Do opioid prescriptions lead to fatal car crashes?

Abstract

Widespread opioid misuse suggests a potential for increased fatal car crashes. However, opioid use may not necessarily lead to additional crashes if drivers respond to opioid prevalence by substituting away from more inebriating intoxicants like alcohol. Combining data on local opioid prescription rates and car crashes from the Fatality Analysis and Reporting System, we use two-way fixed effects models to test the direction of the association between prescribing intensity and crash fatalities between 2007 and 2016. We estimate that a 10 percent increase in the local prescription rate is associated with a 1 percent increase in the number of driver deaths in motor vehicle accidents. The association is robust to several model specifications, and isolated to drivers most affected by the opioid crisis: males and 25 to 34 year-olds.

I. Introduction

Motor vehicle crashes are the leading cause of death for Americans under age 25, and the second most common cause among Americans aged 25 to 44 (Centers for Disease Control and Prevention 2020a). A large fraction of these crashes involve substance use: about a third of fatal crashes involve alcohol, and about 15 percent involve other drugs (National Center for Statistics and Analysis 2017; Compton and Berning 2015). In recent decades, substance use has become an increasingly common phenomenon as prescription opioid use increased. The widespread availability of prescription, and synthetic, opioids represents a potential safety risk on the road. Their use can cause drowsiness, affect cognition and slow reaction time, and the FDA requires that opioid prescriptions be accompanied by a warning against driving or operating heavy machinery (Baldacchino et al. 2012; Menefee et al. 2004; Stout and Farrell 2003). Observational studies using US data have documented increases of up to 700 percent in the proportion of fatal crashes where the driver tested positive for narcotics (including opioids) (Azagba et al. 2019; Chihuri and Li 2017a; Wilson, Stimpson, and Pagán 2016; Brady and Li 2014; Brady and Li 2013). However, no existing studies have investigated whether the increased availability of prescription opioids in communities causes fatal motor vehicle crashes. In this paper, we test this hypothesis by estimating the association between local opioid prescribing intensity and car crash fatalities. We provide suggestive evidence of a causal link between prescription opioid prevalence and fatal crashes on American roads.

It is not clear a prioiri whether increased opioid prevalence should increase fatal car crashes. On the one hand, some lab-based simulation studies have shown that, especially at higher doses, prescription opioid use can impair driving ability (Gibson et al. 2009; Bachs et al. 2006). However, several other experimental studies show that when used at therapeutic levels, prescription opioids do not diminish driving ability. This appears to be especially true among those who are opioid-tolerant due to long-term treatment (Fishbain et al. 2003; Sabatowski et al. 2003; Strumpf et al. 1997).¹ Furthermore, opioid users appear to substitute between drugs, responding to supply-side factors in their use of prescription opioids versus other intoxicants (Carrieri, Madio, and Principe 2020; Evans, Lieber, and Power 2019; Smith 2019; Powell, Pacula, and Jacobson 2018; Alpert, Powell, and Pacula 2018; Livingston et al. 2017; Wen, Hockenberry, and Cummings 2015). There is evidence that, used at conventional levels, alcohol has a larger impact on driving ability than opioids (Romano et al. 2014; Strumpf et al. 1997). If prescription opioids act as a substitute for more inebriating intoxicants like alcohol, higher rates of opioid use among drivers involved in fatal crashes could indicate lower rates of drunk driving. This may perversely imply that widely available opioids could lead to fewer fatal crashes.

Many observational studies have attempted to empirically estimate the relationship between opioid prevalence and fatal crash outcomes in real world settings, and findings have been mixed. Several studies have failed to find any association between opioid use and traffic fatalities (Romano et al. 2014; Gadegbeku, Amoros, and Laumon 2011; Drummer et al. 2004; Fishbain et al. 2003; Ray, Fought, and Decker 1992). Others – many of which use the Fatality Analysis Reporting System (FARS) data used in the present study – have documented that opioids use is positively associated with involvement in fatal car crashes (Azagba et al. 2019; Chihuri and Li 2019; Chihuri and Li 2017a; Chihuri and Li 2017b; Rudisill et al. 2016; Wilson, Stimpson, and Pagán 2016; Reguly, Dubois, and Bédard 2014; Brady and Li 2013, 104–114; Gomes et al. 2013; Bernhoft et al. 2012; Gjerde et al. 2011; Meuleners et al. 2011; Dubois, Bédard, and Weaver 2010; Movig et al. 2004; Mura et al. 2003). These studies, however, tend to rely either on cross-sectional variation in opioid use across drivers, or intertemporal variation in opioid use trends. Studies that use cross-sectional variation in opioid use may suffer from selection bias if underlying characteristics of prescription opioid users are also associated with involvement in fatal crashes (e.g. risk-taking) (Reguly, Dubois, and Bédard 2014; Bernhoft et al. 2012; Engeland, Skurtveit, and Mørland 2007). Studies that rely exclusively on intertemporal variation may also be biased. Increased prevalence of opioids among fatally injured drivers may simply reflect the fact that an increasing proportion of Americans take prescription opioids. In 2012 – the height of the prescription opioid epidemic – US pharmacies filled 81 prescriptions per 100 residents, with county rates as high as six prescriptions per capita in some regions (Centers for Disease Control and Prevention 2020c). Higher opioid use nation-wide will likely lead mechanically to higher use rates among deceased drivers and does not necessarily imply that drug use causes crashes. To date, no existing work has used quasi-experimental techniques to empirically estimate the causal effect of opioid prevalence on fatal car crashes.

We begin to fill this gap by testing the following hypothesis: increased opioid prescriptions in a community cause fatal crashes. Rookey (2018) demonstrates that fatal crashes in the US where the driver tested positive for oxycodone are spatially clustered, suggesting that underlying geographic variation in opioid supply and demand may translate into spatial patterns of use among drivers. We exploit such geographic variation by estimating associations between local opioid prescription rates and fatal crash outcomes. Using data on all fatal car accidents in the US between 2007 and 2016, we estimate Poisson two-way fixed effects models that relate per-capita opioid prescriptions at the commuting zone² (CZ) level to CZ-level counts of fatal crashes and fatalities. Our identifying assumption in this approach is that, net of time invariant, CZ-level factors and secular trends, opioid prescribing practices in a CZ should not affect car crashes through any channel besides the causal one. Our results show a positive association between CZ-level prescriptions and annual CZ-level fatal car crash outcomes. We find that an increase of one prescription per capita in the local opioid prescription rate – about a doubling of the average rate – is associated with about 3.5 additional annual fatal crashes in each CZ. This effect translates into an elasticity of 0.07, meaning that a 10 percent increase in the local annual prescription rate is associated with about 0.7 percent more fatal crashes per year in a commuting zone. Since most fatal crashes kill only one person, these additional crashes translate into about one additional fatality per crash, or about 3.8 more fatalities per CZ. We also show that the fatalities are concentrated among drivers, among whom fatalities increase by 1 percent with a 10 percent increase in the local prescription rate.

We present several additional pieces of evidence to buttress our main results. First, we estimate several alternate specifications of our main model, including specifications controlling for annual CZ-level covariates and state-by-year fixed effects, Ordinary Least Squares linear models, and county-level analyses. Our crash and fatality estimates are highly stable to the inclusion of additional controls, and alternate model specifications. Second, we conduct a series of heterogeneous treatment effect analyses to test whether the associations we uncover between prescriptions and crash outcomes are concentrated among demographic groups that have been hardest hit by the opioid epidemic. Prior work has documented that the bulk of opioid overdose deaths – especially between 2007 and 2016 – occurred among working-age males (Centers for Disease Control and Prevention 2020b; Case and Deaton 2015). Our results show that local opioid prescriptions are only positively related to crashes and fatalities among male drivers, and those between the ages of 25 and 34. These patterns match documented demographic patterns of opioid users.

We also estimate the relationship between local opioid prescription rates and drug and alcohol test results reported in the FARS. If opioid prescriptions cause fatal crashes, we expect to find a positive relationship between the local prescription rate and the number of fatal crash drivers testing positive for narcotics. However, drug and alcohol testing data in the FARS are incomplete, with test reporting rates as low as 10 percent in some states and years. As such, analyses of these variables are not reliable. Our results reflect this fact. While we uncover some evidence that CZ-years with higher opioid prescription rates have more positive drug tests and positive narcotics³ tests among drivers involved in fatal crashes, the estimated effects for these outcomes decrease in magnitude and become insignificant once we include state-by-year fixed effects. This suggests that state-level trends in testing procedures may be correlated with local opioid prescription rates, rendering the results of our drug-use analysis inconclusive. This also suggests that past studies may overestimate the pervasiveness of opioid use among American drivers involved in fatal crashes (i.e. Azagba et al. 2019; Chihuri and Li 2017a; Wilson, Stimpson, and Pagán 2016; Brady and Li 2014; Brady and Li 2013).

To the best of our knowledge, no existing work uses quasi-experimental research methods to test the relationship between prescription opioid availability and car crashes in a real-world setting. Our results contribute to the literature in several ways. Existing literature on the opioid crisis has demonstrated that prescribing behavior was a contributing factor to the large increase in overdose deaths (Barnett, Olenski, and Jena 2017; Alpert, Powell, and Pacula 2018; Alpert et al. 2019; Khan et al. 2019; Powell, Pacula, and Taylor 2020). There is less evidence about how prescription intensity over this period indirectly produced additional deaths due to other causes. Our results suggest that widespread prescribing led to additional deaths due to fatal car crashes. We also show that accounting for state-level trends significantly affects analyses of positive narcotics tests among fatally injured drivers; ignoring such trends can potentially cause researchers to overstate opioid use among fatal crash drivers. This finding underscores the difficulty of using drug testing results in the FARS data. Finally, we contribute to the growing literature documenting the relationship between the local drug environment and fatal car crashes (Cook, Leung, and Smith 2020; Hansen, Miller, and Weber 2020; Santaella-Tenorio et al. 2017; Anderson, Mark D., Hansen, and Rees 2013).

II. Methods

A. DATA

We use data from the Fatality Analysis and Reporting System (FARS), a census of all fatal crashes in the United States collected annually since 1975. Compiled by the National Highway Traffic Safety Administration (NHTSA), the data include information on all individuals and vehicles involved in fatal car crashes, and are collected from police reports and other driver and health administrative records. For our purposes, we use information collected on the fatality outcomes, and the results of alcohol and drug tests reported in the data for all individuals involved in fatal crashes between 2007 and 2016. This gives us information on roughly 320,000 crashes involving 795,000 people.

We classify individuals as fatalities if they suffered a fatal injury in the crash. Toxicology reports in the FARS indicate whether drugs were present in a driver’s blood or urine at the time of the crash. The FARS data report up to three detected drugs for each tested individual. Alcohol tests using blood, breath or urine samples indicate the blood alcohol content (BAC) of the tested individual. Using these pieces of information, we identify drivers for whom drug and alcohol test results are reported in the FARS; ⁴ drivers who have a positive test result for any drug; drivers with a positive test for narcotics (the category that includes opioids); drivers with a BAC greater than zero; and drivers with a BAC greater than 0.08 (the legal limit).

Two complications arise when working with drug- and alcohol-use outcomes in the FARS. First, the prevalence of opioid prescriptions could affect both the likelihood of being in a fatal crash – and therefore being included in the FARS data – and the likelihood that the driver tests positive for narcotics (Levitt and Porter 2001). Thus, interpreting rates of driver drug use among fatal crashes is complicated, since changes in the rate could be driven by changes in the likelihood of a fatal crash, changes in the likelihood of drug use among drivers in fatal crashes, or both. This problem is especially troublesome if opioid prescription prevalence reduces the number of fatal crashes in an area – by reducing drunk driving, for instance. In this case, the rate of drug use among drivers involved in fatal crashes could appear inflated due to a decreasing probability of being involved in a fatal crash. To help address this issue, we convert all outcome measures in the individual-level data into counts of events at the CZ-level. Thus, our analyses reveal how the total number of drivers involved in fatal crashes who have positive drug or alcohol test results change as the local opioid prescription rate changes.

The second complication arises from the fact that drug and alcohol test results are not reported for all drivers in the FARS. Between 2007 and 2016, approximately 52 percent of drivers involved in fatal crashes have alcohol test results recorded in the FARS, and approximately 39 percent have drug test results; among drivers who died in crashes, 75 percent have alcohol test results, and 61 percent have drug test results. The probability that a driver involved in a fatal crash has a drug test result in the FARS changed over our study period: starting from about 38 percent of drivers in 2007, the rate of reported drug tests increased to 43 percent in 2010 before decreasing to 33 percent in 2016. In appendix figures, we also show that reported test rates vary across states, across time within states, and even across counties within states.⁵ Variation in drug test reports in the FARS are driven by differential testing and reporting practices across jurisdictions (Berning and Smither 2014). Interpretation of our results on drug and alcohol use outcomes is affected by this complication. A situation where zero drivers had a positive opioid test suggests something very different in the case where all drivers were drug tested, compared to one where no drivers were tested. Using count data does not remedy this problem. We address this complication in several ways in our analysis – which we detail below – as well as in our discussion of the results. However, this is a fundamental flaw with the drug- and alcohol-testing variables in the FARS data that is not remedied by using count data; analyses of these variables should therefore be interpreted with caution.

We create count outcomes by collapsing the FARS data at the commuting zone (CZ)-by-year level. Commuting zones⁶ are geographic units that capture local economies where people live and work. There are 709 CZs in the US, 127 of which cross state boundaries (for example, Cincinnati, Ohio, whose commuting zone includes both Ohio and Kentucky counties). Commuting zones offer a wider geographic net than counties, one that captures both procurement and use of opioid prescriptions, as well as commuting and traffic ties across space.⁷ While CZs have not previously been used in economic studies of traffic fatalities – since many such studies analyze state-level policies – they have been used in the literature on local labor markets, and patterns of consumer behavior (Autor and Dorn 2013; Autor et al. 2020; Goolsbee and Syverson 2021). For each CZ-year, we count: the number of fatal crashes; the number of deaths in fatal crashes; the number of driver deaths; the number of drivers involved in fatal crashes with drug (or alcohol) test results reported in the FARS; and the number of drivers with a positive test for any drugs; narcotics; BAC>0; and BAC>0.08. Since the FARS is a census, the estimates obtained from count models will reveal changes in the total number of these incidents in the entire population.

We combine the collapsed FARS data with CZ-level data on per capita prescriptions for opioid analgesic medication. These data – which we obtained from the CDC – were collected by IQVIA Transactional Data Warehouse (formerly IMS Health and Quintiles) from a sample of approximately 50,000 retail pharmacies that distribute nearly 90 percent of all retail prescriptions in the United States. The data include the number of initial opioid prescriptions or refills dispensed at these pharmacies and paid for by private insurance, Medicaid, Medicare, or cash (Centers for Disease Control and Prevention 2020c). We create CZ-level prescription rates by using population-weighted averages of the annual county-level prescription rates. Approximately 11 percent of county-year prescription rates are missing from the prescription data.⁸ In cases where missing counties are combined with other counties into a single CZ, we replace the missing prescription rate with the average rate of other counties in the CZ. In cases where a CZ is composed of a single county – as is the case in rural areas – we set the CZ prescription rate as missing if the county rate was missing. This results in missing prescription rates for about 4 percent of CZ-year combinations. Across all CZ-years, the average number of per capita prescriptions is about 0.8 per year. The lowest annual CZ-level rate is 0.19 prescriptions per capita, and the highest rate is 1.95 – meaning that in some areas and years, pharmacies dispensed on average nearly two opioid prescriptions per resident in a single year. We merge the prescription data with the FARS count data at the CZ-year level.

Finally, for each year and county, we obtain population, poverty rates and median household income from the American Community Survey, and unemployment rates and shares of total employment in construction from the Bureau of Labor Statistics. For each, we create annual population-weighted averages for each CZ and use these as control variables. We control for economic factors like the median household income and CZ unemployment rate because existing research has shown that fatalities from car crashes are procyclical and fatalities from drug use are countercyclical (Ruhm, C. J. 2000; Hollingsworth, Ruhm, and Simon 2017). We control for the share of employment in construction for two reasons. First, local labor conditions in industries that tend to employ low-skill labor are especially important correlates of opioid deaths (Betz and Jones 2018). Second, light truck traffic is positively associated with traffic fatalities (Anderson, Michael 2008). We use the share of employment in construction as a proxy for light truck traffic.

Table 1 shows the descriptive statistics for the CZ-level crash data. On average, there are about 47 annual fatal crashes involving 69 drivers per CZ. The crashes result in 51 fatalities per CZ per year; about 33 of these are driver fatalities. Among drivers involved in fatal crashes during our study period, about 74 percent are male. The age distribution of the drivers is relatively uniform between 18 and 64; only 3 percent of drivers involved in fatal crashes are under 18, and about 14 percent are 65 or older. Among drivers involved in fatal crashes, about 39 percent have drug test results recorded in the FARS, and about 52 percent have alcohol test results. Twelve percent of drivers test positive for drugs, 3 percent test positive for narcotics, and about 19 percent test positive for alcohol.

Table 1.

Descriptive Statistics

	Mean	S.D.
Annual CZ-level count outcomes
Number of crashes	46.6	82.6
Number of fatalities	50.9	89.3
Number of drivers involved in fatal crashes	69.3	125.5
Number of driver fatalities	32.5	50.4
Driver characteristics (proportion of drivers)
Male	73.8	44.5
Female	25.6	43.6
Under 18	2.9	16.7
18–24	15.3	36
25–34	18.1	38.5
35–44	14.8	35.5
45–54	14.9	35.6
55–64	11.5	32
65 and up	14.2	34.9
Drug and alcohol test results (proportion of drivers)
Driver drug tested	39.2	48.8
Positive drug test	12.3	32.9
Positive narcotics test	2.7	16.1
Driver alcohol tested	51.8	50
BAC>0	19	39.2
BAC>0.8	16.9	37.5
CZ characteristics
Opioid prescription rate (per capita)	0.8	0.3
Unemployment rate	7.1	2.5
Poverty rate	14.8	4
Median HH income ($10,000)	54.7	11.6
Share of employment in construction	5.7	1.3
Population	455,158	1,164,861
Number of CZ-years	6,863
Number of drivers	475,704

Notes: Data from the Fatality Analysis and Reporting System, 2007 and 2016.

Commuting Zone characteristics weighted by the annual CZ population.

B. EMPIRICAL STRATEGY

We explore the causal effect of opioid prescriptions on fatal car crashes using a two-way fixed effects analysis, which controls for CZ- and year-fixed effects. We estimate the following general, baseline regression model for each outcome (O_cy):

$$O_{cy}=\beta R{x}_{cy}+{\theta }_c+{\lambda }_y+po{p}_{cy}+\gamma {\mathit{X}}_{cy}+{\mu }_{sy}+{\epsilon }_{cy}$$ (1)

Here, Rx_cy is the annual CZ-level prescription rate in CZ c and year y. We express this as the number of opioid prescriptions per resident, per CZ-year. The model also includes CZ (θ_c) and year (λ_y) fixed effects. In our main approach, we estimate Poisson models to account for the fact that our outcomes are count variables, censored at zero and skewed. However, we also estimate linear Ordinary Least Squares (OLS) models in robustness checks. We control for CZ-level population (pop_cy) – by including an offset in our Poisson models, and a linear control in our OLS models – to account for the fact that CZs with more people will mechanically have more traffic fatality events. In all cases, we cluster standard errors at the CZ-level to account for the fact that the error terms are correlated across time within CZs.

In these models, the coefficient estimates of β capture the change in the number of annual CZ-level crashes, fatalities and drug-use incidents associated with an increase of one prescription per capita. The identifying assumption of these models is that, after controlling for CZ and year fixed effects, there are no additional unobserved factors that are correlated with both local opioid prescription rates and crash outcomes. We re-estimate our models after adding CZ-level covariates, X_cy (the unemployment and poverty rates, median household income, and the share of employment in construction). If our identifying assumption holds, we expect that the addition of CZ-level covariates will not significantly alter the estimates of β.

We also test the sensitivity of our estimates to the inclusions of state-by-year fixed effects, μ_sy⁹, an exercise that serves two purposes. First, the state-by-year fixed effects capture any changing state-level policies that could be correlated with both crash outcomes and prescriptions, such as medical marijuana laws. Second, they help us control for changing drug testing environments. It is well known that the drug testing data in the FARS is generally unreliable due to variation in testing and reporting practices (Berning and Smither 2014). We confirm this in Appendix figures A2 and A3, which show the significant variation in drug reports across states, and across time within states. If changing state-level testing and reporting practices are correlated with changing prescription rates, then results for our drug-involvement outcomes will be biased. Inclusion of the state-by-year fixed effects allow us to assess this possibility. After including state-by-year fixed effects, the remaining variation in our analysis is driven by within-state, CZ-specific time trends in prescriptions and crashes.¹⁰ Our identifying assumption in these models is that, net of CZ- and year-fixed effects, as well as changing confounders at the state-level, there are not additional, unobserved, commuting zone-specific factors that covary with opioid prescriptions or crashes. If our results hold up to this more demanding assumption, we will be better able to conclude that the estimated relationship between prescriptions and crash outcomes is causal in nature.

Since the opioid crisis primarily affected working-age men during our study period, we expect any correlation between opioid prescriptions and crash outcomes to be strongest for male drivers between the ages of 25 and 54. To test this, we conduct a heterogeneous treatment effect analysis to explore whether changing prescription rates are more strongly related to fatalities among certain groups of drivers. We create a new set of outcomes that count the number of crashes and driver deaths where the driver had a given characteristic in each CZ and each year. For each CZ- year, we count: the number of crashes and driver deaths with male and female drivers; and the number of crashes and driver deaths with a driver in seven age categories (under 18 years, 18 to 24, 25 to 34, 35 to 44, 45 to 54, 55 to 64, and 65 and over). We estimate model (1) on these outcomes, including the year and CZ fixed effects, the CZ-level covariates, and state-by-year fixed effects.

III. Results

A. DESCRIPTIVE RELATIONSHIPS

National opioid prescription rates and fatal crash rates over our study period follow opposite trends. As demonstrated in Appendix Figure A1, the average population weighted CZ-level prescription rate increased from about 77 annual prescriptions per 100 people to about 82 annual prescriptions per 100 people in 2010. It then decreased to about 66 annual prescriptions per 100 people in 2016. The average fatal crash rate followed the opposite trend between 2007 and 2016, dropping from about 12 crashes per 100,000 people in 2007 to about nine crashes per 100,000 people in 2014.

While the national trends may be driven by macroeconomic factors (such as the 2008 recession), further inspection reveals significant local variation in prescription and crash rate trends. Figure 1 shows the local variation in crashes and prescriptions. Panel a shows the change in annual prescriptions per 100 people between 2007 and 2016 for each CZ. The figure shows that about a quarter of CZs had increases in local prescription rates over this period, while another quarter had large reductions. The figure also reveals some regional differences in these trends. For example, Ohio, Kentucky and West Virginia saw decreases in prescriptions over this period, while the southern and plains states saw increases. Panel b shows a map of changes in CZ-level crash rates over the same period. Again, the map shows that about a third of CZs had increases in the annual number of crashes per 100,000 people between 2007 and 2016, while the remaining CZs experienced reductions in fatal crashes. These maps suggest that the national trends mask significant differences across regions and commuting zones, in both prescriptions and crash rate trends.

Figure 1.

Change in the number of annual prescriptions per 100 people, and the number of fatal crashes per 100,000 people, between 2007 and 2016 for each communizing-zone

Source: Estimated by the authors using Fatality Analysis Reporting System data and IMSQuintiles Prescription data, 2007–2016

Figure 2 shows how the local trends in prescription and crash rates relate to one another. The figure plots the 2007 to 2016 change in the CZ-level fatal crash rate against the change in CZ-level per capita prescriptions, where each bubble is weighted according to the CZ’s 2007 population. Contrary to the national trends, the scatter plot reveals a slight positive relationship between changes in local opioid prescription rates and local crash rates, with a best-fit line slope of 1.8. These figures, while only descriptive in nature, point to the importance of using a disaggregated analytical strategy that allows for a granular level of geographic variation in treatment and outcome variables.

Figure 2.

2006 to 2017 change in CZ-level crash rates versus change in CZ-level prescription rates

Note: Size of each bubble represents the CZ population in the given year. Linear best fit line calculated using population weights. In the interest of readability, 6 CZs with reductions in crashes of more than 50 are not pictured in the figure.

Source: Estimated by the authors using Fatality Analysis Reporting System data and IMSQuintiles Prescription data, 2007–2016

B. CRASHES, DEATHS AND DRIVER DEATHS

Table 2 shows the results of estimating equation (1) for the crash and fatality outcomes. For each outcome, we show estimates from three models. All three models include CZ and year fixed effects, and a control for the CZ-level annual unemployment rate. The second model adds state-by-year fixed effects, and the third adds additional controls for the CZ-level annual poverty rate, median household income, and share of employment in construction. Because we estimate Poisson models, we report both the coefficient estimate on the prescription rate variable, as well as the average marginal effect in square brackets.

Table 2.

Two-way fixed effects Poisson analysis, crash and fatality outcomes

	(1)	(2)	(3)	(4)	(5)	(6)	(7)	(8)	(9)
	Crashes			Deaths			Driver Deaths
Rx per Capita	0.081*	0.085*	0.079*	0.078*	0.077	0.070	0.128***	0.122**	0.113**
	(0.035)	(0.038)	(0.038)	(0.036)	(0.041)	(0.040)	(0.037)	(0.043)	(0.042)
	[3.732]	[3.948]	[3.635]	[3.946]	[3.877]	[3.560]	[4.123]	[3.930]	[3.632]
Unemployment Rate	−0.033***	−0.035***	−0.031***	−0.035***	−0.035***	−0.031***	−0.039***	−0.033***	−0.028***
	(0.003)	(0.005)	(0.005)	(0.003)	(0.005)	(0.005)	(0.003)	(0.005)	(0.005)
Poverty Rate			−0.004			−0.005			−0.008*
			(0.003)			(0.003)			(0.004)
Median HH Income			0.006*			0.007**			0.005
			(0.002)			(0.002)			(0.003)
Construction Share			0.027***			0.024***			0.032***
			(0.006)			(0.006)			(0.007)
State by Year FE	N	Y	Y	N	Y	Y	N	Y	Y
Dep. Variable Mean	46.2	46.2	46.2	50.6	50.6	50.6	32.3	32.3	32.3
N	6,832	6,832	6,832	6,832	6,832	6,832	6,832	6,832	6,832

^*p<0.05;

^**p<0.01;

^***p<0.001

Notes: Estimated on data from the FARS between 2007 and 2016. Poisson models explaining the number of fatal crashes, the number of motor vehicle fatalities, and the number driver fatalities in each commuting zone in each year. Rx Rate is the number of opioid prescriptions per resident in each CZ, in each year. All models include a population offset term, year and commuting zone fixed effects. Robust standard errors clustered at the CZ level in brackets. Average marginal effects in square brackets.

In columns (1) through (3), we report the relationship between the annual CZ-level prescription rate and the number of annual fatal car crashes in the CZ. We estimate that one additional annual prescription per capita is associated with a 0.081 log point increase in the number of fatal crashes per CZ, or about 3.7 additional crashes per year. On average, the annual per capita prescription rate is 0.8, and there are about 47 crashes per CZ. Our estimate therefore implies that a 10 percent increase in the annual per capita prescription rate is associated with about a 0.7 percent increase in annual crashes per CZ. Moving across the columns, the results show that the estimate is stable to the inclusion of state-by-year fixed effects, as well as additional CZ-level controls.

The remaining columns in Table 2 show the results for the number of annual traffic deaths, and driver deaths, in each CZ. Because most crashes have only one fatality, the estimated relationship between prescriptions and deaths is very similar to the relationship between prescriptions and fatal crashes. We estimate that one additional annual per capita opioid prescription is associated with an additional 3.5 to 4 traffic fatalities per year in each CZ – an implied elasticity of 0.7 percent per 10 percent increase in per capita opioid prescriptions. Again, the estimates are relatively stable to the inclusion of the state-by-year fixed effects, and the additional CZ-level covariates, although the estimated coefficients become marginally insignificant when we add these additional controls in columns (5) and (6). In columns (7) through (9), we explore the relationship between opioid prescriptions and driver deaths. Over our sample period, about 64 percent of all traffic fatalities were drivers. However, we find a stronger association between local opioid prescriptions and driver deaths than among non-drivers. One additional annual per capita opioid prescription is associated with about 3.5 to 4 additional driver deaths per year in every CZ. Translating this estimate into an elasticity suggests that a 10 percent increase in the local opioid prescription rate is associated with a 1 percent increase in driver deaths.

In Table 3, we report results of three different approaches to our analysis. Columns (1), (4) and (7) show the results of estimating model (1) using a linear Ordinary Least Squares (OLS) rather than Poisson model. The estimated coefficients on the CZ-level prescription rate from the OLS model are very similar to the marginal effects reported in Table 2 for all outcomes.¹¹ In columns (2), (5) and (8), we show the results of OLS estimates of model (1) on county-level measures of the number of crashes, deaths and driver deaths. The estimated relationships between the local county-level prescription rate and all three crash outcomes remain statistically significant and in the same direction as the CZ-level results. The relative magnitudes of these estimates are smaller than the CZ-level results. For instance, for the number of crashes, we estimate a relative effect size of 7.5 percent using the CZ-level data, and a relative effect of 4.3 percent using the county-level data. However, the county-level estimates are qualitatively similar to the results of the CZ-level analysis.

Table 3.

Alternate specifications, crash and fatality outcomes

	(1)	(2)	(3)	(4)	(5)	(6)	(7)	(8)	(9)
	Crashes			Deaths			Driver Deaths
Rx per Capita	3.470***	0.484***	3.420	3.804***	0.521***	4.310	2.873***	0.329**	3.344
	(0.991)	(0.136)	(2.947)	(1.104)	(0.154)	(3.358)	(0.736)	(0.111)	(2.323)
First Stage Estimate	-	-	-0.069*	-	-	−0.069*	-	-	−0.069*
(PDMP IV)			(0.0275)			(0.0275)			(0.0275)
Model	OLS	OLS	IV	OLS	OLS	IV	OLS	OLS	IV
Unit of Analysis	CZ	County	County	CZ	County	County	CZ	County	County
Dep. Variable Mean	46.2	11.3	11.3	50.6	12.2	12.2	32.3	7.8	7.8
N	6,832	28,091	28,091	6,832	28,091	28,091	6,832	28,091	28,091

^*p<0.05;

^**p<0.01;

^***p<0.001

Notes: Estimated on data from the FARS between 2007 and 2016. Rx Rate is the number of opioid prescriptions per resident in each CZ or county, in each year. All models include CZ or county fixed effects, year fixed effects, and controls for population, the poverty rate, the unemployment rate, median household income and the share of employment in construction. Columns (1), (4) and (7) show results of OLS estimates on CZ-level data. Columns (2), (5), and (8) show results of OLS estimates on county-level data. Columns (3), (6) and (9) show IV estimates using state-level PDMP passage as an instrument for county-level prescription rates. Robust standard errors clustered at the CZ or county level in brackets.

Finally, we use the passage of state-level must-access Prescription Drug Monitoring Programs (PDMP) as an instrument for county-level prescription rates.¹² These programs reduced prescription rates by requiring that medical professionals report prescriptions to a central body, a requirement that reduced the prevalence of doctor shopping, prescription dosage, and other determinants of over-prescribing (Rhodes et al. 2019; Bao et al. 2018; Buchmueller and Carey 2018; Haffajee et al. 2018; Mallatt 2018; Meinhofer 2018). We first predict the annual opioid prescription rate for each county using a binary indictor of whether its state had a must-access PDMP law in place in that year. We then regress the predicted local prescription rate on the crash and fatality outcomes at the county level. Both the first and second stage models include county and year fixed effects, a control for county-level annual population, pop_cy, and the county-level covariates. We cluster standard errors at the state level to account for correlation in the PDMP policy variable over years within states. As with our first approach, the coefficient estimates reflect the estimated change in the number of county-level crashes and drug-use incidents associated with one additional annual opioid prescription per capita in the county. However, in these models the variation in the local prescription rate is driven by state-level changes in the PDMP policy environment.

We report the results of this analysis in columns (3), (6) and (9) of Table 3. The first stage estimates are negative and statistically significant. We estimate that after passing must-access PDMP laws, states saw their county-level prescription rates decrease by 0.069 prescriptions per capita. The average county-level prescription rate is 0.87 annual prescriptions per capita. Thus, passage of a must-access PDMP is associated with about an 8 percent reduction in prescriptions. The second stage estimates are insignificant for all variables. We estimate positive, imprecise coefficients on the crash and fatality outcomes. However, the IV estimates are in the same range as our OLS estimates. For example, the IV estimate of the effect of prescriptions on the number of crashes per county is 3.4 on an average of 11.2 – an effect size of about 30 percent. For comparison, the OLS estimate of the relationship between prescriptions and crashes at the county level is 0.5 (about a 4 percent effect), and then estimate at the CZ level is 3.5 on a mean of 46.2 (7.5 percent).

C. HETERGENOUS TREATMENT EFFECTS

To validate our results, we conduct a heterogenous treatment effects analysis. We estimate model (1) on a new set of outcomes: the number of male and female drivers involved in fatal crashes in each CZ-year; the number of male and female driver fatalities in each CZ-year; and the annual number of fatal crashes, and driver fatalities, in each CZ with a driver in one of seven age categories (under 18 years, 18 to 24, 25 to 34, 35 to 44, 45 to 54, 55 to 64, and 65 and over). We estimate model (1) on these new outcomes using the fully saturated, Poisson specification (akin to the results reported in column (9) of Table 2). We report the result of this analysis in Table 4. Panel A shows the results for the number of crashes by driver demographics, and Panel B shows the results for the number of driver deaths by driver demographics.

Table 4.

Crash and driver deaths by driver demographics

	(1)	(2)	(3)	(4)	(5)	(6)	(7)	(8)	(9)
	Panel A: Crashes
	Male Driver	Female Driver	Under 18 Driver	18–24 Driver	25–34 Driver	35–44 Driver	45–54 Driver	55–64 Driver	65 and over Driver
Rx per Capita	0.135**	−0.062	0.082	0.038	0.238**	0.130	−0.014	−0.005	0.014
	(0.047)	(0.061)	(0.168)	(0.078)	(0.078)	(0.083)	(0.085)	(0.080)	(0.079)
	[6.778]	[−1.106]	[0.168]	[0.406]	[2.977]	[1.332]	[−0.148]	[−0.039]	[0.137]
Dep. Variable Mean	50.1	17.7	2.1	10.6	12.5	10.2	10.3	8.0	9.9
N	6,829	6,784	6,595	6,779	6,786	6,779	6,803	6,768	6,716
	Panel B: Driver deaths
	Male Driver Death	Female Driver Death	Under 18 Driver Death	18–24 Driver Death	25–34 Driver Death	35–44 Driver Death	45–54 Driver Death	55–64 Driver Death	65 and over Driver Death
Rx per Capita	0.140**	0.026	0.104	0.091	0.287**	0.170	0.019	0.055	−0.002
	(0.049)	(0.079)	(0.234)	(0.104)	(0.110)	(0.105)	(0.102)	(0.110)	(0.092)
	[3.468]	[0.196]	[0.095]	[0.457]	[1.639]	[0.170]	[0.093]	[0.218]	[−0.011]
Dep. Variable Mean	24.8	7.5	0.9	5.0	5.7	4.5	4.8	4.0	5.3
N	6,829	6,766	6,307	6,708	6,766	6,685	6,735	6,699	6,716

^*p<0.05;

^**p<0.01;

^***p<0.001

Notes: Estimated on data from the FARS between 2007 and 2016. Poisson models explaining the number of fatal crashes, and the number driver fatalities in each commuting zone in each year, according to driver demographics. Rx Rate is the number of opioid prescriptions per resident in each CZ, in each year. All models include a population offset tern, year and commuting zone fixed effects, controls for the unemployment rate, median household income, the poverty rate, and share of employment in construction, and state-by-year fixed effects. Robust standard errors clustered at the CZ level in brackets. Average marginal effects in square brackets.

In columns (1) and (2) of Panel A of Table 4, we demonstrate that the association between local prescriptions and crashes is driven by crashes among male drivers. We estimate that one additional annual prescription per capita is associated with a 0.14 log point increase in the number of fatal crashes involving male drivers per CZ, or about 6.8 additional crashes per year. This translates into an elasticity of about 0.12. We do not estimate a significant relationship between prescriptions and crashes involving female drivers. In columns (1) and (2) of Panel B, we also confirm that the relationship between the local opioid prescription rate and driver fatalities is isolated to male drivers. We estimate that one additional per capita opioid prescription is associated with about 3.5 additional male driver fatalities, and is unrelated to female driver fatalities.

In the remaining columns of Panel A, we show that the association between local prescriptions and fatal car crashes is only statistically significant at the 5% level among drivers aged 25 to 34; crashes involving younger and older drivers are not significantly related to local prescriptions. We estimate that one additional annual per capita prescription is associated with a 0.238 log point increase in the number of fatal crashes involving a driver between the ages of 25 and 34. This translates into about 3 more annual fatal crashes per CZ among drivers in this age group, or an elasticity of 0.22. Again, the results in Panel B confirm this. We find that one additional per capita prescription is associated with about 1.6 additional deaths among drivers between the ages of 25 and 34.

D. DRUG AND ALCOHOL USE

In Table 5, we report results from estimating model (1) on the drug- and alcohol-related crash outcomes. Panel A shows results for the drug testing outcomes. In columns (1) through (3), we show the results of estimating equation (1) on the number of drivers involved in fatal crashes who have drug test results reported in the FARS in each CZ-year. In column (1), we estimate a relatively large, marginally statistically insignificant coefficient, suggesting that increases in local prescribing rates may be positively associated with more prevalent drug testing among drivers. However, once we add the state-by-year fixed effects, the estimated coefficient decreases in magnitude, approaching zero. The remainder of the columns in Panel A show the results for the drug use outcomes. In columns (4) through (6), we report results for the number of drivers involved in fatal crashes who have a positive drug test reported in the FARS, and in columns (7) through (9) we report the results of drivers with a positive narcotics test result (including opioids). The baseline results in columns (4) and (7) indicate that one additional annual per capita opioid prescription in a CZ is associated with 0.367 and 0.769 log point increases in the number of drug- and narcotic-positive drivers, respectively. Because relatively few drivers test positive for drugs, these estimates are large in magnitude. They suggest that a 10 percent increase in the local per capita prescription rate is associated with a 3 percent increase in drug-positive drivers, and a 7 percent increase in narcotic-positive drivers. However, for both outcomes, the addition of the state-by-year fixed effects in columns (5), (6), (8) and (9), attenuates the estimates, rendering them statistically insignificant.

Table 5.

Two-way fixed effects Poisson analysis, drug- and alcohol-involvement outcomes

	(1)	(2)	(3)	(4)	(5)	(6)	(7)	(8)	(9)
	Panel A: Drug testing outcomes
	Driver Drug Tested			Driver Pos. Drug			Driver Pos. Opioids
Rx per Capita	0.160	0.057	0.051	0.367***	0.070	0.060	0.769***	0.266	0.256
	(0.092)	(0.065)	(0.065)	(0.111)	(0.102)	(0.100)	(0.176)	(0.168)	(0.168)
	[4.322]	[1.537]	[1.387]	[3.135]	[0.601]	[0.513]	[1.619]	[0.561]	[0.539]
State by Year FE	N	Y	Y	N	Y	Y	N	Y	Y
Covariates	N	N	Y	N	N	Y	N	N	Y
Dep. Variable Mean	27	27	27	8.5	8.5	8.5	2.1	2.1	2.1
N	6,811	6,811	6,811	6,690	6,690	6,690	5,910	5,910	5,910
	Panel B: Alcohol testing outcomes
	Driver Alc. Tested			Driver Pos. Alcohol			Driver Drunk
Rx per Capita	0.030	0.034	0.028	0.185*	0.099	0.090	0.158	0.082	0.069
	(0.053)	(0.050)	(0.050)	(0.082)	(0.075)	(0.073)	(0.102)	(0.089)	(0.088)
	[1.066]	[1.208]	[0.984]	[2.406]	[1.282]	[1.177]	[1.837]	[1.032]	[0.802]
State by Year FE	N	Y	Y	N	Y	Y	N	Y	Y
Covariates	N	N	Y	N	N	Y	N	N	Y
Dep. Variable Mean	35.6	35.6	35.6	13.0	13.0	13.0	11.6	11.6	11.6
N	6,829	6,829	6,829	6,826	6,826	6,826	6,826	6,826	6,826

^*p<0.05;

^**p<0.01;

^***p<0.001

Notes: Estimated on data from the FARS between 2007 and 2016. Poisson models explaining the number of each event in each commuting zone in each year. Rx Rate is the number of opioid prescriptions per resident in each CZ, in each year. All models include a population offset term, year and commuting zone fixed effects. Robust standard errors clustered at the CZ level in brackets. Average marginal effects in square brackets.

In Panel B of Table 5, we report the results for the alcohol-involvement outcomes. In columns (1) through (3) we show that alcohol testing is not associated with CZ opioid prescription rates. In column (4), we estimate a positive association between local opioid prescriptions and drivers who have a positive alcohol test recorded in the FARS. Our estimate suggests that a 10 percent increase in the local opioid prescription rate is associated with a 2 percent increase in positive alcohol test results. However, after including the state-by-year fixed effects, the estimated coefficients decrease in magnitude and become insignificant. We do not estimate a statistically significant relationship between the local opioids prescription rate and drivers testing above the legal limit for alcohol in the fully saturated model specification.

IV. Discussion

The results presented above suggest that annual opioid prescription rates and annual car crash fatalities at the CZ-level are related. To build a case for causality, we estimate two-way fixed effects models, and demonstrate that the main fatality estimates are highly robust to the inclusion of covariates, and state-by-year fixed effects, suggesting that our estimates are not biased by omitted state-level factors. We also conduct a heterogeneity analysis. The results of this analysis both extend our main findings, and act as a falsification test. Previous research has shown that opioid use – especially during the current study period – was especially concentrated among males between the ages of 24 and 54 (Case and Deaton 2015; Centers for Disease Control and Prevention 2020b). As such, we expect to find the bulk of our mortality effects concentrated among drivers in these groups. If we found large effects outside of these groups, we would be concerned that the associations could be driven by confounding factors rather than an underlying causal relationship between opioid prescriptions and crashes.

The evidence produced by the heterogeneity analysis supports our main hypothesis. We show that the association between local prescriptions and crashes is only present for male drivers, and drivers between the ages of 25 and 34. We also show that driver deaths and prescription rates are related only for male drivers and drivers between the ages of 25 and 35. The fact that the association between prescriptions and crash outcomes is strongest among groups most affected by the opioid crisis points to a potential causal link between prescription rates and crash deaths.

Along with exploring the relationships between prescriptions and crash outcomes, we also estimate models relating opioid prescription rates to drug and alcohol test outcomes in the FARS. As we detail in the data section, analyses of these outcomes are complicated by two facts: that the FARS include data on fatal crashes only, and that drug and alcohol testing results in the FARS are incomplete. Accordingly, the results of analyses of these variables are less convincing than for the crash and fatality outcomes.

In our baseline model, we estimate that a 10 percent increase in opioid prescriptions per capita is associated with an 8 percent increase in positive narcotics tests among drivers involved in fatal crashes. If all drivers involved in fatal crashes were tested, this result would be strong evidence in favor of a causal link between prescriptions and crashes. However, we find that, unlike our crash and fatality outcomes, the magnitudes of our estimated coefficients for the drug-use outcomes are sensitive to the inclusion of state-by-year fixed effects. This suggests that time varying, state-level factors are correlated with local drug reporting policies. Thus, we cannot rule out the possibility that the associations between prescription rates and driver drug use outcomes reported in the FARS are driven by increased testing rather than increased drug use. Our findings underscore the difficulty in generating reliable estimates of drug-use using FARS data, and raise the possibility that previous studies documenting large increases in opioid use among drivers in the FARS may be overstated (Azagba et al. 2019; Chihuri and Li 2019; Li and Chihuri 2019; i.e. Chihuri and Li 2017a; Wilson, Stimpson, and Pagán 2016; Brady and Li 2014; Brady and Li 2013). As such, we take our crash and fatality estimates to be the most reliable of our study’s results.

Using extrapolated values from our model, and assuming our estimates reflect causal relationships, we can attribute about 2,100 motor vehicle deaths per year to opioid prescriptions. For context, every year over our study period about 35,000 people died from motor vehicle accidents. Thus, motor vehicle fatalities attributable to opioid prescriptions represent about 6 percent of all annual motor vehicle fatalities during the study period. We can also compare our fatality estimates to the effects of other traffic related factors. Studies of the relationship between the unemployment rate and fatal car crashes generally find that a one-point decrease in the local unemployment rate is associated with between a one and three percent increase in traffic fatalities (Ruhm, C. J. 2000; Cotti and Tefft 2011; Ruhm, Christopher J. 2015; He 2016). National unemployment rates over the past 40 years have ranged between about 3.5 percent and 10.5 percent; thus, a one-point increase represents about a 15 percent change in unemployment. This points to motor vehicle fatality elasticities with respect to unemployment in the range of 0.06 to 0.2 – reasonably close to our estimates of the motor vehicle fatality elasticity with respect of opioid prescriptions of 0.07.

We can also compare the estimated effect of opioid prescriptions on motor vehicle fatalities to the effects of various road safety factors. Cohen and Einav (2003) show that a one percent increase in seatbelt usage reduces traffic fatalities by 0.13 percent, and Carpenter and Stehr (2008) show that mandatory seatbelt laws reduced traffic fatalities among high-school aged youths by eight percent. Graduated licensing laws reduced traffic fatalities among 15–17 year-olds by about six percent (Dee, Grabowski, and Morrisey 2005). Several studies have also estimated the effects of alcohol-control policies on traffic fatalities. Dee (2001) estimates that the introduction of BAC laws (limiting Blood Alcohol Content to 0.08) reduced traffic fatalities by seven percent; by contrast, several recent studies have shown limited effects of further reduced BAC limits (Cooper, Gehrsitz, and McIntyre 2020; Carpenter, Christopher 2004; Freeman 2007). Finally, Anderson, Hansen and Rees (2013) show that the introduction of medical marijuana laws has reduced traffic fatalities by at least eight percent.

Our study is limited in several ways. While we endeavor to estimate causal relationships, our main estimates rely on a relatively demanding identifying assumption: that there are no omitted variables that affect both crashes and opioid prescribing trends at the CZ-level. The instrumental variables analysis does not help us in this regard, as it produces highly imprecise estimates. While the direction of the estimates on crashes and deaths aligns with our two-way fixed effects results, the large standard errors could imply that the associations we uncover in the two-way fixed effects models are not causal in nature. However, it could also be that the IV analysis – which relies on state-level policy variation – obscures important local variation in prescription rates. As the descriptive figures and maps demonstrate, trends in aggregate prescriptions and crashes mask associations at the local level. Unfortunately, the fact that the IV analysis is underpowered means that its results do not provide useful evidence in this debate. This is one important limitation of our study.

Our study is also limited by the fact that we are only able to estimate intent-to-treat effects. The estimated effects we report capture the effects of local prescription rates on community-level outcomes. Because we estimate aggregate effects, we are unable to account for the fact that some prescriptions obtained in one CZ may actually be used elsewhere, and may therefore affect traffic fatalities in a different CZ. The fact that we find larger relative estimates using a CZ-level analysis than a county-level analysis could imply that such geographic spillovers in opioid use occur. However, CZs are adequately large to encompass likely commuting areas, and their use as the level of analysis is therefore likely to minimize spillover issues.

Finally, we are unable to capture the effects of additional opioid usage that is not reflected in prescription rates. This includes illegally trafficked prescription drugs, fentanyl and fentanyl analogs, or non-prescription opioids, such as heroin. In this sense, our estimates offer a lower bound on the magnitude of the association between opioid prevalence and fatal car crashes.

V. Conclusion

Over the past two decades, the widespread availability of opioids caused significant increases in overdose deaths. In this paper, we show that opioid availability may have contributed to additional car crash deaths as well. We demonstrate that there is a positive association between local opioid prescriptions and fatal car crashes. At the commuting zone level, we demonstrate that one additional annual prescription per capita – about a doubling of the average prescription rate over this period – is associated with about 4 more fatal crashes and traffic fatalities per CZ. To put these estimates in context, we estimate elasticities with respect to the prescription rate of about 0.07 – suggesting that a 10 percent increase in the annual per capita prescription rate is associated with a 0.7 percent increase in both fatal car crashes, and crash fatalities. We also find evidence that the deaths are concentrated among drivers, leading to a slightly larger implied elasticity of 0.1 among this group. Compared to the average crash, crashes that are associated with local opioid prescribing are more likely to kill the driver of the vehicle. We also show that the association between opioid prescriptions and deaths are isolated to male drivers, and drivers between the ages of 25 and 34. In general, these estimates are highly stable to the inclusion of other CZ-level covariates, and state-level trends.

During our study period, about 46,000 people per year died of drug overdose in the United States. Our estimate suggests that an additional 2,100 people per year may have died in fatal crashes due to prescription opioid availability. Following Florence, Luo and Rice (2021), we estimate that 2,000 motor vehicle deaths per year amount to $20.2billion in lost life (using a Value of Statistical Life of $10.1million), and $2.73billion in lifetime lost productivity (using an estimated, lifetime lost productivity cost of $1.4million per motor vehicle occupant death, derived from the CDC WISQARS cost of injury reports). These costs have not yet been included in estimates of the total societal costs of the opioid crisis.

Online Appendix for Do opioid prescriptions lead to fatal car crashes? Michael Betz and Lauren Jones

Figure A1.

Average annual CZ-level crash rate (per 100,000 people) and opioid prescription rate (per 100 people)

Note: Weighted averages using CZ population weights.

Source: Estimated by the authors using Fatality Analysis Reporting System data and IMSQuintiles Prescription data, 2007–2016

Figure A2.

Proportion of drivers in fatal crashes with a drug test result by county

Source: Estimated by the authors using Fatality Analysis Reporting System data, 2007–2016

Figure A3.

Proportion of drivers in fatal crashes with a drug test result by year and state

Source: Estimated by the authors using Fatality Analysis Reporting System data, 2007–2016

Notes: We report the proportion of drivers involved in fatal crashes for whom we have a drug test result reported in the FARS.

Table A1.

Ordinary Least Squares regression results, selected outcomes

	(1)	(2)	(3)	(4)	(5)	(6)
Panel A: Crash and Fatality Outcomes
	Crashes		Deaths		Driver Deaths
Rx per Capita	3.496*** (0.995)	5.624** (2.124)	3.804*** (1.104)	6.002* (2.408)	2.873*** (0.736)	3.538* (1.537)
CZ Linear Time Trend	N	Y	N	Y	N	Y
Dep. Variable Mean	46.5	46.5	50.9	50.9	32.5	32.5
N	6,863	6,863	6,863	6,863	6,863	6,863
Panel B: Drug-involvement Outcomes
	Driver Drug Tested		Driver Pos. Drug		Driver Pos. Narcotics
Rx per Capita	1.314 (1.362)	3.126* (1.423)	0.344 (0.543)	0.708 (0.647)	0.516** (0.173)	0.876*** (0.246)
CZ Linear Time Trend	N	Y	N	Y	N	Y
Dep. Variable Mean	27.2	27.2	8.5	8.5	1.8	1.8
N	6,863	6,863	6,863	6,863	6,863	6,863
Panel C: Alcohol-involvement Outcomes
	Driver Alc. Tested		Driver Pos. Alcohol		Driver Drunk
Rx per Capita	0.236 (1.250)	2.550 (1.334)	0.236 (1.250)	2.550 (1.334)	0.428 (0.615)	0.271 (0.552)
CZ Linear Time Trend	N	Y	N	Y	N	Y
Dep. Variable Mean	35.9	35.9	13.1	13.1	11.7	11.7
N	6,863	6,863	6,863	6,863	6,863	6,863

^*p<0.05;

^**p<0.01;

^***p<0.001

Notes: Estimated on data from the FARS between 2007 and 2016. Ordinary Least Squares models explaining the number of each outcome in each commuting zone in each year. All models include year and commuting zone fixed effects, as well as controls for annual CZ-level population, unemployment rate, median household income, poverty rate, and proportion of employment in construction. Robust standard errors clustered at the CZ level in brackets.