Can Electronic Prescribing Mandates Reduce Opioid-Related Overdoses?

Abstract

As the opioid crisis has escalated, states have enacted numerous policies targeting opioid access and monitoring possible misuse. Recently, the majority of states have passed electronic prescribing mandates for controlled substances. These mandates require that controlled substances be prescribed electronically directly to the pharmacy. The electronic system maintains a rich patient history that prescribers will observe when issuing a prescription while also reducing opportunities for fraud. The first enforced mandate was implemented in New York in March 2016; thus empirical evidence about the effects of such mandates is limited. We study how adoption of the New York e-prescribing mandate affected opioid supply and opioid-related overdoses. We estimate that the mandate reduced the rate of overdoses involving natural and semi-synthetic opioids by 22%. We find little evidence of any corresponding changes in overdose rates involving illicit opioids.

1. Introduction

Drug overdose deaths have increased dramatically over the past two decades. In 2017 alone, there were more than 70,000 fatal overdoses (Scholl et al., 2019). Overdoses involving opioids are driving this trend, reflecting greater use of both prescription and illicit opioids (Compton et al., 2016). The unprecedented rise in opioid overdose deaths has prompted the Centers for Disease Control and Prevention (CDC) to call this the worst drug overdose epidemic in U.S. history (Kolodny et al., 2015).

Federal and state governments have adopted numerous policies to curb this deadly trend. A key policy target has been access to prescription opioids, especially in circumstances in which overprescribing or misuse appear likely. In just the last few years, a majority of states have passed electronic prescribing of controlled substances (EPCS) mandates. Electronic prescribing or “e-prescribing” refers to the process by which prescribers electronically send “accurate, error-free and understandable” prescriptions directly to a pharmacy through a secure network.¹ Before June 2010, electronic prescribing of controlled substances was not even permitted in the United States. This policy was reversed by the Drug Enforcement Agency (DEA) and, by 2015, all states and the District of Columbia had legalized EPCS.

Since legalization of EPCS, e-prescribing rates for controlled substances have gradually increased. In 2016, more than 45.3 million prescriptions for controlled substances (not just opioids) were delivered electronically--a 256% increase from 2015 (Surescripts, 2017). But overall e-prescribing rates of controlled substances remain low. In 2018, only 31% of controlled substance prescriptions in the United States were electronic, compared to 96% of non-controlled substance prescriptions (Surescript, 2019).²

The first enforced EPCS mandate was implemented in 2016. Since then, an additional twenty-eight states have passed EPCS mandates that will be in place by 2022 and three additional states have pending legislation.³ Beginning in 2021, the Medicare Part D program will mandate EPCS.⁴ Despite heightened interest in EPCS mandates, there have been limited opportunities to study their impacts. Empirical evidence is urgently needed.

We study New York’s implementation of an e-prescribing mandate that took effect March 27, 2016. New York was the first state to pass and enforce an e-prescribing mandate and is the only state with an adequate post-adoption period for analysis. The New York mandate extends to non-controlled substances as well. In 2014, less than 2% of prescribers in New York even had the infrastructure to issue electronic prescriptions (Surescript, 2015) and less than 1% of controlled substances were prescribed electronically. By 2017, likely due to the mandate, 94% of controlled substances were prescribed electronically in New York (Surescripts, 2017). E-prescribing rates have increased in all states, but there were uniquely large gains in New York. Figure 1 shows this growth for New York relative to the rest of the United States.

Figure 1: Electronic Prescribing Rate of Controlled Substances, 2014-2017.

Notes: Using data from Surescripts, we plot the percentage of controlled substances prescribed electronically in New York and all other states. To aggregate the state-level percentages, we weight by the number of opioid prescriptions according to IQVIA data provided to the CDC.³¹

This paper intersects with the broader debate about the potential of supply-side interventions in addressing the opioid crisis (Pacula and Powell, 2018). Evidence of the effectiveness of PDMPs is mixed but suggests that specific types of PDMPs are effective (Pardo, 2017). Recent work has found evidence that “must access” PDMPs reduce measures of misuse as represented in Medicare Part D data (Buchmueller and Carey, 2018) and opioid-related overdoses (Meinhofer, 2018; Kim, 2021). The literature on “must access” PDMPs is relevant to predicting the consequences of e-prescribing mandates given that the systems share similar properties and e-prescribing has often been considered key tool for improving PDMP effectiveness (Perrone and Nelson, 2012). Additionally, Alpert et al. (2020) suggest that the “hassle costs” associated with PDMPs are important in deterring prescribing. E-prescribing mandates may similarly increase the effort necessary to prescribe opioids.

E-prescribing also directly addresses concerns about fraud by providing a complete electronic record that helps evaluate possible diversion and misuse for controlled substances (Gabriel et al., 2016). People misusing controlled substances may alter paper prescriptions by changing the type of the drug, increasing the number of refills, and increasing the quantity of pills. Forging prescriptions has been a growing problem, exacerbated by cheaper, more-available high-quality copying equipment (Wartell and Vigne, 2013). Between three and nine percent of people misusing opioids forged prescriptions to acquire them (O’Donnell, 2016). Prescription drug fraud could also enable diversion of controlled substances to the black market and may target prescribers directly. Ten percent of physicians report their DEA registration number⁵ stolen, and around 30 percent know a colleague who has been the target of fraud (Imprivata, 2016).

Despite the recent transition of the opioid crisis to illicitly-produced opioids such as heroin and fentanyl, prescription opioids -- defined here as natural and semi-synthetic opioids -- are still involved in a substantial fraction of fatal overdoses – more than one-third in 2017.⁶ Appendix Figure 1 provides overdose trends by opioid type. Prescription opioids are also involved in initiating dependence on opioids for individuals who eventually overdose on heroin or fentanyl (Compton et al., 2016).

We study the effect of the 2016 e-prescribing mandate in New York state on overdose deaths and opioid distribution using a difference-in-differences framework. With only one treated unit, we recognize and address three empirical challenges common to such “comparative case studies.” First, it may be difficult to find an appropriate comparison group for one unit since any pre-existing state-specific trends will not be balanced with possible counteracting trends in other treated units.⁷ Second, it is important to reduce concerns that other events or policies in the treated state (and not in the comparison states) are not independently driving outcome changes. Third, inference can be difficult given that we only observe one state’s response to the policy.

To address the first two challenges, we adopt an event study framework to make the analysis as transparent as possible. An event study analysis permits us to plot the conditional differences between New York and comparison states both before and after adoption of the mandate. We select comparison groups motivated by considerations which have been shown to be important in the literature. For our main comparison group, we use states geographically close to New York. This proximity is important given the very different overdose trends in recent years across the country. For example, the trajectories of the opioid crisis in the east and west have diverged considerably due to fentanyl (Abouk et al., 2021). The different opioid environments make eastern states more appropriate counterfactuals for changes in overdose rates in New York. In addition, states in the south have also diverged considerably from northern states. A literature suggests that states expanding Medicaid under the Patient Protection and Affordable Care Act (ACA) have experienced different opioid trajectories, even prior to expansion (Goodman-Bacon and Sandoe, 2017; Abouk et al., 2021). These states tend to be in the south, and this differential growth appears to be related to geography not policy. Consequently, we select on states in Census Divisions closest to New York (discussed below). We will consider alternative comparison groups and use synthetic control estimation.

We consider a range of alternative hypotheses for why New York’s post-treatment trajectories may have varied relative to comparison states, such as differential exposure to fentanyl and adoption of other policies. Our event study approach permits us to consider the timing of the effect, which narrows the range of possible alternative explanations, and we extensively discuss other policies which could influence our outcomes and confound the results. With only one treated unit, we cannot rule out that New York experienced a permanent decline in overdose rates at around the same time as policy adoption for reasons unrelated to the mandate, but our analysis does not find any likely alternative explanations for this reduction.

For inference, we use the approach recently introduced in Ferman and Pinto (2019), which is appropriate for comparative case studies. This method is a permutation-style test while adjusting for heteroskedasticity, which is important given the different population sizes in the analysis sample.

Using the restricted-use geocoded National Vital Statistic System (NVSS) for 2010-2017, we find that New York experienced a 22% reduction in per capita natural and semi-synthetic opioid overdose deaths after introduction of the e-prescribing mandate relative to the counterfactual. We do not observe comparable reductions (or increases) in overdoses involving heroin or synthetic opioids, which are probably illicitly-produced and acquired. We find complementary evidence that the mandate was associated with a reduction in opioid supply in New York. These results are not driven by pre-existing trends, adoption of other policies (in New York or neighboring states), or complementarities with synthetic opioids.

The rest of the paper is organized as follows. Section 2 provides more background on electronic prescribing, New York policy adoption, and the possible role of health technology in fighting the opioid crisis. In Section 3, we introduce the data and the identification strategy. Results are discussed in Section 4 and we conclude in Section 5.

2. Background

2.1. Electronic Prescribing

The first electronic prescription mandate was passed in 2008 in Minnesota with an effective date of January 2011. The law required that all e-prescribing transactions should be conducted using national standards (National Council for Prescription Drop Program or Health Level-7), but this mandate has never been enforced and the Minnesota Department of Health still states that there is “no enforcement mechanism” for the mandate.⁸ Near the end of our sample period (July 2017), Maine implemented an EPCS mandate but, given the short amount of post-treatment data, we defer analysis of Maine’s law to future work and drop Maine from the analysis. Thus, this paper treats New York as the sole adopting state during the sample period given that it has the only enforced mandate with an adequate post-period.

Most existing research on e-prescribing is not specific to controlled substances. Small scale adoption and pilots of e-prescribing have been studied in a variety of settings (e.g., Gawande, 2017; Brady et al., 2014; Moniz et al., 2011; Odukoya et al, 2012; Kaushal et al, 2010; Tan et al, 2009), finding benefits such as cost-savings and reductions in errors. These small-scale pilots have rarely focused on controlled substances or analyzed the effects on opioids specifically. In addition, state mandates are potentially more effective than limited pilots since they promote statewide integrative systems which should have economies of scale in terms of comprehensively documenting opioids received for each patient, reducing inappropriate opioid prescribing, and preventing fraud.

2.2. New York’s Opioid Policy Landscape

In 2011, the New York Attorney General’s office introduced the “Internet System for Tracking Over-Prescribing Act” (or I-STOP), which strengthened the existing PDMP. The act was passed and signed into law in 2012, and I-STOP was implemented on August 27, 2013. I-STOP enacted a “must access” provision for the state PDMP and included a mandate for e-prescribing of controlled substances in 2014. However, the mandate for both controlled and non-controlled substances was delayed until March 27, 2016. There are exceptions to this mandate such as practitioners with approved waivers or prescriptions with extensive directions.⁹ Despite these exceptions, we observe high rates of e-prescribing in New York.

The PDMP program provides a source for consulting about controlled substances (e.g., prescribing history), but it is not designed for submitting prescriptions electronically. Most e-prescribing applications integrate with the PDMP database directly,¹⁰ ensuring (beyond just a legal requirement) that prescribes observe patient histories.

There is limited evidence of changes in opioid supply due to New York’s e-prescribing mandate. Brown et al. (2017) found that the total opioid supply increased following the implementation of I-STOP in August 2013 in New York, in a before-and-after time series study, though they also show some evidence that the number of prescriptions decreased. They do not study the e-prescribing mandate. Danovich et al. (2019) estimate reductions in opioid prescribing in a single emergency department due to the mandate. We are not aware of any statewide evidence about the mandate’s impact on opioid supply or overdoses.

More broadly, it is important to acknowledge that addressing opioid misuse and its harms is an active policy space in New York and most states during this time period. New York enacted a Good Samaritan law in September 2011 and a naloxone standing order in July 2014. Rees et al. (2019) find strong evidence that naloxone access laws reduce overdose rates, though not for standing orders.¹¹

New York began training law enforcement statewide in 2014 on how to carry and administer naloxone.¹² In addition, while not necessarily adopted in response to the opioid crisis, New York legalized medical marijuana dispensaries in January 2016. In terms of timing, though not necessarily scope, most concerning for our analysis is the adoption of a 7-day supply limit for first-time users prescribed opioids for acute pain. This policy was effective starting July 22, 2016, only four months after the e-prescribing mandate.

It is a critical challenge to isolate the independent effects of these policies, and our event study framework will help pinpoint the timing of the effect since most of these policies preceded the e-prescribing mandate. We will also control for policies which the literature has shown may reduce overdose rates. For example, there is evidence that medical marijuana dispensaries reduce opioid-related deaths (e.g., Powell et al., 2018) and opioid prescribing (Bradford et al., 2018). In addition, we control for policies imposing prescribing limits since New York’s policy was implemented shortly after the e-prescribing mandate went into effect. We expect that the prescribing limits should not impact overdose rates, especially immediately, given that they only apply to a small fraction of prescriptions. Nationally (among a large commercially-insured population), only a small share of opioid prescriptions are written for patients who have not previously used opioids (Zhu et al., 2019) and, under the New York policy, providers are still permitted to prescribe additional pills after the initial prescription.¹³ Sacks et al. (2021) find that prescribing limits increase the rate of opioid prescribing with no evidence of effects on extreme use such as doctor shopping.

While we do not expect prescribing limits on first-time users to affect overdoses (and the evidence suggests that supply should be unaffected as well), we will still control for this policy and discuss it further in our sensitivity analyses. Only two states in our comparison group do not introduce prescribing limits during our sample period, which further limits the possible role they can have in explaining the pattern of our results since the main effect sizes generally grow in magnitude throughout the post-period. To provide further empirical evidence on the prescribing limit laws, we conduct a separate event study analysis for this policy and find no evidence of a decline in overdose deatlas because of the adoption of prescribing limits. The results help rule out the possibility that the observed decrease in overdose deaths in New York after the e-prescribing mandate is due to the implementation of the prescription limit laws.

2.3. Possible Mechanisms

New York’s motivation for mandating electronic prescribing was to improve access to patients’ prescription history for prescribers and decrease opportunities for fraud.¹⁴ Prescribers were permitted to select among a set of approved software programs from different vendors, and these programs typically integrated with patient prescription histories (controlled by a central database). See Appendix Figure 2 for an example of how this information is typically presented to a prescriber. In addition, the “must access” PDMP provision had many exceptions (see Danovich et al., 2019 for discussions about exceptions in the context of emergency departments) which the e-prescribing mandate did not have, suggesting even further information gains for some groups of prescribers.

Additionally, prior to the mandate, prescribers used state-issued prescription forms. The mandate potentially had an immediate impact on fraud since the mandate – with some exceptions – eliminated the use of these forms. Pharmacies would have still accepted these forms (potentially falsified) until the date of the mandate. After the mandate, opportunities for this type of fraud would have decreased substantially.

It is also possible that the required use of EPCS increased the hassle of prescribing controlled substances. The e-prescribing mandate in New York requires that use of two-factor authentication, a more complicated login process than required to access the New York PDMP (which does not require two-factor authentication). Hassle costs have been shown to be important in the context of the Kentucky PDMP (Alpert et al., 2020), which uses multi-factor authentication, and more generally when modeling prescriber behavior (Alpert et al., 2019).¹⁵ Danovich et al. (2019) hypothesize that the reduction of opioid prescribing at the emergency department was due to both an increase in hassle costs and improved information flow.

Our empirical analysis focuses on the timing of the effect. In principle, we could see an effect prior to the mandate as prescribers began adopting e-prescribing in anticipation of the mandate. However, we also might expect important “nonlinearities” in the effects of e-prescribing rates since the system should be more effective when a vast majority of prescribers are using it. Additionally, even a week prior to the mandate, the majority of prescribers were not using EPCS, potentially due to hassle costs,¹⁶ suggesting that we should not observe such anticipation effects.

3. Data and Methodology

3.1. Data

We use the restricted-use National Vital Statistics System (NVSS) Multiple Cause of Death mortality files—the census of deatlas in the U.S.— to study annual overdose deatlas from 2010-2017, providing an adequate pre-period for our analysis. We follow the coding used by the CDC to categorize deaths as opiate-related. First, we code deaths as overdoses by using the ICD-10 external cause of injury codes X40-X44, X60-64, X85, or Y10-Y14. Further, we use drug identification codes, which provide information about the substances found in the body at death. We focus on natural (excluding heroin) and semi-synthetic opioids, designated by T40.2, for the main analyses given that these typically best represent prescription opioids. We will also study measures which include methadone (T40.3) and synthetic opioids (T40.4).

We conduct sensitivity analyses in which we also include T40.0 (opium), T40.1 (heroin), and T40.6 (unspecified narcotics). In addition, due to concerns of underreporting of opioid-specific deaths, we also study overdoses including T50.9 (unspecified drugs) but no other drugs. Underreporting is only a concern in our context if New York and the comparison states had differential changes in reporting.¹⁷ We will find sharp effects at the time of adoption so these systematic reporting changes would have had to occur precisely at the time of adoption. We will test for this possibility explicitly.

Information regarding the supply of prescribed opioids within the state is captured in the Drug Enforcement Administration’s Automation of Reports and Consolidated Orders System (ARCOS) from 2010-2017. The Controlled Substance Act of 1970 requires all manufacturers and distributors to report transactions and deliveries of all Scheduled II (and selected Schedule III-V) substances to the Attorney General. ARCOS monitors and records the flows of these controlled substances as they move from manufacturers to retail distributors at the local level.

We construct a composite measure of twelve opioid analgesics: fentanyl, hydrocodone, hydromorphone, meperidine, methadone, morphine, oxycodone, codeine, dihydrocodeine, levorphanol, oxymorphone, and tapentadol. We convert the total grams distributed per capita of each drug into morphine equivalent doses¹⁸ drawing on standard multipliers used in this literature (Paulozzi et al., 2011; Gammaitoni et al., 2003); conversion allows us to aggregate quantities across drugs. Distribution per capita is a different measure of opioid supply than prescriptions; however, we assume that distribution to a state acts as a useful measure of prescription opioid supply and access.

We obtained data about other opioid-related policies from multiple sources. Information about the implementation of medical marijuana laws, PDMPs, and pain clinic regulations are from the Prescription Drug Abuse Policy System. We refer to Sacks et al. (2021) for prescribing limit implementation dates (see Table A.1 in their paper). State annual population data were obtained from the Surveillance, Epidemiology, and End Results Programs (SEER), which we use for total state population as well as constructing demographic shares. We use data from the Annual Social and Economic Supplement of the Current Population Study to construct the percentage of the population with a college degree.

3.2. Main Comparison States

Our analyses rely on states close to New York given concerns about the appropriateness of states in the west and south in generating an appropriate counterfactual. We use the following Census Divisions: New England (Connecticut, Massachusetts, New Hampshire, Rhode Island, Vermont),¹⁹ Mid-Atlantic (New Jersey, New York, Pennsylvania), and East North Central (Illinois, Indiana, Michigan, Ohio, Wisconsin). This set of comparison states excludes states west of the Mississippi River, which have been much less affected by the fentanyl crisis. We exclude states in the south (i.e., the South Atlantic, East South Central, and West South Central Census Divisions) since the majority of states in these Census Divisions did not expand Medicaid and also have experienced different overdose trajectories (Goodman-Bacon and Sandoe, 2017) even prior to New York’s adoption of I-STOP. A further advantage of our comparison group is that these states tended to adopt similar policies as New York. For example, eight of the twelve states implement a “must access” PDMP provision and ten of the twelve enact opioid prescribing limits during our sample period, further reducing the scope that these policies can have on our estimates.

To illustrate the different dynamics in other parts of the country, we plot opioid-related overdose trends in New York relative to both the west and the south (see Appendix Figure 3). We present trends for opioid (T40.2-T40.4) mortality and natural/semi-synthetic opioid mortality. The west does not experience the same increase in overdoses as the east prior to the adoption of New York’s mandate. The south and New York overdose rates are converging prior to 2014, but we then observe a sharp rise in overdoses in New York relative to these states. After the adoption of the mandate, this trend reverses, which is consistent with our findings in this paper. However, given that the states do not appear to be similar prior to the mandate and there are additional reasons (discussed above) to believe that they would not have evolved similarly in the absence of the e-prescribing mandate, we exclude these states.

The opioid policy literature often struggles to find appropriate comparison groups given the different dynamics of the crisis across the country in recent years. For this reason, we provide results using varying definitions for our control group. In sensitivity analyses, we show results in which the comparison group includes all states in the east which, like New York, expanded Medicaid under the ACA. We will also show results using all states in the east and discuss the appropriateness of these alternative comparison groups. We rely on event study analyses to provide evidence of whether our main comparison group is appropriate.

In addition, we will also provide complementary results from synthetic control estimation, which uses a data-driven approach to generate counterfactual outcomes.

3.3. Summary Statistics

In Appendix Figure 4, we replicate Figure 1 but include the e-prescribing rates for our main comparison group. New York’s e-prescribing rate increased at a substantially faster rate than rates in the comparison states. In Table 1, we present summary statistics for New York and the comparison states before the adoption of I-STOP. Before the implementation of these policies, New York had higher but relatively similar opioid overdose rates compared to the control states.

Table 1:

Summary Statistics (January 2010 – June 2013)

	New York	Control States	P-Value (NY = Control)
Overdoses per 100,000
Opioids	1.223	1.059	0.207
Natural/Semisynthetic opioids	0.771	0.689	0.422
Natural/Semisynthetic opioids only	0.649	0.579	0.357
Heroin Only	0.392	0.572	0.050
Synthetic Opioids Only	0.149	0.156	0.607
Demographics / Economic Conditions
% White	72.2%	83.0%	0.000
% Ages 25-44	27.1%	25.4%	0.001
Unemployment Rate	8.4	8.8	0.235
Population Size	19,546,635	6,778,442	0.000
Per Capita Opioid Supply
Morphine Equivalent Doses	2.96	3.32	0.222
Pre-Reformulation Misuse Rate (2004-2009)
OxyContin Misuse Rate (per 100)	0.525	0.633	0.228

Notes: Summary statistics are provided for the period prior to New York’s “must access” PDMP. Control states are defined in the text. Overdoses which include “only” do not include any other type of opioid. The last column presents the p-value for the difference between New York and the comparison states for that variable.

3.4. Methodology

3.4.1. Event Study Analysis

Our primary analysis will estimate an event study specification that accounts for state and calendar quarter fixed effects:

$$y_{st}={\alpha }_s+{\gamma }_t+X_{st}^{\prime }{\beta }_t+P_{st}^{\prime }\theta +{\delta }_{t}1{(\text{New York})}_s+{\epsilon }_{st}.$$ (1)

y_st is the number of opioid overdose deatlas per 100,000 population at the state-quarter level or a measure of per capita opioid supply. The specification includes time- and state-varying controls, X_st, including the share of the population that is white, share of the population ages 25-44, the log of the 2009 population,²⁰ and the share with a college degree. These covariates are permitted to have differential effects in each time period, given recent recommendations in difference-in-differences designs that covariates should be permitted to have this type of flexibility (Jaeger et al., 2018).

We also include a vector of other policies, P_st, including whether the state has a PDMP, a “must access” PDMP, pain clinic regulations, a medical marijuana law, the presence of a legal and active medical marijuana dispensary, and opioid prescribing limits.²¹ We are interested in the δ_t estimates, which we will show graphically. We normalize these estimates to 0 in the quarter prior to enactment of the e-prescribing mandate.

We rely on an event study framework to test for the existence of pre-existing trends. It also allows us to study the timing of the effect. We consider the timing especially important here given that we would like to isolate the effect of the e-prescribing mandate from the “must access” PDMP provision, which was implemented a few years before. Of course, we cannot entirely rule out that the “must access” provision had a delayed effect that happens to coincide with the e-prescribing mandate but studying the timing of the effect will help us tease out which of these policies is driving changes in overdose rates. In addition, e-prescribing rates themselves increased over time in anticipation of the mandate, and it is possible that there was an independent effect of the rising e-prescribing rates before the mandate; however, we expect that there are substantial benefits to the mandate itself, as discussed in Section 2.3.

Since we control independently for “must access” PDMPs, the event study estimates after New York’s adoption of this policy refer to whether New York’s “must access” PDMP had any effect beyond similar programs in other states. We include this control because we are primarily interested in the effect of the e-prescribing mandate. We also show results without this control. The main event study estimates will also not capture any effect associated with the New York prescribing limits since we control for this policy as well.

3.4.2. Difference-in-Differences Model

To summarize the event study estimates, we also present difference-in-differences estimates from the specification:

$$y_{st}={\alpha }_s+{\gamma }_t+X_{st}^{\prime }{\beta }_t+P_{st}^{\prime }\theta +\delta \times 1{(\text{New York})}_s\times {\mathrm{Post}}_t+{\epsilon }_{st},$$ (2)

where Post is equal to 1 beginning in the second quarter of 2016. For the difference-in-differences estimates, we select on the 2014-2017 sample so that the analysis period only includes quarters in which New York had a “must access” PDMP. We drop the first quarter of 2016 since the mandate was adopted in this quarter.²² We rely on the event study estimates to provide evidence of the appropriateness of the difference-in-differences specification.

3.4.3. Inference

Given that we have only one treated unit, traditional clustered covariance estimators often used to estimate standard errors in policy evaluation are likely inappropriate (Conley and Taber, 2011). Permutation tests are frequently used in these situations, but this technique assumes homoskedasticity across units even when population sizes of those units are very different. We use a recent permutation-style approach introduced in Ferman and Pinto (2019), which is similar to the Conley and Taber (2011) method while adjusting the residuals based on population size. This adjustment is important in this context given the relative size of New York compared to the control states. The Ferman and Pinto (2019) method randomly assigns treatment to one of the control states (similar to traditional randomization inference) while also bootstrapping the set of control states.

To calculate confidence intervals, we sequentially enforce a series of null hypotheses. The 95% confidence interval is composed of all null hypotheses that are not rejected at the 5% level. Because we are inverting a set of hypothesis tests, these confidence intervals will not be symmetric. For our event study results, we implement this approach for each time period.²³

4. Results

4.1. Unadjusted Time Series Comparisons

We first show unadjusted opioid overdose trends for New York and our comparison states from 2010 to 2017 in Figure 2. In Panel A, we show the trend for opioid overdose deaths (T40.2-T40.4) while in Panel B, we select on natural and semi-synthetic opioids (T40.2). In general, both trends are relatively flat and parallel before New York’s adoption of the “must access” PDMP provision. Around that time, overdoses began to increase in New York and the comparison states. We observe a relative reduction in overdoses in New York, which would be consistent with a causal effect of adoption of the “must access” PDMP, which we explore further below. After this shift, we do not observe major differences in trends between New York and the comparison states prior to the enactment of the e-prescribing mandate. We test these findings more formally below. After the e-prescribing mandate, we observe very different trends in New York compared with the control states.

Figure 2: Quarterly opioid overdoses per 100,000 in New York, states in the South, and the West for 2010-2017.

Notes: We exclude Minnesota and Maine since they also adopted e-prescribing mandates during this time period. Opioid overdoses in Panel A include T40.2, T40.3, and T40.4. The solid vertical line represents the adoption of New York’s e-prescribing mandate.

4.2. Opioid Supply Event Study Results

The relationship between e-prescribing mandates and opioid distribution is, in principle, ambiguous (Böckerman et al., 2019). The mandate could deter opioid prescribing by providing practitioners with information that patients already have overlapping opioid prescriptions or by giving other signals that might predict misuse. Alternatively, the improved information flow could make physicians more confident when prescribing opioids to patients for whom the data contain no signs of current prescriptions or a history of misuse. Thus, it is unnecessary to observe an effect on opioid supply for there to be downstream effects on overdoses.

We explore the empirical relationship in Figure 3. While we observe movements in the estimates throughout the pre-period, these estimates generally center around zero and do not appear to be trending prior to the mandate. At the time that the mandate took effect, we observe a large and persistent decline in opioid supply. There is a slight delay in the timing of the initial reduction. Since we are studying a measure of orders from manufacturers, a delay is not surprising since it does not perfectly reflect the timing of prescriptions. A decline in prescriptions would likely predict reductions in the size and frequency of future distribution. The results suggest that the mandate reduced the opioid supply in New York. On average, we estimate that the mandate reduced opioid supply by 0.14 morphine equivalent doses per person, equivalent to about a 6% reduction from baseline.²⁴

Figure 3: Event Study Estimates for Per Capita Opioid Supply.

Notes: N=416. 95% confidence intervals estimated using Ferman and Pinto (2019) which accounts for within-unit clustering and heteroskedasticity given only one treated unit. Outcome is the number of morphine equivalent doses supplied to the state divided by the population size. The dotted vertical line signifies New York’s adoption of a “must access” PDMP. The solid vertical line represents the adoption of New York’s e-prescribing mandate. The estimated specification includes state and calendar quarter fixed effects as well as the following variables interacted with quarter indicators: share white, log of 2009 population, share with a college degree, share ages 25-44. We also condition on the following state policy variables: any PDMP, “must access” PDMP, pain clinic regulations, medical marijuana law, legal and operational medical marijuana dispensaries, and prescribing limits. Regression is weighted by population. The estimates reported in the figure are the coefficients on the New York indicator interacted with quarter indicators and are normalized to 0 in 2016q1.

We next turn to whether overdose death rates also responded to the mandate. An e-prescribing mandate may affect overdoses due to reduced exposure to opioids overall, but other mechanisms are also possible. For example, the mandate may permit physicians to better target opioids to those less likely to misuse them, based on their prescription history. It could also deter fraud and fraudulent prescriptions may be especially prone to misuse. Thus, even for a given reduction in supply, a mandate could have a disproportionately large effect.

4.3. Overdose Event Study Results

We first study natural and semi-synthetic opioid overdoses (T40.2) per 100,000 using our event study specification in Figure 4. We observe little evidence of any pre-existing trends dating back to the beginning of the sample period. As discussed above, we are controlling for “must access” PDMPs so the estimates in Figure 4 after adoption of this policy (represented by the dashed vertical line) reflect the change in New York’s overdose rate relative to the expected change given the average effect (in the sample) of a “must access” PDMP.

Figure 4: Event Study Estimates for Natural and Semi-Synthetic Opioid Overdoses.

Notes: N=416. 95% confidence intervals estimated using Ferman and Pinto (2019) which accounts for within-unit clustering and heteroskedasticity given only one treated unit. Outcome in Panel A is the number of natural and semi-synthetic opioid overdoses (T40.2) per 100,000 people. Outcome in Panel B is the number of natural and semi-synthetic opioid overdoses per 100,000 people which do not also involve heroin or synthetic opioids. The dotted vertical line signifies New York’s adoption of a “must access” PDMP. The solid vertical line represents the adoption of New York’s e-prescribing mandate. The estimated specification includes state and calendar quarter fixed effects as well as the following variables interacted with quarter indicators: share white, log of 2009 population, share with a college degree, share ages 25-44. We also condition on the following state policy variables: any PDMP, “must access” PDMP, pain clinic regulations, medical marijuana law, legal and operational medical marijuana dispensaries, and prescribing limits. Regression is weighted by population. The estimates reported in the figure are the coefficients on the New York indicator interacted with quarter indicators and are normalized to 0 in 2016q1.

Despite the challenge of distinguishing effects of the “must access” PDMP from the e-prescribing mandate, the results do not suggest any confounding effects given the lack of differential movements prior to the mandate. We showed earlier that the pre-mandate period is characterized by an increase in e-prescribing rates in preparation for the mandate, but there is also little evidence that this trend is independently affecting overdoses. The timing of this reduction strongly suggests that it is a consequence of the mandate and not a lagged effect of “must access” adoption or other factors. Over time, we observe some evidence of further relative reductions in overdoses.

We report difference-in-differences estimates throughout this section in Table 2. Panel A includes time-varying covariates except for policy variables; Panel B includes the policy variables. For all natural and semi-synthetic opioids, we estimate an average reduction of 0.3 overdoses per 100,000 people. When we add other policy controls (as in Figure 4), this estimate is unaffected. These estimates are statistically significant from zero at the 1% level and imply a 22% reduction in the rate of overdoses involving natural and semi-synthetic opioids.²⁵ Despite evaluating a policy adopted by a single state, the 95% confidence intervals are tight. We can statistically reject a reduction in overdoses smaller than 0.26 per 100,000 (and larger than 0.44).²⁶

Table 2:

Difference-in-Differences Estimates

A: Baseline Controls
Natural/Semisynthetic Opioids	Natural/Semisynthetic Opioids Only	Opioids T40.2-T40.4	Opioids T40.0-T40.4, T40.6
−0.31***	−0.19***	−1.53***	−1.18***
[−0.44, −0.26]	[−0.27, −0.16]	[−2.42, −0.12]	[−1.59, −0.40]
B: Control for Policy Variables
−0.31***	−0.23***	−1.67***	−1.11***
[−0.41, −0.22]	[−0.29, −0.16]	[−2.39, −0.71]	[−1.42, −0.63]
C: Control for OxyContin Misuse
−0.32***	−0.30***	−0.64***	−0.55***
[−0.42, −0.23]	[−0.37, −0.23]	[−1.10, −0.23]	[−0.74, −0.32]

Notes:

^***1%

^**5%

^*10% Statistical Significance. N=195. 95% Confidence Intervals generated using Ferman and Pinto (2019) and are not symmetric. Each estimate represents the coefficient on the interaction of New York and post-adoption of the mandate. Outcome is overdoses per 100,000 people. Natural and semisynthetic opioids are defined by T40.2. Opioids are defined by codes T40.2-T40.4. In the last column, we also include T40.0, T40.1, and T40.6. The estimated specification includes state and calendar quarter fixed effects as well as the following variables interacted with quarter indicators: share white, log of 2009 population, share with a college degree, share ages 25-44. In Panel B, we also condition on the following state policy variables: any PDMP, “must access” PDMP, pain clinic regulations, medical marijuana law, legal and operational medical marijuana dispensaries, and prescribing limits. In Panel C, we add the pre-reformulation non-medical OxyContin use variable interacted with quarter time dummies. Regression is weighted by population. Time period is 2014-2017. We drop 2016q1 since the policy was adopted in this period.

In Panel B of Figure 4, we select on overdoses involving natural and semi-synthetic opioids but not also synthetic opioids or heroin. A concern of our analysis is whether the fentanyl crisis could be disproportionately affecting the comparison states relative to New York. Excluding overdoses involving heroin or fentanyl should reduce concerns about any confounders related to the fentanyl crisis. The pattern of estimates is similar.

The difference-in-differences estimates (Table 2, Column 2) are smaller in magnitude than the estimates when the outcome includes all natural/semi-synthetic opioid overdoses since we are excluding overdoses likely impacted by the mandate. However, the estimates still suggest large and statistically significant effects.

To further test for illicit opioids as a confounder, we include the non-medical OxyContin misuse rate used in Alpert et al. (2018) interacted with time indicators as controls. This variable, which was constructed using the 2004-2009 National Survey on Drug Use and Health, was found to strongly predict the rise in heroin and synthetic opioid overdoses after the reformulation of OxyContin in 2010. We include this variable and permit it have a differential effect in each time period to account for the possible confounding effects of the rise in demand for illicit opioids for reasons unrelated to New York’s policies. The results – which are equivalent to those shown in Figure 4 (Panel A) in terms of outcome and specification – are presented in Appendix Figure 5. The estimates are similar when these additional controls are included.

We include the corresponding difference-in-differences estimates in Table 2, Panel C. The estimates for both natural/semi-synthetic opioid and natural/semi-synthetic opioid only overdoses are generally unaffected by the inclusion of these controls, suggesting that these outcome measures are robust to concerns about the fentanyl crisis.

Next, we study broader measures of opioid overdoses. As we include more illicit opioids, we note that it becomes less clear whether we should expect the negative effects on overdoses to remain. First, we study T40.2-T40.4, which is often defined as a measure of overdoses involving “prescription opioids,” but also includes deaths due to illicitly-manufactured fentanyl. Event study estimates are presented in Figure 5, Panel A. The trajectory of the estimates is similar to those observed above in Figure 4, though the magnitudes are larger. The results imply that the mandate reduced opioid overdose rates by 33%.

Figure 5: Event Study Estimates for Broader Measures of Overdoses.

Notes: N=416. 95% confidence intervals estimated using Ferman and Pinto (2019) which accounts for within-unit clustering and heteroskedasticity given only one treated unit. The outcome in Panel A is the number of opioid overdoses per 100,000 people using codes T40.0-T40.2. Panel B uses T40.0-T40.4 plus T40.6. The dotted vertical line signifies New York’s adoption of a “must access” PDMP. The solid vertical line represents the adoption of New York’s e-prescribing mandate. The estimated specification includes state and calendar quarter fixed effects as well as the following variables interacted with quarter indicators: share white, log of 2009 population, share with a college degree, share ages 25-44. We also condition on the following state policy variables: any PDMP, “must access” PDMP, pain clinic regulations, medical marijuana law, legal and operational medical marijuana dispensaries, and prescribing limits. Regression is weighted by population. The estimates reported in the figure are the coefficients on te New York indicator interacted with quarter indicators and are normalized to 0 in 2016q1.

We broaden this outcome measure even further in Panel B by including T40.0 (opium), T40.1 (heroin), and T40.6 (unspecified narcotics). Again, the event study looks similar. Our inclusion of these overdose deaths, especially overdoses involving unspecified narcotics (which might be natural and semi-synthetic opioids) is primarily due to concerns about under-reporting. The similarity of the results suggests that there was not a systematic change in reporting quality at the time of the e-prescribing mandate.

We summarize Figure 5 with difference-in-differences estimates in Table 2. For both outcomes, we estimate large and statistically significant reductions, though including the broader measures of opioids widens the confidence intervals considerably. Conditioning on policy variables in Panel B does not appear to have much impact on the estimates. However, including the non-medical OxyContin misuse variables noticeably decreases the magnitudes of the effects, suggesting that these broader measures are less robust to systematic changes in illicit opioid markets over this time period. This sensitivity reinforces our decision to focus on natural and semi-synthetic opioids, though it is worth noting that the implied effects for two of the broader opioid measures – even when accounting for differential growth in illicit markets – are statistically different from zero and larger in magnitude than the effects on just natural and semi-synthetic opioids. This suggests that the natural/semi-synthetic opioid results may not fully encapsulate the effects of the mandate.

The event study results presented in this section permit us to study the timing of the response to the mandate. The timing of the effect may be surprising since we find evidence of an immediate effect. The effect generally grows over time which suggests even larger lagged effects. A small immediate effect would be consistent with reduced supply of abusable drugs lowering overdose propensities in the population while the lagged effects include the additional mechanism of reduced exposure over a longer time period.

4.4. Heroin and Synthetic Opioids

In this section, we further consider the role and responsiveness of illicit opioid deatlas. In Figure 6, we examine heroin overdoses that do not also involve any other type of opioid (see Panel A). We observe no evidence of a reduction in heroin overdoses. In Panel B, we study synthetic opioid deaths that do not also involve heroin or natural/semi-synthetic opioids. Of course, synthetic opioids can be prescribed so they could be directly affected by the mandate. We observe less evidence (relative to natural and semi-synthetic opioid overdose deaths) of a reduction in synthetic opioid overdoses, at least until the final two quarters. The fact that reductions are primarily associated with natural and semi-synthetic opioids and not heroin or synthetic opioids strongly suggests that the estimates represent the effects of the mandate and not confounding overdose trends. In addition, these results also suggest little evidence of substitution to illicit opioids.

Figure 6: Event Study Estimates for Heroin and Synthetic Opioid Overdoses.

Notes: N=416. 95% confidence intervals estimated using Ferman and Pinto (2019) which accounts for within-unit clustering and heteroskedasticity given only one treated unit. The outcome in Panel A is the number of heroin overdoses per 100,000 people excluding deaths also involving any other type of opioid. The outcome in Panel B is the number of synthetic opioid overdoses per 100,000 people excluding deaths also involving heroin or natural/semi-synthetic opioids. The dotted vertical line signifies New York’s adoption of a “must access” PDMP. The solid vertical line represents the adoption of New York’s e-prescribing mandate. The estimated specification includes state and calendar quarter fixed effects as well as the following variables interacted with quarter indicators: share white, log of 2009 population, share with a college degree, share ages 25-44. We also condition on the following state policy variables: any PDMP, “must access” PDMP, pain clinic regulations, medical marijuana law, legal and operational medical marijuana dispensaries, and prescribing limits. Regression is weighted by population. The estimates reported in the figure are the coefficients on the New York indicator interacted with quarter indicators and are normalized to 0 in 2016q1.

In Appendix Figure 6, we replicate these event studies while accounting for the effects of pre-reformulation non-medical OxyContin use rates. For these outcomes, we observe more sensitivity (relative to natural/semi-synthetic opioids) of the estimates to the inclusion of these variables. However, our primary conclusions are generally unchanged by including these controls.

4.5. Robustness Checks

4.5.1. Functional Form

We now address additional concerns about the causal nature of our results. First, we examine whether estimating the specification in levels is driving the results. We replicate our Figure 4 (Panel A) results, except that we study the log of the natural and semi-synthetic opioid overdose rate to estimate proportional effects. We present these estimates in Appendix Figure 7. The results are similar and imply comparable level effects.

4.5.2. Other Policies in New York

In Appendix Figure 8A, we exclude the policy controls. The results for natural and semi-synthetic opioid deaths are not meaningfully different. We observe some evidence of a relative reduction in overdoses after the “must access” PDMP adoption, consistent with what we observed in the raw trends (above in Figure 2). This reduction, however, is followed by a gradual increase in overdoses prior to the mandate. After the e-prescribing mandate is implemented, we observe a sharp decrease in overdoses. Overall, our results appear robust to whether we condition on other policy variables.

We also include results for our measure of opioid supply in Appendix Figure 8B since we might expect some of the policies to more directly impact supply than overdoses. We estimate similar effects for this outcome whether we condition or do not condition on additional policy variables. The similarity in results is partially due to the lack of impact of some of these other policies on measures such as opioid supply. It is also partially due to the similar policy landscapes – except for the e-prescribing mandate – in New York and the comparison states. For example, ten of the twelve comparison states adopt prescribing limits during the sample period, usually after New York’s policy. If prescribing limits had meaningful effects on opioid supply or overdoses, then we would expect the gap between New York and the comparison group to close or even disappear by the end of our sample period. Instead, we observe persistent effects.

As an additional test, we focus more directly on prescribing limits.²⁷ In Appendix Figure 9, we include an additional indicator for 7-day prescribing limits since states differ in terms of how restrictive their limits are. The results are similar. We provide results for natural and semi-synthetic opioid overdoses (Panel A) and for opioid supply (Panel B). While prescribing limits are different across states and these indicators may not capture specifics about New York’s policy, it is notable that the estimated effect sizes are not attenuated when prescribing limits are accounted for.

We also independently analyze the mortality effects of prescribing limit regulations. We regress natural/semi-synthetic opioid overdoses per 100,000 on state fixed effects, calendar quarter fixed effects, a set of time-relative-to-adoption fixed effects, and our full set of covariates. The time-relative-to-adoption variables relate to the adoption of prescribing limits. We also select on the same states as the main analysis while excluding New York for the sake of understanding whether these policies have evidence of any reductions in overdoses in other states. While there are differences in terms of the number of days supplied permitted by these policies, the typical law in our sample is 7-days, the same as New York’s.

The results are presented in Appendix Figure 10. There is no evidence of overdose reductions after the adoption of prescribing limits. In fact, there is some evidence that overdose rates increase. Consequently, we are even more confident that New York’s prescribing limits policy is not driving the main estimates of the paper.

In addition, we discussed other policies adopted in New York above. New York adopted a naloxone standing order in July 2014. In 2014, New York also began widespread training of law enforcement to administer naloxone. Our event study analyses do not suggest that these policies, adopted a couple years prior to the e-prescribing mandate, are confounding our main results.

We also study how treatment access changed over time using data from the National Survey of Substance Abuse Treatment Services (N-SSATS). We construct annual state-level measures of the number of substance abuse treatment facilities and the number of facilities operating an opioid treatment program per 100,000. We present annual event study estimates in Appendix Figure 11. There is little evidence of an increase in treatment access which could independently explain the reduction in overdoses. In fact, there is some evidence of a modest drop in opioid treatment programs beginning in 2016. This reduction could potentially be a result of diminished demand due to the effects of the mandate.

4.5.3. Policies in Other States

We have already discussed the similarity of policies adopted in New York and the comparison states. Both New Jersey (November 1, 2015) and Connecticut (October 1, 2015) implemented must access PDMPs near the end of 2015, within months of the implementation of New York’s e-prescribing mandate. One concern is that these policies independently affected opioid access for New York residents, especially those near the border. To test for this possibility, we drop counties in New York City and those bordering Connecticut or New Jersey²⁸ prior to constructing our opioid overdose rate for the state of New York. We then replicate Figure 4. The estimates are presented in Appendix Figure 12 and are generally stronger than the main results, suggesting that policy spillovers from other states are not driving our results.

4.5.4. Comparison States

It is difficult to find appropriate comparison states when studying opioid-related outcomes in recent years. We selected geographically proximate Census Divisions for reasons discussed above. The appropriateness of this comparison group is partially tested by examining the pre-treatment trends in our event study analyses. We only observe differential effects at the time of the mandate despite dramatic rises in overdoses during the sample period. For example, the fentanyl crisis began in 2014 followed by an unprecedented escalation prior to 2016 (as shown previously in Appendix Figure 1). However, our results do not suggest a differential effect before adoption of the e-prescribing mandate (overall or for synthetic opioids specifically), suggesting that the comparison group is appropriately accounting for these secular trends.

As our first alternate comparison group, we make a simple modification to our main comparison group by dropping Wisconsin, the one state in our control group which did not expand Medicaid. We replicate Figure 4A in Appendix Figure 13A. The pattern of estimates is similar.

Instead of restricting ourselves to Census divisions, we can alternatively select states east of the Mississippi River that expanded Medicaid under the ACA as comparison states. These criteria share the properties that are likely most critical for creating appropriate comparison groups. The differences with the main analysis are the additions of Delaware, the District of Columbia, Kentucky, Maryland, Virginia, and West Virginia and the removal of Wisconsin.

We present these results in Appendix Figure 13B. When we use this alternative comparison group, we see similar evidence. In fact, there is even stronger evidence that the differential mortality reduction began immediately upon implementation of the mandate. This immediate reduction is followed by further decreases for about a year before levelling off.

In addition, we use all states east of the Mississippi River as a comparison group. Despite concerns about the comparability of states in the south to New York (as shown above in Appendix Figure 3), we present results in Appendix Figure 13C. We do, in fact, observe evidence of a slight negative trend prior to the adoption of the mandate (followed by a one-quarter increase immediately prior to adoption). However, we still see evidence of a larger drop upon implementation, consistent with our main findings. These results suggest that the main findings of this paper are not driven by the specific choices of the comparison group.

4.5.5. Synthetic Control Results

In our primary analyses, we were careful to select appropriate comparison groups based on general knowledge of how the opioid crisis has evolved throughout the country. As an alternative approach, we implement the synthetic control method (Abadie et al., 2010; Abadie, forthcoming), which uses a data-driven approach to construct counterfactual outcomes. Details about the implementation of this approach and the inference procedure are provided in Appendix B. For inference, we construct a test statistic (explained in Appendix B) and compare it to placebo test statistics generated by estimating synthetic controls for all states and then constructing the same test statistic. Synthetic control weights are provided in Appendix Table B.1.

We plot the outcomes for New York along with the synthetic controls in Appendix Figure B.1. We show the two trends (Panel A) as well as the differences (Panel B) for opioid overdose deaths. We observe only small differences in the pre-period, followed by a large reduction in New York after the mandate. We provide the distribution of the test statistic in Appendix Figure B.2. New York experienced the largest (scaled) reduction in overdoses among all states. Appendix Figure B.3 provides the absolute value of the test statistic. New York ranks seventh. Overall, this section and the previous section suggest that the main conclusions of this paper are not driven by the choice of any specific comparison group.

4.5.6. Opioid Overdose Reporting

Ruhm (2017, 2018, 2019) has raised and analyzed concerns about underreporting of opioid overdoses in death certificate data, and states vary in terms of their reporting quality (Scholl, 2019). These cross-state differences could potentially imply that we would understate the causal effect of the mandate since we are missing some overdoses that were affected by the policy. This possibility assumes that the underreporting remains fixed by state over time.

In our context, the concern is that New York and the comparison states experienced differential changes in reporting quality at the time of mandate was implemented. The event study framework reduces concerns about this possibility since any systematic changes would have to occur at the time of the mandate. To test for this possibility, we study the rate of overdoses involving code T50.9 (unspecified drugs) but no other drug is listed. These results are provided in Appendix Figure 14. We do not observe systematic movements of overdoses involving only T50.9 for most of the period after adoption of the must access PDMP provision. In fact, the point estimates for most of the post-mandate period are negative, implying that the main results are not driven by a differential decline in accurate reporting in New York after adoption of the mandate (which would imply relative increases in unspecified overdoses).

4.6. Discussion of Results

Our results suggest large mortality effects and modest impacts on total opioid supply. As noted above, it is unnecessary to observe large reductions in opioid distribution to explain large changes in overdoses since the mandate may permit better targeting of the opioid supply through changes in prescriber behavior and less fraud. For some patients and prescribers, the mandate may even lead to increases in opioid prescribing given the improvement in information. For example, Böckerman et al. (2019) find that electronic prescribing in Finland increased benzodiazepine use for some populations (while having no effect in aggregate).

We compare our results to other supply-side interventions in the literature with a focus on “must access” PDMPs. Bao et al. (2018) estimate that must access PDMPs lead to reductions in overlapping prescriptions, having 3+ prescribers, and other metrics of problematic prescribing. Buchmueller and Carey (2018) find reductions for a large set of inappropriate prescribing metrics. Patrick et al. (2016) estimate substantial reductions in opioid mortality upon adoption of a PDMP with evidence that features such as the frequency in which the system updates predicts even larger effects. Dowell et al. (2016) study the joint adoption of pain clinic laws and PDMPs, estimating reductions in opioid supply by 8% and decreases in opioid deaths by 12%. Haffajee et al. (2018) estimate that must access PDMPs reduce morphine equivalent doses per capita by 10-18% among a commercially-insured population. Meinhofer (2018) estimates reductions in opioid quantities by 9% and decreases in opioid deatlas by 9% due to must access PDMP adoption.

Most recently, Kim (2021) examines must access PDMPs and finds some evidence of modest reductions in opioid supply (though the analysis cannot reject the absence of a reduction). However, there is much stronger evidence of reductions in prescription opioid mortality on the order of 23-26%.²⁹ As in our context, must access PDMPs can reduce mortality even with limited effects on total opioid supply.

Our results imply that New York’s electronic prescribing mandate decreased opioid supply by 6% and overdoses involving natural and semi-synthetic opioids by 22%. Thus, the reduction in opioid supply is comparable to estimates using similar data sources (i.e., ARCOS) in the must access PDMP literature. The estimated reductions in overdose death rates due to the mandate are close to the top of the distribution of magnitudes observed in the PDMP literature. E-prescribing mandates mechanically force prescribers to observe patient histories, which would suggest one reason that the overdose reductions are larger. They also directly diminish opportunities for fraud, reducing diversion.

We find little evidence of substitution to illicit opioids in response to the mandate, which differs from findings in the PDMP literature (Meinhofer, 2018; Kim, 2021). New York was less exposed to the reformulation of OxyContin than comparison states (refer back to Table 1) which recent evidence suggests was strongly predictive of the development of an illicit opioid market (Powell and Pacula, 2021).³⁰ Mulligan (2020) introduces a model in which supply-side interventions may have different effects based on the existing size of illicit markets. It may be the case that states with more developed illicit opioid markets will experience greater substitution to these markets when their mandates take effect.

5. Conclusion

We provide some of the first quasi-experimental evidence of how an e-prescribing mandate affects opioid-related overdoses. We examine the short-term consequences of an e-prescribing mandate in New York, the first state to adopt and enforce such a policy. We find that New York, after adopting the e-prescribing mandate, experienced a decline in opioid-related overdoses, primarily those involving natural and semi-synthetic opioids, relative to comparison states. We also observe a relative decline in statewide opioid supply.

We do not observe strong evidence of a corresponding increase in overdoses involving illicit opioids: the mandate appears to have reduced prescription opioid harms, as measured by fatal overdoses, without comparable substitution to illicit markets. There are legitimate concerns about using supply-side interventions to curb the opioid crisis, but the New York e-prescribing mandate does not appear to have incurred the unintended consequences associated with other policies targeting access to opioids. As additional states implement this type of policy, it will be possible to observe whether this quality is unique to New York for the reasons discussed in the previous section.

New York’s law relates to both controlled and non-controlled substances, which is unusual for these types of policies. We do not expect this feature to alter its impact in either direction given that, nationally, non-controlled substances are already e-prescribed at such high rates. We also note that New York’s policy was added to an existing, though relatively new, “must access” PDMP. It is possible that e-prescribing mandates interact with PDMPs in a manner to disproportionately impact opioid-related harms given that both potentially improve information flow to prescribers. PDMPs help physicians make more informed prescribing decisions by reviewing patients’ controlled substance prescription history. E-prescribing mandates complement these efforts. Additionally, the size of existing illicit opioid markets may also partially determine the magnitude of substitution to heroin and fentanyl. Understanding how these mandates interact with existing policy and market environments will be important for future research.

Overall, the evidence suggests that e-prescribing mandates offer potential for reducing opioid-related overdose rates. We consider a range of alternative explanations such as other policies impacting overdose deatlas, policies in neighboring states, and illicit opioid market growth. We find little evidence that these alternative explanations can explain the main results of the paper. However, this paper analyzes the experience in just one state and it is impossible to rule out all other possible reasons that New York experienced a reduction in overdose rates relative to the counterfactual at that time of mandate adoption. With only one treated state, it is also difficult to understand whether state-level factors make these mandates more or less effective for the purposes of predicting the impacts of the implementation of future e-prescribing mandates.

While prior evidence has found overdose reductions associated with “must access” PDMPs, e-prescribing mandates can further improve use of information when prescribing controlled substances. In addition, fraud is considered an important pathway for diversion and misuse of opioids, and e-prescribing should substantially reduce the scope for fraud, well beyond the ability of many other types of opioid-specific interventions. There is little experimental evidence of the importance of fraud in explaining opioid-related overdose rates, though descriptive evidence (Inciardi et al., 2009) as well as anecdotal evidence of large crackdowns on fraudulent prescriptions suggests that the scope is potentially large. Future work should try to isolate the mechanisms driving the reductions observed this paper. However, it is notable that we are finding large effects for a policy which most directly minimizes the opportunities for certain types of fraud.

Highlights.

• New York became first state with an enforced electronic prescribing mandate in 2016

• Most states have since adopted this policy or will soon enact a mandate

• There is little evidence about impacts of these mandates on overdose death rates

• We use a difference-in-differences design to compare New York to comparison states

• We estimate that the mandate reduced prescription opioid overdoses 22%