Delayed reward discounting, a measure of capacity to delay gratification, is moderately heritable, 12pct, and it tends to increase with age (changing importance of competing environment factors?)

Genomic Basis of Delayed Reward Discounting. Joshua C. Gray et al. Behavioural Processes, March 12 2019. https://doi.org/10.1016/j.beproc.2019.03.006

Highlights
• Delayed reward discounting (DRD) is a measure of capacity to delay gratification.
• DRD is moderately heritable and associated with mental, physical, and social outcomes.
• DRD is a component of Research Domain Criteria and a putative target for treatment.
• The largest GWAS to date yielded a SNP heritability of 12% and one significant SNP.
• Future priorities include GWAS with larger samples and non-European cohorts.

Abstract: Delayed reward discounting (DRD) is a behavioral economic measure of impulsivity, reflecting how rapidly a reward loses value based on its temporal distance. In humans, more impulsive DRD is associated with susceptibility to a number of psychiatric diseases (e.g., addiction, ADHD), health outcomes (e.g., obesity), and lifetime outcomes (e.g., educational attainment). Although the determinants of DRD are both genetic and environmental, this review focuses on its genetic basis. Both rodent studies using inbred strains and human twin studies indicate that DRD is moderately heritable, a conclusion that was further supported by a recent human genome-wide association study (GWAS) that used single nucleotide polymorphisms (SNP) to estimate heritability. The GWAS of DRD also identified genetic correlations with psychiatric diagnoses, health outcomes, and measures of cognitive performance. Future research priorities include rodent studies probing putative genetic mechanisms of DRD and human GWASs using larger samples and non-European cohorts. Continuing to characterize genomic influences on DRD has the potential to yield important biological insights with implications for a variety of medically and socially important outcomes.

Keywords: delayed reward discountingimpulsivitygeneticsgenomics


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1. Introduction
Thepreference for smaller immediate rewards relative to larger delayed rewards is abehavioral economic concept that reflects the capacity to delay gratification(Green et al., 1994). Delayed reward discounting (DRD) is used to measure how rapidly a reward loses its value based on its temporal distance.Thus, greater DRD reflectsa preference for smaller immediate rewardsrather than larger, delayed rewardsand is one form of impulsivity. Meta-analyses show consistent associations between greater DRD and adverse psychiatric outcomes includingsubstance usedisorders, gamblingdisorder, and attention-deficit/hyperactivity disorder (ADHD) (Amlung et al., 2016a; Jackson &MacKillop, 2016; MacKillop et al., 2011). In terms ofnon-psychiatric healthoutcomes, greater DRD is positively associated withobesity (Amlung et al., 2016b),and negatively associated withglycemic adherence in type 2 diabetes (Lebeau et al., 2016; Reach et al., 2011), obtaining preventative medical care(e.g., flu shots, breast and prostate exams; (Bradford, 2010)), and seatbelt use (Bradford et al., 2014). Finally, even afterattempting to control forparental income andcognitive ability, DRD is negatively associatedwithlifetime outcomes including educational attainment, income, and employment (Golsteyn et al., 2014). Individualswith high DRDappear to be less thoughtful of their future selves, which leads to increased risks for a multitude of deleterious mental, physical, and social outcomes.As such, DRD has been proposed as a target for treatment (Gray &MacKillop, 2015; Lowe et al., 2018; Sheffer et al., 2018)and is one component of theResearch Domain Criteria (RDoC) (Lempert et al., 2018), a National Institute of Mental Health (NIMH) initiative that emphasizes basic dimensions of functioning that span the full range of human behavior from normal to abnormal.Thismini-review will highlight current research relating to the genetic basis of DRD, including data from animal models. We begin with a summary of DRD measurement in humans and nonhuman animals, followed by a review offindings fromheritability and genome-wide association studies (GWASs).We conclude our review by identifying promising future research directions. We will not review the many candidate gene studies that have been conducted on this topic, in part because of the consistent difficulty in replicating candidate loci for complex traits (Chabris et al., 2012; Farrell et al., 2015; Hart et al., 2013), and because candidate genes for DRD have been summarized in two of our recent publications (MacKillop et al., 2019; Sanchez-Roige et al., 2018). Like all psychological traits,DRDis influenced by environmental and genetic factors and presumably also their many interactions. With regard to environmental influences, research indicates that child maltreatment (Oshri et al., 2018a, 2018b), trauma (van den Berk-Clark et al., 2018), and substance use (Mendez et al., 2010; Mitchell etal., 2014; Setlow et al., 2009; Simon et al., 2007)appear to increase levels of DRD. While no-well powered studies have investigated gene-by-environment interactionsrelevant to DRD, it is likely that certain environmental exposures modulate DRDin a genotype-specific manner. Thus, while this mini-review is focused on the genetic basis of DRD, research seeking to understand environmental and gene-by-environment interactions also represent important linesof inquiry.2. Delayed Reward DiscountingMeasurementDRDis typicallyassessed by providing organisms with a choice betweensmaller immediate and larger delayed rewards. In humans, these rewards are usually choices between smaller amounts ofmoneytoday versus larger amounts of money after a delay, though food and drugs have been in place of money(Green and Lawyer, 2014; Odum and Rainaud, 2003; Robertson and Rasmussen, 2018). For example, one of the most widely-used measures, theMonetary Choice Questionnaire (MCQ), consists of 27 questions such as“Would you rather have $24 today or $35 in 29 days?”(Gray et al., 2016; Kirby et al., 1999). Althoughthe rewards are typically hypothetical rather than real, this does not appear to impact responding (Madden et al., 2003; Matusiewicz et al., 2013; Robertson &Rasmussen, 2018). Inanimals such as pigeons androdents, DRD is typicallyassessedusing delayed food or water rewardsand the animals always receive the rewards associated with their choice(Isles et al., 2004; Mazur, 1987; Mitchell, 2014; Richards et al., 2013). In both humans and non-human species, organisms typically devalue delayed rewards in a nonlinear fashion, modeled as ahyperbolicfunction (Vanderveldt et al., 2016). The extent ofDRDcan be quantified in several ways(Myerson et al., 2014),such ascalculatingthe slope of the hyperbolic discounting function (k)ormodel-free methods such asarea under the curveand immediatechoice ratio(Green &Myerson, 2004; Myerson et al., 2001). Figure 1 shows two prototypic hyperbolic demand curvesin humans with differing slopes(more impulsive k= .1, less impulsive k= .01)thatexhibit the discounted subjective value of $100 delayed from 1 day to 1 year. For example, at60 days, $100 is equal in subjective value to $62 today for the less impulsive profileand $14 todayfor the more impulsive profile.Although there are many parallels between the DRD models used with humans and laboratory animals, there are also several notable differences that may affect generalizability across species(for an in depth discussion see Vanderveldt et al., 2016). First, in humans there is a well-documented magnitude effect, whereby humansdiscount small, delayed rewards more steeply than larger delayed rewards. This effect has been shown across reward types including money (Johnson and Bickel, 2002; Madden et al., 2003), food (Odum et al., 2006), and liquid rewards (Jimura et al., 2009). However, the magnitudeeffect has not been consistently observed in nonhuman animals (e.g., Green et al., 2004; Richards et al., 1997). Second, the time frame of the procedures, and presumably the time frame for self-control, differs in humans and laboratory animals. In the animal procedures the delays are in seconds or minutes whereas in most humanprocedures the delays are days to months. Moreover, in the animal procedures,the delays are experienced directly and relate to their immediate thirst or hunger, whereas in humans the delays are communicated by instructionsand typically involve a secondary reinforcer (money) (de Wit et al., 2018). Nonetheless, both humans and laboratory animalsdiscount delayed rewardsin an orderly manner, suggesting a fundamental behavioral homology.3. HeritabilityTheheritability of DRD has been examined in both humans and rodents. In humans, studies with monozygotic and dizygotic adolescent twins provide evidence ofrobust heritability, whichtends to increase through development (i.e. 12 years old (yo) [30%] and 14 yo [51%], (Anokhin et al., 2011); 16 yo [35-46%], 17 yo [47-51%], and 18 yo [55-62%] (Anokhin et al., 2015; Isen et al., 2014; Sparks et al., 2014)). The increase ingenetic influence on DRD throughout developmentmay reflect the changing importance of competing environmental factors and the maturation of the prefrontal cortex in adolescence (Argyriou et al., 2018), a critical region for DRD (Wesley &Bickel, 2014). In mice and rats, a significant proportion ofthe variance in DRD can be attributed tobetween-strain versus within-strain differences(16-50%), which is analogous to the twin model design (Anderson &Woolverton, 2005; Isles et al., 2004; Madden et al., 2008; Richards et al., 1997; Stein et al., 2012; Wilhelm and Mitchell, 2009).The lowest estimate (16%) came from the only study with mice conducted to date (Isles et al., 2004), whereas estimates of heritability in ratsweremuchhigher (40-50%) (Richards et al., 2013; Wilhelm and Mitchell, 2009). However,comparisons across strains of rodents have some limitations.First, strainsweresometimes obtainedfrom different vendors and thus genotype and the different environment of each vendor facility are confounded. Second, studies vary with regard totraining procedure, type of reinforcer (e.g., condensed milk, water), delay range (e.g., 8 vs. 16 seconds maximum delay), number of sessions,and dependent variable (e.g., ratio of delayed choices, AUC, k).On balance, findings from both humans and rodents suggest that DRD is a moderately heritable trait, although the variability in estimates suggests significantmoderators of its heritability. 4. Genome-wide Association StudiesAGWAS is a study of a set of genetic variants sampled across the whole genome to identify polymorphismsassociated with a trait (Visscher et al., 2017). The primary goal of GWAS is to better understand the biology of the trait. Because millions of variants are tested, a stringent significance testing threshold must be employed. It is generally accepted that the significance threshold for any single polymorphism is p< 5 x 10-8. This threshold accounts foran estimated1 million independent tests,and variantsbeyond this threshold tend to replicate (McCarthy et al., 2008; Visscher et al., 2017).Over the past decade, it has become clear that for virtually all common traits, associations tend to be numerous small-effect variants spread across most of the genome, in or near genes that have no obvious biological connection to the trait (e.g., Boyle et al., 2017). Nonetheless, GWASsare thought to yield new insights into the biology of complex traits (Visscher et al., 2017)and ultimately facilitate the discovery ofnovel treatments (Cook et al., 2014; Nelson et al., 2015). To date, two GWASshave been conducted on DRD. Thefirst was conducted incollaboration with thegenetics company 23andMe, Inc., and included23,217 adults of European ancestry(Sanchez-Roige et al., 2018). This study foundsingle nucleotide polymorphism (SNP)-basedheritability of DRD of 12.2%.This SNP-basedheritability is lower than heritability estimates obtained using humantwinsand rodent inbred strains for a number of reasons, includingthat the SNP-basedheritability is an underestimation due to the absence of rare variants(Marouli et al., 2017; Yang et al., 2015),and that pedigreeestimates are inflated due tosharedenvironmental and non-additivegenetic effects (Polderman et al., 2015). In Sanchez-Roige et al., (2018), one SNP, rs6528024,which is located in an intron of the gene GPM6B(Neuronal Membrane Glycoprotein M6B), reached genome-wide significance (p=2.40 × 10-8). This association was supported by an independent cohort of 928 participants(meta-analysis p= 1.44 × 10-8). GPM6Bencodes a protein thatisinvolvedin the internalization of the serotonin transporter and has been implicated in prepulse inhibition and altered response to the 5-HT2A/C agonist DOI in mice (Dere et al., 2015; Fjorback et al., 2009).A large body of research has explored the relationship between serotonergic functioning and DRD; the findings are inconsistent and have primarily relied on rodentmodels. For example, there is some evidence thatserotonin may be more related to increasedconfidence in reward delivery thanto increasedcapacity to wait for a delayed reward (Dalley and Ersche, 2019; Miyazaki et al., 2018). In humans, GPM6Bexpression is downregulated in the brains of depressed suicide victims (Fuchsova et al., 2015)and DRD has been linked to suicide attempts with a pooled odds ratio = 3.14 (95%confidence interval: 1.48-6.67)(Liu et al., 2017). The link between DRD and suicidalityis further supported by genetic correlations identified in the study bySanchez-Roige et al (2018), which foundpositive genetic correlations between DRD and major depression andneuroticismas well as smoking behaviors, ADHD, BMI, and negative associations with years of education and childhood IQ. Thesecond DRD GWASused a sample of986 healthy young adults of European ancestry (MacKillop et al., 2019). That study identifieda genome-wide significant variant (p=2.8x 10-8), rs13395777, on chromosome 2, anassociation that was not observed in the 23andMe cohort(p = .45).There are twomostlikely explanations for this failure to replicate. The finding may have been a false positive, which would explain why it was not detected in a cohort that was ~25x larger. Alternatively,the smaller study was comprised of young adultsand required low levels of substance use, whereas the larger study includeda wider age range, resulting in substantially higher mean age and income,and allowed for psychopathology.5. Future DirectionsDRDis a moderately heritable phenotype that is both phenotypically and genetically associated with an array of negative psychological, cognitive,and health outcomes. The largest GWAS to dateidentified asinglelocus that was associated with DRDand showed that genetic predisposition to high DRD is positively genetically correlated with many of the negative outcomes that have been previously associated with higher DRD. Future studies will be required to further define the geneticbasis of DRD. We are currentlyusing rodents with mutations in GPM6Bto examine DRD and related behavioral traits.We are also continuing to increase the sample size for future GWASsof DRD, which may allow us to identify additional loci (Marouli et al., 2017; Visscher et al., 2017). Another future direction may beto studydiverse ancestral groups,expanding current data from individuals ofEuropean ancestry(Duncan et al., 2018; Locke et al., 2015). Additionally, it will be important to further parse causality betweenDRD and associated outcomes (e.g., addiction, years of education) using methods such as longitudinal designsand Mendelian randomization (Burgesset al., 2015; Grant and Chamberlain, 2014). Finally, DRD is only one element of impulsivity, which is a broader construct that appears to comprise three broad and generally independent domains(MacKillop et al., 2016). Thus, understanding the genetics of impulsivity will also require exploration of othermeasures of impulsivity (e.g., response inhibitionand impulsive personality traits;Gray et al., 2018; Sanchez-Roige et al., 2019; Weafer et al., 2017).

6.  . ConclusionDRDis a heritable trait that can be assessedquickly and reliably both in person and over the internet (Koffarnus &Bickel, 2014; Sanchez-Roige et al., 2018; MacKillop et al., 2018), and influences a variety of health-related outcomes. Although at an early stage, GWASshave begun to identify loci and genes that influence variability in DRD, setting the stage for a deeper understanding of itsmolecular, cellular and circuit-level bases,and perhaps ultimately informing the treatment of psychiatric disorders and other conditions to which it confers risk.

Disclaimer: The opinions and assertions expressed herein are those of the authors and do not necessarily reflect the official policy or position of the Uniformed Services University or the Department of Defense.

From 2018... There is attraction among those with psychopathic personality traits; that relative attraction & observed homophily may be avenues thru which those traits persist in the population

From 2018... Do psychopathic birds of a feather flock together? Psychopathic personality traits and romantic preferences. Ashley L. Watts, Jessica C. Rohr, Katherine L. McCauley, Sarah Francis Smith, Kristin Landfield Howe, Scott O. Lilienfeld. Journal of Personality, April 16 2018. https://doi.org/10.1111/jopy.12394

Abstract
Objective: The goal of the present studies was to investigate whether people are especially attracted to psychopathic traits, and whether there are individual differences in such attraction.


Method: Female undergraduates (N = 270; Mage = 19; 57% White, 20% Asian, 8% Black) and female and male community members (N = 426; Mage = 37; 56% female; 81% Caucasian, 10% African American, 4% Asian) reported on their own personality and constructed their ideal mate for a dating, short‐term, and long‐term relationship from a list of 70 characteristics drawn from well‐validated criteria for psychopathic personality and diagnostic criteria for DSM‐5 personality disorders (PDs).


Results: Across both studies, absolute romantic preferences for psychopathic traits collapsed across time point were low on average, but higher than those for most all other PDs. In addition, they were higher for Factor 1 (i.e., interpersonal/affective) as opposed to Factor 2 (i.e., impulsive, antisocial) psychopathy traits. Participants with marked PD features, including Factor 2 psychopathy traits, were more inclined than others to endorse a preference for psychopathic males.


Conclusions: Relative attraction to psychopathic males and observed homophily may be avenues through which psychopathic traits persist in the population across time.

A growing body of empirical work shows that social recognition of individuals' behavior can meaningfully influence individuals’ choices; the authors find that it doesn't do it efficiently

The Deadweight Loss of Social Recognition. Luigi Butera, Robert Metcalfe, William Morrison, Dmitry Taubinsky. NBER Working Paper No. 25637, March 2019. https://www.nber.org/papers/w25637

　

Abstract: A growing body of empirical work shows that social recognition of individuals' behavior can meaningfully influence individuals’ choices. This paper studies whether social recognition is a socially efficient lever for influencing individuals’ choices. Because social recognition generates utility from esteem to some but disutility from shame to others, it can be either positive-sum, zero-sum, or negative-sum. This depends on whether the social recognition utility function is convex, linear, or concave, respectively. We develop a new revealed preferences methodology to investigate this question, which we deploy in a field experiment on promoting attendance to the YMCA of the Triangle Area. We find that social recognition increases YMCA attendance by 17-23% over a one-month period in our experiment, and our estimated structural models predict that it would increase attendance by 19-23% if it were applied to the whole YMCA of the Triangle Area population. However, we find that the social recognition utility function is significantly concave and thus generates deadweight loss. If our social recognition intervention were applied to the whole YMCA of the Triangle Area population, we estimate that it would generate deadweight loss of $1.23-$2.15 per dollar of behaviorally-equivalent financial incentives.

A growing body of empirical work shows that social recognition of individuals' behavior can meaningfully influence individuals’ choices; the authors find that it doesn't do it efficiently

The Happiness-Energy Paradox: Energy Use is Unrelated to Subjective Well-Being

The Happiness-Energy Paradox: Energy Use is Unrelated to Subjective Well-Being. Adam Okulicz-Kozaryn, Micah Altman. Applied Research in Quality of Life, Mar 12 2019, https://link.springer.com/article/10.1007/s11482-019-09719-y


Abstract: Earth’s per capita energy use continues to grow, despite technological advances and widespread calls for reduction in energy consumption. The negative environmental consequences are well known: resource depletion, pollution, and global warming. However many remain reluctant to cut energy consumption because of the widespread, although, implicit, belief that a nation’s well being depends on its energy consumption. This article systematically examines the evidential support for the relationship between energy use and subjective well-being at the societal level, by integrating data from multiple sources, collected at multiple levels of government, and spanning four decades. This analysis reveals, surprisingly, that the most common measure of subjective well-being, life satisfaction, is unrelated to energy use -- whether measured at the national, state or county level. The nil relationship between happiness and energy use is reminiscent of the well-known Easterlin Paradox, however the causal mechanisms responsible to each remain in question. We discuss the possible causes for the Happiness-Energy paradox and potential policy implications.


Keywords: Energy use Energy consumption Energy intensity of economy Sustainability Happiness Life satisfaction Subjective well-being (SWB)

Prescription opioids can account for 44 pct of the realized national decrease in men's labor force participation 2001-15; a short-term unemployment shock did not increase the share of people abusing them

Opioids and the Labor Market. Dionissi Aliprantis, Kyle Fee, Mark E. Schweitzer. Federal Reserve Bank of Cleveland, Mar 1 2019. WP 18-07R. https://www.clevelandfed.org/newsroom-and-events/publications/working-papers/2019-working-papers/wp-1807r-opioids-and-labor-market

Abstract: This paper studies the relationship between local opioid prescription rates and labor market outcomes. We improve the joint measurement of labor market outcomes and prescription rates in the rural areas where nearly 30 percent of the US population lives. We find that increasing the local prescription rate by 10 percent decreases the prime-age employment rate by 0.50 percentage points for men and 0.17 percentage points for women. This effect is larger for white men with less than a BA (0.70 percentage points) and largest for minority men with less than a BA (1.01 percentage points). Geography is an obstacle to giving a causal interpretation to these results, especially since they were estimated in the midst of a large recession and recovery that generated considerable cross-sectional variation in local economic performance. We show that our results are not sensitive to most approaches to controlling for places experiencing either contemporaneous labor market shocks or persistently weak labor market conditions. We also present evidence on reverse causality, finding that a short-term unemployment shock did not increase the share of people abusing prescription opioids. Our estimates imply that prescription opioids can account for 44 percent of the realized national decrease in men's labor force participation between 2001 and 2015.

　

JEL Classification Codes: I10, J22, J28, R12.

Keywords: Opioid Prescription Rate, Labor Force Participation, Great Recession, Opioid Abuse




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1 Introduction

In her July 2017 Senate testimony, Federal Reserve Chair Yellen stated that she thought the

opioid crisis is “related to the decline in labor force participation among prime age workers” (Yellen

(2017), p 22).1 But as Yellen acknowledged in her testimony, it is challenging to determine whether

the opioid crisis has causal impacts on labor markets or whether it is more a symptom of weak

labor markets.

Although the amount of pain Americans reported did not increase from 1999 to 2010, the

amount of legally sold opioids nearly quadrupled during this period (Ossiander (2014)), so that by

2013 enough opioid prescriptions were written for every American adult to have their own bottle of

pills (CDC (2017)). In addition to the general rise in opioid prescriptions, prescription rates also

vary widely across geography and physician training (Currie and Schnell (2018)).

Krueger (2017) exploits the geographic variation in opioid prescriptions to show that areas

with high prescription rates have lower labor force participation rates for prime-age adults. While

Krueger acknowledges that his results are preliminary and that the direction of causality is dif-

ficult to determine, these results reveal substantial patterns that warrant further examination.

Harris et al. (2017) examine labor market effects of opioid prescriptions but are limited to a panel

of 10 large states over the period 2010 to 2015. They find large negative effects of opioid prescrip-

tions on participation and employment rates. Currie et al. (2018) examine the connections between

prescriptions and the employment rate and find that higher numbers of opioid prescriptions are

associated with a higher employment rate for women and a statistically significant increase in men’s

employment rate.

Alternatively, researchers have studied whether changes in the labor market could be driving the

opioid crisis, motivated by the long-term decline in participation (Abraham and Kearney (2018)).

Short-term fluctuations in local economic conditions have been tied to increased opioid deaths

(Hollingsworth et al. (2017)), and one prominent hypothesis holds that over the long term, declining

labor market prospects lead to “deaths of despair” (Case and Deaton (2015)). Deaths from suicides

and drug overdoses could lead to a steepening education-mortality gradient.2 Currie et al. (2018)

also examine the effects of economic conditions on opioid prescriptions although their results are

more ambiguous on this question. Ruhm (2018) examines the risk of drug deaths over time and

population subgroups and finds that overdoses respond to the drug environment as characterized

in terms of the availability and cost of drugs.

This paper focuses on two aspects of the relationship between opioids and the labor market.

We first use the panel variation in opioid prescription rates in narrowly defined geographies across

1Drug overdose has become the leading cause of death for Americans under 50 years old (Katz (2017)), with the

increase since 2010 due to opioids like heroin, OxyContin, and fentanyl. According to the National Institute on Drug

Abuse (NIDA), “Opioids are a class of drugs that include the illegal drug heroin, synthetic opioids such as fentanyl,

and pain relievers available legally by prescription, such as oxycodone (OxyContin), hydrocodone (Vicodin), codeine,

morphine, and many others.” Quinones (2016) provides a timeline of the crisis.

2Measuring the relationship between mortality and age (Auerback and Gelman (2016)) or education

(Goldring et al. (2016), Bound et al. (2015)) is surprisingly difficult.

2

the United States to identify the effect of the legal opioid supply on labor force participation. A

contribution of our analysis is improved measurement of both prescriptions and labor market status

for both rural and metropolitan areas through the use of Public Use Microdata Areas (PUMAs).

Over the time period we analyze, about one-third of the US population lived in an area where

the specific county is not identified the American Community Surveys (ACS), generally due to not

meeting a minimum population threshold. Using consistently defined geographic areas of adjoining

counties, we are able to examine within-state variation in outcomes and treatments for the US

population.

We find that individuals in geographic areas with higher opioid prescription rates are less likely

to participate in the labor force and have lower employment rates when standard demographic

factors are accounted for. To be specific, our baseline estimates associate a 4.6* percentage point

reduction in labor force participation for prime-age men in a high prescription area (90th percentile)

relative to those living in a low prescription area (10th percentile). Women’s participation rates

are also also lower in high prescription areas: There is a 1.4 percentage point difference between

90th and 10th percentile areas. This general relationship of lower participation in areas with higher

historical prescription rates remains after panel data controls, including a full set of geographic

fixed effects, as well as a variable controlling for local labor market conditions in 2000, a year

largely predating the growth of opioid prescriptions. The measured impacts are largest for men

with a high school diploma or less, where the effects are 7.4 percentage points for whites and 9.7

percentage points among non-whites. The estimated effects are large and robust across a number

of alternative specifications.

Another contribution of this paper is an investigation into the role of reverse causality in gener-

ating these results, using the Great Recession (GR) as an instrument to identify the effect of weak

labor demand on opioid use. The massive increase in nonemployed individuals caused by the GR,

along with the relative stability of the opioid market between 2004 and 2010, provides a scenario in

which the direction of causality can be clearly determined.3 We find that the share of individuals

abusing opioids did not increase due to the GR, and we show that these results are not driven by

heterogeneous effects across different observed characteristics. The evidence on the frequency of

abuse is more ambiguous since observed increases could be the continuation of a pre-trend.

We interpret our results as evidence that the supply of opioid prescriptions is a more important

driver of the opioid crisis than economic misfortune (Ruhm (2018)). Our results on the relationship

between the legal opioid supply and individual-level labor force participation outcomes contribute

to the stock and nuance of evidence on the effects of opioids on the labor market (Krueger (2017),

Harris et al. (2017)). And while the stability of opioid abuse rates in response to the GR is not a

direct test of the “deaths of despair” hypothesis, which pertains to long-term conditions, the lack

of response to such a large labor market shock suggests that the main contributors to “deaths of

3We provide evidence on the stability of the opioid market in terms of the price of heroin, the self-reported avail-

ability of heroin, and legal prescription rates. There were important changes in the legal opioid market (Evans et al.

(2018), Alpert et al. (2017)) at the very end of this time period and in the illegal opioid market just after this time

period (Ciccarone (2017)).

3

despair” would need to be found outside the labor market.4

The remainder of the paper is organized as follows: Section 2 investigates how the supply of legal

opioids affects labor force participation. Section 2.1 describes the individual-level data used in the

analysis, and discusses our empirical specification and identification strategy, with 2.2 presenting

our results. Section 3 investigates the possibility of reverse causality by studying whether weak

labor demand has an effect on opioid abuse. Section 3.3 describes the individual-level data used in

the analysis, with 3.4 discussing our empirical specification and presenting our results. Section 4

concludes.

2 Does Opioid Availability Affect Labor Supply?

2.1 Data on Labor Force Participation and Prescription Rates

We measure the labor market status of individuals using the Integrated Public Use Microdata

Series (IPUMS-USA) 1% sample of the American Community Survey (ACS) from 2006 to 2016.

In this data source, the county of the individual observations are not identified in all cases, with

counties typically being non-identified due to having a population level below a threshold. In those

cases the identified geographic unit is a Public Use Microdata Area (PUMA), which have population

over 100,000. About one third of the US population lived in a non-identi?ed county in our sample

period, shown in the purple areas in Figure 1.

County level observation

Constant Puma observation

Figure 1: Geographic Areas

Note: Identified counties between 2006 and 2016 are shown in tan, and non-identified counties (aggregated into CPUMAs) are

shown in purple.

PUMAs have the desirable characteristics that they generally aggregate adjoining counties that

4The distinction between short-term and long-term is important because the “deaths of despair” hypothesis has

been formulated in terms of a failure of spiritual and social life in the US (Bellini (2018), 2:20), and not in terms of

short-term unemployment shocks (Bellini (2018), 3:40). One potential measure of long-term trends would be wage

growth (Betz and Jones (2017), Schweitzer (2017)).

4

can matched to county-level data sources. Unfortunately, PUMA boundaries change during our

sample period, so we actually use the IPUMS-provided consistent-PUMA (CPUMA) geography,

which “is an aggregation of one or more 2010 US Census PUMAs that, in combination, align closely

with a corresponding set of 2000 PUMAs” (Schroeder and Riper (2016)). In a small number of

cases where CPUMA boundaries cross county lines we have to be further aggregate to identified

consistent areas in both individual-level data and prescription rates.

To clarify the relationship between counties and CPUMAs Figure 2 show maps for two example

using the state of Nebraska and Franklin County Ohio (home of Columbus and the most populous

county in Ohio). In Nebraska, sets of adjoining counties are aggregated into 7 CPUMAs while two

counties are directly identified. Whereas Franklin County includes several CPUMAs, we use the

county as our unit of observation because prescription data is only available down to the county

level.

(a) NE Counties (b) NE PUMAs

(c) Franklin County (d) Franklin County PUMAs

Figure 2: Nebraska and Franklin County, Ohio

We use the Centers for Disease Control and Prevention’s (CDC’s) annual county-level data on

prescription rates from 2006 to 2016 to assign prescription rates to our geographic areas. The

population-weighted average of counties is used when the geographic area is a CPUMA formed

by adding multiple counties together. The CDC notes that prescription opioid dataset is “based

on a sample of approximately 59,000 retail (non-hospital) pharmacies, which dispense nearly 88%

of all retail prescriptions in the US” and “covers 87% of all counties.” According to the CDC, a

prescription is considered “an initial or retail prescription dispensed at a retail pharmacy in the

sample, and paid for by commercial insurance, Medicaid, Medicare, or cash or its equivalent.”

5

In cases where prescription data in a county is not available, which are all smaller counties, the

CPUMA is assigned the average prescription rate of the observed counties within the CPUMA.

Figure 3 shows these data for 2010.

Perscriptions per 100 people, 2010

1st quintile (<67.2)

2nd quintile (67.3-81.6)

3rd quintile (81.7-95.6)

4th quintile (95.7-118.9)

5th quintile (>119)

Figure 3: Prescription Rates by Geographic Areas

Ideally, one would also want information on the strength and duration of each prescription,

however, county-level data on the total milligrams of morphine equivalent (MME) prescribed, rather

than the number of prescriptions, is publicly available only for the year 2015. The correlation

coefficient between a county’s number of prescriptions per person and their MME prescribed is

0.91 in 2015. Further reassuring us about the appropriateness of county-level prescription counts,

the time pattern of national MME quantities are very similar to the time pattern of our average

prescription counts between 2006 and 2016 (FDA (2018)).

2.2 Model and Empirical Specification

Our approach to measuring the labor market effects of prescription opioids follows Krueger

(2017), but our data will allow annual frequency regressions on a broader set of geographic units.

Given the complexity of possible causal relationships between labor market status and opioids, we

begin with a Directed Acyclic Graph (DAG) to highlight the specific identification strategy that

we will use. This approach will also highlight possible robustness tests. Figure 4 shows a DAG of

our assumed model for this problem.

6

R ≡ Region

I ≡ Illegal Opioid Supply

P ≡ Prescription Opioid Supply

X ≡ Individual Characteristics

L ≡ Labor Market Conditions

O ≡ Opioid Abuse

Y ≡ Labor Force Participation

bc I

bP

b

R

bc

O

b

L

bX

b

Y

Figure 4: Directed Acyclic Graph of Opioids Affecting Labor Force Participation

Note: This Figure follows the convention from Pearl (2009) of communicating that a variable is observed by drawing a solid

line to its descendants, and communicating that a variable is unobserved by drawing a dashed line to its descendants.

We model labor market outcomes such as labor force participation, Y , as a function of over-

all labor market conditions, L, opioid abuse, O, and individual characteristics, X, such as age,

education, race, marital status, and gender, so that Yt = f(Lt,Ot,X).

We do not observe the specific relationship between opioid abuse, O, and labor force participa-

tion Y . However, opioid abuse, O, is expected to respond to the supply from both prescription, P,

and illegal sources, I. Observing P and Y allow this path to be identified, but I would have the

potential to affect opioid supplies and therefore individuals’ labor force status.5 In addition, any

factors which might alter use given the supply would make the identification imperfect.

Labor supply may also depend on economic conditions nationally and particular to the indi-

vidual’s region R. These factors will require controls in order for the relationship between opioid

supply and labor force outcomes to be revealed. However, the fact that opioid prescriptions P are

going to vary only by location means that there could be a tradeoff between the specificity of the

controls for national and local economic conditions, L, and the strength of the observed relationship

between P and Y . At the limit, geographic controls that flexibly vary by time period would make

any relationship impossible to identify.

Following the model in our DAG and the approach of Krueger (2017), the primary equation is

a linear probability model on an individual i’s labor force status based on a combination of their

individual characteristics, time effects indexed by t, and spatial effects indexed by j, along with

the average number of opioid prescriptions in their geographic area in the prior year:

Yijt = αPjt−1 + X′

iβ + L′

jγ + δt + ǫit. (1)

The linear probability model summarizes the individual responses into area labor market aver-

ages with demographic controls. The results are reliably away from zero and one, making a linear

probability model a reasonable approach. The lagged prescription rate serves to keep the timing

focused on impacts of opioids on labor market outcomes, although the strong correlation between

prescriptions from one year to the next makes treating the relationship as causal problematic.

While we focus on prime-age labor force participation, we also consider employment and un-

5Some of the influence of the diversion of legal prescriptions to the illegal market will be captured through P.

7

employment probabilities. We include age and age squared, education level dummy variables, race

dummy variables, and marital status for individual characteristics and run all regressions sepa-

rately for men and women, given prior evidence of differential impacts. Our baseline approach to

the geographic patterns is a set of census division dummies and the manufacturing employment

share in the geographic area. These controls should pick up some of the underlying variation in

labor market status that is not explained by variation in individual characteristics. Finally, we

include a time dummy for each year, so that important national events like the Great Recession

are absorbed.

Krueger (2017) runs a regression based on two periods of 3-year pooled Current Population Sur-

vey (CPS) data (1999-2001 and 2014-2016) and county-level data from 2015 on opioid prescription

rates converted to MME. The regression in Krueger (2017) is run on a set of largely metropolitan

counties that are identified in the CPS and state-level averages for the non-identified counties.

While our specification conceptually parallels Krueger (2017), instead of a largely cross-sectional

regression, we have annual, county-level data on prescriptions from the CDC spanning the period

from 2006 to 2016. In addition, we are able to break many rural areas into sets of adjoining counties

within states in the ACS. These features enable us to run panel regressions on individuals’ labor

force status from 2007 to 2016 with CDC data on average prescriptions per person in 648 geographic

units, composed of identified counties and CPUMAs.

Given the importance of some rural areas in the opioid crisis and substantial variation over time

and location in prescription rates, we believe that our approach should yield better estimates of the

effects of opioid prescription rates on labor force outcomes across the nation. However, drawing

from the ACS weakens the link to published labor force statistics that are drawn from the CPS,

and our prescription data are less specific about the effective quantities of opioids prescribed, as

noted in Section 2.1.

2.3 Estimation Results

Prime-age individuals (ages 24 to 54) can be sorted into three distinct labor market statuses: out

of the labor force, employed, or unemployed. Running population-weighted linear probability mod-

els on states produces estimates of the labor force participation rate, the employment-to-population

ratio, and the unemployment rate for areas and the marginal impacts of the regressors on these

rates. Table 1 shows the results of these regressions for prime-age men and women. In the case of

both prime-age men and women, the number of opioid prescriptions in their geographic area in the

prior year is associated with a lower probability of labor force participation and a lower employ-

ment rate with a high level of statistical significance. Because the underlying prescriptions data

are available only for the identified geography, we use robust standard errors, which are clustered

by geographic areas. Consistent with the anecdotal evidence and Krueger (2017)’s estimates, the

effects are substantially larger among men than among women (-0.046 versus -0.014 for labor force

participation). For the fraction of the population that is unemployed, the coefficients on the lagged

opioid prescription rate are an order of magnitude smaller and not statistically significantly affected

8

for prime-age women. The results for the employment-to-population ratio and labor force partic-

ipation are quite similar to each other for both men and women, which implies that the primary

effect that opioid prescription levels have appears to be on the individual’s decision to participate

in the labor market. Recognizing this pattern, we focus our attention on the participation rate

going forward.

Table 1: Labor Market States of Prime Age Men and Women

Men Men Men Women Women Women

Participate Emp/Pop Unem/Pop Participate Emp/Pop Unem/Pop

Lagged Prescrip. -0.046 -0.049 0.004 -0.014 -0.015 0.001

(0.006) (0.007) (0.002) (0.005) (0.005) (0.001)

Age 0.071 0.092 -0.021 0.082 0.085 -0.003

(0.013) (0.015) (0.008) (0.020) (0.020) (0.007)

Age2 -0.293 -0.357 0.064 -0.402 -0.406 0.004

(0.048) (0.055) (0.033) (0.076) (0.077) (0.028)

Age3 0.053 0.062 -0.009 0.084 0.084 -0.000

(0.008) (0.009) (0.006) (0.013) (0.013) (0.005)

Age4 -0.004 -0.004 0.000 -0.006 -0.006 -0.000

(0.000) (0.001) (0.000) (0.001) (0.001) (0.000)

Less than HS -0.200 -0.250 0.051 -0.325 -0.369 0.044

(0.006) (0.008) (0.002) (0.004) (0.005) (0.001)

High School -0.087 -0.126 0.038 -0.134 -0.166 0.031

(0.001) (0.002) (0.001) (0.003) (0.003) (0.001)

Some College -0.040 -0.059 0.020 -0.056 -0.075 0.019

(0.001) (0.001) (0.001) (0.002) (0.002) (0.001)

White 0.019 0.022 -0.003 0.025 0.031 -0.007

(0.002) (0.003) (0.001) (0.003) (0.004) (0.001)

Black -0.068 -0.098 0.029 0.048 0.022 0.026

(0.003) (0.004) (0.002) (0.005) (0.006) (0.002)

Hispanic 0.053 0.061 -0.008 0.012 0.008 0.004

(0.004) (0.005) (0.001) (0.003) (0.003) (0.001)

Married 0.116 0.153 -0.037 -0.080 -0.056 -0.023

(0.002) (0.002) (0.000) (0.003) (0.003) (0.000)

Manufact Share 0.225 0.268 -0.044 0.154 0.149 0.005

(0.050) (0.055) (0.018) (0.043) (0.049) (0.014)

constant 0.436 0.111 0.325 0.336 0.229 0.106

(0.133) (0.152) (0.079) (0.195) (0.197) (0.068)

R2 0.09 0.11 0.02 0.06 0.06 0.02

N 5,835,200 5,835,200 5,835,200 6,021,178 6,021,178 6,021,178

All regressions include year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

The individual controls are generally statistically significant and important individual deter-

9

minants of labor force status that could vary across geographic areas in important ways. Man-

ufacturing share is a reliable predictor of higher likelihood of participation, but declines in the

manufacturing share would reduce this effect similar to the results in Charles et al. (2018). While

not shown, the time dummies and the census division fixed effects are also generally statistically

significant. In the case of the participation rate, the time fixed effects reflect both the effects of the

recession and longer-term trend in participation rates. This treatment, while appropriate, absorbs

most of the aggregate decline in working-age participation.

Evaluating the scale of these coefficients on lagged prescription rates depends on the level

of variation that we see in prescription rates. As the first panel of Figure 5 shows, the difference

between the 10th and 90th percentile prescription rates is roughly 1 log point for most of the period

from 2006 to 2016. In contrast, the time variation in the median is from 4.28 athe beginning of the

period to a peak of 4.41 and back down to 4.19 in 2016. Given the widely varying prescriptions

rate by geography, these estimates suggest that opioids reduced participation rates by roughly 4.6

percentage points for prime-age men in high prescription rate geographies relative to geographies

with very low prescription rates. These are clearly large estimates even when compared to the

overall variation in labor force participation rates across geographic areas. The implications for

women are about a third the size of those for male populations, but a reduction in participation

rates of 1.4 percentage points for those in high-prescription rate areas relative to low-prescription

rate areas is still economically important to communities.

These results are similar to Krueger (2017) in the sign and in the pattern of generally stronger

effects for men than for women. Given Krueger (2017)’s strategy of estimating over two 3-year

periods, the most relevant comparison of his results to ours would be the sum of the “Log Opioids

per Capita” and “Log Opioids x Period 2” coefficients. Using Krueger (2017)’s column 6 regressions,

which are most similar to our regressions, his results indicate a somewhat smaller of log-point

increase MME of about -0.02 for prime-age men and -0.004 for prime-age women. This latter result

(for women) combines a positive impact on labor force participation in the early period with a -

0.014 effect of log opioids in the second period. Overall, our results look similar to Krueger (2017)’s

but with larger estimated effects.

Our results are also generally consistent with Harris et al. (2017) in that the effects are negative

and substantial for participation and employment rates, while positive but small for unemployment

rates. The sizes of Harris et al. (2017)’s effects are larger than our estimates at -0.057 for labor

force participation and -0.064 for employment rates, with the inclusion of county-level fixed effects.

There are a number of possible sources for the different results: Harris et al. (2017) use a county-

level panel, so the regressions are less flexible in accounting for demographic characteristics, the

regressions use contemporaneous opioid prescriptions, and the sample covers 10 states from 2010

to 2015.

Our results are not consistent with Currie et al. (2018). In their county-level panel they find

positive effects of county-level opioid prescription rates on the employment-to-population ratio, for

both men and women and for both the 18-44 and 45-64 age groups. They interpret those results

10

as indicating that opioids facilitate returning to or continuing to work. This is the opposite sign of

our results for the employment-to-population ratio for both prime-age men and women as shown

in Table 1. Currie et al. (2018) obtain this positive results in regressions both with and without

county fixed effects, so it does not seem to be a product of the level of regional controls, which we

find to be important to our results. In addition, while not shown, our results for more narrowly

defined groups are very similar to our main results, although the effects tend to smaller in younger

groups. We do not have access to Currie et al. (2018)’s instrument (opioid prescription rates for

older individuals), but the sign of the coefficients in Currie et al. (2018) are not impacted by the

use of the IV approach. At this point we are unclear what leads to this difference. There are still

other differences in Currie et al. (2018)’s analysis including: different data sources, very limited

demographic controls, the use of quarterly data, the use of a one period lag on opioid prescription

rates, and the aggregation of all counties below 100,000 population into state aggregates. We intend

to further investigate differences in the approaches in subsequent work.

Given the number of observations available in the ACS in each of the geographic units, it is

possible to explore the effects of opioid prescription rates on more narrowly defined subsamples

of the population. Given the influential results in Case and Deaton (2015) and Case and Deaton

(2017), we explore effects by education level and race. For our purposes we split the sample into

non-Hispanic whites (white) and minorities including hispanics (nonwhite). Table 2 shows results

for prime age men by race (white and nonwhite) and education level (high school graduation and

lower versus some college or higher). The coefficients on lagged log prescriptions rates continue to

be significantly negative for men, although there is substantial variation between education levels.

The coefficient for white prime-age males with an education level of high school or less is nearly

four times higher than the equivalent coefficient for white prime-age men with some college or

higher education. This result shows there are quite large effects for relatively disadvantaged white

men along the lines suggested in Case and Deaton (2015) and Case and Deaton (2017). It is worth

emphasizing that this effect is on top of the generally lower participation rate expected for this

group, which is accounted for in the other controls.

While Case and Deaton (2015)’s results focused attention on white households, our results are

just as troubling for nonwhite prime-age men. The coefficient for nonwhite men with a high school

degree or less is -0.097. Nonwhite men with come college or more also experience a larger likelihood

of being out of the labor market in higher opioid prescription areas than their white counterparts

(-0.041 versus -0.019). By our measures it is hard to argue that white prime-age men have been

more affected than minorities.

11

Table 2: Labor Force: Prime Age Men by Race and Education

White White Nonwhite Nonwhite

HS or less More than HS HS or less More than HS

Lagged Prescrip. -0.074∗∗∗ -0.019∗∗∗ -0.097∗∗∗ -0.041∗∗∗

(0.007) (0.003) (0.013) (0.005)

R2 0.07 0.03 0.11 0.04

N 2,053,403 2,418,539 735,239 628,019

All regressions include full set of controls with year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

Table 3 repeats this analysis for groups of prime-age women. For white women with some

college or more, there is no statistically significant coefficient on being in a higher or lower opioid

prescription county. Again, nonwhite women with and without post-high school educations have

statistically significantly lower participation rates in high opioid prescription areas. While most

of the coefficients on lagged log prescription rates continue to be statistically significant for key

demographic splits of prime-age women, the coefficients reported here are generally less than half

the magnitude of the coefficients for equivalent male populations. These patterns help to fill in

some of the nuances on the impacted populations that were not separately identifiable in Krueger

(2017).

Table 3: Labor Force: Prime Age Women by Race and Education

White White Nonwhite Nonwhite

HS or less More than HS HS or less More than HS

Lagged Prescrip. -0.038∗∗∗ 0.004 -0.028∗∗ -0.011∗∗

(0.009) (0.004) (0.008) (0.004)

R2 0.04 0.03 0.03 0.03

N 1,735,326 2,817,007 651,820 817,025

All regressions include full set of controls with year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

Overall, these results suggest an important regional pattern in labor force participation that is

reliably correlated with the frequencies of opioid prescriptions. The effects are also generally larger

for prime-age men with lower education levels regardless of race.

2.4 Weakening Our Identifying Assumptions

The key challenge illustrated in the DAG in Figure 4 is finding appropriate geographic controls

without entirely absorbing the geographic variation in the prescription data. In our preferred

12

specification, we chose to supplement individual controls with the manufacturing employment share

in the individual’s location, Census division fixed effects, and year fixed effects. The variation across

locations seen in prescriptions is a critical source of variation, but there may also be other important

reasons why local markets always have lower labor force participation, beyond the aggregated

individual characteristics and the manufacturing share of employment. We can use more detailed

geographic fixed effects to absorb these other factors, but these effects will also absorb the average

differences in prescription rates. Figure 5 shows the 10th and 90th percentiles of prescription rates

in the data (Panel 1) and after subtracting the mean levels of prescriptions in each geographic

area (Panel 2). This reduced amount of variation is likely to cause an understatement of the

implied effects of opioids, if opioid prescriptions do substantially lower participation for areas where

prescriptions have been steadily higher. To explore the robustness of our results to regional controls,

we examined increasing the level of controls up to the inclusion of fixed effects for all our geographic

units.

3.5 4 4.5 5

LN Prescriptions Per 100 People

2006 2008 2010 2012 2014 2016

Census year

10th Median

90th Mean

Full Variation

3.5 4 4.5 5

LN Prescriptions Per 100 People

2006 2008 2010 2012 2014 2016

Census year

10th Median

90th Mean

State Fixed Effect Removed

Variation in Prescriptions

Figure 5: Identifying Variation

Note: This figure shows the variation in the natural logarithm of prescription rates across our geographic areas (defined in

Section 2.1).

Our first effort to tighten the regional controls uses state fixed effects in the place of the Census

divisions. Table 4 shows these results. First, it is worth briefly noting that the coefficients on the

demographic factors are changed only negligibly. Being geographically determined, the coefficient

13

on manufacturing share in the geographic unit does fall for both men and women. The coefficients

on prescription rates also are altered by the inclusion of state fixed effects. For men, the magnitude

of the coefficients is essentially unchanged, going from -0.046 in the baseline regressions to -0.051,

which is still statistically significant. For women, the inclusion of state fixed effects reduces the

magnitude of the opioid prescription coefficient, so that the coefficient is no longer statistically

significant at the 95% level. When we examine the more impacted, lower-education demographic

groups, the effects continue to be statistically significant. The results for whites show slightly weaker

coefficients, while the estimated coefficients for low-education nonwhites rise. Overall, we conclude

that most of the results are generally robust to the inclusion of state-level regional controls.

14

Table 4: Prime Age Labor Force Regressions with State Fixed Effects

White Nonwhite White Nonwhite

Men Women Men Men Women Women

<=HS <=HS <=HS <=HS

Lagged Prescrip. -0.051 -0.008 -0.073 -0.125 -0.027 -0.036

(0.007) (0.004) (0.008) (0.016) (0.008) (0.009)

Age 0.071 0.081 -0.018 -0.091 -0.151 -0.154

(0.013) (0.020) (0.020) (0.037) (0.029) (0.050)

Age2 -0.293 -0.397 0.024 0.325 0.508 0.548

(0.048) (0.076) (0.077) (0.145) (0.114) (0.198)

Age3 0.053 0.083 0.003 -0.048 -0.068 -0.079

(0.008) (0.013) (0.013) (0.025) (0.019) (0.034)

Age4 -0.004 -0.006 -0.001 0.002 0.003 0.004

(0.000) (0.001) (0.001) (0.002) (0.001) (0.002)

Less than HS -0.199 -0.324 -0.100 -0.121 -0.205 -0.159

(0.006) (0.004) (0.006) (0.007) (0.004) (0.003)

High School -0.087 -0.135

(0.001) (0.003)

Some College -0.039 -0.056

(0.001) (0.002)

White 0.020 0.025

(0.002) (0.003)

Black -0.069 0.050 -0.100 0.021

(0.003) (0.005) (0.004) (0.006)

Hispanic 0.055 0.015 0.099 0.013

(0.003) (0.003) (0.006) (0.005)

Married 0.116 -0.080 0.155 0.170 -0.062 -0.042

(0.002) (0.003) (0.002) (0.005) (0.004) (0.007)

Manufact Share 0.207 0.205 0.308 -0.020 0.290 0.082

(0.055) (0.041) (0.062) (0.167) (0.057) (0.086)

constant 0.442 0.290 1.376 2.199 2.362 2.371

(0.134) (0.191) (0.193) (0.359) (0.277) (0.459)

R2 0.09 0.06 0.07 0.11 0.04 0.03

N 5,835,200 6,021,178 2,053,403 735,239 1,735,326 651,820

All regressions include year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

For our next step, we add participation rates based on the 2000 Census (2000 LFPR) to the

regression in addition to Census divisions and the manufacturing share. The idea is to use each

location’s relative labor market position prior to much of the growth in opioid prescriptions as a

control for the longer-term issues in regional labor markets. Of course, while far lower than today,

opioid prescriptions were nonzero in 2000, but we have no source for county-level prescriptions

prior to 2006. Table 5 shows these results. Not surprisingly the 2000 LFPR is a strongly significant

predictor of individual participation rates. Again, adding this regressor leaves the coefficients

on the demographic controls largely unchanged, but the coefficients on the manufacturing share

15

decline substantially and are often statistically insignificant at conventional significance levels.

The coefficients on lagged prescription rates are generally reduced in their absolute values, but

generally continue to be statistically significant with the notable exception of the coefficient in

the regression for all prime-age women. Focusing on the regressions for less-educated men, the

results continue to indicate substantial effects with moving from a low (10th percentile) to a high

(90th) prescription area, resulting in implied reductions of 5.7 percentage points and 7.9 percentage

points of participation among white and minority prime-age men, respectively. The results for low-

education white and nonwhite women, while smaller, are in no sense trivial, with predicted effects

of 2.3 percentage points and 1.8 percentage points, respectively. These results indicate that post-

2006 opioid prescription patterns are an important factor in the participation rates even for areas

of the United States with persistently weaker labor markets. While we would really like to have

a pre-opioid prescription labor force participation rate for all communities, this result limits the

potential scale of reverse causality being the primary source of the labor force participation patterns

that we see in the data for 2007 to 2016.

To complete the range of regional controls, we introduce fixed effects for each county or aggre-

gation of counties. Krueger (2017) includes this level of controls for one regression and identifies a

smaller but still significant relationship between prescription rates and participation rates. Table

6 shows the results with a full set of fixed effects. Not surprisingly, the coefficients of interest

are smaller, roughly a quarter to a third the size of the baseline coefficients, and less statistically

significant for several groups. Notably, all prime-age men in Table 2 had a coefficient of -0.046

but are at -0.011 and statistically significant at only the 95% level with a full set of geographic

fixed effects. Looking at the effects for workers with high school or lower educations, the effects

were quite large (-0.074 for white and -0.097 for nonwhite prime age men) in Table 2, but these

coefficients are at best a third the size (-0.022 and -0.018, respectively) and for nonwhite men with

a high school degree or less and the estimate is not statistically significant at the 95% level. This

indicates that an important amount of the identification of coefficients in Table 2 and 3’s estimates

relied on between geographic mean differences in prescription rates.

For women, the estimated results in this exercise are quite comparable to the estimates without

the full set of geographic fixed effects, although the estimates are less precise and, in the case of

nonwhite prime age women, no longer statistically significant at the 5% level. At least for women,

the estimates do not rely on between-geographic differences. That said, the importance of persistent

regional patterns in prescriptions still argues for a preferred specification that does not control for

regional differences quite as flexibly.

16

Table 5: Prime Age Labor Force Regressions with 2000 Control

White Nonwhite White Nonwhite

Men Women Men Men Women Women

<=HS <=HS <=HS <=HS

Lagged Prescrip. -0.031 -0.006 -0.057 -0.079 -0.023 -0.018

(0.005) (0.004) (0.006) (0.013) (0.007) (0.006)

2000 LFPR 0.003 0.002 0.004 0.006 0.003 0.003

(0.000) (0.000) (0.000) (0.001) (0.000) (0.001)

Age 0.070 0.081 -0.021 -0.087 -0.152 -0.150

(0.013) (0.020) (0.020) (0.036) (0.029) (0.049)

Age2 -0.290 -0.400 0.036 0.309 0.510 0.532

(0.048) (0.076) (0.077) (0.143) (0.113) (0.197)

Age3 0.053 0.084 0.001 -0.046 -0.068 -0.076

(0.008) (0.013) (0.013) (0.025) (0.019) (0.034)

Age4 -0.004 -0.006 -0.001 0.002 0.003 0.004

(0.000) (0.001) (0.001) (0.002) (0.001) (0.002)

Less than HS -0.194 -0.322 -0.099 -0.120 -0.206 -0.159

(0.006) (0.004) (0.006) (0.007) (0.004) (0.003)

High School -0.082 -0.132

(0.001) (0.003)

Some College -0.037 -0.054

(0.001) (0.002)

White 0.020 0.025

(0.002) (0.003)

Black -0.067 0.049 -0.094 0.023

(0.003) (0.005) (0.005) (0.006)

Hispanic 0.056 0.015 0.098 0.014

(0.003) (0.003) (0.006) (0.005)

Married 0.116 -0.080 0.155 0.168 -0.063 -0.043

(0.002) (0.003) (0.002) (0.005) (0.004) (0.007)

Manufact Share 0.085 0.081 0.103 -0.083 0.099 -0.152

(0.051) (0.041) (0.052) (0.161) (0.051) (0.088)

constant 0.172 0.193 1.102 1.603 2.188 2.105

(0.131) (0.192) (0.191) (0.366) (0.273) (0.457)

R2 0.09 0.06 0.07 0.12 0.04 0.03

N 5,835,200 6,021,178 2,053,403 735,239 1,735,326 651,820

All regressions include year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

17

Table 6: Prime Age Labor Force Regressions with a Full Set of Geographic Fixed Effects

White Nonwhite White Nonwhite

Men Women Men Men Women Women

<=HS <=HS <=HS <=HS

Lagged Prescrip. -0.011 -0.015 -0.022 -0.018 -0.029 -0.023

(0.004) (0.005) (0.007) (0.013) (0.009) (0.014)

Age 0.068 0.079 -0.020 -0.083 -0.156 -0.146

(0.013) (0.020) (0.020) (0.036) (0.029) (0.049)

Age2 -0.284 -0.391 0.035 0.296 0.528 0.513

(0.048) (0.076) (0.077) (0.144) (0.113) (0.196)

Age3 0.052 0.082 0.001 -0.044 -0.071 -0.073

(0.008) (0.013) (0.013) (0.025) (0.019) (0.034)

Age4 -0.004 -0.006 -0.001 0.002 0.003 0.003

(0.000) (0.001) (0.001) (0.002) (0.001) (0.002)

Less than HS -0.191 -0.322 -0.100 -0.116 -0.202 -0.158

(0.006) (0.004) (0.005) (0.007) (0.004) (0.003)

High School -0.079 -0.133

(0.001) (0.002)

Some College -0.035 -0.055

(0.001) (0.002)

White 0.024 0.024

(0.002) (0.003)

Black -0.069 0.051 -0.098 0.024

(0.003) (0.004) (0.004) (0.006)

Hispanic 0.056 0.017 0.092 0.013

(0.003) (0.003) (0.005) (0.005)

Married 0.116 -0.080 0.155 0.162 -0.062 -0.045

(0.002) (0.003) (0.002) (0.005) (0.004) (0.007)

Manufact Share 0.190 0.233 0.216 0.465 0.304 0.466

(0.033) (0.039) (0.050) (0.120) (0.064) (0.141)

constant 0.288 0.327 1.192 1.644 2.408 2.225

(0.126) (0.189) (0.184) (0.338) (0.276) (0.453)

R2 0.10 0.06 0.08 0.15 0.05 0.04

N 5,835,200 6,021,178 2,053,403 735,239 1735326 651,820

All regressions include year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

2.5 Investigating Our Identifying Variation

Our analysis incorporates two features not included in prior work: (1) the broader regional

patterns possible with the use of CPUMAs for non-identified counties, and (2) prescription data

from 2006 to 2016. These enhancements are one of the reasons our results differ from some prior

18

work, but they also open up questions. Notably, are our results the product of including more rural

counties in the analysis? As well, Evans et al. (2018) and Alpert et al. (2017) indicate that opioid

prescription abuse patterns shift after the 2010 reformulation of OxyContin, suggesting that our

results might over- or understate effects after 2010. To investigate the role of our enhancements,

we ran regressions with interactions on the lagged prescription coefficient to account for differences

in the data which are measured at the CPUMA-level or after 2010. The regressions maintain

the coefficients on other controls tobe equivalent as in the prior tables in order to highlight the

particular response of the prescription coefficients to these two innovations.

The results for the interaction of prescriptions with an indicator for whether the data are only

identified at the county or CPUMA level are shown in Table 7. The primary coefficients are all still

statistically significant although in several cases a bit smaller than was seen in Tables 1 to 3. In all

cases the interaction is negative and most cases statistically significant (except in the all prime-age

women regression). This indicates that patterns in these low-population regions are on average

worse than in the high-population identified counties, but not in a way that causes the results to

be dependent on including these counties.

Table 7: Prime Age Labor Force Regressions with CPUMA Interaction

White Nonwhite White Nonwhite

Men Women Men Men Women Women

<=HS <=HS <=HS <=HS

Lagged Prescrip. -0.035 -0.013 -0.057 -0.066 -0.031 -0.022

CPUMA*Prescrip -0.006 -0.000 -0.007 -0.017 -0.003 -0.004

R2 0.09 0.06 0.07 0.12 0.04 0.03

N 5,835,200 6,021,178 2,053,403 735,239 1735326 651,820

All regressions include full set of controls with year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

The interaction with prescription rates after 2010 is show in Table 8. Based on the results

in Evans et al. (2018) and Alpert et al. (2017) we might expect that prescriptions became a less

important indicator after the 2010 reformulation of OxyContin because users appear in their results

to substitute to the illegal market. That is not what we find when we include the post-2010

interaction. The results are stronger after 2010. The base response to prescriptions is negative and

generally statistically significant, but the interaction uniformly increases the scale of the effects after

2010. We have no means to explore the patterns of illegal usage after 2010, but these results could

be consistent with the spatial distribution of the illegal supplies of opioids roughly approximating

the distribution of post-2010 prescription rates.

19

Table 8: Prime Age Labor Force Regressions with Post-2010 Interaction

White Nonwhite White Nonwhite

Men Women Men Men Women Women

<=HS <=HS <=HS <=HS

Lagged Prescrip. -0.036 -0.006 -0.061 -0.082 -0.024 -0.021

Post*Prescrip -0.015 -0.013 -0.021 -0.026 -0.023 -0.012

R2 0.09 0.06 0.07 0.11 0.04 0.03

N 5,835,200 6,021,178 2,053,403 735,239 1,735,326 651,820

All regressions include year and Census division fixed effects.

Robust standard errors with clustering on geographic units.

p < 0.05, p < 0.01, p < 0.001

3 Reverse Causation:

Does the Labor Market Drive Opioid Abuse?

3.1 Model

A reasonable hypothesis is that opioid abuse increases due to poor labor market conditions,

and this reverse causation is what drives the correlation between opioid prescription rates and

labor market outcomes (Case and Deaton (2015)). This would recast the DAG in Figure 4 as the

DAG below in Figure 6: A labor market shock like the Great Recession (GR) could change overall

labor market conditions (L) and an individual’s labor market outcomes (Y ). Note that we assume

prescription rates do not respond to labor market conditions.

R ≡ Region

I ≡ Illegal Opioid Supply

P ≡ Prescription Opioid Supply

X ≡ Individual Characteristics

L ≡ Labor Market Conditions

O ≡ Opioid Use

Y ≡ Labor Force Participation

GR ≡ Great Recession

bc I

bcP

bc

R

b

O

bc

L

bX

b

Y

b

GR

Figure 6: Directed Acyclic Graph of Opioids Affecting Labor Force Participation

Note: This figure follows the convention from Pearl (2009) of communicating that a variable is observed by drawing a solid line

to its descendants, and communicating that a variable is unobserved by drawing a dashed line to its descendants.

Assuming that the drug environment stayed relatively stable over the time period in question,

the DAG in Figure 6 can be recast in terms of a standard model from the program evaluation

literature (Heckman and Vytlacil (2005)) that can be studied with potential outcomes (Aliprantis

(2015)), as shown in Figure 7 where the GR is identified as one of the time periods Z. Measuring

treatment with nonemployment should help to capture the effects of overall labor market conditions

rather than individual-level participation decisions.

20

Z ≡ Instrument (Time Period)

Pre-GR v. Post-GR

(2006+2007 v. 2009+2010)

D ≡ Treatment (U or NLF)

X ≡ Individual Characteristics

O ≡ Opioid Use

W ≡ Variable Violating

Exclusion Restriction

(a) Variables

b

Z

b

D

bX

b O

(b) The Assumed Model

b

Z

b

D

bX

b W

b O

(c) Another Possible Model

Figure 7: Directed Acyclic Graph of Unemployment Affecting Opioid Abuse

Note: This figure follows the convention from Pearl (2009) of communicating that a variable is observed by drawing a solid line

to its descendants, and communicating that a variable is unobserved by drawing a dashed line to its descendants.

We assume that an individual’s selection into treatment follows a latent index model

Di = 1{D∗

i > 0} (2)

where D∗

i = μ(Xi,Zi) − Vi and Vi follows a standard normal distribution. The potential outcome

of individual i in each treatment state Oi(D) is

Oi(0) = μ0(Xi) + U0i; (3)

Oi(1) = μ1(Xi) + U1i. (4)

We divide the NSDUH into years acting as a normal labor market (Zi = 0 in 2006 and 2007),

a period of weak labor demand (Zi = 1 in 2009 and 2010), and a “placebo” period that provides

evidence of time-trends (Pi = 0 in 2004 and 2005 and Pi = 1 in 2006 and 2007). We are interested

in estimating Local Average Treatment Effect (LATE) parameters

△LATE(Z) ≡ E[Oi(1) − Oi(0)|Di(1) − Di(0) = 1] =

E[Oi|Zi = 1] − E[Oi|Zi = 0]

E[Di|Zi = 1] − E[Di|Zi = 0]

.

3.2 Identifying Assumptions

Since we are using the Great Recession as an instrument for nonemployment, the biggest threat

to identification is from a variable, W, violating the exclusion restriction that the instrument only

affects the outcome variable through treatment. Anything that might have changed contempora-

neously with the GR that affects opioid use is a candidate W.

We present evidence that the most obvious potential W’s do not violate the exclusion restriction,

indicating that the basic features of the drug environment did not change between 2004 and 2010.

Specifically, there were no major changes in prices, trends in prescribing rates, the self-reported

ease of access to heroin, the self-reported rate of selling drugs, or impacts from new state-level laws

and enforcement.

21

Looking first at drug prices, we see that the price of heroin, the closest illegal substitute for

prescription opioids, was relatively stable between 2004 and 2010 (Figure 8).6 Similarly in the

legal market, there were no major changes in the price of oxycodone over this time period (see the

Marketscan data in Figure 4 of Evans et al. (2018)).

Looking at other measures of supply, we see that there were no changes in trends in opioid

prescribing rates between 2006 and 2010 (Guy et al. (2017)). In terms of illegal drugs, Table 9

shows self-reported measures from the National Survey on Drug Use and Health (to be described

in the next section). The ease of access to heroin and the share of respondents who reported selling

drugs did not change over the time period under investigation.

0 500 1000 1500 2000 2500 3000

Price (2012 $s)

1980 1985 1990 1995 2000 2005 2010 2015

Year

Source: National Drug Control Strategy, 2016 Data Supplement, Table 74

DOJ/DEA System To Retrieve Information on Drug Evidence (STRIDE)

Price per Pure Gram of Heroin

Figure 8: Average Price per Pure

Gram of Heroin in the United States

Table 9: Potential Ws

Easy to Get Sold

Men 24-64 w HS or Less Heroin (%) Drugs (%)

Mean in 2004+2005 20.2 2.2

Change in 2006+2007 0.2 0.0

(0.6) (0.2)

Change in 2009+2010 -0.4 0.3

(0.6) (0.2)

Note: The values in this table show the mean for the period

2004+2005, and then the change relative to the previous period

for 2006+2007 and 2009+2010.

Finally, we might expect that there were changes in the opioid market through laws and en-

forcement, especially since many states adopted laws between 2004 and 2010 to reduce the abuse

of opioids. Meara et al. (2016) study a national sample of disabled Medicare beneficiaries aged

21-64 years, half of whom used opioids in a given year. Examining the 81 controlled-substance laws

added by states between 2006 through 2012, Meara et al. (2016) find no impact of such laws on

potentially hazardous use of opioids or overdose.7

3.3 Data on Labor Market Outcomes and Opioid Abuse

Because there is no measure of opioid abuse in the CDC or Census data we have used thus far,

we now turn to a new data set. We did not use these survey data earlier in the analysis because

the survey uses nonstandard definitions when measuring labor market outcomes.

The best measurement of drug use among civilians in the United States is the National Survey on

Drug Use and Health (NSDUH). The NSDUH gathers annual, individual-level data on drug use by

means of in-person interviews with a large national probability sample. Every year, about 70,000

6These data on the average price of heroin in the US come from the Drug Enforcement Administration’s System

To Retrieve Information on Drug Evidence (STRIDE) program, and are reported in Table 74 of ONDCP (2016).

7Prescription-drug monitoring programs (PDMPs) are an example of such laws.

22

people from the US civilian, noninstitutionalized population age 12 and older are interviewed.

The surveys are conducted by the US Department of Health and Human Services (HHS) and

use computer-assisted methods to provide respondents with a private and confidential means of

responding to questions. Respondents are given $30 for participating in the NSDUH.

In addition to variables covering drug use in great detail, the NSDUH has the additional strength

for our purposes of having information on demographic characteristics and labor market outcomes

such as labor force participation, employment, and hours worked. The observed characteristics

(Xi) we include in the analysis are indicators for GED status, high school graduation, military

participation, current school enrollment, and having children in the household, as well as four

discrete levels of health status, several age levels, race, and marital status. The NSDUH measures

unemployment for both the week and the year before the respondent took the survey, but only

measures labor force participation for the week before the respondent took the survey. Thus we

measure treatment for the week before the survey. We measure treatment as nonemployment, either

being unemployed or not in the labor force, since there was a large response to the GR in terms of

labor force participation.

We measure outcomes as the non-medical use of prescription pain relievers, which we refer to

interchangeably as opioid abuse.8 We refer to the entire class of pain killers (analgesics) in the

NSDUH survey as opioids, even though a very small share of such pain killers are non-opioids.9

We investigate use over the past year, both in terms of any use and the number of days used.10

3.4 Estimation Results

Table 10 shows that the LATE of nonemployment on ever abusing opioids is zero for prime-age

men. We consider these null effects to be economically significant (Abadie (2018)): If labor market

outcomes drive opioid abuse, it is surprising that a shock as massive as the GR did not increase

opioid abuse. Even if this mechanism operates over a longer time horizon than the one studied

here, one would still expect to find some short-term effects. Table 10 does, however, also give some

evidence that nonemployment increased the intensity of opioid use among those prime-age men

who were using before the labor market shock.

8“Non-medical” means the use of a drug that was not prescribed for the respondent or that was taken only for

the experience or feeling it caused. Respondents are explicitly told that this use does not refer to “over-the-counter”

drugs.

9See footnote 11 in Carpenter et al. (2017).

10The NSDUH asks respondents about drug use in the past year and the past month, and the previous literature

has shown that estimates can be sensitive to the reference period used (Carpenter et al. (2017)). Our use of annual

variables is motivated by results in the literature on the intergenerational elasticity (IGE) in earnings showing how

transitory fluctuations can attenuate results when outcomes are measured over a short time horizon (Mazumder

(2005)).

23

Table 10: LATEs of Nonemployment on Opioid Abuse

Ever Abused in Last Year (%) Days Abused in Last Year

1st Stage 1st Stage

△LATE(Z) P-Value F-Stat △LATE(Z) P-Value F-Stat

All Adults 18+ –4.6 0.04 226 1.4 0.09 226

(2.2) (0.8)

Men 24-64 0.4 0.90 181 2.2 0.15 181

(3.3) (1.5)

Men 24-64 –0.1 0.98 142 3.7 0.07 142

w HS or Less (3.2) (2.1)

Figures 9a-9c decomposes these results graphically. We see the very strong first stage in Figure

9a, where nonemployment increased by 7 percentage points for the sample of prime-age men with

low educational attainment. Given the magnitude of this first stage, the results in Figure 9b may

be surprising, as they show there was no change in the share of people abusing opioids over this

same time period. Figure 9c indicates that the intensity of opioid use increased over time, but that

this increase could be the result of a trend pre-dating the GR.

0 5 10 15 20 25 30

Percent

0 5 10 15 20 25 30

Percent

By Time Period

2004+2005 2006+2007 2009+2010

Source: National Surveys on Drug Use and Health, 2004−2010

Men 24−64 with HS or Less

U or NLF Last Week

(a) E(D|Z)

0 1 2 3 4

Percent

0 1 2 3 4

Percent

By Time Period

2004+2005 2006+2007 2009+2010

Used in Past Year

Source: National Surveys on Drug Use and Health, 2004−2010

Men 24−64 with HS or Less

Opioid Abuse

(b) E(O|Z)

0 .25 .5 .75 1 1.25

Days

0 .25 .5 .75 1 1.25

Days

By Time Period

2004+2005 2006+2007 2009+2010

Days Used in Past Year

Source: National Surveys on Drug Use and Health, 2004−2010

Men 24−64 with HS or Less

Opioid Abuse

(c) E(O|Z)

Figure 9: Nonemployment and Opioid Abuse

Note: Di ∈ {0, 1} is unemployed or not in the labor force in the last week. In (b) Oi ∈ {0, 1} is ever used a pain reliever

non-medically in the last year, and in (c) Oi ∈ {0, 1, . . . , 365} is days used a pain reliever non-medically in the last year. Men

24-64 with high school or less.

3.4.1 Heterogeneous Effects

Since the previous literature has focused on opioid use among prime-age men with low edu-

cational attainment, we focus on the effects of nonemployment for males aged 24-64 with a high

school degree or less who are not currently enrolled in college. We examine these effects in greater

depth with Local Average Treatment Effect (LATE) parameters

△LATE(Xi,Z) ≡ E[Oi(1) − Oi(0)|Xi,Di(1) − Di(0) = 1] =

E[Oi|Xi,Zi = 1] − E[Oi|Xi,Zi = 0]

E[Di|Xi,Zi = 1] − E[Di|Xi,Zi = 0]

24

that account for covariates Xi by applying the Wald estimator to principal strata (terciles) of the

predicted probability of treatment estimated on those with Zi = 0, or terciles of bμ(Xi, 0).

We estimate μ(Xi, 0) using a linear probit model with μ(Xi, 0) = X′

iβ on data from the 2006

and 2007 waves of the NSDUH, and use the estimated coefficients to predict, for each wave of

the NSDUH, an individual’s probability of treatment during a normal labor market. To increase

power and allow for the estimation of LATEs, we discretize estimated values bμ(Xi, 0) into terciles

of bμ(Xi, 0), with the lowest tercile being least likely to be nonemployed, and the highest tercile

being most likely to be nonemployed.

Table 11 presents conditional LATEs. While there is some evidence that the extensive and

intensive margins increased for the group most likely to be nonemployed (the third tercile), it is

difficult to distinguish these results as being distinct from sampling variation. The extensive margin

is estimated to have actually decreased for the first and second terciles. And while the evidence for

the intensive margin increasing for the third tercile might be more compelling, this result starts to

look like noise when we look at the placebo pre-period (Figure 10c).

Table 11: LATEs of Nonemployment on Opioid Abuse

Ever Abused in Last Year (%) Days Abused in Last Year

1st Stage 1st Stage

△LATE(Z) P-Value F-Stat △LATE(Z) P-Value F-Stat

First Tercile –6.8 0.26 98 –1.3 0.24 98

(6.1) (1.1)

Second Tercile –4.7 0.52 38 2.7 0.59 38

(7.2) (5.0)

Third Tercile 7.8 0.12 37 8.0 0.07 37

(4.9) (4.5)

Note: The first tercile is the tercile least likely to be nonemployed (D = 1), while the third tercile is the

group most likely to be nonemployed.).

Looking at a graphical decomposition of these results, Figure 10a shows that there is a steep

slope for the relationship between the actual probability of nonemployment with the estimated

probability of nonemployment. The figure also shows that each of these groups experienced a large

labor market shock due to the GR, even if they each started from much different bases.

The changes in the share of those ever abusing after the GR could be interpreted as sampling

variation over the longer period shown in Figure 10b. And while the changes in days abused is

most compelling for the third tercile, we see evidence of a pre-trend for the second tercile.

25

0 5 10 15 20 25 30 35 40 45 50 55

Percent U or NLF Last Week

0 5 10 15 20 25 30 35 40 45 50 55

Percent U or NLF Last Week

1 2 3

Tercile of Estimated Probability of U or NLF

2004+2005 2006+2007 2009+2010

Source: National Surveys on Drug Use and Health, 2004−2010

Men 24−64 with HS or Less

U or NLF Last Week

(a) E(D|Z)

0 1 2 3 4

Percent

0 1 2 3 4

Percent

1 2 3

Tercile of Estimated Probability of U or NLF

2004+2005 2006+2007 2009+2010

Used in Past Year

Source: National Surveys on Drug Use and Health, 2004−2010

Men 24−64 with HS or Less

Opioid Abuse

(b) E(O|X, Z)

0 .5 1 1.5 2

Days

0 .5 1 1.5 2

Days

1 2 3

Tercile of Estimated Propensity of U or NLF in 2006+2007

2004+2005 2006+2007 2009+2010

Days Used in Past Year

Source: National Surveys on Drug Use and Health, 2004−2010

Men 24−64 with HS or Less

Opioid Abuse

(c) E(O|X,Z)

Figure 10: Treatment

Note: Di ∈ {0, 1} is unemployed or not in the labor force in the last week. In (b) Oi ∈ {0, 1} is ever used a pain reliever

non-medically in the last year, and in (c) Oi ∈ {0, 1, . . . , 365} is days used a pain reliever non-medically in the last year. Men

24-64 with high school or less.

We interpret the analysis of heterogeneous effects as evidence that, aside from sampling error,

the aggregate time series patterns along the extensive margin are stable across observed charac-

teristics that predict nonemployment. We also note that although observed characteristics predict

much different labor market outcomes (Figure 10a), we conclude that these characteristics are not

predictive of the share of people abusing opioids (Figures 10b). We find this evidence difficult to

reconcile with labor market outcomes being a primary driver of opioid abuse.

3.5 Robustness: Alternative Measures of Opioid Abuse

In the main analysis we define opioid abuse as the non-medical use of a prescription pain

reliever. To determine how consequential our preferred measure is in driving our results, we repeat

our analysis with alternative measures of opioid abuse.

We replicate our analysis with a measure of abuse that includes any use of prescription pain

relievers, regardless of use being medical or non-medical. This measure might yield different re-

sults because it is possible that some respondents misreport non-medical use as medical use. As

well, different types of opioid use could have positive or negative relationships with labor market

outcomes (Savych et al. (2018)).

We also replicate the analysis measuring opioid abuse as the use of either pain relievers or heroin.

This variable might be a more accurate measure of abuse if some prescription abusers substituted

to heroin toward the end of our sample period. There is a relationship between non-medical use of

prescription opioids and heroin use (Compton et al. (2016)), and there is evidence this relationship

changed over the time period we consider. Cicero et al. (2015) find that concurrent abuse of heroin

and prescription opioids increased between 2008 and 2014 in a national sample of respondents in

treatment, and the reformulation of OxyContin created an inflection point in heroin deaths in the

last third of 2010 (Evans et al. (2018), Alpert et al. (2017)).

Table 12 shows that the two additional measures of opioid abuse described above yield results

almost identical to those using the preferred measure in the main analysis. The preferred measure

26

used in the main analysis, displayed in the first column, is “Non-Medical Use of Pain Relievers,

Last Year (NM).” Compared to the preferred measure, any (medical or non-medical) use of pain

relievers exhibits similar patterns in changes, but starts at a higher level. The measure displayed

in the final column accounts for heroin use, and the inference is similar to that from the preferred

measure.

Table 12: Use of Pain Relievers within the Last Year

Medical or Medical or

Non-Medical Non-Medical Non-Medical or Heroin

Ever Used (%) Ever Used (%) Ever Used (%)

All Adults 18+

Mean in 2004+2005 2.5 4.3 4.4

Change in 2006+2007 0.2 0.3 0.3

(0.1) (0.1) (0.1)

Change in 2009+2010 -0.2 -0.0 -0.0

(0.1) (0.1) (0.1)

Men 24-64 w HS or Less

Mean in 2004+2005 2.4 5.0 5.2

Change in 2006+2007 0.2 0.7 0.6

(0.2) (0.3) (0.3)

Change in 2009+2010 -0.0 0.3 0.5

(0.2) (0.3) (0.3)

Note: The values in this table show the mean for the period 2004+2005 and the change

relative to the previous period for 2006+2007 and 2009+2010. The preferred measure

used in the main analysis, displayed in the left column, is “Non-Medical Use of Pain

Relievers, Last Year (NM).”

4 Conclusion

The scale of the opioid crisis makes it likely that there would be substantial labor market

impacts, but the specific nature of those relationships is important to clarify. Our analysis highlights

the strong negative relationship between opioid prescription rates and labor force statuses. Taken at

face value, our results suggest that solving the opioid crisis would substantially improve economic

conditions in counties that have had high levels of opioid prescriptions by boosting the prime-

age male participating rate by more than 4 percentage points. And these results are typically

larger and more statistically reliable for demographic groups that have seen weak and declining

participation, namely white and nonwhite prime-age men with a high school education or less. Of

course, individuals may not smoothly return to the labor market, but it is hard to argue that we

should not be trying to bring this group back into the labor market as a response to the opioid

crisis.

With data currently available, it is difficult to identify any strategy that would fully remove

the possibility that individuals are reacting to their circumstances with drugs rather than their

circumstances developing following drug use. Nonetheless, our work using the Great Recession as

a shock on the labor market to identify a response in drug usage cautions against the view that

improving economic conditions will solve the drug abuse problem. In addition, controlling for labor

markets in 2000, before most of the rise in opioid prescriptions, still shows substantial effects of

opioid prescriptions.

Our analysis is just one part of the developing literature on the opioid crisis that should help to

inform policy-makers as they attempt to rein in the crisis. Important issues that we were not able to

address include the rise of illegal, synthetic opioid supplies and deaths associated with opioids. The

challenges inherent in investigating the impacts of illegal opioid use on the labor market primarily

rest with the paucity of data available on the illegal opioid supply. While immediate answers are

wanted for the crisis, improving the data around drugs and the outcomes for individuals could help

to refine policy strategies that are developed.

While many relevant policy issues are outside the scope of this paper, our work serves to show

the scale of the impact of the opioid crisis on the labor market. In our view, the impact of the

opioid crisis on regional labor markets looks to be large and statistically robust.