Tuesday, March 12, 2019

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 = αPjt1 + 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.

New marriages/pairings repeat many things of the previous ones; those in shorter first unions & with higher neuroticism typically experienced decreases in functioning

(Eventual) Stability and Change Across Partnerships. Matthew D Johnson, Franz J Neyer. Journal of Family Psychology, February 2019, DOI: 10.1037/fam0000523

Abstract: Does a new partnership differ from its preceding one? This study investigates whether relationship dynamics change as people transition from one partnership to another and examines a number of predictors that might explain variation in change trajectories. We draw on data gathered from 554 focal participants in the German Family Panel (pairfam) study surveyed at four time points spanning two intimate unions to answer these questions. Latent change score modeling results showed eventual stability in five of seven constructs under investigation. When looking at overall change from Time 1 in partnership 1 to Time 2 of partnership 2, there were no mean-level changes in relationship and sexual satisfaction, perceptions of relational instability, and frequency of conflictual and intimate exchanges. Sexual frequency and partner admiration improved across partnerships. Further analyses showed much change unfolded in the interim; all constructs showed significant deterioration as the first partnership drew to a close, marked improvements as individuals moved from the end of the first partnership into their next union, and worsened across the first year of the second partnership. Neuroticism and relationship length were the most consistent predictors of change across partnerships: those in shorter first partnerships and with higher neuroticism typically experienced decreases in functioning across partnerships. These findings provide support for an eventual stability conceptualization of relationship development across partnerships.

Monday, March 11, 2019

The Role of Motivation, Attention and Design in the Spread of Moralized Content Online

Brady, William J., Molly Crockett, and Jay J. Van Bavel. 2019. “The MAD Model of Moral Contagion: The Role of Motivation, Attention and Design in the Spread of Moralized Content Online.” PsyArXiv. March 11. doi:10.31234/osf.io/pz9g6

Abstract: With over 2 billion active users, online social networks represent an important venue for moral and political discourse and have been used to organize political revolutions, sway elections, and raise awareness of social issues. These examples rely on a common process in order to be effective: the ability to engage users and spread moralized content through online networks. Here, we review evidence that expressions of moral emotion play a key role in the spread of moralized content (a phenomenon we call ‘moral contagion’). Next, we propose a psychological model to explain moral contagion. The ‘MAD’ model of moral contagion argues that people are motivated to share moral-emotional content; that such content is especially likely to capture attention; and that the design of social media platforms facilitates its spread. We review each component of the model and raise several novel, testable hypotheses that can spark progress on the scientific investigation of civic engagement and activism, political polarization, propaganda and disinformation, and moralized consumer behavior in the digital age.

Both girls and boys engage in gender-enforcing behavior (try to exclude others due to their gender); aggression and biased gender-related beliefs are associated with gender-enforcing behavior

Characteristics of Preschool Gender Enforcers and Peers Who Associate with Them. Sonya Xinyue Xiao et al. Sex Roles, Mar 2019, https://link.springer.com/article/10.1007/s11199-019-01026-y

Abstract: Children who try to exclude others due to their gender can be considered as “gender enforcers.” Using multiple methods (observations, interviews) and informants (children, teachers, teacher aides), we investigated the prevalence of gender enforcement, the characteristics of gender enforcers, and potential associations of exposure to gender enforcers. Participants were 98 (Mage = 49.47 months, SD = 11.40; 52% boys) preschoolers from a southwestern city in the United States. Results showed that both girls and boys engage in gender-enforcing behavior. Further, findings suggest that aggression and biased gender-related beliefs are associated with gender-enforcing behavior. Children who spent more time (over months) with enforcers were observed to play more with same-gender peers and to show more biased gender cognitions than were children who spent less time with enforcers. The study extends our understanding of how gender norms are enforced in early childhood, and it provides insights that may help to identify young gender enforcers. These findings have potential to inform future research and practice related to gender-based aggression in childhood.

Keywords: Gender beliefs Gender norms Peer pressure Peer relations


People condemn scientific procedures they perceive to involve playing God; judge a novel scientific practice to involve more playing God and to be more morally unacceptable; happens even to non-believers

Aversion to playing God and moral condemnation of technology and science. Adam Waytz and Liane Young. Phil. Trans. Roy. Soc. B, Volume 374, Issue 1771, March 11 2019. https://doi.org/10.1098/rstb.2018.0041

Abstract: This research provides, to our knowledge, the first systematic empirical investigation of people's aversion to playing God. Seven studies validate this construct and show its association with negative moral judgements of science and technology. Motivated by three nationally representative archival datasets that demonstrate this relationship, studies 1 and 2 demonstrate that people condemn scientific procedures they perceive to involve playing God. Studies 3–5 demonstrate that dispositional aversion to playing God corresponds to decreased willingness to fund the National Science Foundation and lower donations to organizations that support novel scientific procedures. Studies 6a and 6b demonstrate that people judge a novel (versus established) scientific practice to involve more playing God and to be more morally unacceptable. Finally, study 7 demonstrates that reminding people of an existing incident of playing God reduces concerns towards scientific practices. Together, these findings provide novel evidence for the impact of people's aversion to playing God on science and policy-related decision-making.


1. Introduction

In Mary Shelley's Frankenstein, the eponymous Victor Frankenstein animates a human-like creature through scientific experimentation, stating, ‘A new species would bless me as its creator and source; many happy and excellent natures would owe their being to me’ ([1], p. 101). Yet, by the story's end, the experiment has gone horribly wrong, and the creature, a monster, turns against Frankenstein. Many have read Frankenstein as a critique of humans' desire to play God, a romantic indictment of the Enlightenment's scientific advancements.
This critique of playing God pervades people's opposition toward science and technology. Sunstein ([2], p. 539) describes aversion to playing God as a heuristic [3] that guides1 moral disapproval of human intervention in the domains of sex, reproduction and nature: ‘“Do not play God” is the general heuristic here, with different societies specifying what falls in that category and with significant changes over time’. Despite its apparent importance, though, behavioural science has largely ignored the principle ‘Do not play God’ as a topic of study, work emerging in the fields of genetic engineering [4], nature conservation [5] and medicine [6] instead. The current work addresses this gap within behavioural science.
Scholars have put forth several definitions of playing God, with varying specificity. Most broadly, playing God involves what science scholar, Philip Ball [7], refers to as, ‘Mankind assuming powers beyond our station or our ability to control’. The current work adapts this general definition and focuses on a single domain that typifies aversion to playing God—people's responses to human intervention in science and technology.
Aversion to playing God, and its basis in aversion to human interference in the natural order (supported empirically in studies 6a and 6b), resembles other related but conceptually distinct constructs. Moral foundations theory [811], for example, specifies one moral foundation related to aversion to playing God: purity/sanctity. This foundation has theoretical roots in the moral code of purity/divinity, detailed as follows ([12], p. 576, italics added): ‘A person disrespects the sacredness of God, or causes impurity or degradation to himself/herself, or to others. To decide if an action is wrong, you think about things like sin, the natural order of things, sanctity, and the protection of the soul or the world from degradation and spiritual defilement’. The link between impurity and violating the ‘natural order of things' is critical to the code of purity/divinity and yet has gone largely unexplored. We believe that understanding aversion to playing God can illuminate this link.
Closest to this topic is work on naturalness bias—people's preference for natural processes and products rather than those that originate from human-imposed agency on the natural order of things [13,14]. Rozin ([15], p. 31) notes that ‘Human intervention seems to be an amplifier in judgements on food riskiness and contamination’, and Sunstein ([2], p. 539) notes that secular societies endorse a version of the ‘Do not play God’ principle in the form of ‘Do not tamper with nature’. Extensive work reveals people's preference for foods and medicines produced naturally and without human intervention [16,17].
More recent work suggests that naturalness bias might be linked to moral aversion to taboo trade-offs, a social transaction that places a monetary price on a value that people perceive to be sacred [18,19]. Work examining people's aversion to genetically modified food suggests that it elicits dislike not only for its ‘unnaturalness’, but also elicits moral emotional responses (e.g. disgust) similar to canonical taboo trade-offs [20].
Despite the resemblance between people's naturalness bias (and related constructs) and people's aversion to playing God, these constructs are nevertheless distinct. A pilot study (electronic supplementary material) reveals several practices that people perceive to involve tampering with nature but not playing God (e.g. emitting carbon monoxide while driving) as well as practices perceived to involve playing God but not tampering with nature (e.g. airline Chief Executive Officers' conspiring to fix prices). In addition, study 2 presents one case largely unrelated to nature (drone warfare) and establishes a link between aversion to playing God and moral judgement.
The link between principles regarding God and principles regarding nature and the natural order also aligns with extensive work on intuitive theism—people's implicit belief that a supernatural deity has intelligently designed nature itself [2123]. Importantly, we take aversion to playing God to be distinct from religious cognition in three ways. First, our pilot study (electronic supplementary material) distinguishes playing God from judgements of religious violations. Second, across studies we show that religiosity does not explain the relationship between aversion to playing God and moral judgement. Third, we demonstrate that aversion to playing God need not involve any consideration of God as the source of action per se and that aversion to playing God is distinct from religious conviction.
The present research characterizes the relationship between aversion to playing God and moral attitudes primarily in the domains of science and technology. Scientific procedures frequently involve human intervention in nature and sacred aspects of human experience [18]. Our overarching hypothesis is that aversion to playing God corresponds to negative attitudes toward science and technology across diverse contexts. Three archival nationally representative datasets provide initial support for this relationship (electronic supplementary material) and motivate the present empirical work.

2. Overview of studies

Studies 1 and 2 provide initial support that people morally condemn practices to the degree that they see them as involving playing God. Studies 3–5 extend these findings by showing that aversion to playing God corresponds to behavioural intentions and behaviours including willingness to fund the National Science Foundation (NSF), and real monetary donations to organizations supporting stem cell research and genetically modified rice. Given that this is, to our knowledge, the first systematic psychological examination of aversion to playing God, we also examine an important moderator—novelty. Studies 6a and 6b present a case in which the relationship between aversion to playing God and moral condemnation is modulated by the novel versus established nature of the act. Study 7 extends these findings by demonstrating that reminders of existing acts of playing God (i.e. reducing the perceived novelty of playing God) improve attitudes toward scientific practices.

[...]

3. Discussion

These studies establish, for the first time, to our knowledge, aversion to playing God as a valid psychological construct relevant to judgements of science and technology including robotics (drones), GMOs, vaccinations and stem cell research. Importantly, our findings provide critical evidence for the association between aversion to playing God and moral condemnation of novel scientific practices, even when these practices benefit human well-being [27].
Given that this research represents, to our knowledge, the first systematic examination of aversion to playing God, several key questions emerge. One is the degree to which aversion to playing God causally influences moral judgement towards science and technology. Although we acknowledge the plausibility of a bidirectional relationship between these constructs, study 7, in particular, supports a causal pathway from aversion to playing God to moral judgement. Future research can examine this pathway as well, for example, testing whether people condemn a chemical change in an organism that results from human intervention more than one that results from randomness, and whether perceptions of playing God drive any difference. Given that existing work shows that people view human-caused harm as worse than naturally arising harm and harm caused by acts worse than harm by omission [28], and that people prefer natural products and processes (that are chemically identical) to human-made ones [16], we believe these effects are likely.
Another key question is whether aversion to playing God simply reflects general moral condemnation. The present research suggests this is not the case. First, study 5 shows that aversion to playing God positively correlates with support for the Cure Violence charity, and study 6b shows aversion to playing God is unrelated to the moral acceptability of an established practice in the legal domain. In other words, the relationship between aversion to playing God and moral judgement is not consistent across contexts. Second, the inconsistent relationship between aversion to playing God and political ideology suggests that this construct does not merely reflect a particular political profile associated with a particular set of moral foundations [9,10]. Archival studies 1b and 1c (electronic supplementary material) also show little association between ideology and aversion to playing God. Thus, aversion to playing God reflects a specific moral concern that emerges among liberals and conservatives alike.
A related question is whether aversion to playing God simply reflects religious conviction. The present research suggests that aversion to playing God represents a distinct construct from religiosity or belief in God. First, across studies, measures of religiosity and belief in God do not account for the association between aversion to playing God and disapproval of science and technology. Aversion to playing God predicts moral condemnation above and beyond religious constructs. Second, the pilot study (electronic supplementary material) and study 2 showed no association between measures of religiosity or belief in God and aversion to playing God. The inconsistent relationship between religiosity and aversion to playing God across studies may stem from opposing influences of religious belief on perceptions of playing God. As documented here, when a relationship between religious belief and aversion to playing God emerges, it is typically positive. That is, believers deliver harsher moral judgements than non-believers. This pattern probably stems from an explicit code within many Judeo-Christian traditions that calls for respecting God's authority as a sole creator [29,30]; thus, intervening in matters such as reproduction is incompatible with respect for God as an ultimate agent. Yet, some Judeo-Christian sects, such as Lutheranism, teach adherents to carry out the will of God through their actions [31]. Therefore, followers may view certain interventions as essential to their religion. Because no comparisons among religions are offered here, future work is needed to assess whether aversion to playing God is attenuated for religions that explicitly instruct people to be secondary agents for God's plans.
As it stands, one of the current limitations of this work is its generalizability to adherents of non-Judeo-Christian religions, which as of now is an open question. For example, a strict interpretation of the Islamic idea of Tawhid (one should not worship other Gods nor take on Godhead for oneself) would prohibit acts of playing God, yet the Islamic spiritual tradition of Sufism also allows people to take divine traits so that God can act ‘through them’ ([32], p. 417). Other scholars suggest that playing God in the case of cloning is less of a concern for Hinduism and Buddhism because it fits with the idea of reincarnation [29], although these religions' views about the creation and destruction of life complicate this question [33]. Ultimately, future research can test the strength of aversion to playing God in other religions.
Given the prevalence of atheism [34], future research may also examine whether even atheists demonstrate an aversion to playing God at an implicit level. Although our work demonstrates a relationship between increased religiosity and aversion to playing God, aversion to playing God is present across the religious spectrum in all of the present studies. Atheists may therefore demonstrate their aversion at an implicit level, similar to other aspects of religious cognition that emerge even among those who explicitly disavow religious belief [22,35]; indeed, recent studies have shown that religious primes affect moral behaviour and public self-awareness even among atheists [36,37]. At an explicit level, atheists might express their aversion in non-religious terms, such as ‘Do not tamper with nature’, as noted by Sunstein ([2], p. 539).
Overall, our work suggests that most people believe (implicitly or explicitly) that, in the domains of science and technology, human intervention should be avoided and instead left to a more metaphysical source of action—for theists that source might be God, and for atheists or others that source might be fate [38], nature or some other agentic practice already in place. In other words, aversion to playing God may not necessarily reflect an aversion to humans' taking on the role of a religious spirit or creator, but rather an aversion to human agency in a domain in which another agent is thought to be responsible.
Given that playing God is not reducible to religiosity or belief in God, other related beliefs about secular pre-existing systems or agents governing science might similarly affect moral judgements of science and scientific progress. For example, belief in the infallible capacity of nature might impede views on scientific innovation as well. Take, for example, the hotly contested debate over GMOs. Spitznagel & Taleb [39] argue against genetically modified food by stating, ‘The statistical mechanism by which a tomato was built by nature is bottom-up, by tinkering in small steps…In nature, errors stay confined and, critically, isolated’. This belief in nature's near-perfect ability may stifle innovation in food production and farming [40], inspiring beliefs (akin to aversion to playing God) that humans should not interfere in these domains. Study 6b hints at the contribution of belief in a natural order to these attitudes.
In summary, aversion to playing God, which may result from ideas about deference to God or some higher organizing power as the ultimate agent, can increase inertia in moral and scientific domains. Given rapid advances in reproductive technology, pharmaceuticals and robotics and artificial intelligence, and the novelty of these advancements, we expect aversion to playing God to continue to influence public opposition towards these developments. Particularly in the domain of social robotics, as scientists and developers become increasingly Frankensteinian in engineering human-like agents, the present work suggests the importance of understanding where negative attitudes towards these agents originate and how to mollify them, in efforts to facilitate scientific progress.

Ethics

Informed consent was obtained from all participants and institutional review board approval was obtained for all studies we conducted. For the GSS, used in archival study 1a, informed consent was obtained from participants and this survey was approved by the institutional review board at NORC at the University of Chicago. The survey used in archival study 1b was approved by the institutional review board at Johns Hopkins University that granted exempt status for consent. For the polls used in archival study 1c, they were conducted within the CASRO standards for research and all participants received informed consent before participating.

Data accessibility

The data supporting this article are available in the Dryad Digital Repository: https://doi.org/10.5061/dryad.gv7qs12 [41].

Authors' contributions

Both authors designed the studies, analysed the data, drafted the paper and approved the final submission.

Competing interests

We have no competing interests.

Funding

We received no external funding for this study.

Acknowledgements

We thank the GPPC for archival study 1b data, and Kurt Gray, Adam Galinsky, Linda Skitka, Jonathan Baron, Josh Rottman, Ellen Winner, Fiery Cushman and Ryan Miller for helpful comments.

Footnotes

1 Although we assume the causal pathway from aversion to playing God to moral judgement and explicitly support this pathway empirically in study 7, we also acknowledge that people may use assessment of playing God to justify moral judgment post hoc.
2 Our data contained 11 people who made donations outside of 3 s.d. either for Cure Violence or for the National Stem Cell Foundation, and whose exclusion alters the significance of these findings. Given our a priori decision not to exclude outliers and given the bounded nature of this measure, we chose to include these participants in our analyses as they represent meaningful data points of people who feel strongly about donating to one charity or the other. Furthermore, regressing donations transformed by square root (such that they no longer represent values outside of 3 s.d.) on APG reveals the same significant results reported in the primary analyses.
Electronic supplementary material is available online at https://dx.doi.org/10.6084/m9.figshare.c.4381796.
One contribution of 17 to a theme issue ‘From social brains to social robots: applying neurocognitive insights to human–robot interaction’.

Sunday, March 10, 2019

Have Humans Evolved to Be Cheaters? Is it something general? Have other monogamous species did the same?

Have Humans Evolved to Be Cheaters? Nadia Nooreyezdan. The Swaddle, Mar 10, 2019. https://theswaddle.com/have-humans-evolved-to-be-cheaters/

Excerpts (full text with lots of links at the reference above):

[...] Evolutionary psychology experts like Christopher Ryan and Cacilda Jethá, co-authors of the book Sex at Dawn, theorize men and women both have biological motivations for cheating while maintaining a monogamous relationship. Male animals, including humans, have an evolutionary drive to have as many offspring as they can with different mates, while females are motivated to seek out mates with superior genes in order to increase the genetic diversity (and chances of survival) of their offspring. But some animals, humans included, have also evolved, both socially and biologically, to want the security of monogamous relationships; we may still feel jealousy or betrayal if we’re cheated on, wanting our partners to be faithful, while also being sexually attracted to other people.

While this isn’t an excuse for people to cheat, it does suggest humans will always have these opposing biological motivations creating a tension within ourselves and our relationships.

Monogamy is uncommon among animals, with fewer than 5 percent of mammals staying with the same mate. Humans evolved towards monogamy mostly because babies are, in a word, helpless. [...]

Because they needed to be nursed, carried, protected, and fed for several months, if not years, pairs or groups of parents raising the infant became necessary, Ryan and Jethá write. But since male primates didn’t like to be responsible for offspring that wasn’t theirs (an understatement — this usually resulted in infanticide by angry males), pair-bonding became a necessity. Monogamous pairs seemed to be the solution for decreasing male-male competition while still ensuring enough resources for the offspring. But this didn’t mean that primitive man didn’t cheat.

Monogamy was a convenient way to ensure that, in the genetic competition of evolution, one’s offspring reached maturity. It meant staying together basically ‘for the sake of the kids,’ but not necessarily being sexually faithful to one another. Our motivations for reproduction, Ryan and Jethá argue, drive us to seek partners outside of our monogamous relationships.

Reproduction required little investment for males; females, on the other hand, have to choose between the security a male partner may provide, and superior genetic qualities — because as Daniel Kruger, an evolutionary psychologist at the University of Michigan, has pointed out, it’s rare for a man to provide both.

“One long-term strategy is to settle down and have a long-term relationship with a guy who’s a reliable, stable provider, but then have an affair on the side with a guy who has phenotypic qualities and can provide that high-quality genetic investment,” Kruger has said. And genetically, women are predisposed to have this kind of ‘back-up plan,’ which researchers at the University of Texas refer to as the “mate-switching hypothesis.” But in order to maintain the status quo of the monogamous relationship, both men and women have to resort to what Kruger refers to as “strategies and counter strategies.” In other words, humans just try to not get caught.

Not convinced? These same competing impulses are found throughout nature, even among the animal kingdom’s erstwhile paragons of monogamy: birds.

With an estimated 90 percent of feathered species staying monogamous, birds have also been found to be serial cheaters for the same evolutionary incentives humans have. For decades, scientists believed that birds’ social monogamy during breeding season meant that the bonded pairs were prone to loyalty. But further genetic and behavioral research has shown that up to 75 percent of the offspring in a population could be from “extra-pair copulations.” Adultery, jealousy, and cuckolded partners abound, from indigo buntings, to yellow warblers. Even wandering albatrosses, who return back to the same partner every year after months at sea, aren’t always sexually faithful, with 14 to 24 percent of chicks fathered by a male who is not the mother’s life partner. Clearly, social monogamy for birds is strictly separate from sexual monogamy, a far rarer occurrence.

Regardless of species, it seems that cheating while monogamous is possibly the most ideal situation for bonded pairs. The male gets to spread his genes as far and as wide as he can, with next to no repercussions, thus ensuring reproduction with at least one female; and the female gets to increase the genetic diversity among her offspring (in case some have genetic defects, others can survive) without risking the loss of resources provided by her mate. Ideally, males will help provide for all of the female’s offspring (unaware that they might not all be his), and females will be ignorant of their male partners’ mating with others.

It could be great, if we could all be open about this and okay with the idea of raising children regardless of whether they’re biologically ours. However, child rearing à la Plato’s idea of collective parenting feels like an unattainable dream. Like so many things about humans, we must manage conflicting impulses — genetic incentives to stay in monogamous relationships, and ones that lead us to cheat.

In her recent book, The State of Affairs: Rethinking Infidelity, couples’ therapist Esther Perel argues that being honest about our desires is [...].