The Intended and Unintended Effects of Opioid Policies on Prescription Opioids and Crime

2.1 Supply-Side Laws

Prescription Drug Monitoring Programs (PDMP) represent the most common and well-studied supply-side policy.^[9] Since the early 2000s, PDMP have been increasingly implemented across US states. Full national coverage has been reached in 2017 with Missouri, the last state to adopt this type of regulation. It consists of state-level databases that monitor the prescription and the dispensing of controlled substances. The information contained in the system is available to all authorised health-care providers including physicians and pharmacists to prevent improper drug prescription or dispensation.^[10] In some states, under certain circumstances, prescribers and dispensers are required to access PDMP by law (hence, called “must-access” or “mandate”), while in others the use of this system is “non mandated”.

Pain Management Clinics Laws (PMCL) embody all regulations aimed at preventing inappropriate prescribing and dispensing of controlled substances within clinics specialised in pain management. These clinics have been such a great source of prescription drugs that they are sometimes called “Pill Mills”. They have become such a serious issue in the context of the opioid crisis that PMCL have been implemented in one every five states since the mid-2000s. Although there is some heterogeneity across states, regulations associated with PMCL typically provide for requirements concerning the ownership, the licensing procedures, the operational standards and the personnel qualification of pain management clinics, facilities or practice locations. These interventions have resulted in a massive shutdown of pain management clinics that did not meet the new standards (Mallatt 2017).

Both PDMP and PMCL induce a shock on the supply side of the market for prescription opioids because they provide for restrictions to the agents supplying drugs (physicians and pharmacists).^[11] As a consequence, we expect the two policies to have a negative effect on the volume of legally-dispensed drugs. Moreover, this drop might be accompanied by an increase in drug-related crimes due to users turning to the black market in search of drugs. However, the reduced availability of drugs from the legal channel may yield a shortage in the illegal market, hence contributing to a decline in arrests for drug sale or possession.

2.2 Demand-Side Laws

Doctor Shopping Laws (DSL) are also directed at limiting the amount of opioids dispensed but they involve the demand side of the market for drugs, as they impose restrictions on patients rather than on suppliers. They refer to any regulation that prohibits doctor shopping, i.e. the practice of obtaining controlled substances from multiple healthcare practitioners. The number of states that have adopted these laws has doubled since the year 2000 and is currently around a third of the total. DSL limit a patient’s ability to seek medications from multiple providers and prohibit withholding of any information that may be relevant to the physician or the pharmacist.

Theoretically, curtailing access to prescription drugs for non-medical use in this manner is potentially effective as health care providers are the most common source of opioids used non-medically (Substance Abuse and Mental Health Services Administration, 2014). Moreover, the previous medical literature has found a positive relationship between doctor shopping practices and overdose mortality risk (Peirce et al. 2012). Thus, this set of regulations is expected to negatively affect the amount of opioids available on the market from the demand side, especially when prescriptions are unnecessary or excessive. Nevertheless, in the absence of systematic surveillance and large heterogeneity in the legal implementation across US States, the regulation could turn out to be weakly effective, since heavy users especially might have a strong incentive not to disclose the relevant information to health care professionals to obtain more painkillers than necessary.

3.1 Data Sources

The data on prescription opioids comes from the Automation of Reports and Consolidated Orders System (ARCOS), which is run by the Office of Diversion Control of the US Drug Enforcement Administration. Since the Controlled Substance Act of 1970, manufacturers of controlled substances are required to provide information on the amount of drugs produced and dispensed in the US. The yearly ARCOS reports provide a record of the quantities (in grams) of each controlled active ingredient dispensed in the US. This information is disaggregated at the three-digit zip code level across all US states.

We consider a set of opium-based active ingredients available in ARCOS, namely morphine, oxycodone, hydrocodone, hydromorphone, methadone, meperidine, and fentanyl classified as Schedule II or Schedule III drugs.^[12] We build an overall indicator that accounts for the relative potency of these drugs so that each drug is converted into Morphine Gram Equivalent units (MGEs).^[13] Since it considers the overall amount of opium-based active ingredients, this represents our main indicator to quantify the dispensation of prescription opioids.^[14]

Then, we link our dataset to the Uniform Crime Reporting (UCR) Program Data provided by the Federal Bureau of Investigation, which contains the number of arrests disaggregated by county and by type of crime. We take into account drug-related crimes that involve the possession and selling of different substances such as opium, cocaine, marijuana and other synthetic drugs.

Finally, we match the information from ARCOS to the official population intercensal estimates at the county level, which include counts of the overall population and by sex, age band and race/ethnicity group.^[15] The US Census is also the source of all the data used in the heterogeneity analysis about education, health care insurance coverage and employment in health services (County Business Patterns), while income comes from the Bureau of Economic Analysis. Drug and alcohol mortality data are drawn from the Global Health Data Exchange of the Institute for Health Metrics and Evaluation (University of Washington).

Our final sample comprises 3127 counties across the US that we follow during the period 2001–2016. To our knowledge, this is the first paper evaluating the effects of supply- and demand-side opioid state laws on the volume of prescribed opioids and on drug-related crime rates that exploit such an extensive dataset, both in terms of time span and of geographical coverage at the county level.

3.2 Empirical Model

We employ a typical regression difference-in-differences setting such that:

where Y_cst is the outcome of interest measured in county c, in state s and in year t. The set L_st includes dummy variables for each law as from Table 1, which take value 1 when the regulation is in force in a given state and 0 otherwise. Hence, the coefficient β corresponds to the treatment effect of interest, as it captures the effect of regulation on different outcomes while controlling for the other laws. We analyse such effect on the quantity of drugs distributed and on drug-related crime.^[16]

We acknowledge the contemporaneous implementation of other state regulations, specifically aimed at reducing opioid overdose mortality (namely, Naloxone Access Laws and Good Samaritan Laws) by adding a set of two dummy variables (M_st). Their role in this context is discussed in Appendix B. Moreover, we include county (γc), year (δt) and region-year (θrt) fixed effects to control for fixed heterogeneity at local level, at time and region-by-year fluctuations, respectively. Errors are clustered at the state level.^[17]

A critical assumption for our identification strategy is that states that enact opioid laws and those that do not adopt them behave similarly in the pre-implementation period, to ensure that the enactment of the laws is not endogenously related to trends in opioid prescriptions. We already control for time, county and region-year heterogeneity, but the event-study analysis approach helps to check for pre-existing trends, i.e. we verify the existence of parallel trends. This posits that the average change in the comparison group represents the counterfactual change in the treatment group if there were no treatment. If the leads in the event-study analysis are not statistically different from zero, this implies that the treated counties are trending similarly to the untreated counties prior to the policy, and this constant heterogeneity vanishes in difference. Thus, the identifying assumption of the differences-in-differences model would be supported. Hence, we also estimate the following equation:

which allows for five pre- and five post-treatment effects for each law l, while still controlling for the enforcement of all the other laws (−l). According to this specification, the baseline year is the one before the implementation of law l, while leads and lags are identified by the coefficients βl,π and βl,τ, respectively. Here, the β associated to π=−5 and τ=5 include all periods prior to t − 5 and after t + 5, respectively. If the leads βl,π are not statistically different from zero we can assume that the parallel trends assumption holds. The βl,τ coefficients, instead, allow us to examine whether the treatment effect of law l fades, increases or stays constant over time. Additionally, a battery of robustness checks in support of our identification strategy is presented in Section 4.1 where we discuss potential confounding effects.

3.3 Descriptive Analysis

Figure 1 shows the raw average of MGE units per capita dispensed by year since the introduction of each policy. The portion to the left of the dashed vertical line corresponds to the years prior to the onset of each law. The graph depicts a constant increase in the average amount of drugs dispensed per capita, which is only slowed down after the introduction of the policies (i.e. to the right of the dashed line). The only exception to this inversion in trend seems to be associated with DSL, for which we do not observe any change in slope.

Figure 1:

Average MGEs dispensed by year since/to the introduction of the policies.

Note: The labels in the x-axis are such that the zero, the negative and the positive values correspond to the year of, the years before and the years after the introduction of each policy, respectively. Treated states only (49 for PDMP, 10 for PMCL, 20 for DSL).

Table A.2 reports the descriptive statistics of the main outcomes and control variables used in the analysis. Drug quantities are expressed in MGE units per capita to take into account the relative potency of each drug component. Overall, a total of 704 kg of prescription opioids (i.e. 30 g per capita) are dispensed in each county every year. Between 2001 and 2016 the total county-level average of MGE units has increased almost three-fold from 336 to 746 kg. The most commonly dispensed substances are morphine, methadone and hydrocodone, with around 13, 5 and 4 g per capita, respectively.

Figure A.3 in the Appendix describes the geographical distribution of the average MGE units in the years 2001 and 2016 (top and bottom panels, respectively). It is worth noting that had we considered the 2001 quartile distribution, we would have obtained an almost entirely red map for the year 2016. As a matter of fact, the median of the MGE units per capita distribution in 2016 is more than double the one in 2001 (14.51 and 7.08 MGEs per capita, respectively). For this reason, we construct the percentile thresholds based on the average distribution of MGE units per capita in the period 2001–2016. The colder (darker blue) areas, the lower the levels of POs per capita. Vice versa, the warmer (darker red) the area, the higher the dispensation of MGE units. Nevertheless, we observe a remarkable variation both across years and counties. The map for 2016 is much warmer compared to the one for 2001, which indicates that the dispensation of opioid analgesics per capita rises during the period analysed. Besides, the maps display a clear heterogeneity both within and across states.

4.1 The Effect of State Laws on Prescription Opioids

Table 2 shows the main results on the amount of MGE prescription drugs dispensed in each county. In columns 1 to 4 we consider one set of state laws at a time: PDMP, PCML and DSL. Column 1 presents the effect of PDMP alone, while in column 2 we include an interaction term that accounts for the adoption of Mandate PDMP. In line with the existing literature, we find that the effect of Mandate PDMP is substantially higher than that of the non-compulsory PDMP. Coefficients suggest that ordinary PDMP reduces the quantity of MGEs by 4.5% while Mandate PDMP yields a further drop by 8.5%. Conversely, the overall impact of Mandate PDMP on MGE units per capita consists of a decrease by 13%. The coefficient associated to PMCL suggests that imposing more stringent operational restrictions to pain management clinics determines a decrease in the amount of MGE units dispensed by 15% (column 3). Conversely, in column 4, DSL, which compel patients to reveal to health care professionals whether they had already be prescribed or administered prescription drugs, does not appear to have any meaningful impact on the quantity of per capita MGE units.

When we consider all sets of laws in the same model (columns 5 and 6), coefficients maintain the same sign and significance, with the exception of the one capturing the differential between PDMP and Mandate PDMP. Given that the different types of PDMP do not differ in their effect on the quantity of MGEs distributed, column 5 is our main specification.

Our estimates suggest a reduction in prescription opioids per capita following the enforcement of the state laws that aim at reducing abusive behaviour on the supply side, namely PDMP and PMCL. The negative impact in column 5 corresponds to an average reduction in the amount of MGE units per capita by almost 4% following the introduction of PDMP and by more than 15% after the enactment of PMCL.^[18] Given that the average amount of MGEs per capita in the sample is 29.73, these effects translate in a drop by around 1.14 and 4.52 g per capita, respectively. Our results are in line with those of Mallatt (2017) and Meinhofer (2017), who estimate the negative effects of PDMP and PMCL on the total amount of oxycodone dispensed to be around 8 and 17%, respectively. The absence of effects predicted by DSL might be due to its weak implementation as well as to the fact that demand-side interventions generally receive less funding and attention compared to supply-side policies (Alpert, Powell, and Pacula 2018).

We provide evidence on the validity of our estimates with an event-study approach, which allows estimating lagged effects while testing for the absence of pre-existing trends. This is shown in Figure 2. The plots suggest the existence of parallel trends between treated and control units, as the coefficients in the pre-treatment period are never statistically different from zero. This points to the absence of a plausible systematic pattern in the distribution of MGE units per capita before the introduction of any opioid state law, which also allows us to exclude potential anticipation or announcement effects.

Figure 2:

Event-study analysis: effect on drug quantities.

Note: Coefficients estimated as in Eq. (2). The coefficient associated to <t − 5 pertains to all periods prior to the fifth year before the implementation of the law. The coefficient associated to >t + 5 refers to all years from the fifth after the implementation of the law. Standard errors are clustered at the state level and 95% confidence intervals are shown.

Figure 2 also highlights a small but persistent negative impact of PDMP on the outcome, while PMCL yield a sharp and increasingly large decrease in the quantity of MGE units per capita.^[19] The introduction of DSL does not have any impact on dispensation rates. If anything, DSL might bring about a mild increase in the amount of MGE units per capita dispensed, although coefficients are never statistically significant.^[20]

As we are in the presence of staggered time law implementation, we apply the decomposition of our estimates in the spirit of Goodman-Bacon (2018), based on comparisons across different treatment groups (namely, always treated, never treated and units that switch from being untreated to treated). Here, weights are based on the size of each treatment sub-group and on the variance of the treatment, which in turn depends on how distant is the onset of the treatment from the start and the end of the observational window. We apply the procedure to our three main estimates of the impact of opioids laws on the quantity of Morphine Gram Equivalent units. The decomposition exercise in Table 3 shows that the estimated effect for the PMCL coefficient is almost entirely driven by the comparison between never-treated units to those that enact this type of regulation starting from 2009. The comparison across treated units is much less relevant, although the sign of the coefficient is in line with the main estimate. For what concerns PDMP, the coefficient of −0.038 is derived by the comparison across treated units over time (timing groups and always-treated versus timing groups). While this is expected, given that 49 states out of 50 are eventually treated in our sample, it is reassuring that the estimated effect is not driven by the comparison with the sole state that is never treated (Missouri, which implemented PDMP in 2017). Finally, the results on Doctor Shopping Laws appear less precise, although the comparison between treated (timing groups) and never-treated suggests that, if anything, the effect should be slightly negative.

4.2 Robustness Checks

Table A.3 shows a set of robustness checks. In column 1 we account for additional changes in the institutional framework which might potentially interfere with the dispensation of prescription opioids and bias our estimated effects: the introduction of Medicare Part D in 2006 and the reformulation of OxyContin in 2010. Medicare Part D is a federal program that subsidizes the costs of prescription drugs and of prescription drug insurance premiums for Medicare beneficiaries. Thus, it might disproportionately compensate for the incidence of the policies on the amount of prescription opioids dispensed in areas with a larger number of beneficiaries. We proxy the exposure to the program with the share of people aged 65 or over at county level, interacted with a dummy variable that takes value 1 in the years after 2006 and 0 otherwise as in Powell, Pacula, and Taylor (2015).

OxyContin was reformulated in 2010 with the intent of making it more difficult to abuse this drug.^[21]Alpert, Powell, and Pacula (2018) and Evans, Lieber, and Power (2019) show that its reformulation has been followed by a significant drop in the prescribing rates of this drug. At the same time, however, they find evidence of substitution towards other opioid-based substances, especially fentanyl and heroin. Hence, we include an interaction between the amount of oxycodone dispensed in each county in 2000 and a dummy that takes value 1 in the years after 2010 (Alpert, Powell, and Pacula 2018; Evans, Lieber, and Power 2019; Mallatt 2017). We obtain comparable results with the inclusion of such indicators, which suggests that these changes to the institutional framework do not influence the estimated impact of the laws on the amount of dispensed prescription opioids per capita.^[22]

In column 2 of Table A.3 we include a set of time-varying demographic indicators to rule out, or at least alleviate, the possibility that trends in the composition of the population may be correlated with the propensity of a state to institute specific opioid regulations. The absence of confounding effects is confirmed by the fact that the coefficients of interest are not statistically different from the main specification. In column 3 we estimate a model in which state-specific linear time trends are estimated only based on the pre-treatment periods and groups. We partial out pre-treatment trends after de-meaning all the dependent and independent variables following the procedure of Goodman-Bacon (2018), and, reassuringly, we obtain estimates that are almost identical to our main effects.^[23] In the next columns, we include linear and quadratic trends based on the initial level of MGE units per capita and state-specific linear and quadratic trends.^[24]

In column 8 we exclude methadone from the dependent variable. Methadone is considered clinically different from other prescription opioids and often used in the treatment of opioid and heroin addiction in replacement therapies (Paulozzi 2012). Yet, in some states methadone is also one of the most widely diverted and abused drugs (Cicero and Inciardi 2005; Jones 2016). Coherently, the magnitude and significance of the coefficients imply that the enactment of state laws limiting the dispensing of opioids on the supply-side (PDMP especially) disproportionately impacts on the amount of methadone dispensed. Unfortunately, whether this is due to abuse rates falling or to a change in prescribing practices by suppliers cannot be tested here. DSL, if anything, are associated with an increase in the volume of opioids other than methadone, possibly because the detection of “ordinary” patients performing doctor shopping is more difficult for health care professionals in good faith, while methadone users are subject to stricter control.

We also investigate the existence of potential spillovers from the local labour market performance. In the spirit of Pei, Pischke, and Schwandt (2019), we test whether employment and unemployment rates are correlated with the implementation of opioid state laws, finding that the coefficients associated with opioid regulations are not different from zero (Table D.2). Moreover, if we add employment and unemployment rates as controls to the main specification, we obtain identical results.^[25]

Finally, the recent paper by Horwitz et al. (2018) highlights issues deriving from recurring differences in measuring the correct starting dates of PDMP in the literature. Although, as stated by the authors, the definition of the implementation dates is not always clear-cut, a similar point of estimate would support the reliability of our choice of dates. In Table D.3 we compare our measure of PDMP with the list provided by Horwitz et al. (2018). Columns 1–4 display our estimates using four different definitions of PDMP assembled by Horwitz et al. (2018, Table 2, pp. 31–32), namely enactment, contingent on funding, electronic and user access. The last six columns refer to dates taken from publicly available databases, as selected by Horwitz et al. (2018, Table 3, pp. 33–34). The estimated coefficients are similar to our baseline.

4.3 The Effect of State Laws on Drug-Related Crime

Next, because of the predicted disruption to the legal market for opioid painkillers in combination with their high potential for addiction, we estimate whether the opioid state laws have any indirect fallout on the illegal market for drugs. While a few recent studies look at the effects of some opioid state laws on crime (Dave, Deza, and Horn 2018; Doleac and Mukherjee 2018; Mallatt 2017; Meinhofer 2017), the empirical evidence on the unintended impact of these laws on the market for illicit drugs is still scarce.

Table 4 shows the estimated effects of opioid state laws on crime related to the possession and sale of opium and derivatives and of synthetic opioids (column 1). We consider this as our main indicator for drug-related crime as it contains the two categories of drugs that are attributable to the diversion of opioids. We then investigate the effect of the laws on each category of drug-related crimes separately as grouped by UCR (2000): cocaine, opium and their derivatives such as morphine, codeine and heroin (column 2), synthetic narcotics including semi-synthetic and synthetic opioids like oxycodone, methadone and fentanyl (column 3), marijuana and hashish (column 4) and other non-narcotic drugs such as benzedrine (column 5).^[26]

PDMP do not seem to be associated with any changes in drug-related crime, while PMCL have a positive impact on the possession and the sale of drugs, for which arrest rates rise by 21%, i.e. 20 people every 100,000 inhabitants. Conversely, we do not find any statistical significance for DSL. The event-study analyses corresponding to the coefficients from column 1 are shown in Figure A.4, where point estimates indicate an increase in arrests for the possession or sale of opium and synthetic drugs, although the significance is weak. The plots also suggest that the common trend assumption holds in all cases, as the coefficients in the pre-implementation period are never statistically different from zero.

The comparison between coefficients in columns 2 and 3 of Table 4 might suggest that the effect associated to the introduction of minimum requirements to pain management clinics (PMCL) might be driven by the diversion of illicit drugs such as heroin (or cocaine), rather than synthetic drugs (including opioids). However, a more in-depth observation of the phenomenon suggests that the enactment of PCML has significantly increased crimes related to the sale of both types of drugs. This is clearly evident from the plots reported in Figure 3, which demonstrate that Pain Management Clinics Laws produce a large unintended increase in arrests for the sale of these drugs.^[27] As shown in the previous subsection, PMCL constitute the set of policies under analysis that substantially curb the dispensation of prescription opioids. The differential increase in arrest rates following their enactment is coherent with prior works uncovering the existence of a substitution across different opioid drugs when the legal alternative becomes less viable (Alpert, Powell, and Pacula 2018; Evans, Lieber, and Power 2019; Mallatt 2017). Moreover, columns 4 and 5 in Table 4 show that there is no effect on arrests for possession or sale of marijuana or other non-narcotic drugs. This is an expected result, given that the state laws under study are specifically aimed at tackling the over-dispensation of opioid-based drugs.^[28]

Figure 3:

Event-study analysis: Effect on drug-related crime of PMCL.

Note: Coefficients estimated as in Eq. (2). The coefficient associated to <t − 5 pertains to all periods prior to the fifth year before the implementation of the law. The coefficient associated to >t + 5 refers to all years from the fifth after the implementation of the law. Standard errors are clustered at the state level and 95% confidence intervals are shown.

As additional evidence, we investigate whether the introduction of opioid state laws is associated with changes in police forces. We do so to test whether arrest rates related to the dispensation of illegal substitutes of opium are affected by unobserved differences in law enforcement and policing public expenditure across counties. We proxy this by using the number of police officers per 1000 inhabitants as dependent variable and find that this is not correlated to any of the laws under consideration (column 9, Table A.3).^[29]