ABSTRACT
The areas most affected by the opioid crisis have witnessed deteriorating economic conditions, although it is unclear if this represents a causal relationship. I provide new evidence on this question by leveraging a natural experiment that sharply decreased the supply of hydrocodone, the most commonly prescribed opioid in the United States, relative to other opioids. Areas with larger reductions in hydrocodone prescribing experienced relative improvements in labor force participation and employment. However, these areas also witnessed higher growth in drug-related arrests. I find some evidence of reductions in illicit opioid deaths, which are offset by increases in other drug-related deaths.
I. Introduction
Over the last two decades the opioid epidemic has claimed more than 667,000 lives, driving the most deadly drug overdose crisis in U.S. history. Despite numerous interventions by state and federal governments, pharmaceutical companies, and healthcare providers, the crisis shows no signs of abating. The number of opioid overdose deaths in almost every year since 1999 has exceeded the prior year’s total, with 2021 as the deadliest year yet with more than 82,000 deaths. This dramatic rise in opioid abuse and overdose deaths has garnered attention from academics, policymakers, media outlets, and politicians alike (Yellen 2017; New York Times 2019; Trump 2018).
Coincident with the onset of the opioid crisis in the late 1990s and early 2000s, the national labor force participation rate fell from an all-time high of about 67 percent to under 63 percent by 2014, the lowest level since 1983. Further, the areas most affected by the crisis have typically also been the hardest hit by worsening labor market conditions (Krueger 2017). For example, in 2011 West Virginia—the state with the highest rates of both opioid prescriptions and overdose deaths per capita—also had the lowest rate of labor force participation of any state, nearly ten percentage points below the national average.1
Observations like these have led researchers to ask the question: Does opioid abuse cause poor economic conditions, or does declining economic activity drive individuals toward opioid abuse? See, for example, Case and Deaton (2017); Ruhm (2018); Currie, Jin, and Schnell (2019); and Krueger (2017). Despite the strong cross-sectional and time series correlations between overdose deaths and poor economic conditions, the existing evidence on the causal relationship between opioids and economic condition is mixed.
I focus on estimating the causal impact of opioid prescribing on labor market behaviors. I rely on a new source of variation resulting from a regulatory change that suddenly and dramatically decreased the supply of hydrocodone, one of the most prescribed opioids, relative to other similar drugs. Specifically, the Drug Enforcement Agency (DEA) classifies controlled substances into one of five schedules. Lower-numbered schedules consist of drugs that are considered more dangerous and are subject to increasingly stringent prescribing and dispensing regulations. On October 6, 2014, hydrocodone combination products (HCPs) were “rescheduled” from Schedule III to Schedule II, leading to an approximately 36 percent decrease in the amount of hydrocodone distributed in the years following the rescheduling.
Concurrent with this supply shock, the approximately 15-year fall in labor force participation stopped abruptly, with the labor force participation rate stabilizing at around 63 percent. I provide a variety of evidence that the simultaneous reduction in opioid prescriptions and trend break in the labor force participation rate reflect a causal effect of opioid prescriptions on labor force participation.
To estimate the effect of the rescheduling on labor market behaviors, I employ a difference-in-differences framework leveraging variation in the extent to which different zip codes were exposed to the reform. Areas that relied heavily on hydrocodone prior to the rescheduling had more scope to be affected than places that used less hydrocodone to begin with. Similar methodology has been employed in previous work to study interventions with no variation in the timing of treatment, such as the eradication of hookworm from the American South (Bleakley 2007) and the reformulation of OxyContin (Alpert, Powell, and Pacula 2018; Beheshti 2019). Utilizing this variation in pre-intervention hydrocodone consumption, I create a difference-in-differences style estimator to compare differentially treated areas before and after the rescheduling. I first show that the places that prescribed relatively more hydrocodone prior to the rescheduling were indeed the places that saw the largest declines in hydrocodone prescribing after the rescheduling. I find no evidence of substitution towards other opioids, indicating that the effects of the rescheduling were not simply undone via substitution.
Next, I present the main result of the paper: areas that were more exposed to the rescheduling saw relative increases in labor force participation compared to less exposed areas. I find that this result is driven almost entirely by increases in employment; there are no significant effects of the rescheduling on unemployment. In total, the regression estimates indicate an aggregate increase of about 0.8 percent (0.52 percentage points) in the labor force participation rate and a 1 percent (0.61 percentage point) increase in the employment-to-population ratio relative to a counterfactual scenario without the rescheduling. Consistent with higher participation in the labor market, I also find a decrease in Social Security Disability Insurance (SSDI) claimants following the rescheduling.
While the rescheduling has generally positive effects on the labor market, it is not without negative side effects. I document increases in drug-related arrests in areas that saw larger reductions in legal opioid access following the rescheduling, demonstrating some substitution toward illicit drug markets. These arrests are exclusively driven by arrests for drug possession as opposed to sale, reflecting an increase in illicit drug demand rather than changes in the supply side of the market. Results for mortality are somewhat mixed. There is some evidence of reduced opioid deaths, although these are offset by increases in overdose deaths from other drugs.
These findings have important policy implications. The results indicate that more cautious opioid prescribing may have the ancillary benefit of improving local labor market conditions and reducing disability claims. Furthermore, this work suggests a relatively low-cost policy lever with which to reduce opioid prescribing, namely, moving drugs to stricter regulatory categories. Although the majority of opioids are now in the most strictly regulated category of prescription drugs, there are still several commonly prescribed opioids that are subject to more lenient restrictions, such as tramadol and certain codeine formulations. This could also be relevant for several increasingly commonly abused benzodiazepines, most of which are currently in a less strictly regulated category. However, the results underscore important trade-offs associated with restricting access to legal opioids, specifically increased participation in illicit drug markets as users seek out substitute drugs.
In the following, Section II discusses the relevant institutional background, as well as the related literature. Section III outlines the research design, while Section IV discusses the data. The results are presented in Section V. Section VI concludes. The Online Appendix investigates the robustness of the main results and presents the model.
II. Background
A. Background on the Opioid Crisis and Related Literature
1. Opioid Crisis
Opioids refer to a class of drugs derived from opium or with opium-like effects. These drugs are generally used to treat acute and chronic pain, although they are also commonly misused for their recreational effects. Taking opioids in large quantities or in combination with alcohol or other sedative medications (for example, muscle relaxants or benzodiazepines) enhances the recreational effects of the drug, but also causes respiratory depression, which can lead to death. Opioids include prescription painkillers, such as OxyContin, Vicodin, and fentanyl, as well as illegal drugs like heroin. Beginning in the mid 1990s, a combination of factors, including philosophical changes in the way healthcare providers viewed optimal pain management and aggressive marketing by pharmaceutical companies, led to a rapid increase in the frequency with which these drugs were prescribed (Campbell 1996; Van Zee 2009). Unfortunately, painkiller overdose deaths rose in lockstep with the increase in opioid prescriptions, increasing from about 2,600 in 1999 to more than 14,600 in 2017, an increase of more than 500 percent.2 Case and Deaton (2015, 2017) find that opioid overdose deaths constitute one of the two largest factors in the recent increase in mortality rates among middle-aged, non-Hispanic white persons in the United States. Opioid overdose deaths are currently the leading cause of death from accidents in the United States, exceeding the number of car accident fatalities in each year since 2009.
2. Related literature
In reaction to the growing death toll, numerous policies and interventions have been enacted in an attempt to reduce opioid misuse.3 The sudden rise in opioid abuse and related policies has engendered a growing literature examining different facets of opioid prescribing and misuse, including physician education (Schnell and Currie 2018), the introduction of Medicare Part D (Powell, Pacula, and Taylor 2015), and access to marijuana (Powell, Pacula, and Jacobson 2018). Related papers have examined the effectiveness of various interventions, such as prescription drug monitoring programs (Buchmueller and Carey 2018; Dave, Grecu, and Saffer 2017; Paulozzi, Kilbourne, and Desai 2011), increased access to naloxone (Doleac and Mukherjee 2018; Rees et al. 2017), Good Samaritan laws (Rees et al. 2017), the introduction of abuse-deterrent painkillers (Alpert, Powell, and Pacula 2018; Beheshti 2019; Evans, Lieber, and Power 2018), and quantity limits for opioid prescriptions (Sacks et al. 2021). This paper is the first in the economics literature to examine the impact of one of the single largest interventions to the prescription opioid market, the rescheduling of hydrocodone.4 The results indicate that this type of low-cost intervention can have large effects, suggesting another policy lever with which to address not only opioid misuse, but also drug abuse more generally.
A closely related strain of the literature has focused on the relationship between opioids and the labor market. Motivating this segment of the literature are two broad stylized facts. First, the onset of the opioid crisis coincided with the start of a nearly 15-year decline in labor force participation (Figure 1, Panel A). Second, the areas that have experienced the largest deteriorations in labor market conditions are also the areas that have been hit hardest by the opioid crisis (Krueger 2017). Suggesting a causal mechanism driving this observation, Krueger (2017) finds that almost half of prime-age men not in the labor force take pain medication every day. Several different papers have investigated whether there exists a causal relationship between opioid use and labor market conditions, in either direction, using a variety of identification strategies.
Labor Force Participation Rate and Opioid Distribution over Time
Notes: Panel A shows the aggregate labor force participation rate each month from January 1990 to December 2017. Panel B shows the quarterly distribution of hydrocodone (black line, left y-axis) and other nonhydrocodone opioids (dashed line, right y-axis) for 2000–2017. Non-hydrocodone opioids are pooled by converting each to morphine equivalents before adding. The vertical dashed line in each subfigure indicates the period immediately preceding the hydrocodone rescheduling.
Most closely related to this work are studies that investigate the causal effect of opioids on the labor market. Many of these papers instrument for opioid prescriptions in order to alleviate concern of an omitted variable bias (for example, underlying patient demand). For example, Currie, Jin, and Schnell (2019) instrument opioid prescriptions for the young with prescriptions for the elderly and find that increased opioid prescriptions lead to modest increases in the employment-to-population ratio for women, although they do not find any effects for men. In contrast, Harris et al. (2017) instrument for county-level opioid prescriptions using the prevalence of high-volume prescribers in Medicare Part D and find that increases in opioid prescriptions lead to decreases in labor force participation. Relatedly, Savych, Neumark, and Lea (2018) find that injured workers who receive long-term opioid prescriptions have longer absences from work following an injury, instrumenting for an individual’s opioid prescription with county-level opioid prescribing patterns. Several recent papers examine how the introduction of prescription drug monitoring programs (PDMPs) affect labor market behaviors, but reach different conclusions (Kaestner and Ziedan 2019; Kilby 2015; Franco, Wagner, and Whaley 2021; Deiana and Giua 2018).5
In this work, I make two primary contributions relative to this existing literature. First, I provide transparent evidence on the impact of opioids on the labor market by utilizing sharp variation in prescribing behavior induced by a regulatory change. In contrast, prior work has largely relied on observational variation in prescribing patterns, making causal inference challenging.6 Second, this paper provides estimates that are particularly relevant for public policy, as it analyzes the effects of a regulatory change, which both state and federal governments can affect to influence future prescribing.7
Other work investigates the causal relationship between the labor market and opioids in the opposite direction, that is, the effect of labor market conditions on opioid prescriptions, misuse, and mortality. Currie, Jin, and Schnell (2019) use a shift–share instrument based on industry composition to examine the effects of economic conditions on opioid prescriptions and find no effects. This is consistent with work by Ruhm (2018), who finds that only a small fraction of drug mortality can be explained by medium-run changes in economic conditions. However, Hollingsworth, Ruhm, and Simon (2017) find that short-term increases in the unemployment rate lead to increased emergency department visits related to opioids. On net, these papers suggest that transitory changes in unemployment may lead to increases in opioid abuse, although long-running trends in economic conditions do not explain much of the variation in opioid misuse and mortality.
Finally, this paper closely relates to other work that has investigated the effects of pharmaceuticals on the labor market. Specifically, Garthwaite (2012) and Bütikofer and Skira (2018) both exploit the sudden withdrawal of Cox-2 inhibitors (Vioxx, Celebrex, Bextra) to examine how changes in drug use affect labor force participation.8 These papers find large and statistically significant reductions in labor force participation and increases in the number of absences due to sickness, indicating that this medication allowed some individuals to participate in the labor market who would otherwise be incapable of working. In principle, this could be the case with prescription opioids. However, opioids are much more likely to be abused, which would presumably drive individuals out of the labor market. It is theoretically ambiguous which of these effects would be larger. This study investigates these competing effects by leveraging variation from a large, plausibly exogenous change in opioid consumption stemming from a policy change. Empirically, I find that the latter effect dominates, with fewer opioid prescriptions leading to higher labor force participation and employment.
B. Hydrocodone Background and Rescheduling
Hydrocodone is an opioid analgesic synthesized from codeine, a naturally occurring substance in opium poppies. Like many other opioids, it is used in the treatment of both acute and chronic pain. Clinically, hydrocodone has been shown to work as well in the treatment of acute pain as oxycodone (Marco et al. 2005), although a slight majority of recreational users prefer oxycodone (Cicero et al. 2013).9 It is commonly sold under brand names such as Vicodin, Lortab, and Norco, although it is also available in generic form. In 2013, hydrocodone was the most frequently prescribed opioid in the United States with about 137 million prescriptions (Drug Enforcement Agency 2014). In the same year, hydrocodone was the most commonly prescribed drug overall (not just among opioids) in Medicare Part D.10 It was the third highest selling of all generic drugs, generating almost 1.1 billion dollars in 2013.11 Due to its ubiquity, hydrocodone is one of the most commonly misused painkillers in the United States. Approximately 4.9 percent of National Survey on Drug Use and Health (NSDUH) respondents in 2013 reported misusing hydrocodone at some point in their lives. Interestingly, this is more than a percentage point higher than the fraction of NSDUH respondents reporting any lifetime OxyContin misuse at in 2009 (3.6 percent), the peak year of OxyContin misuse. Hydrocodone has been a key contributor to the opioid crisis, implicated in around 3,000 deaths per year from 2011 to 2016 (Hedegaard et al. 2018).12
Although similar to many other opioids in both usage and effects, hydrocodone has historically been less stringently regulated. In the United States, the Drug Enforcement Agency (DEA) classifies prescription drugs into one of four categories, Schedules II–V.13 The classifications have important implications for prescribers and patients, as lower-numbered schedules (for example, Schedule II) are much more strictly regulated relative to other schedules, making these drugs more difficult to obtain. For example, Schedule II drugs require a new prescription each time a patient obtains the drug, while Schedule III drugs can be refilled up to five times in a six-month period.14 Schedule II prescriptions must be handwritten, as opposed to Schedule III prescriptions, which can be faxed to a pharmacy. Additionally, many individual states have laws that further restrict access to Schedule II drugs. For example, some states prohibit mid-level practitioners, such as physician assistants and nurse practitioners, from prescribing Schedule II drugs, while many emergency departments do not distribute Schedule II drugs as a matter of policy (Drug Enforcement Agency 2014).
Historically, most high-potency narcotic painkillers have been placed in the most restrictive category, Schedule II. Although hydrocodone by itself was also classified as Schedule II, if combined with another nonnarcotic analgesic, such as acetaminophen (Tylenol) or ibuprofen (Advil), it was classified as Schedule III. Likely because of this exception, all hydrocodone drugs sold in the United States prior to the rescheduling were hydrocodone combination products (HCPs), that is, hydrocodone with acetaminophen or ibuprofen.15 This “Vicodin loophole” made HCPs such as Vicodin, Norco, and Lortab substantially easier for providers to prescribe relative to non-hydrocodone-based painkillers, such as oxycodone (for example, OxyContin) or hydromorphone (for example, Dilaudid).
The less restrictive regulatory environment surrounding HCPs has been the source of long-running controversy. As early as 2004, the DEA was petitioned to reschedule HCPs to Schedule II.16 In response to this request, the DEA solicited a recommendation from the Department of Health and Human Services (HHS) on this possible change. Four years later, HHS submitted its recommendation to the DEA that HCPs remain in Schedule III. The following year the DEA requested that HHS reevaluate their initial recommendation, although nothing ultimately came of this request. However, following the passage of the FDA Safety and Innovation Act in July of 2012, a newly created FDA advisory committee voted in favor of recommending that HCPs be placed in Schedule II. This ultimately led HHS to submit a new recommendation to the DEA on December 16, 2013, which aligned with the FDA advisory committee’s vote. With the support of the FDA and HHS, the DEA submitted an official proposal February 27, 2014 to reschedule HCPs from Schedule III to Schedule II. After receiving comments, both in support of and in opposition to the proposed rule, the final ruling was published August 22, 2014.
On October 6, 2014, the DEA’s ruling officially went into effect, rescheduling all hydrocodone drugs—regardless of whether or not they were combined with other drugs—as Schedule II. Consistent with the rescheduling making hydrocodone more difficult to prescribe, Panel B of Figure 1 demonstrates an immediate decline in the distribution of hydrocodone beginning in the first quarter of the rescheduling.17 By the end of 2017, the quarterly amount of hydrocodone distributed had fallen by more than 36 percent of its 2013 level. In Section III, I discuss how I use variation in exposure to this drop in hydrocodone prescriptions to estimate the causal effects of the rescheduling. In the following section, I present a conceptual discussion of how changes in opioid access can potentially affect labor market behaviors.
C. Conceptual Discussion on Opioid Access and Labor Market Behaviors
There are several mechanisms by which a reduction in opioid access may affect labor market behaviors. In Online Appendix B, I develop a formal model that discusses these mechanisms and characterizes the conditions under which each may apply. A core feature of the model is that certain channels predict an increase in labor force participation and employment, while others suggest the opposite. In this section, I briefly discuss four of the most likely channels.
1. Reduction in prescription opioid abuse
Opioids like hydrocodone are commonly misused for their recreational properties. Recreational users quickly develop a tolerance for opioids and require progressively higher doses in order to achieve the desired high. This results in many users becoming dependent or addicted to opioids. Those who take opioids over a long period of time experience severe withdrawals when they stop taking opioids, which makes quitting notoriously difficult.
Drug abuse is known to reduce work capacity (U.S. National Research Council and U.S. Institute of Medicine Committee on Drug Use in the Workplace 1994). To the extent that a sudden reduction in opioid availability prevents individuals from experimenting with and possibly becoming dependent on opioids, we can expect a reduction in opioid access to lead to increases in labor force participation and employment relative to a counterfactual in which opioids were more abundant. It is also possible that a reduction in access spurs individuals with an addiction to opioids to seek treatment, which could increase work capacity. However, the presence of substitute drugs, such as heroin, makes this unlikely for a nontrivial subset of users.
2. Increase in illicit drug abuse
While some opioid users may respond to a decrease in prescription opioid availability by stopping use altogether, others may elect to substitute toward other substances. A natural substitute is heroin. Since heroin is stronger than hydrocodone, this substitution is likely to exacerbate labor market problems rather than alleviate them. Park and Powell (2021) find that the reformulation of OxyContin, which spurred substantial substitution towards heroin, led to reductions in employment and increases in SSDI claiming. If the rescheduling of HCPs led to similar substitution we may expect similar labor market impacts.
3. Reduction in beneficial opioid use
The vast majority of prescription opioid consumption is medicinal. Pain can directly inhibit work capacity and can also lead to other adverse health conditions, such as insomnia and depression. In cases where pain cannot be managed with over-the-counter (OTC) drugs like acetaminophen or ibuprofen, opioids may enable individuals to work who would otherwise be incapable of participating in the labor market. For these individuals, a reduction in opioid access is likely to reduce labor force participation and employment.
4. Reduction in medical but work-inhibiting opioid use
Opioids play an important role in treating pain. However, they also come with side effects, such as constipation, nausea, sedation, and confusion. Even absent any misuse, these side effects may limit work capacity. If pain can be alleviated with nonpharmaceutical interventions or OTC drugs, then reducing opioid access should reduce marginal opioid consumption that adversely impacts individual’s labor market participation.
In summary, reductions in opioid access likely have heterogeneous effects depending on why they are being consumed. Recreational use and abuse likely have negative labor market impacts, although even valid medical consumption can inhibit work capacity due to undesirable side effects. In contrast, the pain relief provided by opioids likely allows some individuals to work who would otherwise be forced out of the labor market.
I estimate the reduced form impact of a policy that substantially reduces opioid access; therefore, the estimates I present in Section V represent an average effect of all of the mechanisms listed above. Other work by Kaestner and Ziedan (2019) attempts to estimate these different mechanisms directly by considering differential labor market responses to PDMPs by age and gender. For example, since younger men have higher rates of opioid abuse than other demographic groups, contrasting their labor market responses can help disentangle some of these mechanisms. However, I am unable to follow their strategy since the month-by-county Local Area Unemployment Statistics (LAUS) data do not contain information about age and gender.
D. Relationship of HCP Rescheduling to Other Policies
As discussed in Section II, there have been numerous policies implemented in order to curb opioid misuse and abuse in addition to the rescheduling. Two of the most commonly studied are the reformulation of OxyContin and the implementation of mandatory access PMDPs (MA-PDMPs). In this subsection, I briefly comment on the relationship between these policies.
Conceptually, there are important differences between the rescheduling of HCPs and these other policies. Most importantly, the reformulation of OxyContin only had direct effects on individuals who were misusing OxyContin by crushing, snorting, or injecting it. The reformulation did not inhibit the ability of prescribers to provide OxyContin to those who were taking it as prescribed.
This partially explains why the most severe adverse outcomes documented in the literature are driven by the reformulation of OxyContin. For example, Alpert, Powell, and Pacula (2018) report that the OxyContin reformulation was responsible for four-fifths of the 101 percent increase in heroin overdose deaths between 2010 and 2013. Meinhofer (2018) and Kim (2021), in contrast, document smaller effects of MA-PDMPs on heroin overdose deaths.
The differences between MA-PDMPs and the rescheduling of HCPs are more subtle. On the surface, both policies reduce access to opioids by making it more costly for prescribers to write opioid prescriptions. However, MA-PDMPs provide potentially useful information to the prescriber about the patient’s misuse propensity, whereas the rescheduling provides no such information. In principle, MA-PDMPs could even lead to increases in prescribing for low-risk patients who can now signal their type to the prescriber. The rescheduling also only affects patients who were being prescribed HCPs, as opposed to MA-PDMPs, which affect all opioid patients. This again suggest that we may observe different effects of these policies as they affect different subsets of opioid patients.
Many states implemented MA-PDMPs prior to the rescheduling of HCPs. If MAPDMPs had reduced “slack” opioid prescribing in these states, then there would be little scope for the rescheduling to further reduce opioid prescribing. Alternatively, if states with MA-PDMPs generally had stricter regulatory enforcement, then the effects of the rescheduling may have been amplified in those states. However, even if MA-PDMPs were effective in reducing opioid prescriptions, the additional restrictions put in place by the rescheduling could still have important effects. How the rescheduling interacted with existing MA-PDMPs is ultimately an empirical question. In Online Appendix Section A.2, I report regression results explicitly controlling for whether a state implemented an MA-PDMP over the sample period. Additionally, I examine whether states with MAPDMPs prior to the rescheduling experienced different responses to the rescheduling than states that did not by running separate regressions for each group of states. The results of this exercise indicate states that had already implemented MA-PDMPs prior to the rescheduling were similarly affected in terms of their prescribing behavior after the rescheduling.18
III. Research Design
The aggregate drop in the distribution of hydrocodone (Figure 1, Panel B) and coincident trend break in falling labor force participation (Figure 1, Panel A) around the date of the rescheduling are suggestive of a relationship between the two. However, it is difficult to draw strong conclusions based solely on this type of time series evidence. Evaluation of the causal effect of the rescheduling is further complicated by the fact that the rescheduling took place everywhere on the same date, disallowing a typical difference-in-differences research strategy comparing treated and untreated units. Instead, I use a similar research strategy to several previous papers investigating the effects of aggregate-level events including the eradication of hookworm from the American South (Bleakley 2007) and the reformulation of OxyContin (Alpert, Powell, and Pacula 2018; Powell, Alpert, and Pacula 2019; Beheshti 2019) by comparing units that were differentially exposed to the treatment of interest. In this instance, I exploit preexisting cross-sectional variation in the distribution of hydrocodone to compare places that were more heavily exposed to the rescheduling to places less exposed. For example, an area that typically received large shipments of hydrocodone each quarter prior to the rescheduling had much more scope to be affected than a place that typically received very little hydrocodone.
It is worth noting that this research design captures the net effect of the policy shock, inclusive of any feedback effects. For example, if improvements in labor market conditions in response to the initial reduction in opioid availability lead to further reductions in opioid consumption, this could in turn lead to further improvements in the labor market. Since I am comparing areas based on their baseline exposure to this initial shock, the estimates I report incorporate these dynamic effects, but do not allow me to distinguish between them. However, estimates from the literature on the effects of economic conditions on opioid consumption are relatively small compared to the reduction I observe in response to the rescheduling, suggesting that any feedback effects are small in magnitude.
A. Nonparametric Event Study
Formalizing the idea described above, I begin by estimating nonparametric difference-in-differences regressions of the form
1
where yzt is the outcome in three-digit zip code (zip3) z and period t. Zip3 and time fixed effects are represented by αz and γt, respectively. Time-varying control variables are included in Xzt. The baseline model does not include any additional control variables, although I explore the sensitivity of the regression coefficients to the inclusion of more controls in Section A.2 of the Online Appendix. 
is the average number of milligrams of hydrocodone per person–quarter prior to the rescheduling, which is the proxy for exposure to treatment. The primary coefficients of interest are the βT values, the coefficients of the interaction of 
with time fixed effects. Each of these coefficients can be interpreted as the difference in the outcome variable at time t across zip3s with differing pre-rescheduling rates of hydrocodone exposure. I normalize βSept.2014 to zero, so all coefficients can be interpreted as changes relative to the month (or quarter) prior to the rescheduling. I present confidence intervals that are constructed from standard errors clustered at the zip3 level, as well as more conservative confidence intervals using standard errors clustered at the state level.
The standard identifying assumption for regressions like Equation 1 is that the post-period dynamics of the less treated observations trace out the dynamics that we would have observed in the more treated observations absent the treatment. This is commonly referred to as the parallel trends assumption. This assumption is fundamentally untestable because we do not observe the state of the world in which the treatment never occurs. However, researchers often assess the plausibility of this assumption by examining the βT coefficients in the pre-period. Pre-period βT coefficients that are close to zero indicate that the more and less treated observations were trending similarly prior to the treatment taking place, which lends plausibility to the assumption that they would have trended in parallel in the post-period absent the treatment.
B. Parametric Event Study
As will be shown in Section V, there exist strong, differential time trends in several of the outcome variables across zip3s related to their level of exposure to hydrocodone. This manifests itself as nonzero βT coefficients in the pre-period, which violates the standard parallel trends assumption of this type of difference-indifferences model. Motivated by these results, I follow Dobkin et al. (2018) and also estimate a more parametric model that directly controls for these preexisting trends. Specifically, I estimate
2
The key differences between this and Equation 1 are the inclusion of zip3-specific linear time trends, included as 
, and the fact that the coefficients on the interaction of Hydro
with time fixed effects are only estimated for the post-period. Conceptually, this fits a linear trend based on the pre-period for each zip3 and then allows deviations from this trend in the post-period via the interactions of the time fixed effects and the Hydro
variable.
The identifying assumption necessary for this model to reveal the causal effect of the hydrocodone rescheduling is a slight modification of the identifying assumption discussed above. Rather than assuming that the dynamics of the more heavily treated areas would have followed those of the less treated areas in the absence of treatment, this model requires that we would have observed similar deviations from a linear trend fit based on the pre-period in the more or less treated areas absent the treatment. This assumption is closely related to that of Equation 1.
In fact, it is equivalent to the standard parallel trends assumption after controlling for zip3-specific linear trends. Because Equation 2 only estimates the interaction terms for the post-period, examining the θT coefficients does not provide a sense of how well the linear pre-trend fits the data. Therefore, I follow Dobkin et al. (2018) and rescale the β coefficients from Equation 1 to equal the θ coefficients when presenting the results from this model.19 This rescaling allows the reader to easily see whether the linear trends fit the data well by examining whether the rescaled β coefficients differ from zero in the pre-period.
IV. Data and Identifying Variation
A. Data
1. ARCOS
Data on the distribution of various opioids come from the Automated Reports and Consolidated Ordering System (ARCOS) of the Drug Enforcement Agency (DEA). By law, manufacturers and distributors of certain controlled substances are required to report their transactions to the DEA.20 The DEA compiles these reports into an annual publication. Data are currently available for 2000–2017, at the quarter by three-digit zip code (zip3) level.21
There are several major advantages to these data. First, they are available at the active ingredient level (for example, oxycodone, hydrocodone, etc.) for most commonly prescribed opioids.22 This allows the researcher to observe the geographic distribution of different types of opioids, as opposed to summary measures, which pool across all types of opioids, such as the data on number of prescriptions per capita published by the CDC. This is especially useful in the context of this paper, which examines the effects of a policy intervention that in practice only directly affected opioids that contain hydrocodone. Second, the data are published at the zip3 level. Zip3s are an aggregation of all zip codes with the same first three digits. Generally, these are continuous geographic areas slightly larger than a typical county. This is beneficial as there is not only significant interstate, but also intrastate variation in the distribution of many opioids that would be overlooked with more aggregate (for example, state-level) measures. Third, the data do not rely on survey responses from individuals, but are created from data reported directly from drug manufacturers and distributors to the DEA.
However, these data are not without disadvantages. Most notably, the data measure the distribution of various drugs to different locations, but not necessarily the sale or consumption of the drug. If pharmacies or hospitals stockpile large amounts of opioids differentially across geographies, then this data could misrepresent the areas with the most exposure to the drug. However, to the extent that the distribution of the drug is correlated with consumption, these data will reflect meaningful differences in drug consumption patterns. In order to examine the extent to which the distribution of an opioid is correlated with consumption, I compare data on the amount of various opioids prescribed in Medicare Part D across the United States to the amount distributed as reported by ARCOS. Drawing from the ARCOS data set, Panel A of Online Appendix Figure A1 shows the number of milligrams of hydrocodone distributed per capita in 2013, while Panel B shows the number of “hydrocodone days supplied” per capita in Medicare Part D, both at the zip3 level. As the figure shows, in general the zip3s with large amounts of hydrocodone shipments are also the zip3s with large amounts of hydrocodone prescribed in Medicare Part D. To quantify this correlation further, I regress the measure of hydrocodone distribution from ARCOS on the Medicare Part D consumption measure and report the results in Online Appendix Table A1. Column 1 shows that Medicare prescriptions for hydrocodone are strongly predictive of the aggregate distribution, with an R2 of 0.58 (correlation coefficient of 0.76). Columns 2–7 repeat this exercise for several of the other most commonly prescribed opioids and generally reveal the same pattern. While Medicare Part D is only a subset of the hydrocodone using population, this is suggestive that the distribution of hydrocodone is strongly predictive of consumption.23
Another difference between ARCOS and other measures of opioid consumption, although not necessarily a disadvantage, is that the ARCOS data measure the amount of the drug distributed (in grams) and do not contain information about the number of prescriptions written. In some ways this is an improvement on other data that only report the number of prescriptions, as the amount of the drug prescribed can vary widely across patients. However, a drawback of this is that I am unable to identify separately changes in the consumption of hydrocodone (or other opioids) along the intensive versus extensive margin. It should be noted that this problem is not unique to these data, as most other data sets only contain information about the number of prescriptions.24
2. LAUS
Labor market data come from the Local Area Unemployment Statistics (LAUS). These data are created by the Bureau of Labor Statistics from several different sources, including the Current Population Survey (CPS), Current Employment Statistics, Quarterly Census of Employment and Wages, and the American Community Survey (ACS).25 Data on the number of people employed, unemployed, and participating in the labor force are available at the county-by-month level. The major advantage of these data relative to other sources, such as the CPS or ACS, is that there is no suppression of small counties. The CPS and ACS censor all counties with a population under about 100,000 and 65,000, respectively.26 Because of this, about 91.06 and 74.32 percent of counties are censored in the CPS and ACS, respectively.27 The LAUS, on the other hand, reports for every county in each month. This is particularly important in this context, as much of the variation in hydrocodone exposure is driven by these smaller counties. A disadvantage of these data, however, is that they cannot be disaggregated, so I am unable to examine demographic heterogeneity in labor force responses to the rescheduling.
3. SSA
The Social Security Administration (SSA) administers multiple programs that provide benefits to those with disabilities. Social Security Disability Insurance (SSDI) and Supplemental Security Income (SSI) both provide benefits to disabled individuals with limited work capacity. Both programs have the same medical requirements, while SSDI requires a sufficiently long work history and previous payment of Social Security taxes. In contrast, SSI is based solely on disability status and financial need; SSI beneficiaries must fall below certain income and asset thresholds but do not need to have previously paid Social Security taxes. The SSDI payments crowd out SSI payments among those who qualify for both programs.28 While the number of applications are only available at the state level, the number of SSI and SSDI beneficiaries are available at the county and zip code levels, respectively, although these data are reported annually as opposed to monthly.29
4. UCR
Data on the number of drug-related arrests are taken from the Uniform Crime Reporting (UCR) Program, which is collected and reported by the Federal Bureau of Investigation (FBI). I use the Arrests by Age, Sex, and Race (ASR) data compiled by Kaplan (2021). These files report monthly arrest counts for various crimes, including the sale or possession of drugs. There are four fairly coarse categories of drugs reported: heroin or cocaine, cannabis, synthetic narcotics, and other drugs.30 The data are reported voluntarily by individual law enforcement agencies, which I aggregate to the county-by-quarter level using the provided Law Enforcement Agency Identifiers Crosswalk (LEAIC).31
One important issue with these data is that arrests are reported voluntarily, and not all agencies report data in every month. Therefore, I conduct robustness tests in which I exclude all agencies that do not report arrests in each period, similarly to Hao and Cowan (2020).32
5. Mortality
Data on drug-related mortality are taken from the Multiple Cause of Death (MCOD) files published by the Centers for Disease Control and Prevention (CDC). These data are based on individual death certificates and include information on up to 20 causes of death. A public use version of these data is available at the county or state level, although all cells (for example, state–years) with fewer than ten deaths are suppressed. To get around this censoring issue, I applied for and received access to the restricted microdata, which lists the county associated with every death. These data are very detailed and include codes that indicate whether drugs in specific categories contributed toward the death. I then aggregate these data to the county-by-quarter level to measure death rates related to a variety of different drugs.
6. HUD
The availability of opioid distribution data at the zip3 level is a major improvement over state-level data; however, it introduces an additional complication, as most local area labor force data are measured at the county level. Counties and zip code boundaries are created independently and frequently overlap, which makes mapping between them a nontrivial exercise. Counties for the entire United States are shown in Panel A of Online Appendix Figure A3 in various shades of red, while zip3s are shown in shades of blue in Panel B.33 These panels demonstrate two facts. First, zip3s are generally (although not always) larger than counties. Second, many (but again not all) counties are nested entirely within a single zip3. In order to highlight these facts more clearly, Panel C shows county boundaries in white and zip3 boundaries in black for the state of Texas. Panel D zooms in even further on the central Texas region, in order to demonstrate how zip3s are constructed from zip5s. Zip5 boundaries are shown in gray, with zip3s shown in different colors. As this map makes clear, zip5s are nested entirely within zip3s (by construction). County boundaries are again shown in white. When counties are nested entirely within zip3s, it is relatively straightforward to create zip3-level labor force statistics. However, this is often not the case.
Fortunately, there exist crosswalks that make this type of merge possible. Since 2010, the Office of Policy Development and Research at the Department of Housing and Urban Development (HUD) has published crosswalks to allow researchers to map between various geographies created by the U.S. Postal Service and the Census Bureau.34 These crosswalks are updated quarterly and indicate the fraction of individuals in a particular geographic area (for example, county) who live in each intersecting geography of a different type (for example, zip code). In order to produce labor force statistics at the zip3 level, I utilize these crosswalks to create counts of employment, unemployment, and labor force participation.35 Specifically, let Z be the set of all five-digit zip codes and C be the set of all counties, with z and c representing individual zip codes and counties, respectively. I define ϕcz to be the fraction of people in county c who reside in zip code z. I define 
. In order to map counts from county to zip code, I calculate 
, where X is the count of individuals employed, unemployed, or in the labor force.36 Given the estimate of X at the five-digit zip code, I simply aggregate up to create the zip3 counts. I then convert these into rates by dividing by the population older than 16.
B. Identifying Variation
There exists substantial cross-sectional variation in opioid prescribing patterns across the United States. This fact is widely known and has been the subject of a great deal of discussion among academics and policymakers, although the precise causes of this variation are not well understood.37 Panel A of Figure 2 demonstrates this variation in prescribing, pooling data on several of the most commonly prescribed opioids for 2010–2013. Darker shades indicate more opioid consumption per capita, with lighter colors showing areas where people consumed fewer opioids.
Identifying Variation: Pre-Period Morphine Milligram Equivalent Overall Opioid and Hydrocodone Distributions
Notes: These maps show the spatial variation in the distribution of opioids. Panel A shows the six quantiles of the distribution of all opioids in morphine milligram equivalents per capita–quarter, pooled for 2010–2013. Panel B recreates the same figure but for only hydrocodone. Darker shades indicate more consumption per capita, while lighter colors indicate less consumption.
While the variation in overall opioid prescribing has been widely documented, there has been less focus on the variation in prescribing of specific types of opioids. For example, there existed considerable cross-sectional variation in the distribution of hydrocodone prior to the rescheduling. Panel B of Figure 2 shows the average milligrams of hydrocodone per capita per quarter for each zip3 pooled for 2010–2013, the four years preceding the rescheduling, which I define as my primary treatment variable, 
. As in Panel A, darker shades indicate more hydrocodone per capita with lighter colors showing areas that used less hydrocodone. On average, each zip3 received around 36 milligrams per person–quarter, about the maximum recommended daily dosage for someone older than 18.38 Zip3s in the 75th quartile consumed approximately two and one-half times more hydrocodone each quarter than zip3s in the 25th percentile. The maximum value observed in my sample is about 409 milligrams, enough for each person in the zip3 to be medicated around the clock for about ten days of each quarter, or 40 days per year. Interestingly, the variation in hydrocodone prescribing does not simply mirror the variation in overall opioid prescribing. Even conditional on the total amount of opioids prescribed, there exists significant variation in the composition of opioids (for example, hydrocodone versus nonhydrocodone).39
This map reveals several geographic clusters where hydrocodone use is especially prevalent, including parts of the Southeast and most of Appalachia, as well as parts of Texas and the western United States. However, even within these regions there is still considerable variation in hydrocodone use. Because of this geographic clustering, more heavily treated zip3s likely differ on average from less treated zip3s.40 Of course, given the difference-in-differences design outlined in Equations 1 and 2, average differences across zip3s related to the treatment variable are not important for identification. In order to identify the causal impact of the rescheduling, Equation 2 only requires that preexisting differences in trends in the outcome variable would have continued absent the rescheduling. For example, a sudden improvement in labor market conditions in places with more pre-period hydrocodone use for reasons unrelated to the rescheduling would violate this assumption. In Table A3, I report the results from a series of placebo tests in which I examine whether I observe deviations from trend across zip3s coincident with the rescheduling for variables that would not plausibly be affected by the rescheduling. Each row reports the coefficient analogous to θ from Equation 2, except that in these regressions all of the post-periods are pooled together.41 The first row demonstrates that there is no change in population trends coincident with the rescheduling, while Rows 2–5 show that there are no changes in the gender, racial, or ethnic composition. Finally, Rows 6 and 7 demonstrate that there are no changes in the age distribution. The small and statistically insignificant coefficients for these placebo regressions provide some assurance that the following regression results are not picking up spurious trend breaks that are not actually caused by the rescheduling.
V. Results
A. First Stage
A necessary condition for the identification strategy outlined above to reveal the causal effect of the rescheduling is that areas with differing pre-period levels of hydrocodone consumption were differentially affected by the rescheduling, which I refer to as the “first stage.” Specifically, I expect that areas with high consumption of hydrocodone prior to the rescheduling were more affected than areas with lower consumption. I begin by presenting evidence that this was indeed the case. To do so, I estimate Equation 1 with the amount of hydrocodone distributed per person–quarter as the outcome variable. For this regression I standardize the treatment variable to have a mean of zero and a standard deviation of one, so each coefficient can be interpreted as the treatment effect of a one standard deviation increase in pre-period hydrocodone exposure. The βT coefficients are presented graphically in Panel A of Figure 3, with the mean of the outcome variable shown in the bottom left corner. Prior to the rescheduling in the fourth quarter of 2014 (indicated by the vertical dashed line) the coefficients are generally close to zero, although they do exhibit a slight downward trend. However, beginning with the first quarter after the rescheduling, the coefficients show a dramatic and persistent drop in the amount of hydrocodone distributed, especially in the zip3s with higher pre-period levels of hydrocodone consumption. The post-period coefficients indicate that a one standard deviation increase in exposure to treatment is associated with more than a 10-milligram per person drop in the distribution of hydrocodone each quarter, more than a third of the mean value. Panel B shows the regression results from Equation 2, which directly controls for linear pre-trends. This attenuates the magnitudes slightly, although there is still a clear drop of nearly 22 percent of the mean value immediately following the rescheduling in places with one standard deviation higher levels of pre-period exposure. Online Appendix Figure A4 demonstrates the mechanics of Equation 2 using a discretized version of the raw data. Panel A shows the quarterly distribution of hydrocodone per capita, broken down by the first and fourth quartile of exposure to treatment. This figure reveals that the zip3s in the fourth quartile were trending down slightly faster than those in the first quartile prior to the rescheduling. Panel B fits a linear trend to each quartile based on the pre-period, while Panel C shows deviations from these linear trends. Of course, hydrocodone is just one of many different opioids. Ex ante, it is plausible that the drop in hydrocodone distribution was offset by substitution towards other opioids. In order to investigate this, I run a simpler version of Equation 2 that only interacts 
with a post indicator and then plot these coefficients for all of the opioids reported in ARCOS. These coefficients are shown graphically in Figure 4. Panel A shows the coefficients for a variety of opioids, all of which are converted to morphine milligram equivalents. Consistent with Figure 3, Figure 4 shows a reduction of a little less than 10 milligrams of hydrocodone per person–quarter after the rescheduling in places with one standard deviation more exposure to hydrocodone in the pre-period. Interestingly, there appears to be almost no substitution toward other opioids. The only statistically significant positive estimate is for codeine, although the magnitude is far too small to compensate for the decrease in hydrocodone.
Hydrocodone per Person–Quarter Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show the coefficients on the 
× time interactions from regression Equations 1 (Panel A) and 2 (Panel B) with the number of milligrams of hydrocodone per capita as the dependent variable. The dependent variable is measured at the zip3-by-quarter level. The coefficients can be interpreted as the effect of a one standard deviation increase in pre-period hydrocodone consumption. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the vertical bars and the dashed gray lines, respectively.
Other Opioids: Impact of One Standard Deviation Increase in Pre-Period Hydrocodone Exposure
Notes: These figures show the coefficients from a simple before and after difference-in-differences analogous to Equation 2 for a variety of opioids in the ARCOS data. Explicitly, these are the θ coefficients from the regression 
. The coefficients in black (Panel A) are first converted to morphine milligram equivalents. The coefficients in Panel B do not have obvious conversion factors and so are left in milligrams.
Given codeine’s Schedule III status throughout the sample period, I provide additional evidence on this substitution in Online Appendix Figure A5.42 Panel A plots the quarterly distribution of codeine against hydrocodone. This panel shows that, while the distribution of codeine did increase following the rescheduling, the increase was substantially smaller than the decrease in hydrocodone distribution. Although the aggregate change in codeine prescribing following the rescheduling was quite modest, in Panel B I investigate whether there was a particularly large increase in codeine prescribing in the areas most affected by the reformulation. This panel replicates Panel A of Figure 3 and adds regression coefficients from Equation 1 with the amount of codeine per person–quarter as an outcome variable. This figure again demonstrates modest substitution toward codeine, even in areas particularly exposed to the rescheduling. Finally, Panels C and D provide analogous analysis using data from Medicare Part D. Although these data are only available starting in 2013, I am able to examine the number of prescriptions as opposed to morphine milligram equivalents. These panels show results that are qualitatively very similar to Panels A and B.43
For several of the opioids tracked by the DEA, there was no straightforward conversion into morphine milligram equivalents, so I leave them in milligrams per capita. These coefficients, along with the coefficient for hydrocodone, are reported in in Panel B.44 None of these coefficients are statistically significant, and all are very close to zero.
One notable omission from Figure 4 is tramadol. Tramadol was a previously unscheduled synthetic opioid that was placed in Schedule IV in August of 2014. Because of its late addition to the Controlled Substances Act, tramadol was not reported by the DEA. However, I am able to pull data on the annual distribution of Tramadol from IQVIA (taken from a report by U.S. Food and Drug Administration 2018) and compare it to the quarterly distribution of hydrocodone. This is shown in Online Appendix Figure A6 and suggests that there wasn’t significant substitution toward Tramadol after the rescheduling. However, I do not have access to these data with any geographic coverage, so I cannot use them in my regression framework. Therefore, I rely on data from Medicare Part D to further test substitution toward tramadol. I present this analysis in Panels C and D of Online Appendix Figure A5. Panel C presents the number of annual claims for tramadol, along with HCPs and codeine/acetaminophen for 2013–2017. While there is some increase in tramadol prescribing, it is relatively small compared to the drop in HCP prescribing. Panel D presents the regression results from Equation 1 and indicates that there was virtually no substitution toward tramadol after the rescheduling of HCPs.
In order to explore the possible dynamic responses of other opioids, I present the coefficients from Equation 1 pooling all opioids that can be converted into morphine equivalent doses in Panel A of Figure 5. This figure shows no break around the date of the rescheduling, indicating that there was no immediate substitution toward other opioids after the rescheduling. In fact, the coefficients become negative and statistically significant several quarters after the rescheduling, indicating that if anything there was less consumption of possible substitute opioids. However, the coefficients reveal a steady decline in the pre-period as well. Adjusting for this pre-trend in Panel B shows that there is no effect on other nonhydrocodone opioids.
Other Opioids per Person–Quarter Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show the coefficients on the 
× time interactions from regression Equations 1 (Panel A) and 2 (Panel B) with the per capita morphine milligram equivalent distribution of nonhydrocodone opioids as the dependent variable. The opioids included in this variable are oxycodone, oxymorphone, morphine, methadone, meperidine, codeine, levorphanol, hydromorphone, and dihydrocodeine. The dependent variable is measured at the zip3-by-quarter level. The coefficients can be interpreted as the effect of a one standard deviation increase in pre-period hydrocodone consumption. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the vertical bars and the dashed gray lines, respectively.
Taken together, these results demonstrate that areas with high levels of hydrocodone consumption were in fact the areas most affected by the rescheduling. Furthermore, these effects were not simply undone via substitution toward other prescription opioids. It is possible, however, that some substitution could have occurred toward illegal drugs, such as heroin or illicitly manufactured fentanyl. While I do not have access to data on illicit drug consumption, I examine drug-related arrests and overdose deaths in Sections V.D and V.E. Given the large number of individuals outside of the labor force taking prescription painkillers (Krueger 2017), this lends plausibility to the idea that this intervention may have had effects in the labor market, which I document in the next subsection.
B. Labor Market Results
1. Labor force participation
Given the large, differential reduction in hydrocodone consumption in areas with higher pre-period consumption of hydrocodone, I now investigate whether the rescheduling affected the labor market. First, I examine the effects of the rescheduling on the labor force participation (LFP) rate. Panel A of Figure 6 graphically presents each βT coefficient from estimating equation 1, with βSept.2014 normalized to zero and 95 percent confidence intervals indicated by gray shading. Each of these coefficients can be interpreted as the expected difference in the LFP rate in zip3s that had one standard deviation higher levels of per capita hydrocodone consumption in the pre-period. Examining these coefficients reveals a striking pattern: LFP rates were falling substantially faster in areas with more hydrocodone exposure in the pre-period. However, following the rescheduling this differential trend disappears immediately, suggesting that the rescheduling affected the LFP rate differentially in areas with differing levels of exposure to the rescheduling.45
Labor Force Participation Rate and Employment-to-Population Ratio Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show the coefficients on the 
× time interactions from regression Equations 1 (Panels A and C) and 2 (Panel B and D). Panels A and B show the results for the labor force participation rate, while Panels C and D show the results for the employment-to-population ratio. The dependent variables are measured at the zip3-by-month level. The coefficients can be interpreted as the effect of a one standard deviation increase in pre-period hydrocodone consumption. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the shaded region and the dashed gray lines, respectively.
In order to interpret the post-period regression coefficients as the causal effect of the policy in question, the standard difference-in-difference model requires the assumption that outcomes in differentially treated areas would have continued trending similarly in the absence of the treatment, conditional on the included controls. This is commonly referred to as the “parallel trends” assumption and is generally tested by examining whether the pre-period coefficients differ from zero. The underlying idea is that if outcomes are trending differentially prior to the treatment and these same trends continue into the post-period, a typical difference-in-differences model will erroneously estimate a treatment effect when in reality the policy had no effect. In this context, the typical parallel trends assumption is clearly not met.
However, the regression coefficients demonstrate a sharp break in trend coincident with the date of the rescheduling. Interpreting this trend break as the impact of the rescheduling requires the assumption that in the absence of the rescheduling, the preexisting (differential) trends in the outcome variable would have continued. Put slightly differently, this model assumes that deviations from a linear trend among the observations less exposed to the treatment provide a reasonable counterfactual for the observations that were more exposed to treatment had the treatment not taken place. Conceptually, this is equivalent to the familiar parallel trends assumption after controlling for zip3-specific pre-trends.
I formally describe this regression in Equation 2 and graphically present the regression coefficients in Panel B of Figure 6.46 Each of these coefficients can be interpreted as the average difference from trend in zip3s one standard deviation apart in pre-period hydrocodone consumption. The pre-period coefficients are all close to zero in magnitude and statistically insignificant, indicating that there was very little deviation from trend in the pre-period. However, immediately following the rescheduling the coefficients become positive, indicating a relative increase in the LFP rate in areas that were more heavily exposed to the rescheduling.47 About two and one-half years after the rescheduling, the LFP rate was about 0.44 percentage points above trend in areas with an additional standard deviation of exposure to the treatment. Relative to the mean LFP rate (shown in the bottom left corner of Panel A), this suggests around a 0.7 percent increase in the LFP rate. A more extreme treatment, for example, moving from the tenth to the 90th percentile in terms of pre-period hydrocodone consumption is associated with a more than 0.88 percentage point increase in the LFP rate, about a 1.4 percent increase above the mean.
In order to characterize the magnitude of this result directly in terms of the reduction in hydrocodone, I scale the treatment effect on the LFP rate by the treatment effect on hydrocodone. Specifically, a one standard deviation increase in pre-period exposure to treatment is associated with a 22 percent decrease in hydrocodone and a 0.7 percent (0.44 percentage point) increase in the LFP rate two and one-half years later. Dividing these estimates indicates that a 10 percent decrease in hydrocodone prescriptions is associated with about a 0.32 percent increase in the LFP rate. Extrapolating from this estimate to the 36 percent aggregate reduction in hydrocodone consumption since the rescheduling suggests that the rescheduling could account for an aggregate increase in the LFP rate of about 1.8 percent (1.15 percentage points).48
2. Employment
Mechanically, the increase in LFP could be driven by either increases in employment or by increases in unemployment.49 In order to investigate what is causing the change in the LFP rate, I begin by examining the effects of the rescheduling on the employment-to-population ratio (EPR). Panel C of Figure 6 plots each coefficient from regression Equation 1. These coefficients show an almost identical pattern to the analogous regressions examining the LFP rate: the EPR was falling at a faster rate in places with more exposure to the treatment in the pre-period, although this pattern stops immediately after the rescheduling. In addition to duplicating the same pattern as the LFP rate, the EPR coefficients are nearly identical in magnitude. This indicates that nearly the entire relative rise in the LFP rate can be explained by the change in the EPR. The results from the parametric model that allows for linear pre-trends are shown in Panel D. Again, this approximately duplicates the results from Panel B of Figure 6. Prior to the rescheduling, there was little deviation from a linear trend, although in the post-period all of the coefficients become positive, indicating differential increases in the EPR in places more exposed to the treatment.50
Although the change in EPR can almost completely account for the increase in the LFP rate, I also examine the effects of the rescheduling on the unemployment-to-population ratio (UPR) for the sake of completeness. The nonparametric regression results with the UPR as the dependent variable are shown in Panel A of Online Appendix Figure A8. Unlike the EPR or LFP rate, the UPR does not exhibit any clear trends either before or after the rescheduling. While some of the coefficients are statistically different from zero, they are typically small in magnitude and move somewhat erratically. Although there is no evidence of a linear pre-trend, I still run the parametric regression and report the coefficients in Panel B. Taken together, these estimates suggest that the large changes in LFP are driven primarily by changes in employment as opposed to unemployment.
3. Wages
Next, I investigate the response of wages to the rescheduling. Since the LAUS do not contain information about wages, I present estimates from the ACS. The downside of these data is that they are only measured at the state-by-year level. However, the benefit is that I am able to use data back to 2005.51 Results for the log of annual wage income are reported in Panels A and B of Figure 7. Broadly speaking, the patterns here mirror those in the results examining the LFP and EPR. The post-period coefficients in Panel B are all positive, although modest in magnitude. The average of the three post-period coefficients is 0.002, indicating that a one standard deviation increase in exposure to treatment is associated with a 0.2 percent increase in annual wages. I also construct a measure of hourly wages and present these results in Panels C and D.52 The patterns here are very similar to those in Panels A and B. The average coefficient across the post-period in Panel D is 0.008, indicating an increase in hourly wages of 0.8 percent in response to a one standard deviation increase in exposure to the rescheduling. The estimates here are quite noisy, and I cannot reject a null hypothesis of no change in hourly wages.
Annual and Hourly Log Wage Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show the coefficients on the 
× time interactions from regression Equations 1 (Panels A and C) and 2 (Panel B and D). Panels A and B show the results for the log of annual wages, while Panels C and D show the results for the log of hourly wages. The dependent variables are measured at the state-by-year level. The coefficients can be interpreted as the effect of a one standard deviation increase in pre-period hydrocodone consumption. Standard errors are clustered at the state level.
4. Comparison with related literature
As discussed in Section II, there is a growing literature investigating the relationship between opioid consumption and the labor market. In this section, I briefly discuss how the results presented above compare with this other research. I present an overview of this discussion in Online Appendix Table A4. For the sake of brevity, here I only discuss papers using policy-induced variation in opioid access.
Building off of Alpert, Powell, and Pacula (2018), recent work by Park and Powell (2021) estimates how the reformulation of OxyContin affected employment. They find that states that were most heavily impacted by the reformulation (that is, states that saw larger post-reformulation increases in heroin use) experienced decreases in employment. Similar to my paper, this work is consistent with higher opioid usage resulting in decreased EPR.
A simple comparison suggests that our estimates are within the same ballpark. I find that a 10 percent decrease in HCP shipments is associated with a 0.2 percentage point increase in the LFP rate. In their paper, Park and Powell (2021) find that a 10 percent decrease in exposure to the reformulation (which is associated with less future heroin use) leads to a 0.18 percentage point in the EPR. Both of these estimates indicate that reduced opioid use—whether legal or illicit—is associated with improved labor market conditions.
Several papers examine labor market responses to PDMPs and draw different conclusions. For example, Kaestner and Ziedan (2019) find that PDMPs lead to a decrease in employment. This is consistent with Kilby (2015), who finds PDMPs lead to increases in absences from work. In contrast, Franco, Wagner and Whaley (2021) finds that PDMPs lead to a decrease in workplace absences. Deiana and Giua (2018) finds no effect of PDMPs on the labor market.
Each of these papers uses a difference-in-differences framework, although the legal coding differs. For example, Kaestner and Ziedan (2019) focuses primarily on the adoption of “modern” PDMPs as defined by Horwitz et al. (2018).53 Deiana and Giua (2018) instead focuses on MA-PDMPs using the coding from Mallatt (2018). Franco, Wagner, and Whaley (2021) also focus on MA-PDMPs, although the states and dates of implementation differ from those coded by Mallatt (2018). Kilby (2015) uses the date of implementation of any PDMP using data from the National Alliance for Model State Drug Laws. These differences reflect a broader issue in the literature studying the effects of PDMPs: there is substantial disagreement on which types of laws matter and how to code them (Horwitz et al. 2018). Overall, the differing results across these papers present an unclear picture of how PDMPs affect the labor market.54
The precise reasons for the differences across papers are not easy to diagnose. There are important differences between the rescheduling of HCPs, the reformulation of OxyContin, and the implementation of PDMPs, which may lead to different effects of these policies. My findings are quite similar to the existing literature studying the reformulation of OxyContin. The literature studying the implementation of PDMPs, in contrast, documents labor market effects that are positive, negative, and nonexistent. The main benefit of my paper and Park and Powell (2021) is the source of sharp, transparent variation in opioid consumption, which can be used to estimate the labor market impacts of changes to the opioid market.
C. SSDI
The previous two subsections indicate that the rescheduling of hydrocodone led to a reduction in the supply of hydrocodone and a corresponding increase in the LFP rate and EPR in areas that saw larger reductions in hydrocodone consumption. More individuals participating in the labor market could have an added effect of reducing disability claims if those entering (or not leaving) the labor market would have otherwise enrolled in SSI/SSDI. Krueger (2017) reports that approximately one-half of prime-aged males outside of the labor market regularly take pain medication, suggesting that opioids may play a significant role in disability claims. In light of this, I now investigate the effects of the rescheduling on disability outcomes. First, I examine the effects of the rescheduling on the rate of SSDI beneficiaries per 1,000 population. The results from Equation 1 are shown in Panel A of Figure 8.55 As before, the treatment variable is scaled so that all coefficients can be interpreted as the effect of a one standard deviation increase in 
. For this variable, the pre-period coefficients are generally small in magnitude and not significantly different from zero, indicating no differential trends in outcomes in the pre-period. Beginning with 2014, however, the coefficients begin to fall. In 2017, the coefficient is approximately −0.5, indicating that a standard deviation increase in exposure to the treatment is associated with a reduction of 0.5 SSDI beneficiaries per 1,000 population, about a 1.5 percent decrease relative to the mean.56 This is consistent with Park and Powell (2021), who find that increases in opioid abuse following the reformulation of OxyContin led to increases in SSDI beneficiaries.
SSDI Beneficiaries Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show the coefficients on the 
× year interactions from regression Equations 1 (Panel A) and 2 (Panel B) with the number of SSDI beneficiaries per 1,000 as the dependent variable. The dependent variable is measured at the zip3-by-year level. The coefficients can be interpreted as the effect of a one standard deviation increase in pre-period hydrocodone consumption. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by vertical dashed lines and solid triangles, respectively.
Next, I investigate the possible channels behind this change. Mechanically, a reduction in the stock of SSDI beneficiaries could be driven by individuals giving up their SSDI benefits, as well as by fewer new individuals applying for and receiving benefits. Given the fixed costs associated with applying for SSDI, it appears ex ante more likely that the stock change is driven by the latter mechanism. While I do not have data on beneficiary flows into and out of SSDI at the zip3 level, SSA publishes information about new applications at the state level. I show the regression results examining the number of new applications in Panel A of Figure 9. This panel demonstrates that areas more exposed to the rescheduling had fewer new applicants in the years following the rescheduling, consistent with my hypothesis. However, Panel B casts doubt on this explanation. This figure shows no evidence that the rate of new SSDI allowances (that is, newly accepted beneficiaries) changed following the rescheduling.
SSDI Filing and Allowance Rates: Impact of One Standard Deviation Increase in 
Notes: These figures show the coefficients on the 
× year interactions from regression Equation 1. Panel A shows the results at for the fraction of eligible adults filing for SSDI benefits each year, and Panel B shows the rate of new SSDI beneficiaries. The dependent variables are measured at the state-by-year level. The coefficients can be interpreted as the effect of a one standard deviation increase in pre-period hydrocodone consumption. Standard errors are clustered at the state level.
The reason for this is that the fraction of applications being accepted increased coincident with the rescheduling, offsetting the drop in applications. Mechanically, it is still possible that the change in the stock of beneficiaries is driven by individuals giving up SSDI, although I have no data with which to test this hypothesis. Ultimately, the mechanisms behind this change are unclear.
D. Arrests
The labor market results presented to this point generally point to positive impacts of the rescheduling. However, other research has documented increases in drug-related crime and overdose deaths in response to opioid restrictions (Mallatt 2018; Alpert, Powell, and Pacula 2018). In this section, I explore whether the rescheduling led to any changes in drug-related arrests.
Conceptually, the effect of the rescheduling on drug-related arrests is ambiguous. If the rescheduling prevents individuals from developing a dependence on opioids, then we may expect decreased drug possession arrests. Likewise, the increased cost of obtaining hydrocodone for distribution may have pushed marginal illicit suppliers out of the market. However, if dependent users who formerly obtained their drugs from the legal market transition to the illicit market, we may see increases in arrests.
I investigate the impact of the rescheduling on total drug-related arrests in Panel A of Figure 10. This figure presents regression coefficients from Equation 1 with the total number of drug-related arrests per 100,000 population as the dependent variable. The pre-period coefficients are generally small in magnitude and statistically insignificant, demonstrating the lack of differential trends in arrests across areas with different exposure to treatment. However, immediately following the rescheduling, there is a sharp, persistent increase in the number of drug-related arrests. The coefficients grow somewhat over time, with an average value of 4.03. Relative to the mean value of 109.6 arrests per 100,000, this indicates a 3.68 percent increase in total arrests. The post-period coefficients are jointly significant (p = 0.02).57
Total Drug-Related Arrest Regression Estimates: Impact of Once Standard Deviation Increase in 
Notes: These figures show regression coefficients on the 
× time interactions from regression Equation 1 for drug-related arrest outcomes. The outcome in Panel A is the total number of arrests per 100,000 population. The outcomes in Panels B and C are the number of arrests per 100,000 population for drug possession and sale, respectively. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the shaded region and the dashed gray lines, respectively.
Next, I consider whether the increase in arrests was primarily driven by increases in possession or distribution. I show these results in Panels B and C of Figure 10, respectively. These panels indicate that the entire increase in total arrests was driven by increases in drug possession, as opposed to drug sales. This is suggestive of dependent users transitioning to the illicit market in response to the decreased legal supply, highlighting some of the adverse consequences of reducing the supply of legal opioids.
In Figure 11, I investigate which drug categories are responsible for the increase in total arrests. Each of the panels on the left indicate possession arrests, while the panels on the right show the results for sale arrests. The coefficients in Panel A indicate a large but imprecisely estimated increase in possession arrests related to heroin or cocaine. This is consistent with substitution toward heroin after the rescheduling. This is similar to Mallatt (2018), who finds increases in heroin crimes after the implementation of MA-PDMPs. The average of the post-period coefficients is 0.70, an increase of about 4.4 percent over the mean value of 15.85. However, these coefficients are not jointly significant when clustering at the state level. In comparison, Mallatt (2018) also finds no significant effects of MA-PDMPs on heroin-related crime on aggregate, but an 87 percent increase in counties within the top 10 percent of oxycodone consumption. While it’s difficult to compare our magnitudes directly given the different treatments, scaling my estimates by the difference in exposure to treatment between the minimum and 90th percentile gives an increase in heroin possession arrests of a little more than 10 percent, somewhat smaller than the estimates presented in Mallatt (2018).
Specific Drug-Related Arrest Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show regression coefficients on the 
× time interactions from regression Equation 1 for specific drug-related arrest outcomes. Outcomes in the left column are drug possession arrests for heroin/ cocaine, other drugs, and cannabis per 100,000 population. Outcomes in the right column are for sale of the same drugs. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the shaded region and the dashed gray lines, respectively.
By far the most striking results are shown in Panel C, which present results for “other” drug possession arrests.58 Here we observe a clear, persistent increase in arrests that continues growing through the end of the sample period. The last point estimate in my sample is 3.76, indicating an 17.68 percent increase in arrests relative to the mean. The results for synthetic narcotics and cannabis are shown in Panels E and G, respectively. In both cases, there appears to be a temporary spike in arrests after the rescheduling, although the effects fade away by the end of the sample period. There is no clear evidence of meaningful changes in drug sale arrests, with the exception of the “other” arrests category. Here, the post-coefficients are jointly significant and indicate an 8 percent increase in arrests relative to the mean. Overall, these results demonstrate that while the rescheduling led to improvements in labor market conditions, there were at least some individuals who were adversely affected.
E. Mortality
In this section, I consider whether the rescheduling led to any changes in drug-related mortality. If the primary effect of the rescheduling was to reduce the number of opioid users, then we may expect declines in mortality in the years following the rescheduling. However, if individuals respond to the rescheduling by substituting toward other substances, then we may instead see no changes or even increased mortality.
I present the main result investigating opioid-related mortality in Figure 12. This figure shows the regression coefficients from Equation 1 with the total number of opioid-related deaths per 100,000 as the outcome variable. Although many of the coefficients in the post-period are negative, this is not the case until nearly a year after the rescheduling. Since this figure pools together many different opioid-related deaths, it is possible that this aggregate figure masks some heterogeneity across drugs. I investigate this in Figure 13. The results for natural and semisynthetic opioids, the category that contains hydrocodone, also shows no evidence of an effect of the rescheduling. I find similar results for methadone in Panel B. Taken together, these figures suggest that the rescheduling had little impact on overdoses of prescription painkillers.
Total Opioid-Related Mortality Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: This figure shows the regression coefficients on the 
× time interactions from regression Equation 1 for total opioid-related mortality. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the shaded region and the dashed gray lines, respectively.
Specific Opioid-Related Mortality Regression Estimates: Impact of One Standard Deviation increase in 
Notes: These figures show regression coefficients on the 
× time interactions from regression Equation 1 for opioid-related mortality outcomes. The outcome in Panel A is the number of deaths that list natural and semisynthetic opioids as a cause of death (code T40.2) per 100,000 population. The outcomes in Panels B, C, and D are deaths listing methadone (T40.3), synthetic opioids (T40.4), and heroin (T40.1) per 100,000 population. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the shaded region and the dashed gray lines, respectively.
Next, I consider the impact of the rescheduling on deaths from illicit opioids. Panel C shows the coefficients for synthetic opioids, which are primarily composed of illicit fentanyl deaths. The pre-period coefficients indicate that there were no differential trends leading up to the rescheduling. After the rescheduling, the coefficients drop substantially, although this occurs with a noticeable delay. One potential story that could reconcile this result is that the rescheduling could have deterred some individuals who would have ultimately transitioned from HCPs to the illicit market from using HCPs in the first place. However, given the lack of panel data on individual drug use, I am unable to test this hypothesis. The results for heroin are presented in Panel D. Here again we see little evidence of any substitution. This is in contrast to Alpert, Powell, and Pacula (2018), who find large increases in heroin-related deaths after the reformulation of OxyContin. However, it is worth reiterating that the only individuals affected by the reformulation of OxyContin were recreational users, who likely have a much higher propensity to transition to the illicit market than users of HCPs.
Finally, I investigate non-opioid-related or unspecified drug-related deaths. This is important for two reasons. First, 20–25 percent of all fatal overdose deaths do not list any specific drug on the death certificate (Ruhm 2018). Second, the frequency of overdose deaths involving nonopioid drugs, specifically sedatives and psychotropics (often in combination with opioids) has grown over time (Ruhm 2018). For example, in 2014, Ruhm (2016) estimates that 68.7 and 47.9 percent of opioid overdose deaths also involved sedative or psychotropic drugs, respectively. Therefore, even if there is no change in opioid-related mortality, we may still observe changes in mortality involving these other drug categories.
Panel A of Figure 14 shows the regression coefficients from Equation 1 with unspecified overdose deaths as the outcome variable. This figure demonstrates an immediate decline in deaths following the rescheduling. Quantitatively, the regression coefficients indicate that a one standard deviation increase in exposure to the rescheduling led to almost a 25 percent decrease in unspecified drug overdose deaths. Of course, the major issue in interpreting these results is that we do not know what drugs led to these deaths, so it is difficult to draw strong conclusions about how the rescheduling affected these deaths. One plausible story is that these are primarily HCP-related overdose deaths that were averted by the rescheduling. However, there are other possible explanations that I cannot distinguish between.
Other Drug Overdose Death Regression Estimates: Impact of One Standard Deviation Increase in 
Notes: These figures show regression coefficients on the 
× time interactions from regression Equation 1 for opioid-related mortality outcomes. The outcome in Panel A is the number of deaths from unspecified drugs per 100,000 population. The outcomes in Panels B, C, and D are deaths listing psychotropics (T43.0–9), psychostimulants (T43.6), and nonbenzodiazepine sedatives (T42.0–3, T42.5–8) per 100,000 population. The 95 percent confidence intervals using standard errors clustered at the zip3 and state levels are indicated by the shaded region and the dashed gray lines, respectively.
Next, I examine psychotropic drug-related deaths in Panel B. Psychotropics are a broad category and include antidepressants, antipsychotics, and stimulants. In contrast to unspecified deaths, these results show a clear increase following the rescheduling. Given that these drugs are frequently used along with opioids, this is consistent with increasing reliance on psychotropics as opioids become less accessible after the rescheduling. Panel C shows the results for stimulants, a subcategory of psychotropics, which includes various amphetamines. This figure demonstrates that the increase in psychotropic drugs shown in Panel B is entirely driven by increases in stimulant-related deaths. Similarly, I find an increase in nonbenzodiazepine sedatives in Panel D, although these effects dissipate quickly.59
The results in this section present a somewhat nuanced picture. There seems to be no change in prescription opioid deaths following the rescheduling, although there is some suggestive evidence of a delayed decrease in illicit synthetic opioid deaths. There is a clear decrease in unspecified drug-overdose deaths, which could be driven by any number of drugs. In contrast, there is a clear rise in overdose deaths related to drugs that are commonly used in conjunction with opioids, specifically psychotropics and sedatives. These results are broadly consistent with the rescheduling preventing future synthetic opioid overdose deaths for some HCP users, while pushing others toward heavier reliance on other components of common drug cocktails.
A series of robustness tests supports a causal interpretation of these findings. I find that the results are driven specifically by areas with high levels of pre-rescheduling exposure to hydrocodone as opposed to high opioid consumption more generally. I also present regression results explicitly controlling for other opioid-related policy changes and find similar effects. Finally, I show that the results are not sensitive to the specific measure of hydrocodone consumption, nor alternate methods to measure exposure to the rescheduling. I discuss these tests in detail in Online Appendix Section A2.
VI. Conclusion
The proliferation of opioid prescriptions in the United States coincided not only with rises in opioid abuse and mortality, but also with deteriorating labor market conditions. This labor market decay has been particularly pronounced in areas hit hardest by the opioid crisis, provoking researchers to ask whether opioids have a causal impact on the labor market. However, the lack of plausibly exogenous variation in opioid prescribing has made it difficult to answer this question. In this paper, I provide new evidence on how opioids affect the labor market by exploiting variation stemming from a natural experiment. I find that a 10 percent drop in hydrocodone prescriptions causes a 0.32 percent increase in the labor force participation rate, which is driven almost entirely by relative increases in employment. These estimates suggest that the rescheduling of hydrocodone can account for around a half percentage point (about 0.8 percent) increase in the LFP rate and a 1 percent (0.61 percentage point) increase in the EPR. In total this amounts to about 800,000 additional individuals being employed relative to a counterfactual in which the rescheduling never happened.
While the rescheduling has primarily positive effects on the labor market, it is not without adverse consequences. I find increases in drug possession arrests and overdose deaths for certain drug categories, consistent with substitution toward illicit markets as legal opioids become more difficult to access.
These findings inform several aspects of the academic discussion of correlates that affect opioid prescriptions, as well as the effects of opioids on a variety of different outcomes. For example, a variety of other interventions with the goal of reigning in opioid prescriptions have been implemented with varying degrees of success. The findings here suggest a simple, low-cost intervention to decrease drug prescribing, namely, drug rescheduling. This type of intervention could be effective for any drugs that the DEA currently regulates, not just opioids. For example, there is growing concern surrounding stark increases in the abuse of benzodiazepines, almost all of which are currently in a less stringently regulated drug schedule (IV). Extrapolating from the rescheduling of hydrocodone combination products suggests that prescribing of benzodiazepines could be substantially reduced via rescheduling.60
This paper further contributes to our understanding of how opioids affect the labor market. While previous evidence using a variety of different estimation strategies is mixed, the findings of this study suggests that the effects of opioids on the labor market is primarily negative—that is, reductions in opioid prescribing improve labor market conditions. This is consistent with several other papers (for example, Harris et al. 2017; Savych, Neumark, and Lea 2018; Laird and Nielsen 2016; Aliprantis, Fee, and Schweitzer 2019), although it is qualitatively different than others (for example, Currie, Jin, and Schnell 2019; Kilby 2015). Further research is needed in order to understand what drives these differences.
The direct effects of policies geared toward reducing opioid prescriptions on the number of prescriptions ordered, as well as spillover effects onto the labor market and illicit drug markets are important components in evaluating these policies. However, they are not sufficient for a complete welfare analysis. There is one particularly salient concern that suggests caution in taking further steps to reduce access to opioids: improvements in the labor market need to be weighed against increased suffering among legitimate pain patients. Alarmingly, more than a quarter of respondents to an online survey of hydrocodone patients reported thoughts of suicide after the rescheduling, highlighting the trade-offs inherent in reducing access to pain medication (Chambers et al. 2015). New ways to help providers separately identify recreational users, diverters, and legitimate pain patients would be useful in developing targeted interventions that could reduce opioid abuse while continuing to provide pain relief to patients.
Footnotes
The author is grateful to Marika Cabral, Cooper Howes, Mike Geruso, Kevin Kuruc, Melissa LoPalo, Rich Murphy, Emily Weisburst, two anonymous referees, and seminar participants at the University of Texas at Austin and the Stata Texas Empirical Microeconomics conference for helpful comments and suggestions. The author has no conflicts of interest to disclose. This paper uses restricted mortality data from the National Vital Statistics System. These data can be obtained by submitting an application to the National Center for Health Statistics. For more information, visit https://www.cdc.gov/nchs/nvss/nvss-restricted-data.htm. The author is willing to assist (david.beheshti{at}utsa.edu). All other data and code can be found on the author’s website (https://sites.google.com/view/davidbeheshti).
Color version of this article is available online at: https://jhr.uwpress.org.
Supplementary materials are available online at: https://jhr.uwpress.org.
↵1. Sources: CDC State Prescribing Maps, CDC WONDER Online Database, and BLS Local Area Unemployment Statistics.
↵2. Refers to deaths with MCD Codes T40.2 and T40.3. Including deaths from heroin and synthetic opioids (for example, fentanyl) makes the rise even more dramatic, with the number of total opioid overdose deaths increasing by more than eight times over the same period.
↵3. See Doleac, Mukherjee, and Schnell (2018) for a review of the recent literature regarding the opioid epidemic.
↵4. Several papers in the medical literature also investigate the rescheduling and find reduced access to hydrocodone, consistent with the findings in this paper (for example, Chambers et al. 2015; Jones, Lurie, and Throckmorton 2016). This paper further expands on these papers by considering the effects of the rescheduling on outcomes beyond prescribing behavior, specifically labor market behaviors.
↵5. PDMPs are state laws that allow (or sometimes require) prescribers to check a patient’s prescription history before dispensing narcotics.
↵6. The literature studying the effects of PDMPs also relies on policy-induced variation, although the findings from this literature are somewhat mixed. Another exception is Laird and Nielsen (2016), which examines behaviors of individuals in Denmark who move to high opioid prescribing areas and finds that these movers consume more opioids and reduce their labor force participation after the move. However, opioid use and abuse in the United States is substantially higher in both levels and growth rates than in Denmark. Related work by Finkelstein, Gentzkow, and Williams (2018) finds that SSDI beneficiaries in the United States who move to high-prescribing areas are substantially more likely to receive an opioid prescription. However, given the population they are studying, Finkelstein, Gentzkow, and Williams (2018) are not able to examine labor market behaviors.
↵7. States can add additional requirements regarding the prescribing and dispensing of controlled substances above and beyond federal regulations.
↵8. Cox-2 inhibitors are anti-inflammatory drugs used to treat a variety of conditions, especially arthritis.
↵9. Hydrocodone was ranked the as the second most preferred opioid among recreational users, and was the drug of choice among around 30 percent of those surveyed.
↵10. Author’s calculation using the 2013 Part D Prescriber Public Use File, available at https://www.cms.gov/Research-Statistics-Data-and-Systems/Statistics-Trends-and-Reports/Medicare-Provider-Charge-Data/Part-D-Prescriber.html (accessed May 17, 2023).
↵11. Source: https://www.pharmacytimes.com/publications/issue/2014/july2014/top-drugs-of-2013 (accessed May 17, 2023).
↵12. Despite being the most commonly prescribed opioid in the United States, hydrocodone is less frequently mentioned in popular accounts of the opioid crisis, which have mainly focused on the role of OxyContin in driving opioid abuse and mortality (Quinones 2015). This is due at least in part to the ease with which OxyContin could be abused prior to its reformulation in 2010 (Alpert, Powell, and Pacula 2018; Evans, Lieber, and Power 2018; Beheshti 2019). This ease of abuse led to oxycodone playing an outsized role in opioid-related mortality relative to its prescribing and reported misuse. Hydrocodone was the fourth leading cause of death among painkillers for 2011–2016, following oxycodone, morphine, and methadone.
↵13. Schedule I drugs are those that are considered to have no accepted medical use and high potential for abuse, and are therefore not available via prescription.
↵14. Title 21 Code of Federal Regulations (https://www.ecfr.gov/current/title-21/chapter-II/part-1306/subject -group-ECFRe4ae2bfb4eae102/section-1306.22, accessed May 17, 2023).
↵15. Currently, two extended-release hydrocodone (only) drugs are available in the United States, Zohydro ER and Hysingla ER. These were not released until after the rescheduling.
↵16. It is not clear who initiated this petition. Legally, any interested party may do so according to 21 U.S.C. 811(a).
↵17. Similar figures are shown with the number of hydrocodone prescriptions and tablets dispensed immediately before and after the rescheduling in (Jones, Lurie, and Throckmorton 2016) using proprietary pharmacy data from the IMS Health National Prescription Audit. Their data cover the period between 2011 Q4 and 2015 Q3.
↵18. Results available upon request.
↵19. In principle, this just subtracts the implied time trend out from the nonparametric model. More specifically, Equations 1 and 2 imply βt – θt = a + b · t ∀ t > Sept. 2014, where a and b are constants. Using this relationship I can recover the implicit pre-period θT coefficients, that is, θt = βt – a – b · t ∀ t. Dobkin et al. (2018) do this in reverse, superimposing the θ coefficients onto the β coefficients and plotting the implied time trend along with the nonparametric coefficients.
↵20. Title 21, United States Code, Section 827(d) (1), and Title 21, Code of Federal Regulations, Section 1304.33.
↵21. Data can be downloaded here: https://www.deadiversion.usdoj.gov/arcos/retail_drug_summary/index.html
↵22. Data include hydrocodone, oxycodone, remifentanil, oxymorphone, powdered opium, morphine, methadone, meperidine (pethidine), levorphanol, hydromorphone, fentanyl base, dihydrocodeine, codeine, buprenorphine, sufentanil, and opium tincture. One notable omission is tramadol, for which ARCOS does not publish any data. Data at the ingredient level is also available through the Medicare Part D prescriber files (https://www.cms .gov/Research-Statistics-Data-and-Systems/Statistics-Trends-and-Reports/Medicare-Provider-Charge-Data /Part-D-Prescriber.html, accessed May 17, 2023). This is only reflective of prescriptions to Medicare beneficiaries enrolled in Part D.
↵23. Because of this, for the remainder of the paper I use the terms distribution and consumption interchangeably.
↵24. Medicare Part D is an exception, although again this only provides information about a segment of the population.
↵25. For more information, see https://www.bls.gov/lau/laumthd.htm.
↵26. The CPS does not explicitly report a population threshold for data suppression, although all but seven of the counties identified in the CPS have a population greater than 100,000. The Census Bureau explicitly states that CPS estimates are not reliable (or even available) for most counties (https://www.census.gov/programs -surveys/cps/about/faqs.html#Q3, accessed May 17, 2023).
↵27. This corresponds to approximately 51.85 and 16.43 percent of the population, respectively. The counties identified are shown in Online Appendix Figure A2.
↵28. See Deshpande, Gross, and Su (2021) for more detailed discussion of the institutional background of both programs.
↵29. SSI data available at https://www.ssa.gov/policy/docs/statcomps/ssi_sc/index.html (accessed May 17, 2023). SSDI data available at https://www.ssa.gov/policy/docs/statcomps/oasdi_zip/index.html (accessed May 17, 2023).
↵30. The heroin or cocaine category also includes other opiates including morphine, codeine, and opium.
↵31. I do not use the County-Level Detailed Arrest and Offense data because of issues in the imputation process used to fill in missing data. These issues are described in detail in Maltz and Targonski (2002) and summarized at https://www.openicpsr.org/openicpsr/project/108164/version/V4/view (accessed May 17, 2023). I exclude extreme outliers using the process described in Weisburst (2019).
↵32. These results are qualitatively very similar to what I show in Section V and are available upon request.
↵33. The colors represent randomly generated data; they are only included to help visually identify county and zip3 boundaries.
↵34. Data available here: https://www.huduser.gov/portal/datasets/usps_crosswalk.html#data (accessed May 17, 2023).
↵35. It is also possible to map from zip3s to counties. However, since counties are typically smaller than zip3s, mapping from county to zip3 is less reliant on the HUD crosswalks since many counties are nested within zip3s. In practice, this does not significantly affect the regression results.
↵36. This calculation assumes that employment and unemployment counts are distributed uniformly throughout each county, which likely introduces some measurement error.
↵37. Most surprisingly, the variation in opioid prescribing does not appear to be driven by underlying differences in patient pain across locations (https://www.aaaceus.com/courses/nl0116a/nl0116a_Article2.pdf, accessed May 17, 2023).
↵38. A typical hydrocodone prescription is one or two 5-milligram hydrocodone/325-milligram acetaminophen tablets every four to six hours as needed, with a maximum of eight pills per day (https://www.healthline.com /health/acetaminophen-hydrocodone-oral-tablet, accessed May 17, 2017).
↵39. Note that this measure includes all hydrocodone use as opposed to just misuse. In contrast, the literature studying the effects of the OxyContin reformulation tends to focus on misuse. The reason for this difference is that the reformulation of OxyContin only affected individuals who were misusing the drug, whereas the rescheduling of HCPs affected both recreational users and legitimate pain patients.
↵40. I explore whether several different characteristics, such as population, racial composition, Hispanic origin, and age distribution differ by pre-period exposure to hydrocodone in Online Appendix Table A2. Columns 1–4 display summary statistics for each of these demographic variables broken down by quartile of
. Interestingly, none of these variables seem to vary systematically in relation to .↵41. Explicitly, I report the θ coefficient from the regression
↵42. Similar to hydrocodone, codeine is a Schedule II drug. However, certain combination products, such as codeine with acetaminophen, are classified as Schedule III.
↵43. Seago et al. (2016) report extremely large percentage increases in codeine prescriptions following the rescheduling using a sample of 14 pharmacies in Texas. In analysis not presented here (available upon request), I show that (i) these results are unique to Texas, and (ii) the quoted magnitude of the increase is driven mostly by much lower prescribing of codeine at baseline, which inflates the percentage change.
↵44. The hydrocodone coefficient is identical in both panels since a milligram of hydrocodone is equivalent to a milligram of morphine.
↵45. This pattern is demonstrated with the raw data in Panel A of Online Appendix Figure A7, where I plot the LFP rate broken down by the first and fourth quartiles of exposure to treatment.
↵46. The process for inferring the pre-period coefficients is described in Section III.A.
↵47. Panel B of Online Appendix Figure A7 shows an analogous plot using the raw data. The lines in this figure show the deviations from a linear trend fit separately for the first and fourth quartile of exposure to treatment.
↵48. This calculation attributes the entire aggregate drop in hydrocodone to the rescheduling, which likely overstates the magnitude of the effects. I conduct counterfactual simulations in Online Appendix Section A.1, which rely on a more conservative first stage.
↵49. In addition, a drop in population holding the number of people in the labor force constant would have the same effect. However, Column 1 of Online Appendix Table A3 shows that this is not the case.
↵50. Raw data plots of the EPR by quartile of exposure to treatment are shown in Panels C and D of Online Appendix Figure A7. Although the pre-trends in Panel C are not as obvious as Panel A, the detrended data in Panel D shows a very similar pattern as Panel B.
↵51. I present event studies examining the LFP and EPR using these data in Online Appendix Figure A9.
↵52. The ACS reports annual wage income, number of weeks worked, and ranges of “usual hours worked.” I assign each hours worked for each individual as the midpoint of their reported interval.
↵53. “Modern” PDMPs refer to PDMPs that are electronic and available to any authorized user.
↵54. In addition to these papers that rely on policy-induced variation in access to opioids, several other papers use other designs to estimate how opioid access affects the labor market. I’ve included brief descriptions of several of these papers in Online Appendix Table A4. This table highlights the differences in signs and magnitudes of estimates of the effects of opioids on the labor market.
↵55. As this outcome is only available annually, I normalize 2013, the last full year before the rescheduling, to zero.
↵56. While there is no evidence of a pre-trend, for completeness I also show the parametric results allowing for a linear pre-trend in Panel B. Not surprisingly, the results look very similar. I do not, however, find any reduction in the number of SSI beneficiaries. This is consistent with Park and Powell (2021).
↵57. This is computed using the more conservative strategy of clustering the standard errors at the state level.
↵58. It is unclear from the documentation whether the “other” category includes unspecified drug arrests.
↵59. In separate results not presented but available upon request, I find no change in antidepressant, antipsychotic, or benzodiazepine-related deaths.
↵60. This is meant as an illustrative example, not an actual policy recommendation.
- Received March 2020.
- Accepted July 2021.
References
This article requires a subscription to view the full text. If you have a subscription you may use the login form below to view the article. Access to this article can also be purchased.
Log in using your username and password
Purchase access
In this issue
Jump to section
Related Articles
Cited By...
- No citing articles found.