Changes in Postpartum Opioid Prescribing After Implementation of State Opioid Prescribing Limits

Data Source and Sample

We used a commercial claims database (MarketScan; Merativ) that includes enrollment data and medical/pharmacy claims for a population of commercially insured people in the US younger than 65 years in all 50 states and Washington, DC. This study was deemed exempt by the Vanderbilt University institutional review board and followed all Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) analysis and reporting requirements for observational studies.

Using a previously validated algorithm and diagnosis and procedure codes, we identified all deliveries to enrollees between age 18 and 54 years in the commercial claims database between 2014 and 2021 (eAppendix and eTable 1 in Supplement 1).¹⁸ Data from 2013 were used as a lookback period for deliveries that occurred during the first quarter of 2014. We further identified deliveries by type (vaginal vs cesarean; eTable 2 in Supplement 1). For the relatively small number of deliveries (approximately 5%) that did not have a diagnosis or procedure code specifying vaginal vs cesarean delivery, we assumed that the deliveries were vaginal in the main analyses, as there are billing incentives for clinicians to code cesarean deliveries when they occur. Our results were robust to this decision. We also identified predelivery opioid status. Enrollees were considered opioid naive if they did not have an opioid prescription during the 3 months before delivery; all others were considered nonnaive.

We required enrollees to be continuously enrolled in insurance coverage 3 months before and 1 month after the date of delivery to measure previous opioid exposure and comorbid conditions. Multiple deliveries from the same person were included if they met the inclusion criteria for both pregnancies. We excluded deliveries that could not be attributed to a state by the employee geographic location provided in the commercial claims database.

Exposure and Outcomes

In line with previous studies, we defined opioid prescribing limits as those that restrict the quantity or dosage of opioid analgesics that can be prescribed to a patient at one time.^8–11,19 We included all laws that met this definition and were implemented between July 1, 2016, and January 1, 2019 (eTable 3 in Supplement 1). Using these criteria, 36 states implemented an opioid prescribing limit (ie, the treatment or exposure group) that applied to adults. The 12 states (plus Washington, DC) that had not implemented an opioid prescribing limit by January 1, 2019, and Nebraska (whose prescribing limit only applied to minors) composed the comparison group. The limit in Illinois was implemented in 2012, and Hawaii’s limit only applied to benzodiazepine and opioid coprescribing; both states were excluded from this analysis.

We identified all opioid analgesic prescriptions indicated for treating pain that were filled during the 30 days after delivery (eFigure 1 and eTable 4 in Supplement 1). The outcomes were the (1) total number of opioid prescriptions per delivery, (2) proportion of prescriptions with a supply greater than 7 days, (3) number of milligrams of morphine equivalent (MMEs) prescribed per delivery, and (4) number of MMEs per prescription. As most of these limits restricted each prescription to a 7-day supply of opioids, clinicians could compensate for the introduction of these limits by writing more prescriptions for shorter durations or by substituting more potent formulations of opioid pain relievers. The US Centers for Disease Control and Prevention’s Opioid and Oral MME Conversion were use to standardize the dosages of each opioid prescription.²⁰

We excluded monoproduct buprenorphine products (ie, Probuphine and Subutex) and buprenorphine-naloxone combination products, as these are commonly used to treat opioid use disorder rather than pain. We included any opioid analgesic prescriptions filled 3 days before and 30 days after the delivery date to account for scheduled deliveries for which opioids may be prescribed in advance.^9,21

Statistical Analysis

We conducted a staggered treatment timing DID analysis to compare changes in outcomes in states that implemented a limit with states that did not before and after the limit was implemented. A 2-way fixed-effects (TWFE) DID design assumes that the untreated states are a reasonable counterfactual for what would have happened in the treated states without a limit. Previous literature has suggested that using a TWFE DID with multiple adoption points may result in bias.²² To improve validity and decrease bias, we used the estimator proposed by Callaway & Sant’Anna,²³ as it can account for staggered implementation and group-varying and time-varying treatment effects when there are more than 5 treated states per period. This estimator extends the strict parallel trends assumption to include covariates; conditional on covariates, the comparison group represents a reasonable counterfactual for the treated group absent treatment. We implemented the doubly robust estimator, which uses stabilized inverse propensity treatment weighting regression in addition to the outcome regression. In a doubly robust analysis, only 1 of these regressions must be correctly specified to produce unbiased estimates.

The Callaway & Sant’Anna estimator does not have an option to conduct nonlinear regression models, so we used linear regression models with standard errors clustered at the state level (the level of intervention). Additionally, staggered adoption estimators allow researchers the choice of comparison groups; we included not yet and never treated states (ie, the not yet treated option) as the comparison group in the main analyses. Not yet treated states were more like the states that adopted an opioid prescribing limit in terms of opioid burden and willingness to implement such a limit.

In DID, confounders are things that covary with the outcome or exposure over time and by group.²⁴ Measurable confounders should be included as covariates in DID regression models to address the bias induced by them. In our study, we included a measure of substance use disorder prevalence in the population of interest, as increased rates of substance use disorder maybe associated with a state’s propensity to implement a prescribing limit and the amount of opioid pain relievers prescribed. Other covariates may be included to increase the precision of estimates. In our analysis, we include age in years at delivery, a pregnancy-related comorbidity score,²⁵ and the prevalence of comorbid mental health conditions to help with the precision of our estimates (eTable 4 in Supplement 1).

We also conducted 2 analyses to test the mechanisms through which changes in opioid prescribing may be occurring. First, we stratified our analysis by type of delivery. Opioid prescriptions for vaginal deliveries may be more responsive to prescribing limits, as these medications are generally not indicated for a vaginal delivery.²⁶ Additionally, we stratified our analyses by opioid-naive status as most limits only apply to opioid-naive patients. Thus, we would expect to see a clearer and stronger signal among deliveries to opioid-naive patients. Because some of the implementation dates had 5 or fewer treated units (2016 had 3, 2019 had 5) and the Callaway & Sant’Anna estimator may underperform in these situations, we also implemented 2 other staggered adoption estimators, a stacked regression DID estimator and the extended TWFE estimator proposed by Wooldridge,^27,28 to examine the robustness to our choice of staggered adoption estimator. In the stacked regression DID, we included the 2 years before and after the limit was implement in each subexperiment. For comparison with Callaway & Sant’Anna, we chose a linear regression model in the extended TWFE and stacked DID regression estimators.

We considered statistical significance to be at the α = .05 level. Cohort construction was done in SAS, version 3.81 (SAS Institute), and statistical analyses were conducted in R (version 2023.09.1+494; R Foundation).

DID Estimates

In covariate-adjusted DID regression analysis, the rate of opioid prescribing within the first 30 days postpartum decreased among all deliveries by 148.70 MMEs per delivery (95% CI, −657.97 to 360.57) in states that adopted an opioid prescribing limit compared with states that had not yet adopted such a limit (Table 2). This decline was not statistically significant. States that implemented a prescribing limit in 2017 experienced the greatest decline in MMEs per delivery (−323.94; 95% CI, −1266.39 to 618.52), while states that implemented in 2018 experienced an increase in MMEs per delivery (70.35; 95% CI, −61.15 to 200.86). Neither difference was statistically significant. Similarly, the MMEs per prescription declined by 104.41 MMEs (95% CI, −608.65 to 399.84) overall, in 2017 (−232.62; 95% CI, 1296.90–930.06), and in 2019 (−33.04; 95% CI, −93.68 to 27.59); none of these changes were different from 0.

Prescribers may have adjusted their opioid prescribing along other margins to be within new limits while maintaining patient access to opioid pain relievers. To be within day-supply constraints (how many states’ limits are defined), prescribers may have written more prescriptions for a shorter duration per delivery. However, we found no statistically significant change in the number of prescriptions per delivery (−0.06; 95% CI, −0.15 to 0.04) or the proportion of prescriptions with a greater than 7-day supply (−0.001; 95% CI, −0.03 to 0.03) (Table 3). These outcomes met the conditional parallel trends assumption (Table 3; eFigure 2 in Supplement 1).

Changes in prescribing by delivery type may be obscured by the average treatment effects. Postpartum opioid prescribing was higher among cesarean deliveries in all states with potentially more room for decreases. Conversely, the adoption of a limit may have alerted prescribers to the lack of indication for most vaginal deliveries. Postpartum opioid prescribing among cesarean deliveries declined after the adoption of a prescribing limit (−242.27; 95% CI, −1174.04 to 689.51) in states that adopted a limit compared with those that did not (Table 3). Declines in limit states were smaller among vaginal deliveries and not statistically significant (−90.45; 95% CI, −441.57 to 260.67).

Additionally, most limits only applied to patients receiving new opioid prescriptions. So, we might expect to see larger and more precisely estimated changes among opioid-naive enrollees. When we stratified by opioid naivete, we estimated nonstatistically significant declines in MMEs per delivery (−106.25; 95% CI, −595.83 to 383.32) and prescription (−124.31; 95% CI, −827.37 to 578.74) among opioid-naive patients in states that adopted a prescribing limit compared with states that did not. Caution is warranted in interpreting both results for opioid-naive patients, as neither outcome meets the parallel trends assumption (Table 3).

Robustness and Sensitivity Analyses

Unadjusted regression estimates reflected the same pattern of results as the covariate-adjusted estimates; the unadjusted regression estimates were roughly 20% smaller than the covariate-adjusted estimates (eTable 6 in Supplement 1). Finally, our unadjusted estimates using the extended TWFE and stacked DID estimators (−75.5 and −165.79 MMEs per delivery, respectively; eTable 7 in Supplement 1) were very similar to that produced by Callaway & Sant’Anna, providing evidence that our results are not sensitive to the estimator chosen.

Limitations

As is true with all observational study designs, our study had limitations. First, we used commercial insurance claims rather than Medicaid claims or an all-payer claims database; 40% of all deliveries are paid for by Medicaid, and pregnant people receiving Medicaid are more likely to fill an opioid prescription postpartum than pregnant people with commercial insurance.^14,30,31 Thus, these results may be an underestimate of the association of these limits with opioid prescribing in the population overall. This was echoed by a recent article that found reductions in opioid prescribing after a limit was implemented among Medicaid beneficiaries. Second, states implemented other policies around the same time to address the opioid crisis. To the extent that these policies were implemented in the same states at the same time as opioid prescribing limits, our analytic strategy cannot differentiate between these policies and an opioid prescribing limit. Third, we could not assess any pain-related outcomes that occurred as a result of these limits. Finally, our analyses relied on counterfactual assumptions that are not directly testable; the test used by Callaway & Sant’Anna estimator is indirect.