3

Setting the Stage

INTRODUCTION

This chapter provides background for a broad audience and lays out the committee’s approach and rationale for using the target trial emulation (TTE) framework to address the effect of prescribed opioid pharmacotherapy¹ on all-cause mortality and suicide mortality. In addition, it presents the common aspects of the study design applied across each of the emulated target trials² in the report.

TARGET TRIAL EMULATION FRAMEWORK

In line with the 2019 National Academies report, the current committee employed a TTE framework. A TTE framework is applied in the observational studies to mirror a randomized trial. Randomized controlled trials (RCTs) are experimental studies in which participants are randomly assigned, or randomized, to treatment strategies (Mansournia et al., 2017a). Randomization of a treatment minimizes confounding and assures balance across treatment groups (NASEM, 2019). While RCTs³ are the gold standard for assessing the causal effects of medical treatments, they often face practical, ethical, cost, and feasibility barriers to implementation. These include prohibitively high costs and time demands, ethical dilemmas around the random allocation to medications with potentially negative side effects, potential for mistreatment of historically vulnerable populations, and potentially small sample sizes in the case of rare medical disorders (Goldstein et al., 2018). At the same time, clinicians and policy makers also need to decide about medical treatments that are not amenable to study in RCTs and must utilize the best available evidence.

In the last three decades, notable progress has been made in estimating the causal effects of medical treatment beyond the confines of RCTs. Approaches that leverage observational data, or data from non-experimental studies (non-RCTs), to analyze the effects of these treatments in the most rigorous way possible are critical. One advance in the modern causal inference literature is the approach of designing an observational study to mimic a

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¹ The committee uses the term “pharmacotherapy” throughout the report instead of “medications,” “prescriptions,” or treatment, especially when referencing the committee’s analyses and results.

² The committee uses the terms “emulated target trial” and “study” synonymously when referring to the committee’s studies and corresponding analyses.

³ A key advantage of RCTs is protocol-based outcomes ascertainment, which is a limitation with observational studies. This ascertainment can help reduce bias due to misclassification of outcomes, exposure, and confounders.

hypothetical randomized experiment, or target trial. TTE is an approach that helps ensure the observational study compares realistic clinical treatment strategies, avoids biases related to mishandling time zero, and improves upon conventional methods to address baseline and time-varying confounding (Hernán et al., 2022; Hernán and Robins, 2016). TTE has played a role in rectifying historical discrepancies between observational and randomized results, as seen in instances such as estrogen replacement therapy and risk of cardiovascular disease (Hernán et al., 2008).

With the increasing availability of administrative and clinical health data, such as electronic health records (EHRs) and health insurance claims, there are growing interests in leveraging these observational data to conduct analyses to estimate causal effects. These are most useful in addressing critical medical and public health questions where RCT evidence is not feasible or available. These datasets can have the advantage of being readily available and have large sample sizes to study heterogeneity of effects (Hubbard et al., 2024). Although applying modern causal inference methods using EHR or administrative data may still result in biases due to the lack of randomization, evidence suggests that rigorously designed and conducted emulated trials can yield valid and actionable evidence when RCTs are unavailable (Wang et al., 2023). In a 2023 study by Wang and colleagues, 32 target trials, using observational data, emulated the design of 32 corresponding, high-quality RCTs. The effect estimates were similar between the two approaches, especially when the target trial design elements were closely matched with those in the RCTs (Wang et al., 2023). Thus, both RCTs and observational studies can facilitate causal inferences.

APPLICATION OF TARGET TRIAL EMULATION FRAMEWORK TO ADDRESS THE STATEMENT OF TASK

Recent literature has helped to establish how causal inference can inform clinical practice. In 2024, JAMA published a report outlining an approach to lay out when inferring causality using observational data (Dahabreh and Bibbins-Domingo, 2024). The use of causal language when describing these studies is crucial for effective communication in medical journals. The six core questions are the following:

• What is the causal question?
• What quantity would, if known (causal estimand or causal effect of interest), answer the causal question?
• What is the study design?
• What causal assumptions are being made?
• How can the observed data be used to answer the causal question in principle and in practice?
• Is a causal interpretation of the analyses tenable?

The authors state that adhering to this guidance can facilitate better communication between authors, reviewers, editors, and readers (Dahabreh and Bibbins-Domingo, 2024).

The committee applied the TTE framework, reflecting current best practices in the causal inference methodology field, and addressed the six questions. The approach included precise definitions of the causal objectives and effects, comparing clinically realistic treatment strategies, valid assignment of time zero, and thorough adjustment for baseline and time-varying confounding variables. By using the TTE framework, the committee intended to eliminate common structural biases common in observational studies, such as immortal time bias—which stems from utilizing post-baseline treatment information for treatment assignment—and selection bias, from analyzing prevalent users.

DEVELOPING THE CAUSAL RESEARCH QUESTIONS FROM THE STATEMENT OF TASK

The committee developed causal research questions to align with the four items in the statement of task:

1. the effect of opioid prescribing for pain, relative to alternative non-opioid pain treatments (study 1),
2. the effects of higher dosages relative to lower dosages of opioids (study 2),

3. the effect of co-prescribing a benzodiazepine among individuals already receiving opioids, relative to alternative treatments for anxiety and other indications for benzodiazepines (study 3), and
4. the effect of initiating opioids among individuals already taking benzodiazepines (study 1).

The committee combined tasks (a) and (d) and developed one causal research question (study 1). The committee interpreted both (a) and (d) as examining the effect of initiating opioids on mortality compared to those not initiating non-opioid pain pharmacotherapy. The committee interpreted task (d) as a subset of task (a) in that it further examined the effect of initiating opioids on mortality in those without and with a current benzodiazepine prescription. For task (b), the committee interpreted it as examining the effect of escalation dosage strategies on mortality (study 2). The committee considered two aspects of escalation: the starting, or initial, baseline dosage, and the trajectory, or speed at which dosage can increase over time. The committee interpreted task (c) (study 3) as examining the impact of initiating benzodiazepine pharmacotherapy co-prescribing versus alternative non-benzodiazepine pharmacotherapy on mortality among individuals already receiving long-term opioid pharmacotherapy. The benzodiazepine comparator group are those individuals with conditions, specifically anxiety and insomnia, that can also be treated with benzodiazepine pharmacotherapy.

For all studies, the committee did not include “chronic pain” in the causal question given challenges in its measurement and capture (potential underreporting of both pain and chronic pain diagnoses. Preliminary analysis indicated that 37.7 percent of eligible participants who were dispensed an opioid pharmacotherapy did not have a diagnosis code related to chronic pain as defined in Mayhew et al., 2019, and the term is not reflected in the statement of task. In the causal questions, the term “pain” is only used to specify the non-opioid pharmacotherapies included in study 1. Given the challenges in capturing pain and chronic pain, the committee assumed that most individuals who were dispensed an opioid prescription received it to manage pain. See also Chapter 1 for more details on committee’s rationale.

Causal Research Questions

The committee developed three causal research questions to reflect the statement of task:

Study 1: The Effect of Opioid Prescription on All-Cause Mortality, Including Suicide

Among veterans receiving care in the Veterans Health Administration (VHA) who were not consistently dispensed⁴ pain pharmacotherapy between 2007 and 2019, what is the effect of newly dispensed opioid versus non-opioid pain pharmacotherapy on all-cause mortality (primary outcome) and suicide mortality (secondary outcome) among those without and with current use of benzodiazepine pharmacotherapy within a 12-month follow-up period?

Study 2: The Effect of Prescribed Opioid Escalation on All-Cause Mortality, Including Suicide

Among veterans receiving care in the VHA newly dispensed full agonist⁵ opioid pharmacotherapy between 2007 and 2019, what is the effect of different initial opioid dosage and escalation strategies on all-cause mortality (primary outcome) and suicide mortality (secondary outcome) within a 12-month follow-up period?

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⁴ The committee notes differences in types of pharmacy data measures. Pharmacy data can be categorized into three measures: prescribed (prescriber submits a prescription to a pharmacy), filled (pharmacy completes the requested prescription), and dispensed (individual picks up/is mailed the prescription from the pharmacy). The committee used dispensed pharmacy data in its analyses.

⁵ There are two types of opioids: full and partial opioid agonists. Full agonists fully activate the mu receptors in the brain, enabling the opioid to have “full” effect, such as morphine, codeine, oxycodone, and fentanyl. Partial agonists also activate mu receptors in the brain but to a lesser degree, such as butorphanol or tapentadol.

Study 3: The Effect of Co-Prescribed Opioids and Benzodiazepines on All-Cause Mortality, Including Suicide

Among veterans receiving care in the VHA who were consistently dispensed opioid pharmacotherapy between 2007 and 2019, what is the effect of newly dispensed benzodiazepine versus alternative non-benzodiazepine pharmacotherapy for anxiety and other common indications for benzodiazepines on all-cause mortality (primary outcome) and suicide mortality (secondary outcome) within a 3-month follow-up period?

Causal Effect of Interest

The causal effects of interest are the per protocol effect and the intent-to-treat (ITT) effect. The per protocol effect corresponds to the effect of consistently following the assigned treatment strategy during follow-up. Modern causal inference methods enable estimation of per protocol effect without potential selection bias by conditioning the analysis on those who adhere fully to the treatment regimen during follow-up. The ITT effect, on the other hand, characterizes the effect of initiating the treatment strategy at baseline, irrespective of either cross-over to another exposure group or treatment discontinuation during follow-up. Valid estimation of both ITT effect and per protocol effect require adjustment for preinitiation variables to adjust for confounding related to initial treatment selection. The per protocol effect is as important as the ITT effect; otherwise, treatment strategies with substantial inconsistent use can misleadingly suggest that harmful medications are safe or effective interventions are ineffective.

Estimating the Causal Effects in Each of the Studies

In study 1, the committee conducted both per protocol effect (main) and ITT effect (secondary) analyses to provide a range of estimates capturing the effect of opioid pharmacotherapy—from initiation, without requiring continuous use, to fully adhering to the treatment strategy. The committee only estimated per protocol effect for study 2 (using the parametric G-formula), given that the interpretation of the statement of task was to address the causal effect of different dosage levels (consistent with per protocol effect) rather than to start at higher or lower dosages (consistent with ITT effect). The committee only estimated ITT effect for study 3, given that the research question, which reflects the statement of task, focused on the effect of newly dispensed benzodiazepine pharmacotherapy and not long-term use for those already receiving long-term opioid therapy. See Table 3-3 for definitions of how key methodological terminology were employed in this report. Valid estimation of the per protocol requires additional adjustments for post initiation variables related to treatment switching or discontinuation. The class of analytic approaches that have been developed to adjust for post initiation variables are called “G-methods.” Commonly used G-methods include inverse probability weighting (IPTW), parametric G-formula, and G-estimation (Naimi et al., 2017; Mansournia et al., 2017b).

Study Design

The design of each of the target trials was an active-comparator, new-user (Lund et al., 2015; Ray, 2003), retrospective cohort target trial emulation study (Hernán and Robins, 2016). Details on treatment strategies for each study, including defining the index start date (time zero), are described next.

Causal Assumptions

The committee reviewed the assumptions required for causal inference in the TTE approach and sought to adhere to these assumptions. The committee outlined the assumptions by Murray and colleagues (2020) and applied them in consideration of the designs of studies 1, 2, and 3. Table 3-1 reflects six key assumptions: conditional exchangeability for treatment, conditional exchangeability for adherence, conditional exchangeability for loss to follow-up/censoring, positivity, well-defined intervention, and correct model specification. The table also describes the efforts of the committee to address each assumption.

Regarding missingness in variables, the committee’s approach was to consider including all variables that were important to address the research question and keep the impact of missing data minimal. Based on descriptive

TABLE 3-1 Assumptions Required for Valid Causal Inference

SOURCE: Adapted from Murray et al., 2020.

statistics, missing data was minimal for continuous variables (≤40 percent) and the committee used missing indicator approach for categorical variables. Due to time and resource constraints, the committee chose the missing indicator method instead of complete case analysis (which generally introduces more bias). In addition, in determining causality, the committee considered the Bradford Hill criteria, which describe a set of conditions that increase confidence that an observational relationship is causal and include coherence with existing information (biologic plausibility, consistency of the association, time sequence, specificity, strength of the association, dose–response relationship, and study design) (Strom, 2021; Hill, 1965).

Leveraging the Observed Data to Answer the Causal Question

Studies 1 and 3 report death rates (per 100,000 person-years) and hazard ratios (HRs), which compare the risk of the outcome of interest (all-cause mortality and suicide mortality) in individuals initiating treatment versus those initiating treatment in the comparator group. In study 2, mortality risk (percentage) and risk ratios are reported. One risk ratio compares the outcome of interest in individuals with higher baseline dosages to low dosage at baseline; the other compares dosage escalation strategies to those with stable dosages during the follow-up period. In addition to the unadjusted estimates, weighted and adjusted estimates (using IPTW or parametric G-formula) were calculated to adjust for potential confounding. Confidence intervals (CIs) are also calculated and reported as an indicator of the uncertainty in these estimates (more details are provided later in the chapter).

Causal Interpretation

Limitations in Application of Results in Current and Future Clinical Practice

The committee notes that the statement of task specifically mandated the study period (2007–2019) to understand the implications of opioid treatment on mortality in veterans. This is in contrast with the more typical goal of clinical research, a forward-looking endeavor aiming to provide generalizable results that will inform clinical decisions (such as receiving opioid pharmacotherapy for acute and chronic pain). Instead, the statement of task directed the committee to delve into the past, serving as a historical exposition, analyzing the implications of past practices on mortality rates and overall health. Therefore, the findings of this report are not intended by the committee to be applicable to current practices or behaviors, including those of the VHA. Because of significant changes in opioid prescribing practices both within and outside of the VHA over the past 15 years (see Chapters 1 and 2), the distinction between a goal of estimating causal effects of past practices versus informing future practices was fundamental in the committee’s choices about the treatment patterns studied in the emulated trials. For example, the rapid dosage escalation strategy examined in study 2 reflected a clinical practice that is no longer common, especially given changes to clinical practice guidelines (VA/DoD, 2022, 2017).

In addition, these retrospective studies are inherently forensic, reflecting the effect of past care rather than being indicative of the mortality risks of current practices, particularly given the changes in opioid prescribing practices, the policy landscape, mental health care, and the nature of the opioid overdose epidemic in the intervening years. As reflected in the statement of task and expert perspectives, many unanswered questions remain about the causal effects of past opioid prescribing practices on mortality, especially in light of ecologic data indicating that U.S. opioid- and benzodiazepine-pharmacotherapy–related mortality has continued to climb in recent years.

In sum, the committee sought to address the statement of task in the least biased and most internally valid way, which calls on the committee to utilize best practices and recent advances in the modern causal inference literature, including TTE techniques. The committee applied this strategy to estimate causal effects of several key opioid and benzodiazepine pharmacotherapy prescribing decision points—to initiate opioid pharmacotherapy, increase opioid dosages over time, and co-prescribe opioid and benzodiazepine pharmacotherapies (Neuberger and Tallis, 1999). The committee is explicit in the causal objective, which can reduce ambiguity in the scientific question and errors in data analysis and clarify assumptions required for causal inference (Hernán, 2018). The committee adheres to best practices from the modern causal inference literature, including (1) designing the observational analysis to emulate a target trial and (2) selecting confounding adjustment variables using expert knowledge and clear articulation of the causal structure of the study question.

STUDY POPULATION, DATA SOURCES, AND MEDICATIONS OF INTEREST

For all target trials, the study population is defined as veterans receiving care in the VHA, and the study period is from January 1, 2007, to December 31, 2019.⁶ The earliest index date, or start date, was January 1, 2007. The latest possible index date was December 31, 2018, in studies 1 and 2 and October 1, 2019, in study 3. To assess exclusion and eligibility in the study and follow-up, data from 2006–2019 were pulled for analyses.

Data sources include the following:

VHA Corporate Data Warehouse (CDW): The CDW hosts data from across the VHA and includes health data, such as veteran insurance, inpatient and outpatient data, laboratory results, and prescription information (Culbreath and Gonsoulin, 2019).

United States Veterans Eligibility Trends and Statistics (USVETS): This Department of Veteran Affairs (VA) dataset includes data on U.S. veterans, such as military history, demographics, socioeconomics, and utilization of VA benefits and services, and is maintained and administered by the VA (VA, 2019).

National Death Index (NDI): This national dataset includes mortality data, from death certificates. The data include deaths from all 50 states, including Washington, DC, reflecting date and cause of death. The dataset is maintained by the National Center for Health Statistics (NCHS) (NCHS, 2024). NDI data for this project were obtained through the VA/Department of Defense Mortality Data Repository.

Centers for Medicare & Medicaid Services (CMS) Medicare Data: Through the VHA, Medicare and Medicaid Analysis Center provided access to Medicare Parts A, B, and C encounter data (which includes data on health conditions, defined by International Classification of Diseases [ICD] codes in the EHR) and Medicare Part D prescription drug events⁷ (commonly referred to as “claims”). The Medicare data supplemented prescription dispensing data and other study covariates unavailable from the VA, CDW or USVETS.

The data files were linked based on the combination of a veteran’s unique individual internal control number, Social Security number (SSN), and date of birth.

Westat, the subcontractor, had access to, and analyzed, the data available through the outlined sources. Only Westat had access to personally identifiable health information and personally identifiable information; all access to the data and analyses occurred within the VA firewall and data ecosystems. Final analytic aggregated results were removed from VA Informatics and Computing Infrastructure and provided to the committee only after privacy review. All approved data analysts on this study were also subject to a VA background check, maintained up-to-date human subjects training, and worked within Westat’s designated workspace on the server. The National Academies of Sciences, Engineering, and Medicine (the National Academies) Institutional Review Board approved the study. Results are presented in tables and figures in each of the chapters.

Medications Included in Each Study

Medication data are from either VHA EHRs or Medicare Part D pharmacy claims data. The pharmacy data can be categorized into three measures: prescribed (prescriber submits a prescription to a pharmacy), a fill (pharmacy completes the requested prescription), and dispensed (individual picks up/is mailed the prescription from the pharmacy). In the emulated target trials, based in retrospective observational data, treatment assignments were based on the observed dispensed prescription data. It is important to distinguish the measurability of prescription dispensing data from the measurability of that ingested by the individual. A dispensed prescription does not necessarily mean that the medication was consumed, since these medications are commonly prescribed to be taken “as needed.” For this study, a measure of individuals ingesting the prescription was not available in the dataset; the committee used prescription dispensing data as a proxy for medications ingested by the individual.

The committee included only systemically absorbed medications, specifically oral and sublingual medications and fentanyl patches. The committee excluded medications that are intravenously administered or are suppositories as these types are most commonly administered during end-of-life care or in inpatient settings. Additionally,

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⁶ Latest possible index date was December 31, 2018, in study 1 and 2 and October 1, 2019, in study 3.

⁷ For the purpose of this report, the committee refers to prescription drug events as “claims” (ResDAC, 2024).

medications to treat seizures (nasal midazolam and rectal diazepam) were excluded; however, individuals with a diagnosis of seizures were not excluded from the study sample.

Several medications were excluded because they were either not approved for use or not available during the study period. Propoxyphene was included in the medication list of all three studies until 2010, when it was removed from the market (FDA, 2018). Paregoric, an opioid analgesic administered orally, is not approved by the Food and Drug Administration (FDA) to treat pain (Drugs.com, 2024). Valdecoxib, a non-steroidal anti-inflammatory (NSAID), was removed from the market in 2005, and zuranalone, an antidepressant, was not approved until 2023. Quetiapine, an atypical antipsychotic medication used off label for insomnia, was excluded, as it is most frequently used for mental health conditions in the VA, has known harms, and a black box warning indicating increased mortality and suicidal ideation in specific populations (VA/DoD, 2019). These exclusions were applied during pre-index, baseline, and follow up. Table 3-2 includes the full list of medications included in each study. The committee grouped medications by drug class, based on FDA or VA drug class classification. Table 3-2 shows the drug classes, corresponding medications, and role in each target trial.

Medications Identified for Treatment Strategies

In identifying medications for treatment strategies (either the treatment or comparator groups) in each study, the committee relied on clinical expertise, FDA-approved indications, VA drug classifications, and existing literature with defined comparator groups (VA, 2024; Edinoff et al., 2021a,b; Brummett et al., 2019; Deeks, 2019; LiverTox, 2019; Ali et al., 2017; Park et al., 2015; Schug and Stannard, 2011; DailyMed, n.d.). Medications included in the study were not limited to those on the CMS or VA formularies. Also, note that Medicare covered benzodiazepines beginning in 2013 (CMS, 2012). The committee included the following pharmacotherapies in the studies (for more details, see Chapters 4, 5, and 6):

• For study 1, two target trials were emulated. Study 1a focused on veterans without a current benzodiazepine pharmacotherapy, and study 1b focused on veterans with current benzodiazepine pharmacotherapy. There were two treatment strategies: The treatment group in each study included individuals newly dispensed opioid pharmacotherapy, which included full agonists and some atypical opioids (tapentadol and butorphanol) due to their widespread use in pain treatment and impact within the pain neurotransmitter route. The comparator group in each study included individuals newly dispensed non-opioid medications with a primary (e.g., NSAIDs) or secondary indication for pain: tetracyclic antidepressants (TeCA), serotonin-norepinephrine reuptake inhibitors (SNRIs), muscle relaxers, and gabapentinoids.
• For study 2, two target trials were emulated. Study 2 evaluates two prescribing strategies for individuals newly dispensed opioid pharmacotherapy (full agonist). In study 2a, veterans received varying initial dosages (low, medium, high), and in study 2b, veterans received varying dosage escalation strategies (stable, slow, and fast).
• The study 3 treatment group included benzodiazepine pharmacotherapy. The study 3 comparator group, alternative non-benzodiazepine pharmacotherapy, included medications from the VA antidepressants class (indicated for anxiety) and insomnia medications. Study 3’s population of interest were those who were consistently dispensed opioid pharmacotherapy (full agonists and two atypical⁸ opioid pharmacotherapy, tapentadol and butorphanol).

Medications Identified as Covariates

The committee adjusted for several medications, some of which could be confounders, to improve covariate balance between treatment and comparator groups. Specifically, acetaminophen is a covariate in all the studies. It is not included as a non-opioid analgesic comparator group in study 1 because it is not an equal comparator to

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⁸ Study 3’s research question is focused on those consistently dispensed opioid pharmacotherapy, unlike in study 1 and study 2, which both focused on an opioid naïve population. Study 3 does not limit opioid pharmacotherapy to only full agonists.

opioid pharmacotherapy; individuals in either the treatment (opioid pharmacotherapy) or comparator group (nonopioid pain pharmacotherapy) could be dispensed acetaminophen as well to manage pain. In addition, migraine medications are included as a covariate in all the studies rather than an exposure, because they are used to manage pain specific to the pathophysiology of migraines, not general pain. The committee notes that some medications were included in the analyses differently to reflect the study’s research question. For example, in study 2, which is the only study focused on opioid dosage, the committee censored levo-alpha acetyl methadol (LAAM), buprenorphine, methadone for opioid use disorder (OUD), and naltrexone. Dosage calculations for these medications and application in the analyses were challenging given that the standard morphine milligram equivalent (MME)/day is lacking (e.g., buprenorphine and naltrexone (which is used to block effect of opioid analgesics)) and the availability of data in health records (the dose of methadone used for OUD is not recorded in VHA records). The committee adjusted for these pharmacotherapies in study 1, as they were considered possible confounders of the association between receiving opioid pharmacotherapy and mortality.

Medications Used as Exclusion Criteria

The committee excluded individuals with prescription for medications for opioid use disorder (MOUDs) at baseline because those prescribed an MOUD may not be opioid “naïve.” The committee acknowledges that medication naïvety is difficult to assess; in the context of this report, the phrase “opioid naïve” refers to an individual without a dispensed prescription for opioids or MOUD in the washout period. MOUDs refer to specific formulations of methadone (including liquid and diskette formulations typically used for OUD), LAAM (used primarily for OUD), and buprenorphine (FDA formulations approved for OUD). Naltrexone, an opioid antagonist (blocks opioid receptors) used for treating OUD and other conditions, was excluded at baseline for similar reasons. In addition, buprenorphine for pain was excluded at baseline from studies 1 and 2 and butorphanol and tapentadol were excluded from study 2 at baseline because none of these medications are used as first-line treatments for pain; thus, individuals dispensed these medications would more likely not be “naïve.” Individuals who are newly dispensed medications may not be new starts as this would be outside of normal clinical practice. Buprenorphine for pain was excluded at baseline from study 3 because clinicians may prescribe non-MOUD formulations of buprenorphine when a patient is known to have an OUD diagnosis or where OUD is suspected.

The committee excluded individuals with dispensed MOUD at baseline to capture those who are more likely to be opioid naïve. Additionally, the committee excluded individuals with dispensed MOUD as preliminary analyses at baseline identified that not many individuals with MOUD were receiving a simultaneous opioid prescription.

SPECIFICATIONS FOR THE EMULATED TARGET TRIALS

As mentioned, the committee employed a TTE framework to address the causal research questions. The committee specified a target trial, which is a hypothetical randomized trial, and then designed the emulated target trial using observational data. Table 3-3, which is from the 2019 National Academies report, outlines components for both the target and emulated trials. Study-specific protocols are outlined in more detail in Chapters 4 to 6. Each chapter includes a flowchart of the selection process of including eligible VHA veterans in the study.

The following section outlines each of the target trial components common across the three studies. Chapters 4, 5, and 6 provide further detail of aspects of each component specific to each study. In addition, given the complexity of each study, the committee developed a figure for each study that reflects key temporal aspects of the longitudinal study design, specifically the index or date of entry into the study, exposure washout period, windows for exclusion and covariate assessments, and follow-up time (Schneeweiss et al., 2019).

TABLE 3-2 Pharmacotherapy by Drug Class Included by Study

¹ LAAM: Levo-Alpha Acetyl Methadol.

² MOUD: medication for opioid use disorder.

³ Desvenlafaxine, venlafaxine, and mirtazapine are included in study 2 in the antidepressant covariate.

TABLE 3-3 Key Components of a Target Trial Protocol

^* ITT effect: comparative effect of assignment to the treatment strategies at baseline; per protocol effect: comparative effect of receiving the treatment strategy as specified in the protocol.

^** More specifically, investigators should adjust for pre- and post-baseline prognostic factors associated with treatment and loss to follow-up.

NOTE: This table was developed by the National Academies 2019 committee and included in its report, additional clarifications have been added by the current committee.

SOURCE: NASEM, 2019.

Eligibility Criteria

For each calendar month from January 1, 2007, to December 31, 2019,⁹ the committee identified eligible individuals who met the following criteria: (1) be a U.S. veteran, (2) be 18 years or older, (3) have a valid SSN, and (4) have at least 1-year continuous enrollment in the VHA between 2006–2019,¹⁰ defined as at least one encounter in the VHA in the 12-month pre-index period. Eligible individuals also included veterans with at least one encounter in the VHA in the 12 months before index date within the eligible study period but only had a pharmacy claim through Medicare Part D (no VHA pharmacy claim). In addition, those who were eligible did not have an encounter or dispensed pharmacotherapy in Guam, Manila, or Singapore VHA facilities. These veterans were excluded given that mortality data collected in these regions are not reflected in the NDI data. See “exclusion criteria” for further information.

Eligibility Exclusion

Each study had an exclusion assessment window of 365 days before the index date. VHA veterans who received hospice or palliative care or had a cancer diagnosis (except non-melanoma skin cancer) were excluded from the study. ICD diagnosis codes from Medicare and VHA encounter data were used to identify conditions (see Appendix I for list of codes). Individuals receiving palliative care and/or in hospice were excluded, given that

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⁹ Latest possible index date was December 31, 2018, in study 1 and 2 and October 1, 2019, in study 3.

¹⁰ Given that the earliest index date is January 1, 2007, the earliest pre-index data are January 1, 2006.

having a terminal illness (and thus being eligible for these services) is related to both death and more permissive opioid prescribing and thus a confounder in the relationship between receiving opioid pharmacotherapy and death. In addition, individuals with cancer have an increased risk of mortality and often receive an opioid prescription to manage cancer-related pain. Decisions regarding opioid initiation, co-prescribing, and dosage increases may differ for cancer compared to non-cancer pain; policies and practices for opioid prescribing is (generally) more permissive for individuals with cancer (VA/DoD, 2022, 2017, 2010, 2003; Manchikanti et al., 2017; Dowell et al., 2016). Furthermore, the study exclusion criteria are in line with published studies examining opioid pharmacotherapy which excluded individuals with cancer (Song et al., 2022; Coyle et al., 2018; Berna et al., 2015; Turner and Liang, 2015; Gomes et al., 2011; Dunn et al., 2010). As a result, having cancer may be a confounder between treatment regimen and mortality; therefore, individuals with cancer, other than non-melanoma skin cancer, are excluded.

To ensure that individuals receiving MOUD treatment were excluded from the study, due to complexities to measuring MME exposure, the committee excluded any individuals who had received ≥1 dispensed MOUD formulation of LAAM, methadone, buprenorphine, or naltrexone in the 90-day pre-index period.

The committee aimed to capture all newly dispensed opioid pharmacotherapy exposure (except cancer-related and end-of-life pain, given the increased likelihood of mortality). Individuals may initially manage acute pain related to surgery, injuries, and/or other procedures using opioid or non-opioid pain pharmacotherapy and are sometimes prescribed longer-term pain pharmacotherapy (which may or may not include opioid pharmacotherapy) to manage chronic pain. Also, chronic pain often starts from an injury or experience that may be expected to result in short-term pain. Studies 1 and 3 determined that by excluding these individuals, the sample would not be generalizable to those who experience this common pathway to chronic pain. Study 2 excluded individuals with recent surgery or an acute painful injury because dosage increases are not an expected component of short-term or acute opioid prescribing.

Based on the criteria listed, each study has a figure that illustrates the selection process of veterans for the unique emulated target trial.

Treatment Strategies

The following are clinically realistic treatment strategies for each emulated target trial:

Study 1 focused on comparing the treatment group (initiating opioid pharmacotherapy) to those in the comparator group (initiating non-opioid pain pharmacotherapy). Study 1 further stratified those without and with current dispensed benzodiazepine pharmacotherapy.

Study 2 focused on comparing opioid pharmacotherapy strategies. Among veterans initiating opioid pharmacotherapy, study 2a focused on initial dosages and compared medium and high to low dosages. Study 2b focused on escalation of opioid dosages and compared slow and fast escalation to stable dosage.

Study 3 focused on comparing the treatment group (initiating benzodiazepine pharmacotherapy) to those in the comparator group (initiating alternative non-benzodiazepine pharmacotherapy for the same indications) among those consistently dispensed opioid pharmacotherapy.

Additional details on treatment strategies by study are provided in Chapters 4 (study 1), 5 (study 2), and 6 (study 3).

Treatment Assignment

In the hypothetical target trial, eligible individuals would be randomly assigned to a strategy and would be aware of their treatment assignment. In the emulated target trial, based on retrospective observational data, treatment assignments were based on the observed prescription drug events (claims) from Medicare Part D or dispensed pharmacotherapies from the VHA EHRs. Thus, the analyses considered prescription dispensing records at baseline to assign treatment group, unlike in the hypothetical target trial, for which researchers would determine the treatment assignment, which could be different from what medications ultimately are dispensed. Additional information on study-specific treatment assignment of individuals is provided in subsequent chapters.

Start and End of Follow-Up

The start date, or the index date, is when the eligible veteran was first dispensed the medication in the treatment or comparator group and all baseline eligibility criteria were met. To facilitate computation, the index date was transformed into an index month, as the analyses were conducted using aggregated monthly data. Follow-up time was 12 months¹¹ for studies 1 and 2 and 3 months¹² for study 3. The committee utilized all available followup data (through the end of 2020) with prespecified landmark analysis at 12 months. Censoring was applied to all target trials according to trial protocol. For per protocol (target trials 1 and 2), given the interest is in observing the effect of initiating and continuing the treatment strategy over a specified follow-up period, eligible individuals are followed from the time of treatment initiation (baseline) until death (or death due to other causes, in analyses of suicide mortality), cancer diagnosis (except non-melanoma skin cancer), receipt of hospice or palliative care, non-adherence to treatment (≥3 months without dispensed opioid pharmacotherapy) (not applicable to study 2), or the administrative end of follow-up (12 months in both target trials 1 and 2), whichever happens first. For ITT, eligible individuals are followed from the time of treatment initiation (baseline) until death (or death due other causes, in analyses of suicide mortality) or the administrative end of follow-up (12 months in target trials 1 and 3 months in target trial 3), whichever happens first.

Outcomes

The outcomes outlined in the statement of task are all-cause mortality and suicide mortality, which were identified through linked data from the NDI. The committee determined all-cause mortality as the primary outcome and suicide mortality as the secondary outcome. Suicide mortality was identified by the ICD-10 death codes X60-X84 (intentional self-harm), U03 (intentional self-harm (suicide)), and Y87.0 (sequelae of intentional self-harm) (Hirsch et al., 2016; CDC, 2002). The period of outcome measurement varied based on the length of follow-up for each study. The terms “primary” and “secondary” are those most commonly employed by epidemiological studies and do not reflect hierarchy of importance.

Causal Contrast: Intent-to-Treat and Per Protocol Effects

For study 1, both per protocol (main) and ITT (secondary) effects were estimated. For study 2, per protocol effect was estimated. For study 3, ITT effect was estimated.

Study Design

The design of all studies was an active-comparator, new-user (Lund et al., 2015; Ray, 2003), retrospective cohort target trial emulation study (Hernán and Robins, 2016).

Covariates

To strengthen causal inferences, the committee controlled for many covariates to adjust for baseline and/or time-varying confounding and achieve balance between the treatment and comparator groups.

• Sociodemographics,
• Health conditions and behaviors,
• Supplemental health insurance to VHA coverage,
• Health care utilization,

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¹¹ The committee selected 12 months of follow-up for studies 1 and 2 to provide longer length of follow-up than other initiation studies (Larochelle et al., 2022), yet sufficient length to reduce non-adherence.

¹² The committee selected a 3-month follow-up for study 3 to capture the acute effect of concomitantly dispensed opioid and benzodiazepine pharmacotherapy on mortality.

• Specific pharmacotherapies,
• Facility,
• Facility-level characteristic, and
• Calendar month of eligible dispensed pharmacotherapy.

Additional covariates include month and the interaction of state and year as fixed effects. Baseline covariates included demographic characteristics (e.g., age, sex, race/ethnicity, marital status, disability status), supplemental insurance to VHA coverage (i.e., Medicare, TRICARE, or private insurance), housing security (e.g., history of homelessness status), physical and mental health conditions/disorders (e.g., acute painful injury, anxiety, chronic obstructive pulmonary disease, cardiovascular disease, substance use disorders, diabetes), military status (e.g., service era, military branch, combat service), body mass index, health care utilization in prior year (e.g., VHA outpatient visits, inpatient hospital admissions, nursing home stay), VHA facility-level characteristic (e.g., urbanicity), and specific pharmacotherapies that the committee considered as potential confounders (which varied for each study, such as migraine medications, anxiolytics, and anticonvulsants; see Table 3–3 for the detailed medication list). The committee evaluated candidate variables readily available in the study clinical and administrative databases. See Appendix I for a list of all health conditions and corresponding ICD codes.

The studies did not require participants to have a chronic pain diagnosis in the primary analysis. Studies have shown that individuals identified with chronic pain did not have a pain diagnosis or pain was underreported in electronic medical records compared to pain reported in a patient-based survey (Frank et al., 2019; Goulet et al., 2016).

Lastly, based on a priori hypotheses that effects may vary by specific individual subgroups, the committee identified a subset of variables to be evaluated for effect modification (see the “Subgroup Analyses” section) (Suda et al., 2023; Gellad et al., 2018).

Time-Varying Covariates

In studies 1 and 2, pain intensity, which is measured by the average of all documented pain intensity ratings¹³ (also referred to as “pain scores”) within a month in the VA EHR, was considered as a time-varying covariate. The measure was updated monthly in the dataset and incorporated in the IPTW. When a new measurement was unavailable, the last observation was carried forward indefinitely until a new measurement was available or the individual was censored. In study 2, pain score and benzodiazepine prescription are time-varying covariates. Preliminary analyses demonstrated that most individuals in the study had 1 pain score. Those who had multiple pain scores were typically hospitalized for some time during the month. Both the exposure (average daily opioid dosage) and this variable were measured over month periods. Study 3 does not include any time-varying covariates.

Accounting for Secular Trends and Variation by Facility

Facility and calendar time (12 months) were captured as fixed effects to capture facility-specific variation (e.g., clustering of individuals within a facility, geographic variation by facility) and reflect changes over time (e.g., variation in behaviors (health care seeking, prescribing)) and prevalence of conditions during a year. The committee also included the interaction term (i.e., product term) between state and year to capture variation over time and by states, such as when state or facility policies related to opioid prescription were implemented (e.g., when states began to participate in the Prescription Drug Monitoring Program) or secular trends in state-level policies and intensities during the opioid epidemic.

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¹³ Current pain intensity ratings were based on the numeric rating score survey, with 0 = no pain to 10 = worst pain imaginable, obtained during clinical encounters.

Statistical Analysis

The causal effects of target trials were either per protocol effect (studies 1 and 2) or ITT effect (studies 1 and 3). Studies 1 and 3 estimated the effects using an unadjusted and adjusted (IPTW) pooled logistic regression model. In study 2, per protocol effect was estimated using parametric G-formula. All analyses were conducted using SAS 9.4 and SAS Enterprise Guide (Logan et al., 2022). Study results do not report data if sample sizes were 10 or fewer individuals. This helps to ensure confidentiality of individuals in the study and is in line with CMS data policy and NCHS recommendations (NCHS, 2023; HHS, 2020). Furthermore, cells are marked as unreliable where sample sizes were 20 or fewer (NCHS, 2023).

Accounting for Baseline Differences: Inverse Probability Treatment Weights

To account for the baseline difference between treatment and comparator groups in each target trial, analyses were weighted using IPTW for studies 1 and 3. IPTW is a method used to adjust for covariates and potential confounding in observational studies that uses a function of the propensity score (PS) of receiving treatment based on individual factors. By weighting each individual included in the analysis by the inverse of the probability of receiving the treatment or comparator treatment helps achieve balance between the treatment and comparator groups (Xu et al., 2010; Robins, 1986).

To calculate the IPTW,¹⁴ first the committee performed a logistic regression to calculate the PS, or the likelihood of being the treatment versus comparator group. The PS was modeled by fitting a logistic regression of the medication received (treatment versus control) as a function of the covariates described above. For per protocol analysis, IPTW was a function of both baseline and time-varying covariates; for ITT analysis, the IPTW was a function of only the baseline covariates (Robins et al., 2000). Second, the IPTW was calculated using the inverse of the PS, or 1/PS, for those in the treatment group and 1/(1-PS) for those in the comparator group.

To limit the influence of extreme weights on the results, the committee winsorized weights to the middle 98 percent by applying the first percentile weight to all observations below the first percentile and the 99th percentile weight to all observations above the 99th percentile. The distribution of the propensity scores by treatment group was depicted using histograms. In addition, the balance of baseline covariates between the two groups before and after IPTW was assessed using the absolute standardized mean difference (ASMD). An ASMD of ≤0.1 between the two groups after weighting suggests reduction of imbalance between the group due to bias (Austin, 2009). Missing values were handled using the missing covariate indicator methods, which assigned a missing category in the model (e.g., Hispanic ethnicity, non-Hispanic ethnicity, missing ethnicity).

Study 2 uses an alternative method, the parametric G-formula, given the sustained treatment strategies of interest (more detail described below and in Chapter 5) which uses an extension of the standardization approach to ensure balance of covariates between treatment strategies. Under this method, outcomes are estimated as if the entire sample had received a given treatment regimen. This process is repeated for each treatment regimen. Thus, the covariates of individuals are balanced and reflect the underlying distribution of covariates in the eligible individual population.

Per Protocol Effect

The per protocol effect corresponds to the effect of adhering to the assigned treatment strategy over the followup. In per protocol analysis, the committee required individuals, regardless of treatment strategy group, to consistently follow the treatment protocol. Individuals were censored if they stopped following the study’s treatment protocol. To account for the baseline difference between veterans of differing treatment strategies, per protocol

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¹⁴ More detail in calculating the IPTW for per protocol (only study 1): To adjust for risk factors associated with treatment initiation (or adherence), time-varying non-stabilized inverse-probability weights are estimated via a pooled logistic regression model for the monthly probability of treatment that includes baseline (ITT and per protocol effect) and time-varying factors (per protocol effect). The following weights were calculated: (1) a baseline treatment weight to adjust for measured confounding in the likelihood of initiating the treatment versus comparator group (i.e., the IPTW described above); (2) an adherence weight (monthly); and (3) a censoring weight for loss to follow-up (monthly).

analyses were weighted using IPTWs (not applicable to study 2). In the per protocol analysis, the pooled logistic regression was fit after censoring individuals if, and when, they deviated from their initial treatment strategy using the time-dependent medication follow-up variable. In study 1, the per protocol model was adjusted for baseline covariates (same as in ITT), time-varying variables, and adherence to treatment protocol.

Intent-to-Treat Effect

The ITT effect corresponds to the effect of being assigned to a treatment strategy (e.g., initiating opioid versus non-opioid pain pharmacotherapies at baseline) on mortality, irrespective of subsequent cross-over or treatment discontinuation occurring during follow-up. In the ITT analysis, the committee estimated HRs, risk ratios, mortality rate, mortality risk) of death for each treatment strategy using pooled logistic regression models. In the ITT model, assuming a low monthly risk of death, an HR measured the risk of all-cause and suicide mortality between treatment strategies.

Parametric G-formula

The parametric G-formula is an innovative causal inference analytic approach to estimate effects of sustained treatment strategies. This is useful for studying interventions that are defined as a course of a stable treatment for a certain length of time or one that changes under specific conditions (i.e., a dynamic treatment strategy). A common issue with studying sustained treatment strategies is the problem of misalignment of time anchors. Parametric G-formula methods overcome this via simulation. Compared to traditional observational study methods, the parametric G-formula also can appropriately adjust for treatment-confounder feedback. The parametric G-formula is a three-step process: (1) generate prediction models using regression for all time-varying covariates used in the study and the outcome, (2) conduct Monte Carlo simulation to iteratively estimate the outcome at each follow-up time if all individuals in the sample received a specific treatment strategy (repeated for each strategy), and (3) use bootstrapping (repeat steps 1 and 2) to generate 95 percent CIs for the estimates. The committee identified a minimum of 399 bootstraps as sufficient (Davidson and MacKinnon, 2001).

Additional Analyses

Subgroup Analysis.

Subgroup analyses were conducted by age (with two categorical comparisons: 18–64 versus ≥65 and 18–34, 35–54, 55–74, ≥75), race (White, Black, Native American/Alaskan Native, Asian, Hawaiian and Pacific Islander, more than one race, and missing), ethnicity (Hispanic and non-Hispanic), sex (male and female), time period (2007–2012 versus 2014–2019), and by payment source of dispensed medications (only Medicare Part D prescription claims, only VHA prescription claims, or both during the episode). The committee selected these subgroups to examine differences given older age groups, specific racial and ethnic groups, and males have been shown to be at increased risk for mortality (Bohnert and Ilgen, 2019; Bossarte et al., 2012). In addition, age categories used in the reports on veteran suicides were included in the subgroup analysis for consistency (VA, 2018).

The committee included time period as a subgroup to examine temporal changes in mortality risk. The committee selected before or after 2013, given the introduction of the VHA’s Opioid Safety Initiative that year. The committee stratified by payment sources of dispensed pharmacotherapies during an episode: Individuals were grouped as having prescriptions dispensed from only the VHA, only Medicare Part D, or both. Payment source of dispensed medication is a proxy for care, access, and coordination. Other research examining payment source suggest that multiple sources of payment are associated with risky opioid prescribing, such as concurrent prescribing of opioids and benzodiazepines and prescribing with a high MME/day for opioid pharmacotherapy (Becker et al., 2017).

In addition, for studies 1 and 3, the committee repeated the main analysis for those with and without a recent surgery or outpatient procedure. Studies 1 and 3 included veterans with acute painful injury or inpatient/outpatient surgery/procedures because (1) the committee aimed to focus on pain itself, (2) treating acute pain can

result in overdose or OUD, and (3) these individuals may initially manage acute pain related to surgery and/or other procedures using short-term opioid pharmacotherapy and be eventually prescribed opioid pharmacotherapy to manage chronic pain.

Sensitivity Analysis.

Study 3 conducted two sensitivity analyses to examine the impact of (1) increasing from >1 to >5 tablets and (2) extending the follow-up period from 3 to 12 months.

Table 3-4 lists terms used throughout the report.

LIMITATIONS

The committee acknowledges several limitations to consider in emulating the target trials in the studies, especially for the exposure/treatment of interest, outcome of interest, and methods applied. Additional study-specific limitations are included in Chapters 4, 5, and 6.

Generalizability of Results

The focus of this report was on veterans receiving care from the VHA, in keeping with the statement of task. Given their unique characteristics, caution should be taken in generalizing these findings to non-VHA veterans and non-veteran populations.

Measuring Exposure

Other sources of the treatment of interest were not available to the committee. For example, the committee did not have access to data on other sources of opioids (e.g., opioids used outside of the therapeutic setting), past exposure to prescription opioid pharmacotherapy, such as during active duty or through coverage from other payers and by payer type (e.g., commercial, TRICARE, self-pay), and over-the-counter use of medications such as NSAIDs or acetaminophen. Furthermore, methadone administered through methadone clinics (opioid treatment programs) may not be fully captured. Additionally, a measure of whether multiple medications were ingested together or separately was not captured; the proxy used is co-occurring dispensed pharmacotherapies.

Another limitation is accurately capturing an active-comparator design. For example, although tricyclic antidepressants (TCAs), SNRIs, and gabapentin are common adjuvants for pain management and included as comparators in study 1, they are also used for other indications, such as anxiety and depression. In addition, per the statement of task, the study did not assess non-pharmacotherapies that individuals may have used to help manage pain prior to study enrollment. Notably, nonpharmacologic treatments for pain (e.g., physical therapy, acupuncture, or chiropractic care) are included in VA benefits and have been increasing in utilization in recent years.

Pharmacotherapies in each active comparator group (study 1: non-opioid pain pharmacotherapy; study 3: alternative non-benzodiazepine pharmacotherapy) have potential for confounding by indication. A perfect active comparator to opioid pharmacotherapy in terms of their efficacy in nociceptive pain reduction and safety risks does not exist. TCAs, SNRIs, muscle relaxants, and gabapentinoids are indeed options for chronic pain management—including neuropathic, nociceptive, and other types of pain—but the committee acknowledges that they differ from opioids in their efficacy and safety profiles. The committee’s rationale for selecting these medications as active-comparators stems from their common use in treating various forms of chronic pain. While they are not identical to opioids in terms of efficacy and safety, the committee believes that comparing individuals dispensed opioid pharmacotherapy to those dispensed non-opioid pain pharmacotherapy provides a less biased approach than comparing those newly dispensed opioid pharmacotherapy to those not newly dispensed an opioid pharmacotherapy, which could introduce greater confounding. The committee conceptualized the active comparator to benzodiazepine pharmacotherapy in study 3 similarly.

Opioid dosage was measured based on MMEs; the MME is ideal to measure the intensity of opioid exposure, as it standardizes opioid prescriptions, considering differences in the potency, quantity, and strength of different

TABLE 3-4 Key Methodological Terms: National Academies VA Opioids Study

NOTES: MME = morphine milligram equivalents; VA = Department of Veterans Affairs.

types of dispensed opioid pharmacotherapy. The committee calculated MMEs using conversions from the Centers for Disease Control and Prevention (Dowell et al., 2022).

For benzodiazepine pharmacotherapy, the committee examined other conversion methods but did not identify one as standard as the MME conversion for opioid medications. In addition, no standard definition of low, moderate, or high doses exists. Thus, comparing presence or absence of different dosages of benzodiazepine pharmacotherapies, while not ideal, was the best method available. Alternative non-benzodiazepine pharmacotherapy has the same issues (lack of a standard conversion and definition of low to high dosage). Similar to opioid pharmacotherapy, the committee did not examine historical or non-therapeutic use of benzodiazepine pharmacotherapy and/or those paid for through other sources (e.g., TRICARE, private payer). Per the statement of task, the study did not assess non-pharmacologic therapies to manage anxiety, sleep, or other indications for which benzodiazepine pharmacotherapy may be prescribed. Many veterans are at increased risk for adverse events (e.g., gastrointestinal bleeds, renal/liver dysfunction) from non-opioid pain pharmacotherapy (Kovac et al., 2010). Individuals who are at higher risk of NSAID-related adverse events likely have a higher propensity for being prescribed opioid pharmacotherapy as an alternative to NSAIDs, therefore potentially increasing risk for mortality or opioid-related adverse events.

Measuring Suicide Mortality

There are challenges in distinguishing between unintentional and intentional injury deaths. In general, cause of death of individuals may be classified as intentional (self-inflicted, or suicide) or unintentional. However, some individuals who died by suicide may have been inaccurately recorded as an unintentional death or vice versa—some individuals who died by an unintentional death are recorded as a suicide. In addition, the intent of some deaths remains unknown. Lastly, the committee did not include in the analysis history of suicide attempt or overdose.

Variation in Prescribing Practices

Over the last two decades, the VHA continues to promote reducing high-risk prescribing of opioid pharmacotherapy for pain. However, variation exists across providers and facilities in behaviors related to reducing high-risk opioid prescribing practices, including clinical practice based on the most recent updated clinical guidelines. This variation impacts the ability to capture the practice of these risk mitigation strategies and control for them in the analyses.

An observed increased risk of exposure to multi-source opioid medications or co-prescribing across the study period could be due to care coordination, increased “access” to opioid pharmacotherapy (by non-VHA and VHA providers), less evidenced-based care generally provided in the private sector, and VHA’s implementation of opioid risk mitigation initiatives before the private sector. Variation in prescribing practices by provider and time were captured by including facility, state, month, and year, and year in the analyses.

Potential Underreporting and Inaccuracies in Health Record Data

Despite the advantages in using data from health records, limitations exist in leveraging real-world data to generate evidence that be applied in clinical practice; however, unmeasured confounding may still remain. One concern is the reliability of data documented in structured data fields in EHRs, including diagnostic codes and similar clinical data, which could be measured with validated algorithms. The committee was unable to adjust for misdiagnoses or inaccuracies in clinical data reporting or distinguish between varying severity of conditions.

Although a comprehensive approach was employed to identify and adjust for known variables that could influence prescribing, a range of provider and individual-level factors remained unmeasurable from the structured components of medical records. Examples included provider decision to prescribe individual socioeconomic status such as income, education, employment; other sources of opioid or benzodiazepine pharmacotherapy; travel distance to the VHA facility; and insurance type other than VHA or Medicare. These factors could influence prescribing of opioid or other non-opioid pain pharmacotherapies or recommendation of an alternative pain management approaches. The same is true for decisions regarding prescribing benzodiazepine and alternative non-benzodiazepine pharmacotherapies. Differences in factors that influence prescriptions used in the treatment versus the comparator groups are only partially addressed by the analytic approaches employed.

Furthermore, veterans receiving care in the VHA are widely known to have higher rates of co-occurring medical and mental health disorders, and it is not uncommon for them to be prescribed multiple medications, including psychotropic medications that may negatively interact with opioid and benzodiazepine pharmacotherapies. Although the committee adjusted for multiple physical and mental health disorders, the committee was unable to adjust for unmeasured instances of polypharmacy that may interact with opioids and benzodiazepine pharmacotherapies. Concerns about polypharmacy and potentially inappropriate medications among veterans in the treatment and comparator groups are only partially addressed by the analytic approaches employed.

Despite excluding or censoring veterans receiving MOUD, this analysis likely retained veterans with untreated OUD, who may have an increased risk of overdoses, including those that are fatal. This may contribute to overestimation of mortality risks. Additionally, it is possible that veterans had an end-of-life diagnosis but had not yet received palliative care services or been placed in hospice. As a result, some veterans included in the analysis may have had opioid treatment patterns reflective of practices where the need for end-of-life pain management outweighed any risk of an opioid-related adverse event. In addition, uptake of palliative care and hospice increased over the study period.

Additional and specific limitations are reflected in the study-specific chapters.

REFERENCES

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