposed to prohibition and the mortality rate due to nonalcohol-related causes of death.13

13. The negative coefficient on prohibition exposure when all nonalcohol-related causes of death is the depen- dent variable also suggests that prohibition did not induce substitution from alcohol-related causes of death into other

In Panel B of the same table, we replace our preferred measure of prohibition expo- sure with the measure used by the literature (Statewide_Dry_Enacted). Once again, we find that this approach weakens or removes any rela- tionship between prohibition and mortality. For the cause-specific mortality rates, the coefficients are all much smaller in magnitude. We also find no relationship when we use the decisions index as the dependent variable.

As before, we reestimated the regressions including state-specific trends (see Panel C). In these regressions, the signs and magnitudes of the coefficient on Share_Dry are similar with or

causes of death. We further investigate this issue by using the total mortality rate from all causes as the dependent variable. In this regression, the coefficient on prohibition exposure is −46.65 (with a SE of 31.09) when we use Share_Dry as the dependent variable but do not include state-specific trends. When we include state-specific time trends, the coefficient falls to −81.18 (with a SE of 37.57). Accordingly, there is no evidence of substitution into nonalcohol-related causes of death.

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without state-specific trends. However, the coef- ficient is now larger and more precisely estimated for accidents, homicides, suicides, and the deci- sion index. Finally, in the last column of Panel C, we redo our falsification test of looking at all nonalcohol-related causes of death while includ- ing state-specific trends and find no relation- ship between prohibition and nonalcohol-related causes of death.

VI. AREA-LEVEL ANALYSIS: WET URBAN AREAS VERSUS SEMI-DRY NONURBAN AREAS

As discussed earlier, prohibition coverage increased gradually in many states, with county- level prohibition preceding the adoption of statewide prohibition. Rural areas were gen- erally the first to become dry, and large urban areas — which housed large immigrant popula- tions and were centers for the production and distribution of alcohol — were often the last. Indeed, large cities in many states only became dry with the adoption of either statewide or national prohibition. It seems possible that the health and safety consequences of state or fed- eral prohibition might therefore vary within a state, with the adoption of statewide or federal prohibition having a larger (negative) impact on alcohol-related mortality rates in wet urban areas than in rural areas that were partially dry and where the mortality benefits of prohibition may have already been realized. Because the Mortality Statistics include data on a limited set of morality outcomes for cities with population greater than 100,000 from 1910 to 1920, we can compute separate cause-specific mortality rates for wet urban areas and semi-dry nonurban areas within the same state that will allow us to test this hypothesis. A benefit of using area-level data instead of state-level data is that it allows us to more closely match prohibition exposure to mortality outcomes.

To be counted as a wet urban area for our anal- ysis, a city had to satisfy three criteria. First, the city had to be within a wet county prior to the adoption of state or national prohibition. Second, the city had to be situated in a Mortality Statis- tics registration state.14 Third, the city had to be within in a state that was not mostly or entirely wet between 1910 and the adoption of statewide

14. We excluded cities from nonregistration states because we cannot compute mortality rates for their nonurban counterparts.

or national prohibition (whichever came first).15

Using this selection criteria left us with 23 cities located within 12 states (for more details see the section A3).

The Mortality Statistics’ city-level data includes information on total population, total mortality, and four alcohol-related death counts (deaths due to cirrhosis, accidents, suicides, and infant mortality). We collected these data for the 23 cities that survived our selection process to obtain annual mortality counts for 23 wet urban areas. Our unit of observation is an area-year with every state having at least two areas in each year, a nonurban area that is partially dry prior to state or federal prohibition, and at least one urban area that is wet prior to state or federal prohibition. In total we have 23 urban areas and 12 nonurban areas. As shown in Table 1A, prior to federal prohibition mortality due to alcohol- related causes was substantially higher in the wet urban areas than the partially dry nonurban areas suggesting a relationship between alcohol consumption and mortality.

Our treatment variable (Share_Dry_Area) is coded as follows. For the wet urban areas, it is equal to 1 in the year that either state or federal prohibition becomes effective (whichever comes first), prorated by the month in which prohibi- tion became effective, and 0 otherwise. For the nonurban areas, it is computed as the share of the population of the nonurban area within a state liv- ing in a dry county, also prorated for the month in which statewide prohibition became effective. Share_Dry_Area will therefore evolve differently for urban areas and the nonurban area within each state. Specifically, the change in the value of this variable brought about by either state or federal prohibition will be greater for the urban areas than for the non-urban area. Prior to national prohibition, the urban areas in our sample were almost entirely wet, while the nonurban areas were more than 50% dry (see Table 1A for sum- mary statistics and accompanying discussion).

To test our hypothesis, we estimate the follow- ing difference-in-differences regression equation for each mortality outcome: (3)

Mdat = αa + φt + ηShare Dry Areaat + ϵdat

15. If a wet urban area was within a state that was mostly wet prior to state or federal prohibition, then state or federal prohibition is unlikely to have a differential impact on alcohol-related mortality rates in urban areas relative to rural areas. In our specification that includes state-by-year fixed effects, these fixed-effects would capture the impact of changes in prohibition laws.

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TABLE 5 Impact of Prohibition on Wet Urban Areas Versus Partly Dry Nonurban Areas, 1910 – 1920

Panel A: Excluding State-by-Year Fixed Effects

Cirrhosis Infant Mortality Accidents Suicides All Other Causes

Share_Dry_Area −2.11** −5.64 −11.76*** −2.52* −103.90*** (0.927) (7.053) (3.870) (1.358) (33.010)

N 367 367 367 367 367 R2 .864 .898 .809 .851 .89

Panel B: Including State-by-Year Fixed Effects

Cirrhosis Infant Mortality Accidents Suicides All Other Causes

Share_Dry_Area −4.49*** 2.37 −2.26 −3.75* −72.30*** (1.944) (10.37) (4.286) (1.965) (22.96)

N 367 367 367 367 367 R2 .908 .94 .904 .908 .958

Notes: Each column represents a separate regression. Each regression was estimated using data from 1910 to 1920. Area-level and year fixed effects are included in each regression. Panel B also includes state-by-year fixed effects. The units of all dependent variables are deaths per 100,000. Robust standard errors clustered by area are reported in parentheses.

*denotes statistical significance at the 10% level; **denotes statistical significance at the 5% level; ***denotes statistical significance at the 1% level.

In this regression, Mdat is a cause-specific mortality rate per 100,000 for disease d in area a in year t, 𝛼a is a fixed effect for area a, 𝜑t is a fixed effect for year t, and 𝜖dat is an error term. The coefficient of interest is 𝜂. If prohibition reduces mortality within an area, then 𝜂 < 0. We report robust standard errors, clustered at the area level.

For each year, we have at least two observa- tions per state. Accordingly, we can also esti- mate the model with state-by-year fixed effects, which we could not include in our earlier analysis using state-level data. State-by-year fixed effects control for any state-level changes (for instance, changes in economic conditions or public health policies) that could affect mortality rates. When we include state-by-year fixed effects, the coef- ficient on Share_Dry_Area tells us the differ- ential impact of state or federal prohibition on wet urban areas relative to partially dry nonurban areas within a state.

Table 5 presents our regression results, with and without state-by-year fixed effects. As before each column represents a separate regression. Although these results use a different source of variation than our state-level results, the over- all findings are complementary. With the excep- tion of infant mortality, the estimated coefficients are negative and economically significant in all regressions. Our estimates suggest that prohibi- tion reduced suicides by 2.5 – 3.7 per 100,000 whereas the suicide rate in urban areas prior to prohibition was 21 per 100,000. For cirrhosis,

we find that prohibition reduced mortality by 2.1 – 4.5 per 100,000 relative to a mortality rate in urban areas of 17.4 per 100,00 prior to pro- hibition. Accordingly, the area-level evidence suggests the adoption of statewide or federal pro- hibition reduced alcohol-related mortality.

As before, we conduct a falsification exercise by regressing our measure of prohibition on the mortality rate due to all causes unrelated to alco- hol which is computed as the difference between the total mortality rate and the sum of the four alcohol-related mortality rates. This measure of nonalcohol mortality differs from the measure computed for our state-level analysis because we have eight fewer alcohol-related causes of death at the area level than at the state level. As a result, deaths due to alcoholism, ulcers, other liver diseases, peritonitis, stomach diseases, cir- culatory diseases, homicides, and syphilis — all of which may be alcohol related — are included in this measure of all other causes of death. The results from this exercise are shown in the final column of the table. In these regressions, the coefficient on the treatment variable is negative and statistically significant, regardless of whether we include state-by-year fixed effects.

We have two explanations for this finding. First, during this time, overall mortality out- comes may have been improving faster in cities than in rural areas, perhaps due investments in urban infrastructure like sewage systems and clean water systems, and these improve- ments may have been concentrated in states that

694 ECONOMIC INQUIRY

adopted prohibition. Second, the estimates may simply be picking up the fact that our measure of nonalcohol-related mortality rates includes many causes of death that are alcohol related because the variable is computed subtracting out a smaller set of alcohol-related mortality outcomes than the variable we used for our state-level analysis. Accordingly, the results of our falsification exercise are inconclusive.

VII. CONCLUSION

The evidence accumulated suggests that early prohibition laws did indeed reduce mortality rates due to alcohol-related causes. Taking advantage of county, state, and federal variation in prohibition laws between 1900 and 1920, we estimate the impact of prohibition on 12 different mortality outcomes using a continuous treatment difference-in-difference estimator. Our findings using state-level mortality data are less ambigu- ous than the literature’s because we examine the impact of prohibition on a broader range of mortality outcomes and we reduce measure- ment error in prohibition exposure. Importantly, when we aggregate mortality outcomes into two summary indices — an alcohol-related disease mortality index and a poor decisions mortality index — we find a sizeable negative relationship between prohibition exposure and alcohol- related death rates. Accordingly, we can be confident that prohibition had the general effect of reducing alcohol-related mortality rates, and that our conclusions are not driven by false pos- itives arising from multiple hypothesis testing bias. Given that a similar share of the population drinks alcohol today, we believe our findings may be relevant for current debates about alcohol control policies.16

The baseline estimates (see Table 3, Panel A and Table 4, Panel A) suggest that prohibition reduced the annual death rates per 100,000 due to alcoholism, circulatory disease, ulcers, acci- dents, and homicides by 2.65, 6.59, 0.41, 8.16 and 1.43 respectively. Since the population of the United States was 106,021,567 in 1920, this implies that if the nation switched from entirely wet to entirely dry in that year, prohibition would have saved at least 20,380 lives that year.

16. The earliest available Gallup poll data indicate that 58% of Americans consumed alcoholic beverages in 1939, 6 years after the end of national prohibition. In 2019, the share was 65%. See https://news.gallup.com/poll/1582/ alcohol-drinking.aspx.

We also investigate the effects of prohibition on a smaller set of mortality outcomes using data on urban and rural areas within states. With this approach we can include state-by-year fixed effects, which allow us to estimate the impact of prohibition within states as opposed to across states. Our area-level results are consistent with our main findings. In particular, we find that pro- hibition reduced deaths from cirrhosis, accidents, and homicides.

We can attempt a back-of-the-envelope esti- mate of the benefits of prohibition in terms of the value of lives saved per year. Fishback (1992) and Costa and Kahn (2004) estimate that the value of a statistical life in 1920 was between $200,000 and $800,000 in 1990 dollars (i.e., between $375,000 and $1,500,000 in 2017 dol- lars). If a switch from entirely wet to entirely dry in 1920 would have saved 20,380 lives, the annual benefits in terms of the value of lives saved would therefore have been between $7.64 billion to $30.57 (in 2017 dollars), or between 0.91% and 3.63% of U.S. GDP (gross domestic prod- uct) in 1920.17 We acknowledge that this is an imperfect estimate of the benefits of prohibition. Historically, total prohibition did not arise within a single year; many areas were already dry prior to 1920; our estimates were obtained using data from a subsample of states; and, importantly, if individuals are utility maximizing, value of life measures lose meaning since they do not incor- porate the lost utility from forgone alcohol con- sumption. Nevertheless, these figures suggest that the benefits of prohibition may have been poten- tially quite large. Whether or not these bene- fits exceeded the costs of prohibition remains an open question.

APPENDIX

A1. NOTES ON THE MEASUREMENT OF PROHIBITION EXPOSURE

Data on the year in which a state’s prohibition law was enacted is taken from Dills and Miron (2004), with updated information from Evans et al. (2016). Information on the year in which a state’s prohibition law became effective was taken from Pickett, Wilson, and Smith (1917), National Association of Distillers and Wholesale Dealers (1918), and online searches of historical society websites. We did not gather information on states where statewide prohibition was enacted prior to 1900 and remained in effect throughout the period.

To compute the share of a state’s population that was dry prior to state or federal prohibition we used county-year data collected by Sechrist (2012) on prohibition coverage

17. U.S. GDP in 1920 was $842 billion in 2017 dollars.

https://news.gallup.com/poll/1582/alcohol-drinking.aspx

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and county-population data from the U.S. decennial censuses (linearly interpolated for noncensus years). We code a county as dry if at least one source, according to Sechrist (2012), claims that the county was dry in that year. We did not compute this share for states that entered the registration area after the date that statewide prohibition became effective.

A2. NOTES ON THE MORTALITY DATA

From 1900 to 1909, the Mortality Statistics reported mor- tality data separately for urban and rural areas in each reg- istration state. We summed these series to obtain state-level mortality counts. From 1910 onward, total mortality numbers were reported for each state.

We attempted to gather data on every cause of death reported in the Mortality Statistics that might be plausi- bly related to alcohol consumption. The following discus- sion details our choices about which mortality categories we included and excluded from our analysis.

We included peritonitis because an important cause of peritonitis is pancreatitis, which is related to alco- hol consumption.

Other diseases of the liver are included because this cat- egory may include diseases like hepatitis that can be exacer- bated by excessive alcohol consumption. Liver cancer, which is also linked to chronic drinking, is not included in the cate- gory “other diseases of the liver.” We would have liked to have included data on liver cancer deaths but because the Mortal- ity Statistics included it with other cancers that may not be related to alcohol consumption we did not collect this data.

The Morality Statistics reported data on deaths due to yellow atrophy of the liver, which may be related to excessive drinking. However, these mortality figures are only available from 1900 to 1909, we have limited state-year variation in prohibition during this period, and this cause of death was exceedingly rare. Accordingly, we do not include this cause of death.

Deaths due to gastritis, another disease linked with alco- hol, were reported for 1900 to 1909, as were deaths due to “other stomach diseases.” From 1910 onward, gastritis was no longer reported but “other stomach diseases” continued to be reported. Accordingly, our variable “diseases of the stomach” is the sum of gastritis and “other stomach diseases” from 1900 to 1909 and other diseases of the stomach from 1910 onward. We henceforth refer to this amalgam of diseases as “stomach diseases.”

The Mortality Statistics also reported deaths due to gon- orrhea but we did not collect these data since the incidence was too infrequent (less than 1% of all sexually transmit- ted diseases).

We believe that Grant Miller’s data on accidents includes all forms of violent death that are not suicides, including homicides. Accordingly, to obtain our measure of accidents, we subtracted homicide deaths (collected directly from the Mortality Statistics) from Miller’s accident data.

We cleaned the data in the following ways. For the Grant Miller data, we did the following. For circulatory diseases, we replaced a missing value for Connecticut in 1902 using data from the Mortality Statistics and replaced the value for Pennsylvania in 1910 with data from the Mortality Statistics because Miller’s number seemed too small by a factor of 10 relative to adjacent years.

We omitted North Carolina from the panel because of unexplained breaks in its mortality data series. For several mortality rates, the numbers were different between 1910 and 1915 by an order of magnitude. Some mortality rates seemed

implausibly low relative to the rest of the sample. Our results are nevertheless robust to including North Carolina.

A3. NOTES ON THE AREA-LEVEL ANALYSIS

The Mortality Statistics include consistent city-level mor- tality counts for 50 cities between 1910 and 1920. We excluded one city (Washington, DC) because it was not located within a state and it therefore has no correspond- ing nonurban area. Two cities (Portland, Oregon and Rich- mond, Virginia) were in counties that were already dry prior to the adoption of state or federal prohibition. Five cities (Birmingham, Alabama; Atlanta, Georgia; Omaha, Nebraska; Memphis and Nashville, Tennessee) were within states that were not in the registration area when state or federal pro- hibition was adopted and therefore lack mortality data for their nonurban counterparts. Finally, 19 cities (Bridgeport and New Haven, Connecticut; Boston, Cambridge, Fall River, Lowell, and Worcester, Massachusetts; Jersey City, Newark, and Paterson, New Jersey; Albany, Buffalo, New York City, Rochester, and Syracuse, New York; Providence, Rhode Island; Seattle and Spokane, Washington; and Milwaukee, Wisconsin) were within states that were either entirely wet or mostly wet prior to the adoption of either state or federal pro- hibition. The remaining 23 cities that survive this selection are as follows: Los Angeles, Oakland, and San Francisco (Cali- fornia); Denver (Colorado); Chicago (Illinois); Indianapolis (Indiana); Louisville (Kentucky); New Orleans (Louisiana); Baltimore (Maryland); Detroit and Grand Rapids (Michigan); Minneapolis and St Paul (Minnesota); St Louis and Kansas City (Missouri); Cincinnati, Cleveland, Columbus, Dayton, and Toledo (Ohio); and Philadelphia, Pittsburgh, and Scran- ton (Pennsylvania).

To obtain mortality counts for the mostly dry nonurban area of each state, we subtracted the wet city mortality counts from the statewide mortality counts collected for our state- level analysis. If a state contained more than one wet city, the mortality count for the partly dry nonurban area of the state was computed by subtracting the sum of all wet urban area mortality counts within a state from the statewide count. We then divided each mortality count by the relevant population total to obtain cause-specific mortality rates per 100,000 for each area in each year.

Table 1A presents summary statistics for each mortality outcome for our urban areas and nonurban areas. We report means and standard deviations for our key variables for two time periods, 1910 through 1919, and 1920. As shown in Panel A, from 1910 to 1919, the mean value of our prohibition coverage variable (Share_Dry_Area) was 0.05 in the urban areas and 0.52 in the nonurban areas while by 1920 (when national prohibition was in effect), the variable is equal to 1 in all areas. By comparing the change in mortality rates in urban relative to nonurban areas across these time periods, we can see if national prohibition disproportionately reduced alcohol-related mortality rates in (wet) urban areas relative to nonurban (semi-dry) areas.

For cirrhosis (Panel B), mortality rates between 1910 and 1919 were higher in wet urban areas (16.61 per 100,000) than in semi-dry nonurban areas (9.38 per 100,000). By 1920, when all areas are dry, the death rates due to cirrho- sis were quite similar in urban and nonurban areas (9.15 per 100,000 in urban areas and 6.79 per 100,000 in nonur- ban areas). Accordingly, the gap in cirrhosis mortality rates between urban and nonurban areas fell over time, from 7.23 (= 16.61 – 9.38) deaths per 100,000 in 1910 – 1919 to 2.36 (= 9.15 – 6.79) deaths per 100,000 in 1920. For the remaining

696 ECONOMIC INQUIRY

TABLE 1A Summary Statistics for Area-Level Analysis

Panel A: Share_Dry_Area