Participants

Participants were ≥18 years of age, prescribed OPRs exclusively for CNCP for ≥3 months from 2013–2015, and able to communicate in English. Potential participants were identified through patient registries maintained by each clinic in the San Francisco Health Network (see Fig 1). Providers were contacted to obtain permission to contact patients. Interested patients were scheduled for an in-person visit, whereupon the historical reconstruction was completed. Participants were compensated $75 for their time. Following this visit, staff blinded to interview data conducted chart abstractions.

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Fig 1. Recruitment flow chart.

https://doi.org/10.1371/journal.pone.0232538.g001

Historical reconstruction procedures

At the study visit, the interviewer first collected demographic and lifetime substance use data. The historical reconstruction involved construction and visual display of a personal timeline from January 1, 2012, to the interview date (2017 or 2018) using major autobiographical landmarks (e.g., marriage, divorce, deaths, incarceration, housing transitions) as well as societal events (e.g., natural disasters, sporting outcomes, local news) relevant to each participant. The personal timeline was used to provide cues to facilitate more comprehensive and accurate recall of relevant events. [16] Measures using autobiographical landmark methods have been shown to be valid and reliable in assessing alcohol consumption. [17, 18] This visually displayed personal timeline served as a foundation for the reconstruction and dating of historical data collection.

To obtain historical data on heroin and non-prescribed OPR use, we modified a structured interview procedure from the Lifetime Drinking History interview and the Lifetime Drug Use Questionnaire, [19, 20] which construct substance use patterns over an entire lifetime in terms of different phases of use, defined by quantity and frequency. These phases are defined by the interviewee and begin with onset of regular substance use and end with current patterns of use, honing in on the dates when use patterns change and frequency of use within each distinct phase. These interview methods have been shown to have strong validity and reliability in retrospective assessment of substance use among multiple populations, including strong correlations with prospective measures, [21] highly significant test-retest correlations, [17–19, 22] and agreement between subject-collateral reports, [23] for up to 13 years in the past. [21, 24] In our modified approach, we limited the recall period to 2012 onward and defined periods as quarters (i.e., January-March, etc.). For example, if a participant reported use of heroin or non-prescribed OPRs, the interviewer would start by assessing use at the beginning of 2012, using the established autobiographical landmarks and societal events as reference points (discussing sensitive behaviors that occurred in the more distant past allowed for building of rapport and less stigma early in the interview [25]). The interviewer would then move forward in time using the visually displayed personal timeline and probe for changes in use. Different phases of use were added to the visual display and documented by the interviewer.

Each quarter included a code for frequency of heroin, non-prescribed OPRs, methamphetamine, cocaine, and alcohol use. Use frequency was coded as none, once, intermittent, less than weekly or weekly, multiple times per week, and daily or nearly daily, which we collapsed to none, once or intermittently (“intermittently”), less than weekly to multiple times per week (“weekly”), and daily or nearly daily (“daily”) to mitigate sparsity. The interviewer also documented episodes of using medications to treat opioid use disorder (OUD).

Interviews were conducted by trained staff after shadowing at least five interviews and being shadowed in an additional three interviews. Sessions were audio-recorded for review, to ensure comprehensive data collection and quality assurance.

Chart abstraction procedures

Manual review of electronic medical charts of each patient was conducted after in-person visits by trained and blinded staff. The following data were abstracted by date from 2012 to study visit: opioid prescriptions (opioid type, dose, quantity per 30 days); exposure to opioid prescribing guideline interventions (naloxone prescription, controlled substance agreement, CSMP checks, yellow flag behaviors [such as ongoing illicit substance use] documented by the provider); and emergency department (ED) visits by opioid-relatedness. All abstracted charts were subsequently reviewed by the study physician to ensure accuracy and uniformity of coding.

Longitudinal analysis measures

To be consistent with the timescale on which the outcomes were collected, the primary exposure of prescribed OPR dose change and other relevant longitudinal covariates were mapped to quarters.

Prescribed OPR dose change for each patient-quarter of follow-up was defined by comparing a patient’s daily dose in MME across all prescriptions on the first day of each quarter to their dose on the last day of each quarter. A dose increase was defined as any increase from zero MMEs or a relative increase of at least 30% from a non-zero starting dose; a decrease was defined as any relative decrease of at least 30%, excluding discontinuation; a discontinuation was defined as any decrease for which the patient ended the quarter on zero MMEs. The 30% threshold was used to capture clinically meaningful dose changes and aligns with the CDC’s most conservative taper recommendations. [26]

Longitudinal covariates were mapped to quarters and defined using their maximum values over lookback periods of one to four quarters prior to each dose change exposure quarter, using the lookback period duration for each covariate that maximized the log-likelihood in an unadjusted continuation-ratio regression model relating each covariate to each outcome. Prior alcohol use frequency was defined as maximum frequency reported during the lookback period; prior cocaine or methamphetamine use, opioid-related ED visits, yellow flag behaviors, controlled substance agreements, CSMP checks, naloxone prescription, and self-reported medications for OUD were defined as presence or absence of these at any time during the lookback period. Past values of outcomes were also operationalized as covariates in the same way and defined as the maximum frequency reported during the lookback period.

See S1 Table for detailed definitions and data sources for all analysis measures.

Analysis design

Consistent estimation of the association between opioid dose change and subsequent use of heroin and non-prescribed OPRs was complicated by time-varying confounding, requiring specialized analysis methods. Specifically, providers may consider history of heroin and non-prescribed OPR use in prescribing OPRs, thus confounding our primary exposure by past values of the outcome. Similarly, other time-varying covariates (e.g., opioid-related ED visits) may both affect and be affected by the time-varying primary exposure. A repeated measures analysis adjusting for past outcomes and other covariates as time-varying confounders would not consistently estimate the overall effect of OPR dose changes, because the exposure effect would be partly mediated through covariates and past outcomes included as covariates in the analysis. [27]

To address this difficulty, we adopted a nested-cohorts approach, [28] in which effect estimates could be adjusted for baseline covariates only. In this set-up, follow-up for each participant began on January 1, 2012, or at entry into the San Francisco Health Network. The first year of follow-up was set aside for stable estimation of baseline dose and not used in defining nested cohorts. Subsequently, participants were included in multiple nested cohorts, one for each quarter, through the penultimate quarter. In each nested cohort, exposure and confounder history were fixed as of the cohort-defining baseline quarter. Follow-up for outcomes began in the next quarter and was censored at the first subsequent change in OPR dose or the final quarter of follow up for each participant. Outcomes occurring in the cohort-defining baseline quarter or the quarter of subsequent dose change were excluded to ensure that the exposure always preceded the outcome, and the outcome always preceded any subsequent dose changes. All nested cohorts were pooled for analysis.

Statistical analysis

The main analysis used logistic continuation-ratio models (CRMs) to estimate the overall association between prescribed OPR dose change and each outcome, frequency of heroin and non-prescribed OPR use. CRMs estimated the log odds of reporting more than a particular frequency of use, given that the patient reported at least that frequency. The model thus implicitly made three conditional comparisons: (1) any use versus no use, in the overall sample; (2) weekly or daily versus intermittent use, in the subset with at least intermittent use; and (3) daily versus weekly use, in the subset with at least weekly use. The standard CRM assumed that the odds ratios relating each exposure to the outcome were constant across these three conditional comparisons. Because Wald tests showed that this assumption did not hold, we also present extended CRMs that allow the odds ratios to vary across the three conditional comparisons.

The models also controlled for potential confounders with either established or hypothesized relationships with both changes in prescribed OPR dose and use of heroin or non-prescribed OPRs. [29–35] Potential confounders that were essentially fixed (e.g., demographics) were included as baseline covariates that remained static over the study period whereas potential confounders that changed over time were included as lagged covariates that could change over the study period. Specifically, each model controlled for continuous patient age; race/ethnicity (non-Hispanic white, non-Hispanic black, Hispanic, non-Hispanic other/mixed race); gender (male, female, transgender or other); education (less than high school, high school graduate, some college less than Bachelor’s, Bachelor’s degree or higher); any heroin or non-prescribed OPR use prior to baseline (defined as the first quarter included in the analysis); mean OPR dose during the first year of follow-up (i.e., the year prior to baseline); and OPR dose change in the quarter prior to the cohort-defining quarter, the initial OPR dose that was used to define the dose change in the cohort-defining quarter. Each model also controlled for the following lagged covariates: alcohol use frequency (collapsed to none, intermittently, weekly, and daily); any use of either cocaine or methamphetamine; any opioid-related ED visits; any yellow flag behavior; any controlled substance agreement; any CSMP check; first naloxone prescription; and any self-reported medications for OUD treatment. The models also controlled for a lagged value of heroin or non-prescribed OPR use frequency as a single ordinal variable. Finally, we controlled for cohort-defining quarter and quarter of cohort follow-up; as with age, these continuous factors were modeled using restricted cubic splines if indicated by the Bayesian Information Criterion, and otherwise as linear.

Censoring by subsequent changes in opioid dose could be affected by outcomes and other confounders measured after each nested-cohort baseline. To avoid selection bias [36] without adjusting away indirect effects of OPR dose changes, we used time-dependent stabilized inverse probability of retention weights (sIPRWs). [28] To estimate the sIPRWs, we used two pooled logistic regression (PLR) models for quarters to subsequent dose change, the first including only covariates observed at nested-cohort baseline, and the second including time-varying post-baseline as well as the same baseline covariates. We then obtained the estimated probabilities of the participant remaining uncensored through each quarter, and finally, following standard methods, [37] calculated the sIPRWs as the ratio of the first and second probability estimates for each quarter.

All models used cluster-robust standard errors to account for repeated observations by participant. Analyses were conducted using Stata 15; CRMs were estimated using the user-written gencrm package. [38]

Sensitivity analyses

To assess the sensitivity of results to the data-driven selection of covariate lookback periods, we generated models in which longitudinal covariate lookback periods were universally set to one or four quarters.

To assess the presence of interaction effects between prescribed OPR dose change and past illicit opioid use, we fit models that included interaction terms between prescribed OPR dose change and heroin use (for the heroin outcome model) or non-prescribed OPR use (for the non-prescribed OPR outcome model) prior to baseline. We also stratified each standard CRM model by heroin or non-prescribed OPR use prior to baseline.

In response to comments from a reviewer, we fit additional models that included any benzodiazepine prescription as a lagged covariate, with the optimal lookback period selected as described previously.

Strengths and limitations of the study

Our study design has both strengths and weaknesses. We conducted a blinded comparison of subjective (self-reported illicit substance use) and objective (chart prescription records) data, overcoming potential recall bias. Nonetheless, our comparisons of changes in OPR prescribing in one quarter and illicit substance use in subsequent quarters assumed accurate timing of recall in both self-report and medical charting that may have obscured actual associations. In addition, restrictions on access to California CSMP data and the limits of medical chart data restricted our ability to confirm dispensation or consumption of prescribed OPRs. While the historical reconstruction interview we utilized has strong validity and reliability, we adapted it for use in this study. Furthermore, our sample was limited to patients who were alive, able to be located, and willing to come to a visit; we may have missed the most vulnerable patients who were no longer living or were lost to follow up, and thus may have underestimated the impact of prescribing changes on patient care. Finally, results are observational and may not generalize beyond safety-net settings or settings without high levels of lifetime illicit substance use.

Findings in context

Our results are consistent with recent literature, including a model suggesting that interventions intended to improve OPR prescribing could at least temporarily increase opioid-related harms due to increased use of illicit opioids. [39] Moreover, an analysis of Medicaid beneficiaries in Vermont found that the rapidity of OPR discontinuation was associated with a higher likelihood of subsequent opioid-related emergency department visits and hospitalizations. [40] Thus, our results support the CDC’s recent warning to exercise caution when reducing and discontinuing OPRs, and to avoid when possible unilaterally or arbitrarily discontinuing OPRs outside of a collaborative care decision. [41] Although a patient-centered plan to reduce reliance upon OPRs may result in reduced pain and improved function and quality of life, [42] achieving such a goal in clinical practice can be challenging. Additional interventions such as training and education on tapering, multi-modal pain treatment and behavioral health therapy, and increased access to medications to treat OUD may help to manage at-risk patients. In fact, of the 237 patients in our sample who experienced at least one opioid discontinuation during follow-up, only five reported initiating medications for OUD treatment in the first year following discontinuation.

The association of increased OPR dose with more frequent heroin use among those who used heroin at least intermittently, as shown in Fig 2, is concordant with CDC Guideline recommendations to exercise caution when increasing OPR dose. Our data did not permit determination of the reason for this finding, which may have been due to worsening pain conditions resulting in supplemental heroin use, increasing tolerance to opioids, or exchange of prescribed OPRs for heroin. We did not identify an association between reduced OPR dose and more frequent heroin use, yet there was an association between reduced OPR dose and more frequent non-prescription OPR use that was inconsistent across conditional comparisons in the extended CRM.

Disclaimer

The findings and conclusions in this report are those of the authors and do not necessarily represent the official position of the Centers for Disease Control and Prevention, the Agency for Toxic Substances and Disease Registry, or of the San Francisco Department of Public Health.