The Impact of the Opioid Crisis on Firm Value and Investment

Abstract

We show a negative effect of opioid prescriptions on subsequent individual employment among employers in our sample using doctor-opioid-prescribing propensity as our instrument. This finding has implications for firms that must now contend with lower local labor supply. We find a negative relationship between opioid prescriptions and subsequent establishment growth. However, firms respond to labor shortages by investing more in technology, replacing the relatively scarcer labor with capital, especially when they are not financially constrained. We find positive abnormal returns, upon the passage of state laws intended to limit opioid prescriptions, that are driven by firms more reliant on labor.

Employee health directly affects worker productivity and the labor supply. Yet its implications on firm outcomes have not been adequately studied in the corporate finance literature. In this paper, we focus on the opioid epidemic and its large negative effects on health outcomes. Opioid abuse in the United States has reached unprecedented levels. The federal government estimates that, as of 2016, 2.1 million Americans were addicted to opioids and 11.4 million Americans (3.5% of the population) had misused opioids in the previous year (National Survey on Drug Use and Health Mortality in the United States 2016). A growing literature, starting with Krueger (2017), has shown a negative relationship between opioids and future labor market outcomes. This, in turn, has implications for firms that must now contend with a smaller or less productive pool of workers.^1,2

We document two main effects of the opioid epidemic on firms. First, we show that establishments in areas experiencing high opioid growth are subsequently characterized by lower sales and decreased employment growth. Second, we show that firms invest more in automation in the hardest-hit areas. The mechanism explaining these effects is a labor supply channel wherein opioid use affects the subsequent employment stability of working individuals. Labor scarcity should negatively affect firm growth as labor is a key input of production. However, we document that, surprisingly, firms respond by using automation to substitute for the relatively scarcer labor in harder-hit areas. In all these tests, we follow the medical literature and use opioid prescriptions as a proxy for opioid abuse (Cicero et al. 2007; Harris et al. 2019). Studies have shown that legal opioid prescriptions are an important driver of opioid addiction (Schnell 2019).³ Moreover, Cicero et al. (2007), Dasgupta et al. (2006), and Wisniewski, Purdy, and Blondell (2008), among other studies, have demonstrated a positive correlation between rates of prescriptions in a given geography and subsequent opioid abuse in the area.

We first validate that the labor supply mechanism holds in the data, using detailed individual-level evidence. To this end, we use prescription data extracted from individual-level health care claims paid by employer-sponsored insurance available from MarketScan. For this analysis, we match two individuals identified as full-time employees aged 18 to 60 and who live in the same county, receive the same medical diagnosis, and are of the same age and gender, but where one individual receives an opioid prescription for the first time in a given year and the other does not. We then observe whether the individual remains employed within the sample of firms covered in MarketScan 5 years later, a measure that indicates employment stability. To address endogeneity concerns, we instrument for the probability of being prescribed an opioid using the propensity of the doctor they visited to prescribe opioids for their medical condition the prior year. Our instrument follows the key finding in the literature that doctor practices are responsible for the spread of opioids in the United States (e.g., Barnett, Olenski, and Jena 2017; Currie and Schwandt 2021; Finkelstein et al. 2022; Eichmeyer and Zhang 2023).

We find a 2-percentage-point decrease in the probability of being employed by firms in MarketScan 5 years after the instrumented opioid prescription. These results are estimated with county-year-age-gender-diagnosis fixed effects, thus absorbing any time-varying shocks affecting demographic groups within a county. However, this may be insufficient to address all endogeneity if, for example, drug-seeking individuals visit doctors who have a reputation for readily prescribing opioids. To address this concern, we replicate our analysis using different subsamples in which we drop high-opioid prescriber doctors or drop high income-inequality counties where, within the same county-year-age-gender-diagnosis, there could still be sorting of lower-income individuals to lower-quality doctors.

Moreover, to the extent that doctor-patient matching is not random, it might be possible that sicker individuals match with higher opioid prescribers, even conditional on the same diagnosis. To this end, we drop cancer diagnoses throughout the analysis as these diagnoses often involve greater variation in prognoses. Similarly, we show that our results are robust to also dropping diagnoses for chronic conditions from the sample. Alternatively, we control for past doctor visits and past nonopioid medications prescribed to proxy for the health of the patient. We show that these additional controls do not affect our coefficient estimates, suggesting that our results are less likely to be driven by differences in illness severity. In an additional test, we proxy for emergency room (ER) visits, which are less subject to the “doctor-patient matching” concern. We construct our ER proxy by limiting the sample to the top-10 most common ER diagnoses in our data, as identified by the AAPC.^4,5

Having established a labor supply channel using detailed individual-level data within our sample, we next use establishment-level data to study how the opioid epidemic in a given county affects firms. Given the strong persistence in local opioid use, we use two observations of aggregated opioid use per county in a (long) stacked first-differences specification. As such, we measure the change in the rate of opioid prescriptions between 2002–2006 and 2006–2010 on the subsequent change in establishment employment, from 2007 to 2011 and 2011 to 2015, respectively. In our specifications, we control for firm-period fixed effects, thereby comparing the effect of opioids on establishments in the same firm and during the same time period but located in counties experiencing different historic opioid prescription growth. We also include industry-period fixed effects, to control for differential trends at the industry level, and controls for observable economic and demographic characteristics. We find that, on average, establishments in high opioid growth counties have lower employment 5 years later, as compared to establishments in low opioid growth counties. The economic magnitudes are also meaningful: an increase in opioid prescriptions from the 25th to the 75th percentile (an increase of 0.3/person) is associated with a 0.6% decline in employment. On the extensive margin, we document a negative and significant effect on establishment exits in counties that experience greater opioid prescription growth.

As labor is a key input of production, opioid use should also be negatively associated with sales growth. Indeed, using the same specification of 4-year stacked first-differences, we find that opioid prescriptions are negatively associated with establishment sales. In economic terms, an increase in opioid prescriptions from the 25th to the 75th percentile (an increase of 0.3/person) is associated with a 1.5% decrease in sales, on average. We confirm this result using data on establishment expansions at the county level, where we estimate a negative and significant effect.

Firms appear to respond to this labor shortage by changing their production processes toward greater use of capital. We use data on IT spending and the stock of computers to proxy for investment in automation. As before, we compare establishments within the same firm and time period but located in different counties, and control for time-varying firm and local economic and demographic characteristics as well as industry trends. We find that, on average, establishments in high opioid growth counties spend relatively more on IT 5 years later, compared to establishments at the same firm in low opioid growth counties. The results are economically important: an increase in opioid prescriptions from the 25th to the 75th percentile is associated with a 3.2% increase in IT budget and a 1.95% increase in the number of PCs.

We uncover substantial heterogeneity in the investment results. First, we provide evidence in support of a labor channel, by exploiting variation across industries that rely on labor easily replaceable by technology. To this end, we use a measure based on the fraction of each industry’s hours spent by workers on tasks that can be performed by industrial robots (Graetz and Michaels 2018). Consistent with the intuition that our results are driven by a labor shortage mechanism, we find that the increase in automation is more pronounced in establishments that belong to industries reliant on labor more easily replaceable by technology and where substituting capital for labor is more feasible. Second, we document that access to financing is a key driver of firms’ response to the opioid epidemic. We use firm size as a proxy for financial constraints, as in Hadlock and Pierce (2010). Consistent with the intuition that financial constraints determine firms’ ability to invest, we find that the increase in automation is driven entirely by larger or less financially constrained firms in our sample.

A potential concern with our establishment-level analysis is the endogeneity of opioid abuse. In particular, individuals may be more likely to abuse drugs when they feel that job opportunities are limited. Our key identifying assumption requires that opioid prescriptions written by doctors are independent of economic conditions 5 years later, after controlling for time-invariant unobservable and time-varying observable county differences. Although a plethora of evidence in the existing literature shows that deteriorating economic conditions are not a significant driver for geographic differences in opioid abuse, we present several pieces of evidence to mitigate the concern that omitted variables drive our findings.

First, the estimated coefficients of interest are similar when estimated with or without economic and demographic controls as well as industry trends. Likewise, our results are robust to including fixed effects, which absorb time-varying firm changes and differences in establishment-specific trends. Second, results do not depend on counties’ economic performance during the financial crisis. Third, we estimate similar results when we repeat the analysis in just the tradeable sector, which suggests that the results are not driven purely by changes in local demand. Fourth, to address concerns that trade shocks, such as cheaper Chinese imports, contribute to the demise of certain geographic areas, which are then more likely to suffer from the opioid epidemic, we drop from the sample all manufacturing industries, since Chinese imports affect specifically the manufacturing sector. Alternatively, we identify counties with the worst exposure to Chinese imports following Autor and Dorn (2013) and exclude those from our analysis. Our results are robust.

Fifth, we instrument opioid prescriptions with opioids prescribed following the most common ER diagnoses. Our identifying assumption is that emergency physician visits are driven by an unexpected and sudden deterioration in health, requiring immediate treatment, most likely in an emergency department, where doctors are randomly assigned. This immediacy and randomization across doctors reduces the probability that we are picking up intentional behavior seeking opioids. We find quantitatively similar effects of opioid prescription on sales, employment, and investment in technology. These results mitigate the concern that an omitted variable could be driving both drug-seeking behavior and long-term firm outcomes.

Finally, we show value implications by exploring announcement returns around state initiatives to reduce opioid use. We find that the opioid crisis hurts firm value using stock price reactions upon the passage of state laws intended to limit opioid prescriptions. The first law was passed in Massachusetts in 2016 and, since then, another 24 states have passed similar actions to limit opioid abuse. At the passage of such a law in the firm’s state of headquarters, we document a statistically significant abnormal return of 20 basis points, on average. Naturally, we show that this effect is driven by those firms whose state of headquarters contains a large fraction of its employees. Consistent with our argument that firms can mitigate some of the costs associated with opioid abuse by investing more heavily in automation, we show that the positive returns upon passage of these laws are more pronounced for the set of firms with low ex ante capital intensity. On average, these low capital-intensive firms realize a stock price gain of 60 basis points.

Our conclusion that deteriorating economic conditions do not seem to explain our results is consistent with a large literature that studies the determinants of opioid abuse. Currie and Schwandt (2021) summarize the literature and lay out the facts as to why neither contemporaneous nor long-term economic conditions can explain the opioid epidemic.⁶ Instead, they argue that opioids spread in the United States due to a combination of three factors: a change in beliefs amongst physicians that pain was not treated adequately, aggressive marketing by pharmaceutical companies falsely claiming that a new generation of opioids was effective at treating pain with minimal risk of addiction, and little public oversight (until recently) of opioid prescriptions by doctors.

Our paper contributes to the literature studying the economic costs of the opioid epidemic in affected communities.⁷  Cornaggia et al. (2021) and Li and Zhu (2019) show the impact of opioids on municipal bond rates. Jansen (2023) examines the impact of opioids on auto loans. Custodio, Cvijanovic, and Wiedemann (2023) examines the impact of opioids on real estate prices. Our paper is the first to study the impact of the opioid epidemic on firm outcomes. We show that opioid abuse has an economically important negative association with firm growth and valuation, and a positive association with firm investment in automation. Despite the absence of an exogenous shock to opioid abuse, our baseline estimates remain robust to a battery of tests mitigating alternative interpretations of these results. Beyond being the first paper to study the linkage between opioids and direct firm outcomes using granular data, our results also speak to the long-term implications for affected communities, which must now struggle with both high rates of drug abuse and job losses through automation.

Moreover, we contribute to the literature showing the negative link between opioid prescriptions and the labor supply (Krueger 2017; Aliprantis, Fee, and Schweitzer 2019; Harris et al. 2019; Savych, Neumark, and Lea 2019; Park and Powell 2021; Powell 2021; Alpert, Schwab, and Ukert 2022; Mukherjee, Sacks, and Yoo 2022; Beheshti 2023).⁸ Our results add to the literature in several important ways. First, we use individual-level data, in terms of both opioid use and employment stability, covering a representative sample of working-age Americans. Critically, individuals in our sample are working at the time of opioid use. Moreover, we are able to control for county-year-diagnosis-age-gender time-varying omitted variables. Instead, the extant literature either connects aggregate opioid use with aggregate employment outcomes or uses detailed data but for a selected sample of the population. Although we ultimately do not observe a random source of variation in opioid prescriptions, our instrumental variables analysis and the plethora of robustness tests allowed by the granularity of our data provide strong support for the validity of these findings.

Finally, we build on the growing literature in finance focused on drivers of firms’ decisions to automate. Tuzel and Zhang (2021) show that tax incentives through regulation affect firms’ propensity to automate. Bena, Hernán, and Simintzi (2022) show that employment protection prompts firms to change their production processes via labor-saving automation. Geng et al. (2022) show how minimum wage increases in China are associated with capital investment, especially when firms have room to improve technologically. Ma, Ouimet, and Simintzi (2022) show that M&As are followed by technology adoption for target firms. We instead show that an unprecedented health crisis can be surprisingly linked to higher automation for affected firms, through a labor supply mechanism.

1. Origins and Determinants of the Opioid Crisis

There are three phases of the opioid crisis: the first phase, which extends through 2010, relates to opioid prescriptions by doctors; the second phase, which concludes in 2013, is characterized by a shift to heroin consumption, while the third phase, starting in 2013, is characterized by a shift toward synthetic opioids, such as fentanyl (Maclean et al. 2020). Our focus in this paper is mostly on the first phase of the opioid epidemic, attributable to doctor prescriptions as described by (Maclean et al. 2020).

Starting in the 1980s, the medical community in the United States began to push for a more aggressive approach to treating pain. A view that pain was relatively undertreated in the United States became prevalent (Weiloo 2014). Following the arrival of a new generation of prescription opioids, such as the 1995 Food and Drug Administration (FDA) approval of OxyContin (oxycodone controlled-release), the American Academy of Pain Medicine and the American Pain Society advocated for greater use of opioids. They argued that the long-term risk of addiction from these drugs was minimal. This stance became further institutionalized in 2001 when the Joint Commission on Accreditation of Healthcare Organizations (TJC) determined that the treatment and monitoring of pain should be the fifth vital sign, thus creating a new metric by which doctors and hospitals would be judged (Fiore 2016). Even as late as 2011, the Institute of Medicine released a study arguing that pain was being undertreated in America.⁹ Concerns about the possible overuse of opioid prescriptions for chronic pain conditions became more common in the 2000s. In 2014, the Agency for Healthcare Research and Quality (AHRQ) concluded that there is limited, if any, evidence-based medicine to support opioids’ use in chronic nonterminal pain (Chou et al. 2014). In 2016, the FDA and the Centers for Disease Control and Prevention (CDC) issued new policy recommendations for prescribing opioids, with an emphasis on the large public health costs.¹⁰ In 2017, the TJC issued new standards on the treatment of pain.

Pharmaceutical companies, like Purdue Pharma, reiterated the same message in their marketing materials. In advertising their new drug OxyContin, Purdue Pharma made no mention of its addiction potential, relying on two small retrospective studies from the 1980s.¹¹ According to training materials, Purdue instructed sales representatives to assure doctors—repeatedly and without evidence—that “fewer than one percent” of patients who took OxyContin became addicted (Keefe 2017). OxyContin was promoted as safe for chronic pain as well as for simple conditions like wisdom tooth extraction, where alternative pain relief treatments were available (Currie and Schwandt 2021). The FDA later accused Purdue Pharma of false advertising. In 2007, Purdue Pharma pleaded guilty to misbranding OxyContin, paid a fine of over $600M, and agreed to cut its sales force in half.¹² In 2019, Purdue Pharma filed for bankruptcy in the face of mounting litigation for the company’s involvement in the opioid epidemic (Mulvihill 2019).

During this time, the lack of a clear nationwide guidance for doctors and limited public oversight of opioid prescriptions led to a lack of consensus among doctors on best practices and significant heterogeneity in doctor approaches to prescribing opioids (Tamayo-Sarver et al. 2004; Cantrill et al. 2012; Poon and Greenwood-Ericksen 2014; Paulozzi, Mack, and Hockenberry 2014; Kuo et al. 2016; Jena, Goldman, and Karaca-Mandic 2016). Moreover, doctors in the United States had significant discretion in prescribing opioids to patients. In contrast, other countries follow more restrictive policies, such as having a lower maximum allowable opioid dosage, requiring doctors to undergo special training or use special prescription pads, or requiring patients to register in order to take opioids (Ho 2019).

Case and Deaton (2015) brought much-needed attention to the opioid crisis when coining the term “deaths of despair” and suggesting that economic conditions played a role. However, subsequent papers using better data have shown that economic conditions are not a significant driver of regional opioid use. In fact, most deaths attributed to opioids occur in states with low unemployment rates (Currie and Schwandt 2021).¹³

Specifically, Currie, Jin, and Schnell (2019) find a positive relationship between employment and 1-year-lagged opioid prescriptions at the county level for the period 2006 through 2014. This is consistent with the observation that the vast majority of people taking opioids are employed in their sample. Ruhm (2018) finds that economic conditions can predict opioid prescriptions in the cross-section of counties. However, controlling for demographics and persistent county characteristics washes away the explanatory power of the controls for economic conditions. Other papers, using specific economic shocks for better identification, likewise find that economic conditions are not a key driver of opioid use. For example, Pierce and Schott (2020) show that an interquartile increase in trade exposure can explain only one-tenth of drug overdose deaths. Schwandt and Von Wachter (2020) study whether long-run effects of entering the labor market in a recession could explain the opioid mortality rate. Even under the extreme assumption that all cohorts entered the labor market in a recession, their model could explain only one eighth of opioid deaths. Consistent with the argument that doctor practices are responsible for the epidemic, Finkelstein et al. (2022) show that the regional differences in the supply of prescription opioids from doctors is a key contributor to opioid abuse, as opposed to patient-specific factors, such as mental health or poor economic prospects.

The question as to why doctors have different prescribing practices during the first wave of the opioid crisis is beyond the scope of our paper. However, several papers strive to understand what drives such differences across doctors in opioid-prescribing behavior. Hadland et al. (2019) and Alpert et al. (2022) show that aggressive marketing by pharmaceutical companies is associated with higher opioid-related mortality rates. Schnell and Currie (2018) and Eichmeyer and Zhang (2023) discuss the role of education and of doctors’ pain management skills, respectively, and argue that lower education quality seems correlated with higher-volume prescribing patterns. Neprash and Barnett (2019) show that even within the same doctor, there is variation in terms of prescribing opioids depending on doctors’ busyness. When doctors see patients toward the end of their day, they tend to prescribe opioids more. Taken together, this evidence suggests that different doctor practices are likely responsible for differences in the supply of opioids and the uneven spread of the epidemic, as in Finkelstein et al. (2022).

As the epidemic grew and the addictive nature of opioids increasingly occupied the public discussion, awareness about the damaging effects of misusing opioids has increased. In response, several states have taken more drastic measures to curb opioid adoption with legislation that sets explicit limits on opioid prescriptions (with some exceptions, such as cancer treatment). In 2016, Massachusetts became the first state to limit opioid prescriptions to a 7-day supply for first-time users. As of 2018, 25 states have legislation limiting the quantity of opioids that can be prescribed. In October 2017, the U.S. government declared opioids a public health emergency. In 2019, Medicare adopted a 7-day supply limit for new opioid patients at the federal level.

2. Data

We identify opioid prescriptions at the individual level using data provided by Merative MarketScan Research Databases (Adamson, Chang, and Hansen 2008). MarketScan covers anonymized individual-level health data for 37.8 million individuals with employment-based private insurance through a participating employer.¹⁴ For each individual, we observe all medical expenditures covered by their medical insurance. We observe the date of service and diagnosis code, drugs obtained, and date the prescription was filled. We also observe county of residence, age, gender, and employment status for each individual.

We aggregate data to the county level to measure local opioid prescription intensity.¹⁵ We use historic county-level opioid prescriptions as a proxy for local opioid abuse. Legal opioids can lead to abuse through two main channels. First, the original consumer of the opioid can end up unintentionally addicted. In a widely cited meta-analysis, Volkow and McLellan (2016) find that up to 8% of patients who fill an opioid prescription will end up with a diagnosed opioid addiction and 15% to 26% will misuse opioids. According to the National Institute on Drug Abuse (2020), 21% to 29% of patients prescribed opioids for chronic pain misuse them, 8% to 12% develop an opioid use disorder, and 4% to 6% of those who misuse prescription opioids start taking heroin. Eichmeyer and Zhang (2023) exploit quasi-random assignment of doctors to patients and show that assignment to a top prescriber increases the probability of long-term opioid use by 20% and the probability of an opioid use disorder by 4%. Second, legal opioid prescriptions have been shown to be a major source of diverted opioids, as in Compton, Boyle, and Wargo (2015) and Shei et al. (2015). These diverted pharmaceuticals are then typically consumed in the local community, leading to a relationship between rates of opioid prescriptions in a given geography and opioid abuse in the area, as in Cicero et al. (2007).¹⁶

We use rates of historic (5-year-lagged) opioid prescriptions to allow for time between the initial prescription and the onset of drug abuse. However, using 5-year-lagged prescriptions is unlikely to attenuate the relationship between opioid prescriptions and opioid abuse as opioid addiction is a chronic condition. Flynn et al. (2003) find that only 28% of opioid addicts are in recovery 5 years later. Alpert et al. (2022) also find that differences in state-level opioid prescription regulations affect opioid overdose deaths with a lag that grows in intensity over time.

In Table 1, panel A, we report summary statistics on county-level opioid prescription rates. We measure opioid prescriptions as the average opioid prescriptions per (MarketScan) enrollee in that county and year. The sample covers 3,080 unique counties during the time period 2002 through 2010.¹⁷ On average, we report a per enrollee opioid prescription rate of 0.48. Our measure of opioid prescriptions per enrollee is modestly lower than the per capita prescription rates reported by the Centers for Disease Control and Prevention (CDC), likely reflecting healthier demographics of our employed population, as compared to the full adult population in the CDC data.^18,19 We use MarketScan as our baseline data because it is available for a longer time series and, specifically, provides information on opioid prescriptions among current labor market participants. According to Currie, Jin, and Schnell (2019), the majority of people perscribed opioids are working-age individuals and prescriptions are paid for by employer-provided health insurance (precisely the source of our data). Moreover, the richness of MarketScan data allows us to look within county at individual-level outcomes.²⁰

In panel A, we also report summary statistics for key county-level demographic and economic variables. The unit of observation is at the county level, and we continue to report statistics for all years in our data (2002–2010). Economic control variables include median household income. Demographic control variables include total population, distributions by race and age, and neoplasms mortality. The appendix defines all variables.

In panel B, we report summary statistics of establishment-level data on information technology from the Computer Intelligence Technology Database (CiTDB), a proprietary database that provides information on computers and telecommunication technologies installed in establishments across the U.S. CiTDB generates its data using annual surveys of establishments. The data contain detailed information on IT investment and use, including the stock of existing technology and budgets for new investments. The data also specify information on the county of each establishment, a firm-level identifier, and establishment-level revenue and employment.²¹

We summarize the establishment-level data for years 2007–2015. In our analysis, we drop observations in highly regulated (agriculture, education, and utility) or public sector industries. We also drop all establishments in the health care sector, given opioids may affect health care through channels other than labor scarcity. Labor demand may increase as a result of the opioid epidemic due to greater need for medical personnel (McNeely et al. 2022). Moreover, the opioid epidemic constitutes a substantial burden for the health care system, which may now need to draw resources from other activities and rebalance their services toward treating opioid abuse (Douglas et al. 2019). We also limit our sample to establishments with a minimum of 20 employees in the first year an establishment appears in the two-period sample (i.e., 2007 or 2011), to ensure that our results are driven by economically important establishments. We end up with 577,121 unique establishments of 126,241 unique firms. The average establishment has $37.6 million in revenue, 120.6 employees, invests $0.5 million in IT, and has a stock of 83.6 PCs.

3. Opioids and Individual Employment

Given our hypothesis that the impact of opioids on firms is driven by a labor supply channel, we start by identifying the effect of the opioid crisis on the labor market. We explore whether individuals who have taken a prescription opioid in a given year have different future employment outcomes, compared to similar individuals, seeking treatment for the same medical condition, who were not prescribed opioids that year. We then compare an individual who has taken a prescription opioid to an otherwise similar control individual without such a prescription history and measure the marginal difference in employment outcomes 5 years later.

To be specific, our dependent variable is defined as the probability of being employed within the MarketScan sample 5 years later. If an individual does not remain employed within one of the firms that shares its data with MarketScan, it means that they transitioned either to a different job or to unemployment. Both outcomes are consistent with opioids being associated with a lower labor supply: individuals may become unemployed or drop out of the labor force because of their addiction (e.g., via death, imprisonment, or entry into a rehabilitation center), they may not be able to find a job because of their addiction and thus remain unemployed (e.g., failing drug tests), or they may change jobs after being terminated due to lower productivity. All those arguments are consistent with either a lower quantity (dropping out of employment) or a lower quality (higher turnover due to low productivity) of the labor supply, except that the former involves larger negative consequences. Despite the caveat that we cannot disentangle these different channels, our measure is unique to the literature due to the strict confidentiality of individuals’ health data in the United States. They therefore cannot typically be matched to other data sources with information on individuals’ labor market outcomes.²²

For this analysis, we require individuals to be employed full-time and be between the ages of 18 and 60, to avoid including individuals who are expected to retire within a 5-year window. Moreover, given the addictive nature of opioids, we limit our sample to individuals who have not previously received an opioid in our data. We further restrict our data to exclude individuals who have been diagnosed with cancer in the current or prior year, as cancer diagnoses are characterized by large variation in prognoses.²³ We identify treated individuals as those who receive their first opioid prescription during the period 2001 through 2010. We start our analysis in 2001 to allow for a window to measure previous opioid use. We stop in 2010 to allow for 5 years until the end year of our data. We randomly pick control individuals among those who did not receive an opioid prescription in that year and, as with the treated sample, did not receive an opioid prescription in previous years. We also require treated and control individuals to be of the same age and gender, to reside in the same county, and to receive the same medical diagnosis when they visit the doctor that year.²⁴

In Table 2, columns 1 and 2, we start by directly comparing treated and control individuals by estimating the following ordinary least squares (OLS) specification:

where |$ i $| indexes individuals, |$ d $| indexes doctors, |$ s $| indexes diagnoses codes, and |$ t $| indexes year. |$ FE $| includes fixed effects for county-year-age-gender-diagnosis and insurance plan type.²⁵ Standard errors are clustered at the county level.

We find that treated individuals, who are being prescribed opioids for the fist time, are less likely to remain employed within the MarketScan sample by 1.7 percentage points, and this coefficient is statistically significant at the 1% level. Given that the OLS results are difficult to interpret due to potential endogeneity, we next instrument for the original opioid prescription by using doctor propensity to write opioid prescriptions for that given diagnosis. We measure doctor-opioid-prescribing intensity as the rate with which they prescribed opioids for the same medical diagnosis during the prior year. Eichmeyer and Zhang (2023), using a setting in which first-time patients are randomly assigned to a doctor within a facility by an administrative clerk, show that assignment to a top opioid prescriber increases the probability of long-term opioid use by 20% and the probability of an opioid use disorder by 4%. Similarly, Barnett, Olenski, and Jena (2017) find that whether or not a Medicare patient is randomly assigned to a high-opioid-prescribing doctor is a significant predictor of long-term opioid use. These differences in doctors’ propensity to prescribe opioids to patients motivate the doctor fixed effect captured in our data.

We estimate our first-stage equation as follows:

where |$ i $| indexes individuals, |$ d $| indexes doctors, |$ s $| indexes diagnoses codes, and |$ t $| indexes year. |$ FE $| includes fixed effects for county-year-age-gender-diagnosis and insurance plan type. Standard errors are clustered at the county level.

In the second stage, we estimate differences in employment rates 5 years later, using the instrumented probability of receiving an opioid prescription.

where |$ i $| indexes individuals, |$ d $| indexes doctors, |$ s $| indexes diagnosis codes, and |$ t $| indexes year. |$ FE $| includes fixed effects for county-year-age-gender-diagnosis and insurance plan type. Standard errors are clustered at the county level.

We present the 2SLS results in Table 2, columns 2 and 3. The first-stage results, in column 2, show that doctor-opioid-prescribing intensity significantly predicts whether an individual will receive an opioid. Our instrument is significant at the 1% level with a first-stage F-stat of 6,846, well above the 10 threshold. The second-stage result, in column 3, shows that individuals who receive an opioid prescription are 2% less likely to be employed at a firm within MarketScan 5 years later. In our analysis, we include insurance plan fixed effects, which control for the fact that individuals with better insurance coverage may have better health care access. We also control for interacted county-year-age-gender-diagnosis codes, thereby comparing individuals who live in the same county, are of the same age and gender and who receive the same diagnosis code when they visit the doctor in the same year. This absorbs any time-varying local shocks specific to a given demographic group that could be driving the estimated differences.

One concern for our analysis would be if individuals with worse future job opportunities seek out doctors who are more likely to write opioid prescriptions. To address this concern, we show that our results are robust to excluding individuals more likely to exhibit drug-seeking behavior. First, in columns 4 and 5, we exclude doctors with opioid-prescribing intensity in the top 10% of our sample. A patient seeking medical care for the purpose of drug seeking will try to target those doctors with the highest opioid-prescribing tendency.²⁶ Second, in columns 6 and 7, we exclude counties with income inequality (measured by the Gini index) in the top 10% of our sample. In those high-inequality counties, there might be sorting of lower income individuals to lower-quality doctors, who might be more likely to prescribe opioids. Although controlling for insurance plan fixed effects alleviates this concern to some extent, dropping counties with large inequalities further addresses the fact that differences in the quality of health care access within counties could still drive results.

Alternatively, despite the fact that we exactly match on diagnoses, it might still be possible that individuals with worse prognoses will also have worse employment outcomes and these individuals match to doctors with higher opioid-prescribing propensities. As we previously mentioned, we drop cancer diagnoses throughout this analysis. Moreover, the results presented earlier, dropping top opioid prescribers, mitigate this concern. In addition, we present further robustness in Internet Appendix Table B3. In columns 1 and 2, we repeat Table 2, columns 2 and 3, but drop chronic conditions because they are more likely to have a greater range of prognoses.²⁷ We also control for the underlying health of the patient by controlling for past medical visits (columns 3 and 4), past prescriptions (columns 5 and 6), and number of unique providers visited in the prior year (columns 7 and 8). Across specifications, the inclusion of these controls does not change the coefficient of interest and we continue to find a 2% reduction in the probability of employment 5 years after the first opioid prescription.

Finally, in Table 2, columns 8-9, we repeat our analysis using just the top 10 most common emergency room (ER) diagnoses in our data. We define ER diagnosis codes following the AAPC classification.²⁸ Our assumption is that individuals covered by health insurance receive care in ERs only when facing a health emergency, at which point random assignment to doctors is more likely.²⁹

Our results are robust across all these different tests, which alleviates concerns that nonrandom individual-doctor matching within counties can explain our findings, conditional on the controls. However, we should reiterate the caveats to this analysis. In our data, we can observe whether an individual who is employed in a given year, remains employed among the set of firms in MarketScan 5 years later. While we refer to this as being “employed” for ease of exposition, what we technically observe is when a worker is no longer matched to his/her original employer or to another employer who also participates with MarketScan. This can represent being (1) unemployed, having exited the workforce or (2) matched to another firm not in our sample. Since we are comparing the estimates for our treated sample to a matched control sample, we are controlling for unconditional rates of transitions out of employment and job-to-job transitions. Our coefficient of interest is jointly estimating any deviation, relative to the mean, in either explanation 1 or explanation 2. Although both explanations are consistent with negative impacts on the labor supply from opioids, the former involves larger negative consequences. It is also important to note that changes in individual employment is only one measure of how opioids can affect the labor market. Employment status does not capture changes in the quality of the pool of workers, conditional on the same job being filled. Individuals abusing opioids are presumably more likely to miss work, be involved in on-the-job injuries, and be less productive overall. As such, our estimate of the impact on individual employment likely underestimates the impact of the opioid crisis on labor.

Overall, these results suggest a negative association between higher rates of opioid prescriptions and the subsequent supply of labor available to firms. This can have important implications for firms, which we examine in the following section.

4. Opioids and Firm Outcomes

4.1. Methodology

Next, we investigate the relationship between local opioid use and firm outcomes with a model using two-stacked long differences. We measure the change in establishment-level outcomes between 2007 and 2011 and between 2011 and 2015. We start at 2007 and end in 2015, the first and last years, respectively, of our CiTDB sample.³⁰ We use historic 5-year-lagged opioid prescriptions, consistent with the lag structure in the previous analysis, as it takes time for opioid abuse in the community to accumulate. Our choice of long lag structure is consistent with findings by Alpert et al. (2022), who show that differences in state-level opioid prescriptions affected opioid overdose deaths with a lag that grows in intensity over time. Specifically, in our analysis, we measure opioid prescriptions as the change across 2002–2006 (matched to establishment-level outcomes across 2007–2011) and as the change across 2006–2010 (matched to establishment-level outcomes across 2011–2015). We thus estimate the following specification:

where |$ \Delta $| denotes the long (4-year) difference operator, |$ c $| indexes county, |$ i $| indexes establishments, |$ f $| indexes firms, and |$ t $| indexes time period. |$ \Delta Opioid\ prescriptions $| is the change in opioid prescription per enrollee. |$ \Delta y $| is the change in establishment-level outcome variables, including sales, employment, and investment in IT. |$ \Delta X $| controls for changes (contemporaneous to the change in opioid prescription rates) in economic and demographic characteristics as well as the underlying cancer rate in the county. Specifically, these controls include the logarithm of population, the logarithm of median household income, the white ratio, the age 20-64 ratio, the age over 65 ratio, and the rate of neoplasms mortality. |$ FE $| includes firm-period fixed effects, absorbing time-varying differences in firm quality and industry-period fixed effects, absorbing time-varying differences across industries. We double-cluster standard errors at the county and firm levels.

4.2. Sales and employment growth

We first explore the relation between opioid prescriptions and growth in establishment sales and employment. Table 3 reports the results. In column 1, we find a negative and significant correlation between opioid prescription rates and subsequent establishment sales in the county. In column 2, we estimate similar results after controlling for economic and demographic county characteristics. We find a positive correlation between changes in county population and subsequent establishment sales, consistent with the idea that firms will enjoy greater demand in growing counties. We also find that increasing cancer rates in the county negatively correlate with subsequent establishment sales’ growth, presumably as firms enjoy stronger demand when located in healthier communities. Our baseline finding is economically important: an increase in opioid prescriptions from the 25th to the 75th percentile (an increase of 0.3 prescriptions/person) is associated with 1.5% decrease in sales in that establishment relative to the average establishment within the firm.

In column 3, we also find a negative correlation between opioid rates and subsequent establishment employment, a relationship that is robust to including economic and demographic controls in column 4. In economic terms, an increase in opioid prescriptions from the 25th to the 75th percentile is associated with a 0.6% decline in employment in that establishment relative to the average establishment within the firm.

Given that we include firm-period fixed effects in these regressions, the results should be interpreted as showing within-firm reallocation. However, we find similar results if we exclude firm fixed effects (Internet Appendix Table B6), which suggests that the same patterns identified within firms are also observed across firms. These results also help address potential concerns that an omitted variable associated with firms located in high-opioid counties drives our results. In addition, we find consistent results on the extensive margin using U.S. Census administrative data. Using counts of establishments at the county level, we find a statistically positive (negative) relation between opioid prescription rates and subsequent firm deaths (expansions) (Internet Appendix Table B7).

4.3. Investment

Next, we examine whether firms change their production choices in response to labor shortages attributable to the opioid epidemic. To the extent that opioids reduce the number and quality of available workers, firms may choose to substitute capital for labor by investing in automation technologies (Autor, Levy, and Murnane 2003). To test this prediction, we use data on IT spending available from CiTDB. Specifically, we use the IT budget and the count of computers (PCs) to proxy for investment in automation and the stock of installed technology, respectively. While investment in IT is not inclusive of all forms of automation, our assumption is that an increase in automation would also be paired with an increase in IT.

In Table 4, we report results using measures of IT investment, in both levels (log-transformed) and normalized by establishment revenue and employment. We follow Equation (4) and control for firm time-varying trends (firm-period fixed effects), industry time-varying trends (industry-period fixed effects), and economic and demographic controls.³¹ We find a positive and significant association between increases in opioid prescriptions in the county and subsequent increases in IT investment across specifications.³² Thus, firms increase IT investment relatively more at their establishments located in counties with higher growth in past opioid prescription rates as compared to establishments located in counties with lower growth in past opioid prescription. In terms of economic magnitude, an increase in opioid prescriptions from the 25th to the 75th percentile (an increase of 0.3 prescriptions/person) is associated with a 3.2% increase in IT budget and a 1.95% increase in the count of PCs.³³

Moreover, in Table 5, we show that our results also hold with adding establishment fixed effects. This analysis is estimated using only the establishments observed over both time periods. Establishment fixed effects allow us to further control for differential trends by establishment. The results are quantitatively similar, with the exception that we lose statistical significance on the change in employment (even though the coefficient is of similar magnitude as in Table 3).

In Internet Appendix Table B14, we confirm that our findings are robust to using alternative measures of investment in automation. In column 1, we match CiTDB and Compustat and for the subset of publicly listed firms’ establishments that we are able to match between our data sets. We repeat our analysis by looking instead at changes in capital expenditures over employment. We find a positive association, driven by changes in capital expenditures (column 2) rather than by employment (column 3). In column 4, we instead use the share of process innovation as the dependent variable. This approach captures the shift of firms’ innovation mix toward devising innovation that reduces firms’ production costs (Bena and Simintzi 2022). This measure is available for both public Compustat firms and private firms, which we match to our data. We find a positive association, driven by the level of process innovation (column 5), while the level of nonprocess innovation remains unchanged (column 6). These results are consistent with the argument that firms invest in automation to change their production processes and substitute capital for labor as a response to labor shortages in opioid affected areas.

5. Cross-Sectional Heterogeneity

Next, we present cross-sectional heterogeneity evidence consistent with the capital deepening mechanism we document in Section 4.3. We first exploit heterogeneity in the labor channel, providing further evidence that the labor supply is a key driver of our baseline effects. Second, we examine variation in firms’ access to financing as a key driver of their ability to respond to the labor shortage through automation.

5.1. The labor channel

We consider heterogeneity in labor replaceability rates by industry, since investing in automation should be especially relevant in industries where technology can readily replace labor. We use the proxy created by Graetz and Michaels (2018), who measure the fraction of hours spent by workers in a given industry in tasks that can be performed by industrial robots.³⁴

In Table 6, panel A, we interact |$ \Delta $|  opioid prescriptions with an indicator variable (high labor repl.) that takes a value of one if the establishment is matched to an industry with labor replaceability above the sample median, and zero otherwise. We find that the positive relationship between opioid prescriptions and long-term establishment automation is significantly more pronounced for high-replaceability industries. These findings are consistent with the intuition that firms in these industries can better mitigate the costs of labor shortages through substitution with capital. Specifically, we find a stronger positive relation between opioid prescriptions and IT investment (across five out of six measures) in firms operating in high-replaceability industries.

5.2. Financial constraints

We consider heterogeneity in firms’ financial constraints as we predict that firms’ ability to finance their investment in automation should affect their response to the labor supply shortage due to the opioids epidemic. We use firm size to proxy for financial constraints as in Hadlock and Pierce (2010). We compute firm size as the sum of employment across all observed establishments in the CiTDB data for a given firm as of 2007 and 2011, for the first and second periods in the sample, respectively.

In Table 6, panel B, we interact |$ \Delta $|  opioid prescriptions with an indicator variable (high firm size) that takes a value of one if firm size is above the sample median in that period, and zero otherwise. In this analysis, we include industry-year fixed effects but do not include firm-period fixed effects, as our intention is to capture differential responses to the opioid epidemic within as well as across firms of different sizes. Consistent with the intuition that better access to finance allows firms to more easily invest in automation, we find a positive interaction coefficient across all specifications. These results also suggest that the average baseline effect in Table 4 is driven by larger firms, which are less financially constrained.

6. Identification

6.1. Robustness tests

Given the absence of exogenous variation in opioid prescriptions, a key concern with our analysis is that individuals may be more likely to seek out opioid prescriptions in areas with worse job opportunities. Despite the view in the economics literature that medical practices rather than differences in economic prospects are the primary driver of the opioid epidemic, we perform several tests to mitigate this concern that deteriorating economic conditions may explain our results.³⁵

In Table 7, we interact |$ \Delta $|  opioid prescriptions with changes in counties’ economic conditions measured during the financial crisis during the period 2007 through 2010. In panel A, we consider low |$ \Delta $|income, an indicator variable that takes the value of one if the change in the mean county-level household income from 2007 to 2010 is below the sample median, zero otherwise. The interaction coefficient is statistically insignificant across specifications while the baseline effect remains significant, suggesting that the associations between opioid growth and firm outcomes do not differ across counties that follow different trends during the crisis. Similarly, we interact |$ \Delta $|  opioid prescriptions with low |$ \Delta $|house price in panel B and with low |$ \Delta $|county emp. in panel C, indicator variables that take the value of one if the change during the period 2007–2010 places the county-level housing price index and county-level employment, respectively, below the sample median, and zero otherwise. These interaction coefficients are also statistically insignificant with the exception of column 2, panel B, which is only weakly significant. Collectively, the results in Table 7 do not provide support for the concern that the effect of the opioid epidemic on firm outcomes depends on the severity of the financial crisis at the county level.³⁶

Second, we address a related concern that an increase in Chinese imports might have affected certain geographies in the United States, dampening local economic conditions (Autor and Dorn 2013). This might in turn lead the local population in those depressed areas to abuse opioids.³⁷ In Internet Appendix Table B13, panel A, we empirically address this concern by dropping from the sample those establishments in manufacturing industries, namely, those industries shown in the literature to have been affected by cheaper Chinese imports. We find that our results are robust. In panel B, we instead drop from the sample the top quartile of counties with the highest exposure to Chinese imports as of 2000, and find that our results continue to hold.³⁸

Third, we consider the concern that declining local demand could be driving the results. The increased use of opioids could be, for example, responsible for dampening demand locally. In this case, opioids could still explain the decline in firm growth, albeit not through a labor channel. Alternatively, a decline in demand could be capturing local economic shocks. To examine whether these alternative interpretations could drive our results, we repeat our baseline analysis in Internet Appendix Table B13, panel C, using tradeable industries only (industries with more than 50% tradeable employment, as in Delgado, Bryden, and Zyontz 2014), namely, industries that are least affected by local demand, and estimate qualitatively similar results.

6.2. Pill mills

“Pill mills” helped seed the opioid crisis in certain areas. A typical pill mill consists of a storefront pain clinic in which one or more doctors write opioid prescriptions after brief consultations and typically with limited proof of medical appropriateness. These clinics typically provide the prescription (written by a staff doctor), which they also fill, so as to avoid issues with external pharmacies challenging the prescription’s legitimacy. These prescriptions represent opioids that are likely to be misused and, hence, likely to have labor market impacts that can subsequently impact local firm characteristics. However, the identification concern is that some of these pill mills serve drug seekers, who may travel from outside the county to get easy access to opioids. As such, including these counties in our analysis may introduce noise if the opioids in these counties are not consumed locally. Alternatively, if pill mills are endogenously located in areas with weaker labor markets, then including them in our data could potentially introduce bias.

To address these concerns, we identify counties most likely to contain a pill mill and drop those from the analysis. We identify pill mills using the Automation of Reports and Consolidated Orders System (ARCOS) data.³⁹ We use these data to identify a pill mill as a pharmacy that dispenses opioid morphine miligram equivalents (MME) in the top 5% of the sample. We then drop from the sample those counties with the highest 25% of these pill mills. In Table 8, panel A, we show that our results are robust to dropping these counties. In panel B, we also show that our results are similar if we exclude Florida, the state known for having the highest concentration of pill mills (Spencer 2019).

6.3. Instrumental variable

Next, we employ an instrumental variable analysis to further address concerns that omitted variables, such as local economic conditions, could be driving the relationship between county-level opioid prescription growth and subsequent establishment outcomes. We use opioids prescribed in response to the 10 most common emergency room diagnoses in our sample as our instrument. The idea is that our instrumental variable proxies for emergency visits and, in an ER, doctors are typically randomly assigned, thereby mitigating the concern that our results might be driven by intentional drug-seeking behavior on the part of the patient. In addition, our MarketScan data cover only employed individuals, thereby mitigating the concern that those without jobs and insurance may seek opioids at an ER, which is required to treat patients.

We estimate the following two-stage least square specification:

where |$ \Delta $| denotes the long (4-year) difference operator, |$ c $| indexes county, |$ i $| indexes establishments, |$ f $| indexes firms, and |$ t $| indexes time period. |$ \Delta ER\ opioid\ prescriptions $| is the change in ER opioid prescriptions per enrollee. |$ \Delta Opioid\ prescriptions $| is the change in opioid prescriptions per enrollee. |$ \Delta y $| is the change in establishment-level outcome variables (sales, employment and investment in IT). |$ \Delta X $| controls for changes in economic and demographic characteristics as well as the underlying cancer rate in the county. |$ FE $| includes firm-period fixed effects and industry-period fixed effects. We double-cluster standard errors at the county and firm levels.

Table 9, column 1, presents the first-stage results. Changes in ER opioid prescriptions significantly predict changes in overall opioid prescriptions. Columns 2-9 report the second-stage results. Our results are statistically significant across specifications and F-stats are well above the 10 threshold. Notably, the magnitudes are similar to those of the OLS estimation presented in Tables 3 and 4. An increase in opioid prescriptions from the 25th to the 75th percentile (an increase of 0.3 prescriptions/person) is associated with a 1.5% decrease in sales, 0.5% decrease in employment, 4.4% increase in IT budget, and 1.9% increase in the number of PCs. These results provide corroborating evidence that our findings are not driven by individuals who have poor future job opportunities and thus seek out opioids.

7. Laws to Limit Opioid Prescriptions and Firm Value

The opioid crisis has prompted states to respond. Massachusetts was the first state to pass a law limiting opioid prescriptions. Effective on March 14, 2016, the law established a maximum 7-day supply on prescriptions for opioids when issued to an adult for the first time, and for all opioid prescriptions for minors. Exemptions existed for cancer pain, chronic pain, and palliative care. According to the local press, the law “comes as Massachusetts grapples with a deadly drug crisis that claims about 100 lives per month” (Miller 2016). By 2018, 25 states had passed laws imposing limits on opioid prescriptions (Figure 2). A short description of the state laws passed is included in Internet Appendix Table A. Consistent with the anecdotal evidence from Massachusetts, Internet Appendix Table B15 shows that the only variable that significantly predicts passage of these laws in the cross-section of states is the (age-adjusted) opioid overdose death rate, while economic conditions or political economy do not seem to matter.

Given the timing of these laws, we cannot estimate their long-term effects on labor market outcomes or firm performance. Instead, we estimate firms’ stock price reaction at the announcement of their passage. We use firms listed in Compustat, CRSP, and CiTDB to estimate the daily average abnormal return for each event date using the Fama-French three- or four-factor model. To mitigate the concern that these laws could affect firms through a different channel, we drop health care industries from our analysis.⁴⁰ The date assigned for each law’s passage (⁠|$ law\ passage $|⁠) equals the date the law passed the state House or state Senate, whichever occurred first.⁴¹

Since all firms show up at each event, we account for the cross-correlation between firms using the portfolio approach suggested by Sefcik and Thompson (1986). Specifically, for each event, we construct portfolios of firms in our sample, weighted by |$ law\ passage $|⁠. We conduct a time-series analysis using daily returns for the portfolio between [–219,+1], where zero is the day of the event. We then regress daily returns in excess to risk-free returns on a dummy |$ I\{[-1,+1]\} $|⁠, which takes the value one between [–1,+1],and zero between [-219,-2], and Fama-French factors, controlling for event fixed effects and clustering standard errors at the event level. We present the average abnormal returns for each of the 3 days around the passage of opioid laws in Table 10.

In columns 1 and 2, we consider all firms and use the Fama-French 3-factor and 4-factor model, respectively. Firms exhibit a 7-basis-point average stock price reaction on each of the days around the passage of the legislation, statistically significant at the 5% level. The cumulative abnormal announcement return for the 3 days surrounding the law passage is 20 basis points. In columns 3–6, we divide all firms into two groups for each event, depending on whether or not the share of their employees located in the headquarters state (HQ. empl. ratio) is above the sample median. We define |$ HQ\ empl.\ ratio $| to be the share of a firm’s employment in the state of headquarters, using the CiTDB data to collect information on a firm’s establishment employment. The first and second groups include firms with headquarters employment ratios in the top and bottom 50%. We anticipate larger effects in the former group of firms, because the law change affects a larger share of their workforce.

In columns 3 and 5 (4 and 6), we use the Fama-French 3-factor (4-factor) model. We find the |$ law\ passage $| to be statistically significant in high HQ empl. firms in columns 3 and 4, consistent with the fact that firms that employ a large fraction of their workers in the state of the law passage respond to the law’s impact on their labor supply. The effect is also economically important, as indicated by the 50-basis-point cumulative abnormal return over the 3-day window surrounding the law passage. In contrast, |$ law\ passage $| is not statistically significant when a low fraction of employees is located in the firm’s state of headquarters (low HQ empl. firms). Overall, these results indicate that firms benefit from state legislation that intended to limit opioid prescriptions. This relationship is in line with our findings in Section 4.2 that the opioid crisis impedes firm growth.

One caveat of this analysis concerns whether these laws are contemporaneous with other changes that might benefit firm value, for reasons other than the effect on the labor pool. Although we cannot perfectly rule out this possibility, in Table 10, columns 7–10, we further explore heterogeneity in firms’ capital intensity. We proxy capital intensity using the count of PCs over employment pretreatment, as of 2015 (PC/empl).⁴² We split our observations by the sample median of PC/empl and report the regressions for these two subsets in columns 7–10. We find positive and significant average daily abnormal returns for firms with low capital intensity pretreatment. The cumulative effect over the 3-day window is equal to 60 basis points (columns 7 and 8), which denotes a stronger effect among firms most reliant on labor. In contrast, we find no effect for high capital intensity firms in columns 9 and 10. This is consistent with our earlier findings that firms invest in automation to mitigate the negative effect of labor market shortages due to opioids. These results indicate that the set of firms that are less capital intensive, and as such are more exposed to the labor shortages brought by the opioid crisis, benefit the most from states’ legislation aimed at reducing opioid abuse. The findings also mitigate the concern that an alternative interpretation unrelated to the labor pool drives our findings.

8. Conclusion

The opioid crisis was fueled, to a large extent, by physician prescriptions. Physicians prescribed opioids with the belief that this class of drug could improve the well-being of their patients, by reducing pain with minimal risk of addiction. Opioids, legally prescribed by doctors, marked the first wave of the opioid epidemic as defined by Maclean et al. (2020), which extends through 2010 and has been the primary focus of this paper. Unfortunately, opioids legally prescribed by doctors did indeed pose a significant risk of addiction, ultimately impairing the health of those abusing them. This negative health shock, in turn, has implications for the supply of productive workers, as evidenced by our finding that individuals prescribed opioids are less likely to be employed within the set of MarketScan firms 5 years later, compared to otherwise similar individuals who were not prescribed opioids when they visited a doctor for the same medical condition.

This is the first paper to document a negative link between opioids and (long-term) firm growth and valuations via this labor supply channel. We show that establishments located in counties that experience a higher growth in opioid prescription rates have lower employment and sales growth, compared to establishments within the same firm located in counties with a lower growth in opioid prescription rates. We also show that firms respond to opioid-associated labor shortages by investing in automation technologies to substitute capital for labor. We show a positive and significant relation between the growth in opioid prescriptions and subsequent IT investments, with a more pronounced effect for industries in which labor is more easily substitutable by technology and for firms that are less financially constrained.

Our findings imply that firms mitigate some of the costs that would otherwise be anticipated from a reduction in the labor supply. This response, however, changes the production processes at firms, a change that can have lasting negative impacts on the local labor markets for those jobs at risk of technology substitution.

Acknowledgement

We would like to thank Itay Goldstein (the Editor), Janet Gao, Xavier Giroud, William Mann, and Ben Zhang; seminar participants at Boston College, Brigham Young University, Elon University, Erasmus University, Florida State University, Georgia Tech, HEC Paris, Indiana University, Johns Hopkins University, London Business School, McGill University, Michigan State University, Peking University HSBC Business School, Rice University, Stockholm School of Economics, Temple University, Texas A&M University, University of Arizona, University of Kentucky, University of Maryland, University of North Carolina, University of Oregon, University of Pittsburgh, University of Texas, University of Toronto, University of Washington, Vanderbilt University, Virginia Tech, Warwick Business School, Washington University in St. Louis, Yale School of Management, York University, and the online seminar in Corporate Finance and Investments; and conference participants at the AFA Conference, the ASU Sonoran Conference, the Bahamas RCFS Conference, the FOM Conference, the Labor and Finance Group, and the Society of Labor Economists Annual Meeting. We would like to thank Sarah Kenyon and Huan Lian for valuable research assistance. We would also like to thank the Frank H. Kenan Institute of Private Enterprise for generous support. The research was reviewed and approved by UNC IRB (Study #19-0601). Supplementary data can be found on The Review of Financial Studies web site.

Footnotes

Author notes

Authors have furnished an Internet Appendix, which is available on the Oxford University Press Web site next to the link to the final published paper online.

References

Appendix: Variable Definitions

A1. Individual-Level Variables

|$ Doctor\ opioid\ intensity $| is the count of the doctor’s patients that subsequently fill an opioid prescription (within 7 days) following an outpatient service, normalized by the doctor’s total outpatient services. Source: MarketScan.

|$ Opioid\ prescribed\ $| takes the value one if the individual is prescribed opioids for the first time in our sample in a given year, and zero otherwise. Source: MarketScan.

|$ ln(visits) $| is the count (log-transformed) of the total medical visits of the patient over the prior year plus one. Source: MarketScan.

|$ ln(prescriptions) $| is the count (log-transformed) of the total number of prescriptions given to the patient over the prior year plus one. Source: MarketScan.

|$ ln(providers) $| is the count (log-transformed) of the total number of unique providers visited by the patient over the prior year plus one. Source: MarketScan.

A.2. County-Level Variables

|$ Opioid\ prescriptions $| is the count of total opioid prescriptions, normalized by the number of enrollees in a given county. Source: MarketScan.

|$ ER\ opioid\ prescriptions $| is the count of opioid prescriptions filled (within 7 days) following a diagnosis (within past 7 days) that was among the top-10 most common emergency room diagnoses in our data. This count is then normalized by the number of enrollees in a given county. Source: MarketScan.

|$ Income $| is the median household income in a given county. Source: Census.

|$ Population $| is the total population in a given county. Source: Census.

|$ White\ ratio $| is the white population divided by the total population in a given county. Source: Census.

|$ Age\ 20-64\ ratio $| is the population aged 20 to 64 divided by total population in a given county. Source: Census.

|$ Age\ 65+\ ratio $| is the population at or above 65 years old divided by the total population in a given county. Source: Census.

|$ Neoplasms\ mortality $| is the number of deaths due to neoplasms (cancer), normalized by population times 1,000 at a given county. Source: CDC (https://wonder.cdc.gov/ucd-icd10.html).

|$ Low\ \Delta income $| is an indicator variable equal to one if the change in the mean county-level household income during the period 2007–2010 was below the sample median, and zero otherwise. Source: Census.

|$ Low\ \Delta house\ price $| is an indicator variable equal to one if the change in the county-level housing price index during the period 2007–2010 was below the sample median, and zero otherwise. Source: Federal Housing Finance Agency.

|$ Low\ \Delta county\ emp. $| is an indicator variable equal to one if the change in county-level employment during the period 2007–2010 was below the sample median, and zero otherwise. Source: Census.

A.3. Establishment-Level Variables

|$ IT\ budget $| is the total IT budget for the establishment. Source: CiTDB.

|$ PC $| is the total number of personal computers in the establishment. Source: CiTDB.

|$ Sales $| is the estimated revenue for the establishment. Source: CiTDB.

|$ Employment $| is the total number of employees in the establishment. Source: CiTDB.

|$ High\ labor\ replaceability $| is an indicator variable equal to one if an establishment belongs to an industry whose labor replaceability is higher than the sample median, and zero otherwise. Labor replaceability is the fraction of each industry’s hours worked in 2000 that was performed within occupations prone to be replaced by robots (Graetz and Michaels (2018)). Source: American Community Surveys.

|$ High\ firm\ size $| is an indicator variable equal to one if a firm’s total employment across all observed establishments is higher than the sample median, and zero otherwise. Source: CiTDB.

|$ ln(CAPEX/firm\ emp) $| is the logarithm of one plus firm capital expenditures divided by firm employment. Source: Compustat.

|$ ln(CAPEX) $| is the logarithm of one plus firm capital expenditures. Source: Compustat.

|$ ln(Firm\ emp) $| is the logarithm of firm employment. Source: Compustat.

|$ Share\ process\ innovation $| is the count of process claims divided by the count of total claims. Source: Bena and Simintzi (2022).

|$ asinh(Process) $| is the count of process claims transformed using the inverse hyperbolic sine. Source: Bena and Simintzi (2022).

|$ asinh(Nonprocess) $| is the count of nonprocess claims transformed using the inverse hyperbolic sine. Source: Bena and Simintzi (2022).

A.4. State Legislation Analysis Variables

|$ HQ\ empl\ ratio $| is the share of a firm’s employment (observed in CiTDB) in the given firm’s headquarters state. Sources: CiTDB and Compustat.

|$ Low\ PC\ empl $| is equal to one if the stock of installed PCs at the firm level over the number of employees in the firm, measured in 2015, is below the sample median, and zero otherwise. Source: CiTDB.