This article originally appeared at https://papers.ssrn.com/sol3/papers.cfm?abstract_id=3063288
39 Pages Posted: 2 Nov 2017 Last revised: 25 Aug 2018
University of Connecticut – Department of Economics
Andrew Young School of Policy Studies, Department of Economics; Institute for Corruption Studies
University of Connecticut
Date Written: August 23, 2018
We use retail scanner data on purchases of alcoholic beverages across US counties for 2006-2015 to study the link between medical marijuana laws (MMLs) and alcohol consumption. To do this we first exploit differences in the timing of marijuana laws among states and find that they are substitutes. We show that unlike traditional national-level analysis, focusing on contiguous border county-pairs provides unbiased estimates of the effect of MMLs on alcohol sales. Specifically, counties located in MML states reduced monthly alcohol sales by 12.4 percent. Results are robust to including placebo effective dates for MMLs in treated states.
The dramatic change in attitudes towards marijuana consumption in recent years has spurred a wave of research that aims at better understanding the impacts of cannabis on a broad number of socio-economic variables. This has taken some urgency given the fact that, surprisingly, not very much is known about the short and long term consequences of cannabis consumption.1 Unsurprisingly, there has been particular interest on the possible interrelations between marijuana and alcohol, two of the most commonly abused substances in the world, as the potential policy implications of this link may have major consequence on public health issues. For instance, if consumption of marijuana and alcohol complement each other it would not be difficult to envision a dramatic increase in alcohol-related health issues, ranging from alcoholism to cirrhosis, due to marijuana consumption (National Institutes of Health, 2015). However, if these two substances substitute each other it may well be the case that the overall public health impact may be positive to society, perhaps even when accounting for any negative externalities associated with cannabis, if any. This simply highlights the importance of carefully studying the possible link between these two substances more so in light of recent public policy measures in different countries, and in particular, the ongoing advances in marijuana-related legislation in several states in the U.S. as well as in other countries such as Canada, Uruguay, Australia, Switzerland, Mexico, Peru and several others. In Uruguay, for example, marijuana consumption was fully legalized in 2017. The law allows for residents to grow six plants at home and to buy cannabis from a local pharmacy or even create cannabis clubs, which lets members to withdraw up to 40 grams of marijuana from the common crop each month (Hudak, et al., 2018). Closer to the United States, Canada is scheduled to fully legalize recreational marijuana in all provinces and territories in 2018.
The current evidence on the link between marijuana and alcohol, while relatively abundant, is rather mixed. Subbaraman (2016) provides an interdisciplinary review of the literature on the link between these two substances and finds that the majority of existing studies, about 40 percent of the total, provide evidence of a substitution effect between marijuana and alcohol, while around 26 percent of them show evidence of complementarity between the two substances. In addition, a significant number of studies, 34 percent of the total, support no association between marijuana and alcohol. When focusing on the economics literature, we find a somewhat analogous split in the evidence, which slightly points towards the existence of a substitution effect between marijuana and alcohol, but with still rather significant evidence that points towards complementarity or neutrality (e.g., Wen, et al., 2015; Anderson, et al., 2013 and Crost and Guerrero, 2012, 2013, among others).
Given its public policy importance and in light of the mixed evidence, we contribute to the literature by taking a fresh look at the impact of medical marijuana laws (MMLs) on alcohol consumption. First, we use data that have not been previously used in marijuana-related research. In particular, we employ county-level retail scanner data on monthly purchases of alcoholic beverages in grocery, convenience, drug, liquor or mass distribution stores covering over two thousand U.S. counties for the period 2006-2015. While strictly speaking these data do not necessarily reflect the alcohol consumption of the population, they are reasonable proxies that also present substantial advantages. Since the data come from retailers, our measure of alcohol consumption does not suffer from potential bias resulting from underreporting issues of selfreported drinking behavior, commonly present in surveys. Second, the retail scanner data offer a broad and detailed coverage of alcohol sales across U.S. counties, which allows us to apply a contiguous-county estimation approach across MML and non-MML states along the lines of recent work by Dube et al (2010) who show that this approach greatly increases precision and reduces bias by accounting for spatial heterogeneity in alcohol trends. Methodologically, we exploit differences in the timing of the change of marijuana laws among states and compare a noncontiguous approach along with our preferred contiguous method in order to confirm or deny potential increases in precision as well as bias reduction.
We first compare purchases of alcoholic beverages between counties located in states where MMLs have been implemented to purchases in states where MMLs have not changed before and after the change in MMLs.2 The coverage of these data allows us to adopt a Difference-inDifferences (DID) research design by estimating a reduced-form model conditioning on county and year-month fixed effects while also controlling for state-specific time trends. The latter allows for different trends of alcohol sales in each state and thus relax the parallel trend assumption that is required in the DID approach. Second, we move away from a national-level approach and estimate the impacts on alcohol sales using the subsample of contiguous counties across MML and non-MML shared borders only. This provides a rigorous test, as it allows us to control for unobserved spatial heterogeneity in alcohol sale trends. It is also reasonable to believe that bordering counties are very similar in alcohol sales trends and potentially confounding factors. Indeed, we show that while a more standard DID approach lead to failure of trend assumption, using a sample of contiguous border county-pairs provides much cleaner evidence of parallel trends. In addition, we consider the heterogeneity in the MMLs provisions across states and estimate effects for different provisions within these laws. This breakdown allows us to identify the policy characteristics that specifically contribute to the change in alcohol consumption. This is important from the public policy perspective since states decide on these provisions in the lawmaking process. We contrast results from a traditional DID analysis with local estimates based on a county-pairs sample showing that alcohol trends are much better behaved when we use the latter approach. In terms of the effect of MMLs on alcohol sales, we show that counties in states that legalize the use of medical marijuana experience a significant decrease in the aggregate sales of alcohol (beer and wine). We find that the legalization of medical marijuana reduces alcohol sales by more than 12 percent, a much stronger substitution effect than previously estimated (e.g. Anderson et al. 2013). We argue that our use of retail data at the county level, combined with a more rigorous estimation strategy exploiting time variation across bordering county pairs in MML and non-MML states provides compelling evidence toward the true relationship between alcohol and marijuana. Moreover, the effects are not short lived, with significant reductions observed up to 24 months after the passage of the law. An event study analyses as well as a placebo test confirm the robustness and causal interpretation of our findings. Finally, we also find a significant impact of provisions on collective cultivation, open dispensaries, and patient registration, all leading to a reduction in sales of alcohol products.
The paper is organized as follows. The next section provides the general context and the state of the current empirical literature. Section 3 introduces the data. Section 4 presents the empirical strategy and different estimation methods. In Section 5 we discuss results. In Section 6 we apply a robustness check. Section 7 discusses our findings in the context of similar literature on marijuana and alcohol. Finally, in the last section we provide a brief summary and conclusions.
2. Basic Context and Literature Review
In the last two decades, growing evidence has lent support to the efficacy and safety of marijuana as medical therapy to alleviate symptoms and treat diseases (e.g., Amar, 2006; Campbell and Gowran, 2007; Krishnan et al., 2009; Pertwee, 2012). This growing body of clinical evidence on marijuana’s medicinal value has propelled many states toward a more tolerant legal approach to medical marijuana. Starting from the mid-1990s, several states have taken legislative measures toward legalizing the sale and consumption of medicinal and recreational marijuana. In 1996, California and Oregon became the first states to allow the consumption of said drug for medical purposes. Since then, twenty-four other states and the District of Columbia have passed amendments to their constitutions in order to decriminalize consumption of medical marijuana. Legislative changes pertaining to the recreational consumption and sale thereof, have been much less prevalent; a third of these states allow it. With almost half of the states in U.S. legalizing marijuana use, researchers are looking into the relationship of marijuana use with related outcomes such as consumption of alcohol and other substances (Wen et al., 2015), risky sexual behavior (Rees et al., 2001) and labor market outcomes (Ullman, 2016).3 There is consensus that the legalization of medical and non-medical marijuana has increased the rates of marijuana users (Cerda et al., 2012; Wen et al., 2015; Mason et al., 2015; Williams and Bretteville-Jensen, 2014). Furthermore, there is evidence of an increase in marijuana related arrests and marijuana treatment admissions to rehabilitation facilities among male adults post the passing of these laws, which points toward an increase in illegal marijuana use and consumption (Chu, 2014).
As it was mentioned above, the evidence stands somewhat inconclusive in the link between marijuana and alcohol, with some studies estimating that these two are substitutes, while others find either complementarity ore neutrality between the two. For instance, Wen et al. (2015) use a traditional DID approach with a two-way fixed effects model and find increased frequency of binge drinking as a result of legalizing marijuana. Likewise, Yörük and Yörük (2011) exploit the cut-off of 21 years as the minimum legal drinking age through a regression discontinuity design on NLSY data. They find that, conditional on having used marijuana at least once, legal access to alcohol increases consumption of both alcohol as well as use of marijuana, indicating that the two are complements. Pacula (1998), utilizing variation in state beer taxes, also concludes that alcohol and marijuana are complements.
With respect to substitution, Williams et al. (2004) find evidence of substitutability between marijuana and alcohol based on a bivariate Probit model that exploits the variation in alcohol control policies. Crost and Guerrero (2012, 2013) use a sharp discontinuity design to identify the effect of the legal minimum drinking age on alcohol and marijuana use and find the two to be substitutes; a finding that conflicts with Yörük and Yörük (2011). Likewise, DiNardo and Lemieux (2001) find that increase in the minimum drinking age increases use of marijuana. Their structural estimation documents this evidence as being attributable to standard substitution effects. In addition, studies specifically exploiting medical marijuana laws also present mixed evidence. Yamada, et al. (1996), Chaloupka and Laixuthai (1997) and Saffer and Chaloupka (1999) find that marijuana decriminalization is associated with a decrease in alcohol consumption, suggesting that marijuana and alcohol are substitutes. Pacula et al. (2015) and Wen et al. (2015) also utilize selfreported alcohol use data to examine the relationship between MML and alcohol consumption. Using data from the National Longitudinal Survey of Youth and the Youth Risk Behavior Survey, Pacula et al. (2015) find little evidence of association between MML and alcohol use. Further, when considering different policy dimensions of MML, they find mixed evidence depending on specifications and data sets. Wen et al. (2015) on the other hand use the National Survey on Drug Use and Health and find that a MML is associated with an increase in the binge drinking among adults. In particular, Wen et al. find a 10 percent increase in the likelihood of binge drinking among individuals 21 and over. Moreover, they find evidence of simultaneous use of both substances. According to their results, MMLs increase the probability of marijuana smoking and binge drinking in the same occasion by 18 percent. However, they find no significant impact on alcohol consumption of adolescents and young adults. Using average annual sales for US states from Brewers Almanac, Anderson et al. (2013) show that the implementation of an MML decreases the state level per capita beer sales (in gallons) by about 5 percent. In addition, they find significant decreases in alcohol consumption and binge drinking based on survey data from the Behavioral Risk Factor Surveillance System.
Our analysis improves on two dimensions. First, apart from Anderson et al. (2013), most of the literature has investigate the question using survey data. While surveys suffer from potential bias resulting from underreporting issues of self-reported substance abuse (e.g., Greene et al. 2018), data on alcohol sales do not suffer from that typical bias. Moreover, existing literature using sales and not self-reported consumption data reports finding from traditional DID analysis that exploit cross-section variation (across states) in MMLs over time to identify the effect of the policy change. This approach is likely to produce biased estimates of the effect of MMLs on, in this case, alcohol sales. This is because it fails to account for unobserved spatial heterogeneity in alcohol sales trends. That implies that time-varying differences in underlying characteristics of the states may confound the effect of changes in MMLs on alcohol sales. Given the availability of data at the county level, we follow Dube et al. (2010) by focusing on a sample of contiguous border county-pairs and exploit discontinuity of MMLs at state borders, shared by county pairs, to identify the unbiased effect of MMLs on alcohol. This method uses in fact only variation in MMLs within each cross-state pair of counties allowing us to address the bias due to spatial heterogeneity.
3.1 MML implementation indicator
We use a dichotomous variable to denote the states that implemented medical marijuana laws. The variable takes value equal to 1 for each month from the effective date of the implementation, and a value of 0 otherwise. MML states are defined as treated states. The variable also takes value equal to 0 for states that did not have MMLs in our sample period 2006-2015.4 Information on approved and effective dates of MMLs as well as the date at which different MMLs provisions were implemented come from previous literature (e.g., Choi et al., 2016; Sabia et al., 2017). Table 1 presents a list of effective-dates used to define the MMLs indicators used in our analysis. We observe 14 states that legalized medical marijuana in our sample period.
Following previous work (e.g., Pacula et al. 2015), we also consider four specific provisions of MMLs: (i) requiring patient registration, (ii) allowing prescription for non-specific pain, (iii) establishment of licensed dispensaries, and (iv) home and collective marijuana cultivation. Patient registration implies a stricter control on medical access and can thus reduce marijuana use in non-medical population. On the contrary, the establishment of dispensaries has a supply effect, which could increase marijuana use in general population. Allowing prescription for non-specific pain creates ambiguity in the conditions for which medical marijuana can be recommended, which could allow access to patients with less severe conditions or even to recreational users pretending to suffer from chronic pain. The provision allowing home or collective cultivation for multiple patients could increase supply and thus access. Table 1 presents the effective dates for when each state implemented the specific provision, if ever. Note that in several states not all provisions have been implemented, and in most states legal dispensaries were opened years after the main law was implemented.
3.2 Alcohol Sales
Our identification strategy is based on the availability of data on alcoholic beverages purchases observed in the Nielsen Retail Scanner database in MML and non-MML states before and after MMLs became effective. The database contains purchases of products in all categories for grocery, convenience, drug, or mass distribution stores across the United States over the period between 2006 and 2015. These data include detailed product characteristics, price, and quantities for alcoholic beverages. Using the Scanner data presents several advantages with respect to previous literature. First, the data offer extensive spatial coverage of sales of thousands of products across the U.S. including weekly sales for all alcoholic beverages for the 52 designated market areas located in the 48 contiguous states of the U.S. While data on alcohol sales does not strictly represent alcohol consumption, sales do not suffer from the underreporting issues typical of selfreported data collected with surveys. The Scanner database also offer a wider coverage of the sales of alcoholic beverages as it contains sales for all products (UPC code) across U.S. counties, which allows us to better measure the extensive margin of alcoholic beverages consumed
Our analysis focuses on sales of aggregate alcohol, beer, and wine. To our knowledge, only one paper that has looked at the relationship between MMLs and alcohol examines the effect on alcohol sales (Anderson et al., 2013). Overall, we have sales data for more than two thousand U.S. counties. Table 2, Panel A, shows descriptive statistics for sales for beer, wine, and aggregate alcohol for MML and non-MML states. Purchases in MML states are slightly higher than in nonMML states for alcohol in aggregate and beer, while average county sales for wine are similar for the two groups. Figure 1 shows average annual county sales for aggregate alcohol (wine and beer) for MML and non-MML states in our sample period. The series indicate that alcohol sales were increasing until mid-2009. Thereafter, sales in non-MML states exhibited a downward trend, while in MML states they stabilized around 500 thousand dollars (monthly county average). The figure also shows the difference in average county sales between MML and non-MML states (treated minus control). Interestingly, the positive gap in sales between the treated and control is increasing over time up until late 2014, possibly indicating different trends in alcohol sales between treated and control states. This difference seems to have a time-varying component probably due to underlying state characteristics that change over time. This would suggest including state-specific linear trends. However, this may not address the problem given that trends may be themselves affected by the policy change, as indicated by Wolfer (2006) in the context of divorce laws, and Dube et al. (2010) in the case of changes in minimum wage. For this reason we focus on an analysis using a sample of contiguous border county-pairs.
We control for a set of time-varying covariates that could potentially influence alcohol sales and be correlated with MMLs. We include annual county-level variables to capture variation in county economic conditions over time such as the unemployment rate and median household income. We also add a set of demographic characteristics for the county, including total population, percentage of male and Hispanic population, and the share of population by age groups. Information on economic characteristics comes from Local Area Unemployment Statistics and Small Area Income and Poverty Estimates. Information on demographic variables was gathered from the Census Bureau.5 Summary statistics for economic and demographic variables are presented in Panel B of Table 2. It is important to notice that summary statistics for covariates in counties in treated and control states are almost all identical and thus control states provide a good comparison group. The only notable difference is that treated states have larger counties, in terms of population, and have a higher median household income.
Because of previous concerns with the existence of contemporaneous policies (Wen et al., 2015), we also gathered relevant information on other marijuana policy changes. Specifically, there are states that became more lenient towards marijuana possession or legalized recreational marijuana use. To control for this, we construct dichotomous state-month indicators for states that decriminalized and legalize marijuana consumption; we also include annual state-level data on beer and cigarette tax rates to control for other policy changes during the study period that may be correlated with MMLs implementation. State cigarette and beer tax information is based on several sources: American Petroleum Institute, state revenue departments, Distilled Spirits Council of the U.S., Commerce Clearing House, and Tax Foundation. Summary statistics for these state-level covariates are presented in Panel C of Table 2.
4. Empirical Methodology
4.1 All Counties Sample
Our initial empirical strategy follows the MML literature and exploits spatial and time variation in the implementation of medical marijuana laws (MMLs) using a Difference-InDifferences approach to the evaluation of their causal effect on alcohol. Simply put, we compare monthly sales between counties located in states where MMLs have been implemented to sales in counties in states where MMLs have not changed in our sample period (2006-2015), before and after the change in MMLs. In other words, we assign states to treatment and control groups depending on the implementation (or not) and the timing of MMLs. We estimated the following model:
(1) ݕ௧ ൌ ߚ ߚଵܮܯܯ௦௧ ܆ଵ௧ ܆ଶ௦௧ ߜ ߛ௧ ߩ௦߬ ߟ௧,
where yct denotes the log of alcohol sales in county c on time period t, MML is an indicator for whether in state s medical marijuana law is effective in time period t. The term ߛrepresents a county fixed effect; and ߜ௧, represents the time period, year-month, fixed effect that is constant across counties. ܆ଵ௧ and ܆ଶ௦௧ are full vectors of county-level and state-level covariates. Conditional on observable characteristics, and using fixed effects to eliminate the influence of unobservable characteristics, counties located in different states will be different only in alcohol sales because of difference in the implementation of the laws on marijuana use. Following the literature, (e.g., Almond et al., 2011; Anderson et al., 2013; Wen et al., 2015), we include statespecific time trends ߩ௦ ݐto control for systematic trend differences between treated and control states. This also controls for unobservable state-level factors evolving over time at a constant rate. The key coefficient of interest ߚଵ represents the estimated effect of the legalization of medical marijuana on sales of alcoholic beverages. The identification of ߚଵ relies on the assumption that trends in the outcome variable in counties in the control group are a reasonable counterfactual, i.e., that sales trends in the states that did not implement MMLs would have been the same in the absence of the treatment. Finally, following Almond et al. (2011) and Simon (2016), we balanced the event study by including events that were at least eighteen full months in the pre-legalization phase and twenty-four full months in the post period. This eliminates the potential bias generated by demographic changes due to states entering and exiting during the event study period.
4.2 Preferred Method: Contiguous Border County-Pair Sample
We then conduct a boundary analysis using a panel of county boundaries that allows us to control for systematic differences between cross-border counties. Specifically, we restrict our analysis to a sample consisting of all the contiguous county pairs sharing a state border where one of the counties belongs to a treated state (MML state) and the other to a control state (non-MML state). In this case, the identification relies on cross time variation in counties in the legalization of medical marijuana to identify the effect of MMLs on alcohol sales. In other words, we compare change in MMLs over time to the change in alcohol sales across state boundaries. As observed by Dube et al. (2010), counties sharing the border with counties located in a treated state provide a better control group than other control county in the US because they can be expected to be relatively similar, in this case relative to alcohol sales trends, to adjacent treated counties. Starting from a full set of set of 2,191 counties, which yields 322 distinct county-pairs, balancing the data as for the all-county sample, we are left with 164 county pairs.6 Figure 2 displays the location of these counties on a map of the United States.
Using the sample of contiguous border county-pairs, we first estimate a specification similar to equation (1) with county and common time fixed effect and state-specific trends:
(2) ݕ௧ ൌ ߚ ߚଵܮܯܯ௦௧ ܆ଵ௧ ܆ଶ௦௧ ߜߛ௧ ߩ௦ߟ ݐ௧,
where ݕ௧ denotes the log of alcohol sales for county-pair p. This specification allows us to compare sales of alcoholic beverages between two counties that share a border where the policy differs across state border controlling also for systematic differences between counties. A comparable approach was employed by Ponticelli and Alencar (2016) and Marinescu (2017). Because there are multiple observations for counties sharing borders with more than one other county standard errors are clustered at the county-pair level. Then, following Dube et al. (2010) and Dhar and Ross (2012) we modify equation (2) by allowing for pair-specific time effect ߪ௧, which captures county-pair changes over time:
(3) ݕ௧ ൌ ߚ ߚଵܮܯܯ௦௧ ܆ଵ௧ ܆ଶ௦௧ ߜߛ௧ ߪ௧ ߟ௧.
As in Dhar and Ross (2012), we assume that ߪ௧ takes the form of a pair-specific time trend, i.e., ߪ ߪ ൌ .ݐAlso notice that the county fixed effect ߛaggregates to county-pair fixed effect and controls for time invariant characteristics of the bordering counties. Finally, we also allow each county to have its own time trends to capture factors that changes over time that are specific to counties, .ݐߩ
4.3 Event Study
The identification strategy for the DID approach is based on the assumption that trends in alcohol sales in counties located in MML and non-MML states are parallel in the period preceding the policy change and thus provide a valid counterfactual. While we control for systematic trend differences in alcohol sales between states there may still be the case that the identification of the treatment effect (the implementation of MMLs) comes from trends in sales that are correlated with the legalization. To investigate the existence of pre-existing trend differences between treatment and control states we estimated the following equation:
(4) ݕ௧ ൌ ଼∑ ߚୀି ߠ1ሺ߬௧ ൌ ݅ሻ ܆ଵ௧ ܆ଶ௦௧ ߜ ߛ௧ ߩ௦ߟ ݐ௧,
where ߬௧ indicates the event month-year, which takes value equal to one when an observation is i quarters away from the quarter the legalization of medical marijuana became effective. We use quarters to reduce noise. The case ሺ߬ ൌ 0ሻ denotes the quarter of the policy change. For ሺ߬ െ1ሻ MML states were untreated (alcohol sales before MMLs were effective). The coefficients ’ߠs were estimated relative to one year before the policy change ሺ߬ ൌ െ4ሻ, the omitted coefficient.7 Note that i equal to -7 or 8 denotes more than six, or seven, quarters before or after, respectively, MMLs became effective. We also formally test whether contiguous counties are more valid controls by repeating the event study on the contiguous border county sample with a structure similar to equation (4) but where we control for county-pair time effects and county-specific instead of statespecific trends:
(5) ݕ௧ ൌ ଼∑ ߚୀି ߠ1ሺ߬௧ ൌ ݅ሻ ܆ଵ௧ ܆ଶ௦௧ ߜߛ௧ ߪ௧ ߟ ݐߩ௧.
The event study is also useful to investigate dynamic responses to the treatment. For the case of the legalization of medical marijuana it is conceivable that evolving social norms may create a more favorable support for marijuana consumption leading to more states legalizing not only medical, but also recreational consumption. Slow diffusion of information about patient’s eligibility may result in a change in the number of medical users or spillovers to non-patient population, as indicated by, e.g., Chu (2014) and Wen et al. (2015). But also the progressive rollout of the law itself may generate different effects over time. In fact, specific provision of the MMLs often do not come into effect at the same time as the main law, e.g., such as patient registration or the establishment of public dispensaries.
4.4 Impact of Individual Policy Provisions
Not all MML states provide the same access to medical marijuana. In fact, medical marijuana laws include specific provisions regarding cultivation and distribution that legalizing states have implemented in different fashions, or not implemented at all. For instance, in most states where the law includes specific provisions for dispensaries the actual implementation of the provision or the opening of the dispensaries is delayed with respect to the effective date of the law. The importance of such heterogeneity in the policy implementation has been recognized in previous studies as it could affect acceptability and access to marijuana. Pacula et al. (2015) find that the specific dimension of these laws influence consumption in different ways. Patient registration has a negative effect on recreational use, while the legal establishment of dispensaries positively affects recreational use. Wen et al. (2015) find that the non-specific pain provision increases marijuana use and alcohol use in individuals aged 21 or above, while patient registration and the opening of dispensaries have no discernable effects. Others have found heterogeneous effects on body weight (Sabia et al, 2017), tobacco use (Choi et al., 2017), or effect on opioids addiction (Powell et al, 2018).
To examine the heterogeneous effect of MML laws we estimated a regression that includes a dichotomous variable for each of the specific policy provisions as well as one for the main law:
݊௦௧݅ݐܽݎݐݏܴ݁݃݅ସߚ ௦௧ݕݎܽݏ݁݊ݏ݅ܦଷߚ ݊௦௧݅ݐܽݒ݅ݐ݈ݑܥଶߚ ଵܲܽ݅݊௦௧ߚ ߚ ௧ ൌݕ )(6௧ߟ ݐߩ ௧ߪ ௧ߜ ߛ ଶ௦௧܆ ଵ௧܆
where ,ߚwith i=1, …, 4, denotes the effect of the specific provisions of MMLs. Equation (6) is estimated first including one policy dimension at a time and finally in its complete specification.
For the empirical analysis, we restrict our sample to a balanced panel of states with at least 18/24 months before/after MMLs were implemented and for counties having sales for all months within the observed period, 2006-2015.8 All regressions are estimated for aggregate sales of alcoholic beverages.9 Regressions were weighted using county-year population.10 For estimation using the all-county sample, standard errors are clustered at the state level allowing for within state serial correlation in the error terms while assuming these are independent across states because unobserved factors may be correlated over time (Bertrand et al., 2004). Notice that in the case of our preferred method, the county-pair sample, the fact that a single county can appear in multiple pairs, the error terms may not be independent because of correlation across county-pairs (Dube et al., 2010; Dhar and Ross, 2012). To account for this correlation, for the regression using the county-pair sample we cluster at the county-pair level.
5.1 Event Study
Figures 3 and 4 show that the trend in the pre-treatment period is much better behaved when we use the contiguous border county-pair sample. The event study for the all-county sample, Figure 3, indicates that pre-existing trend differences in alcohol sales cannot be excluded. Indeed, we find that trends for alcohol sales in treated and control counties are downward sloping in the earliest period before MMLs implementation. At three quarters before the implementation the trend is reversed and stabilizes around zero.
The event study shown in Figures 4 uses our preferred methodological approach namely the county-pair sample and indicate that there are no pre-existing trend differences in alcohol sales.11 Indeed, we find that trends for alcohol sales in treated and control counties are flat, i.e., that estimated ߠs are both in magnitude and statistically not different from zero in the years before MML implementation. This confirms that the counterfactual trend behavior of treatment and control groups are statistically the same and support the causal interpretation of the treatment effect (Angrist and Pischke, 2008).12 With respect to both magnitude of the effect and precision of the estimate the two alternative specifications for border counties are virtually identical.
The Event Study captures differences in the short-term and long-term effects, which we expect to exist due to time variation in the implementation of specific provisions as well as delays in the diffusion of information about the availability and access to medical marijuana. When focusing on our preferred approach of bordering counties, Figure 4, we observe that MMLs lead to a reduction in alcohol sales at the time of the legislation being passed and all the quarters thereafter. Immediately after the effective date of MML implementation, counties in treatment states decreased alcohol sales. In line with our expectation, the immediate effect is lower than the average as it takes time for the law to be fully in place as well as delays in information. During the following months, there is a further decline in sales. The evidence provided by the event studies provides validity to the identification strategy based on discontinuity at the state border.
5.2 Overall Effect
Table 3 shows the estimates of the effect of access to medical marijuana on alcohol sales using a standard difference-in-difference approach for all available counties. Starting from the baseline results indicate that legalizing marijuana for medicinal purposes leads to a decrease in aggregate alcohol sales. In particular, counties located in MML states reduced monthly alcohol sales by 13.1 percent (e-0.140 – 1 = -0.131). Notably, this result is consistent across several empirical specifications. Adding controls for demographic variables, local economic conditions, and state policy controls on cigarette and beer taxes do not change the qualitative or quantitative point estimates significantly, while it improves the precision of the estimate. With respect to aggregate alcohol sales, we conclude there is evidence indicating that marijuana and alcohol are substitute goods.
Table 4 show results from our border analysis using the contiguous counties sub-sample described in our methodological section above. When using this approach, we find further confirmation that there is a substitution effect between access to marijuana and alcohol sales. The point estimates are however slightly lower, in absolute value. Indeed, we find a decrease of between 11.2 and 12.4 percent. Interestingly, this effect is larger than in the case of the full sample shown above in Table 3. This appears to be an indication that the overall findings in a more typical DID analysis are a lower bound to the true substitution effect between marijuana and alcohol. We argue that these results provide a rather rigorous methodology that further confirm our findings above given the fact that focusing on bordering counties provides better controls counties to the treatment counties. In this context, it is reasonable to believe that using this approach provides greater support for the assumptions of equal trends as well as to the notion of significant similarities across unobservables between treatment and control counties.
5.3 Heterogeneity in Policy Provisions
Not all states provide access to medical marijuana in the same way; some have implemented different provisions, or none at all, which allows for the estimation of the impact of specific MML policy characteristics on alcohol sales. Table 5 reports the heterogeneous effects by provision type, as well as a complete specification for the continuous border county-pairs analysis including the main policy and all provisions combined. Results from columns (1)–(4), show the impact for each MML provision separately. Consistent with the main result of a substitution effect, most provisions reduce alcohol sales in the aggregate. However, these estimates are limited given that each provision rarely occurs in isolation; hence, the most relevant results are those from column (5) in which all provisions are accounted for. All analyses and interpretation hereafter refer to the full specification shown in Column (5). Results show that provisions on collective cultivation and open dispensaries cause a decrease in alcohol sales by 32 and 25 percent, respectively. These findings are consistent with theory given that both of these provisions impact the supply of marijuana by increasing access to the general public. Hence, results indicate that provisions which increase access to marijuana lead to a decrease in alcohol sales; a substitution effect.
We also find evidence of a strong substitution effect regarding the patient registry provision of MMLs. In particular, we find that patient registries reduce monthly alcohol sales by 25 percent. This may be a counter intuitive finding given that previous literature has found this provision decreases the use of recreational marijuana (Pacula et al. 2015). However, it is important to note that others (e.g. Wen et al. 2015) find no discernable effect of patient registries on marijuana consumption. This lack of consensus may be explained by the fact that the estimated impact corresponds to the net effect of the different mechanisms through which each provision affects marijuana and thereby alcohol consumption. For example, in the case of patient registries, this provision limits the demand for marijuana by creating additional costs to access. This in turn would lead to an increase in alcohol sales, assuming a substitution effect between marijuana and alcohol consumption. On the other hand, there may be positive indirect impacts, given that access to marijuana becomes easier conditional on having registered. For example, registered individuals can become intermediaries through whom friends and family now have access to marijuana. This in turn would lead to an increase in overall marijuana consumption, and a decrease in alcohol sales. Overall, the effect estimated is the net impact, which considers both of the aforementioned mechanisms. Results are expected to vary depending on which effect dominates.
On the other hand, results show that the non-specific pain provision causes an increase in alcohol sales. Although this may be a counterintuitive finding, neither theory nor empirical evidence supports a clear prediction of the result. There is theoretical ambiguity regarding the impact of the provision on marijuana consumption. It may be the case that blurring the conditions to prescribe medical marijuana can lead to an increase of use among patients with less chronic pain, possibly leading to an increase in recreational use. On the other hand, this provision may lead to differential doctor prescription behavior leading to physician-own discretion and greater heterogeneity in the type of patient that receives access to medical marijuana. This theoretical ambiguity is coupled with lack of empirical evidence; Wen et al. (2015), for example, find no discernable effect of this provision on marijuana consumption.
6. Robustness Checks
We examine the sensitivity of our results and preferred specification. Specifically, we check that the effects we find are not spurious by estimating the regression, equation (5), using placebo effective MMLs dates. Specifically, we test for the potential impact of placebo (fake) effective dates for MMLs in the treated states. Using a uniform distribution, for each MML state we draw randomly 1,000 dates in the time period that goes from 06/2007, to two years before the actual effective MML date. This time window is consistent with the main analysis in the sense that for each state we have sales data for at least 18 months prior to until 24 months after the policy change. The data observed for treated states form the actual effective date until the end of the sample period are dropped from the sample. The treatment indicator, MMLst, is defined according to the placebo dates. That is, it takes value equal to one starting from the placebo date for state s, zero otherwise. Then, we estimate the same specification as for equation (5) for each of the 1,000 placebo dates. This gives us a distribution of the treatment effects for the placebo treatment
Table 6 shows estimates for the date placebo test and falsification test, respectively. As expected, both of these regressions find no effect which provides support that the main results are not spurious correlations, but rather treatment effects. Across the alcohol groups, we find no effects of the placebo treatment. The estimated effects are close to zero and are statistically insignificant at any conventional level. The estimated coefficient of the placebo MML was negative and statistically significant at the 10% level 135 times out of 1,000 for aggregate Alcohol.
As mentioned above, when using our preferred methodological approach we find that counties located in MML states reduce monthly alcohol sales by 12.4 percent, which is consistent across specifications. This estimated effect is substantial and may be driven by spillover of marijuana use to a larger population (extensive margin) and higher marijuana consumption by current users (intensive margin).13 These findings are hard to reconcile with the existing literature that, as seen above, points in all directions, from complementarity, to substitutability, to neutrality between marijuana and alcohol. Whereas it is difficult to come up with a definitive explanation on the nature of the observed differences between ours and other studies, we follow Pacula and Sevigny (2014) to broadly categorize previous studies in such a way as to better understand our contribution to the literature.14 They argue that in spite of the fact that the vast majority of studies employ difference-in-differences approaches results vary tremendously due to three likely factors. First, legitimate differences in the response of the populations examined, as specific age groups and subgroups represent different types of users or margins of use. This clearly applies to the studies that are closest to ours in terms of data and methodology, in particular, Wen et al., (2015) and Anderson et al, (2013). The former finds that among those aged 21 or above, MMLs increased the frequency of binge drinking by 10 percent, but MMLs did not affect drinking behavior among those 12-20 years old. On the other hand, the latters estimates an 11 percent reduction in the number of drinks consumed (age 20-29) and a 15 percent decrease in the number of drinks consumed (age 19-22). Second, analyses making use of the simple dichotomous indicators such as MMLs may suffer from limitations as laws are not homogenous, nor are they static, so that interpretation of findings over any given time period will not necessarily reflect a true overall treatment effect. Furthermore, as Pacula and Sevigny (2014) argue, strict marijuana registration requirements are negatively associated with self-reported alcohol use and alcohol-related traffic fatalities for both adults and youth, while dispensaries were found to be positively associated with both, which is consistent with the finding of Wen et al., (2015) who, in fact, employ self-reporting data unlike ours and Anderson et al (2013), which focus on objective data. This is compounded by the fact that the use of self-reported data may be problematic (Bertrand and Mullainathan, 2001). Third, an additional reason that may help explain the observed differences in our findings with other studies may be related to the timeframe of the corresponding studies as medical marijuana policies evolve in important ways after initial adoption and as more information is gained in terms of court interpretation of the legitimacy of these policies and the federal response to them (Pacula and Sevigny, 2014). In fact, while our research focuses on the years 2006 to 2015 finding substitution between cannabis and alcohol, while Wen et al., (2015) begin at an earlier year, 2004 and ends in 2012 and find complementarity between these substances.
As mentioned above, there are also some recent set of studies that apply regression discontinuity approaches and find substitutability between marijuana and alcohol. For instance, Crost and Guerrero (2012) exploits the discontinuity created by the minimum legal drinking age of 21 years to estimate the causal effect of increased alcohol availability on marijuana use and find that the consumption of alcohol increases, suggesting that marijuana and alcohol are substitutes. It should be noted that in this study and similar ones, the causality tends to go from alcohol laws to marijuana consumption, deals with very specific ages, and cover specific neighboring states. Unlike this type of studies, we consider the opposite causality, we take into account broad age groups, and we include all bordering available counties in the country during our period of study.
Overall, we believe that given our comprehensive methodological approach, the use of objective data at the county level, as well as our extensive robustness testing, our research provides significant additional credibility that the “true” causal link between medical marijuana laws and alcohol consumption may be negative as all the different empirical paths pursued point consistently towards the same direction. Given the relatively large impact of our findings, it is conceivable to believe that there may be occurring spillovers to recreational use. In fact, while early state adopters had little monitoring of cannabis supply, this was not the case with late adopters, which in theory leaves little room for potential spillovers to non-medical use (Anderson and Rees, 2014, 2014a). However, recent studies that exploit MML variation for late adopters find significant spillover effects (Wen et al., 2015; Choi et al., 2018). Several mechanisms explain the reason why this may occur. First, enacted laws are difficult to enforce because cannabis is transportable, which undermines distribution restrictions (Mikos 2015, Hansen, et al., 2018; Hao and Cowan, 2017). Second, marijuana potency has greatly increased in recent years (ElSohly et al., 2016; Sevigny, et al., (2014). Finally, a perception of laxness penalties, more social acceptance, price reduction in the black market, and more focused suppliers who tend to focus on the adult population may also play a role (Anderson et al., 2013, 2015).
8. Summary and Conclusions
In this paper we study the link between medical marijuana laws on alcohol from a different perspective. We use data on purchases of alcoholic beverages in U.S. counties for 2006-2015 to study the link between marijuana laws and alcohol sales. To do this we exploit the differences in the timing of the of marijuana laws among states and find that these two substances are strong substitutes. We compare results from a traditional national-level difference in difference analysis to a local identification strategy that takes advantage of differences in medical marijuana laws between pairs of contiguous counties. We show that this strategy provides an unbiased estimate of the effect of legalizing medical marijuana on alcohol sales. This evidence is provided by a cleaner event study analysis, which show that when focusing on border county-pairs there are no preexisting trend differences between counties in treated and control states. Using this sample, we find that counties located in MML states reduced monthly alcohol sales by 12.4 percent. Using this as our preferred specification we also show the effect of the single provisions included in MMLs. That is, patient registration, collective cultivation, and open dispensaries have considerable negative effects on alcohol sales. Remarkably, our findings are quite robust. In fact, when we test for both the potential impact of placebo effective dates for MMLs in the treated states, which provides further support that the main results and border analysis are not simply spurious correlations.
We believe that the implications of our findings may be a useful contribution to economic policy not only because they provide strong evidence that can give a better understanding on the type of relationship between alcohol and marijuana, but also because the confirm the presence of spillover effects of medical marijuana laws on use of other substances that might contribute to negative health and social outcomes. Whereas complementarity would indicate that legalizing marijuana may exacerbate the health and social consequences of alcohol consumption for instance, in the form increased traffic injuries and fatalities, substitutability, which is what we find, may help allay such concerns and help focus on the positive first order impacts of pursuing the legalization of marijuana. Hopefully, this paper adds credibility that the link between cannabis and alcohol is negative based on the strength of our comprehensive methodological approach, the use of objective data at the county level, and extensive robustness testing.16
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