Estimates of 5-year cumulative incidence (percentage) of substance-related morbidity among adolescents and young adults without preexisting substance-related morbidity initiating prescribed opioid analgesics relative to demographically matched nonrecipient individuals, individuals initiating nonsteroidal anti-inflammatory drug (NSAID) treatment (with inverse probability of treatment weighting), and nonrecipient co-twins and other multiple births. Error bars indicate pointwise 95% CIs.
eMethods. Description of Linked Registers
eTable 1. Inclusion and Exclusion Criteria, Definitions, and Cohort Derivation
eTable 2. Anatomical Therapeutic Chemical Codes for Included Medications
eTable 3. International Classification of Diseases (ICD) Codes for Included Diagnoses
eTable 4. Weighted and Unweighted Variable Distributions for Active Comparator Design
eTable 5. Initial Opioid Prescriptions Dispensed to Birth Cohort
eTable 6. Contributing Pairs for Stratified Cox Regressions in Demographically Matched Comparison
eTable 7. Results of Sensitivity Analyses
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Quinn PD, Fine KL, Rickert ME, et al. Association of Opioid Prescription Initiation During Adolescence and Young Adulthood With Subsequent Substance-Related Morbidity. JAMA Pediatr. 2020;174(11):1048–1055. doi:10.1001/jamapediatrics.2020.2539
Is initiation of prescription opioid analgesics during adolescence and young adulthood associated with greater risk of substance-related morbidity?
In a nationwide Swedish cohort, 12.6% of opioid-prescription-naive adolescents and young adults were dispensed opioid prescriptions from 2007 to 2013. Opioid recipients had approximately 1% to 2% greater absolute risk of substance-related morbidity within 5 years compared with nonsteroidal anti-inflammatory drug recipients and nonrecipient co-twins (among twins and other multiple birth individuals).
Findings from this study suggest that opioid initiation during adolescence and young adulthood may be associated with a small increased risk of substance-related morbidity.
Concerns about adverse outcomes associated with opioid analgesic prescription have led to major guideline and policy changes. Substantial uncertainty remains, however, regarding the association between opioid prescription initiation and increased risk of subsequent substance-related morbidity.
To examine the association of opioid initiation among adolescents and young adults with subsequent broadly defined substance-related morbidity.
Design, Setting, and Participants
This cohort study analyzed population-register data from January 1, 2007, to December 31, 2013, on Swedish individuals aged 13 to 29 years by January 1, 2013, who were naive to opioid prescription. To account for confounding, the analysis compared opioid prescription recipients with recipients of nonsteroidal anti-inflammatory drugs as an active comparator, compared opioid-recipient twins and other multiple birth individuals with their nonrecipient co-multiple birth offspring (co-twin control), examined dental prescription as a specific indication, and included individual, parental, and socioeconomic covariates. Data were analyzed from March 30, 2019, to January 22, 2020.
Opioid prescription initiation, defined as first dispensed opioid analgesic prescription.
Main Outcomes and Measures
Substance-related morbidity, assessed as clinically diagnosed substance use disorder or overdose identified from inpatient or outpatient specialist records, substance use disorder or overdose cause of death, dispensed pharmacotherapy for alcohol use disorder, or conviction for substance-related crime.
Among the included cohort (n = 1 541 862; 793 933 male [51.5%]), 193 922 individuals initiated opioid therapy by December 31, 2013 (median age at initiation, 20.9 years [interquartile range, 18.2-23.6 years]). The active comparator design included 77 143 opioid recipients without preexisting substance-related morbidity and 229 461 nonsteroidal anti-inflammatory drug recipients. The adjusted cumulative incidence of substance-related morbidity within 5 years was 6.2% (95% CI, 5.9%-6.5%) for opioid recipients and 4.9% (95% CI, 4.8%-5.1%) for nonsteroidal anti-inflammatory drug recipients (hazard ratio, 1.29; 95% CI, 1.23-1.35). The co-twin control design produced comparable results (3013 opioid recipients and 3107 nonrecipients; adjusted hazard ratio, 1.43; 95% CI, 1.02-2.01), as did restriction to analgesics prescribed for dental indications and additional sensitivity analyses.
Conclusions and Relevance
Among adolescents and young adults analyzed in this study, initial opioid prescription receipt was associated with an approximately 30% to 40% relative increase in risk of subsequent substance-related morbidity in multiple designs that adjusted for confounding. These findings suggest that this increase may be smaller than previously estimated in some other studies.
Increasing opioid overdose–related mortality in the US1 and elsewhere2 likely results from diverse socioeconomic and health-related factors.3 Particular concern regarding the role of excessive or inappropriate opioid analgesic prescription4 has led to major changes in prescription guidelines and policies.5-7 At present, however, the extent of iatrogenic effects of initiating opioid therapy in contrast to the use of diverted8 or illicit opioids9 remains poorly understood.10,11
Evidence on the incidence of substance use disorder and related morbidity among patients starting opioid therapy is heterogeneous and has several limitations.12 Reviews have noted a substantial potential for confounding in observational studies,13 including from unmeasured mental health conditions and socioeconomic status, as well as family-level mental health history and opioid and other substance involvement.14-20 In addition, research has often relied on health care claims data, which presents challenges regarding generalizability, as well as limited measurement of opioid initiation (eg, unreimbursed prescriptions) and substance-related morbidity beyond clinically recognized opioid overdoses (eg, untreated substance use disorder, unrecorded deaths, and criminal justice involvement).10,13,21 Addressing these limitations has the potential to inform harm-benefit decisions in policy-making and for individual patients.5
Moreover, there has been relatively less research on adverse outcomes among adolescents and young adults,22,23 despite the high prevalence of opioid prescription, misuse, and overdose among younger people.24-26 Early self-report studies found associations between adolescent opioid prescription and subsequent opioid misuse but not broader substance use disorder symptoms.27,28 More recent health care data have demonstrated associations of at least some opioid prescription patterns with overdose and other adverse events.29-31 However, these studies face similar challenges to those noted above.32 For example, a recent study found a 10-fold relative increase in the risk of opioid-related morbidity among privately insured young people initiating dental opioid prescription relative to demographically similar controls, although the study could not rule out bias owing to unmeasured confounding, misclassification, or sample selection.33
The present study used Swedish register-based data to examine the association of opioid prescription initiation in adolescence and young adulthood with subsequent substance-related morbidity. We followed recommendations for opioid research by integrating nationwide health care, mortality, and criminal justice data to examine broadly defined substance-related morbidity.13,21,34 Moreover, we used multiple approaches to address confounding, including an active comparator design,35 which ruled out confounders shared across analgesia initiators (eg, pain indications) by comparing opioid recipients with recipients of another analgesic class, and a co-twin control design,36 which ruled out factors shared across siblings. We also examined dental prescription as a specific, common analgesia indication that may be less associated with a preexisting risk of substance-related morbidity.37
We analyzed data through December 31, 2013, on adolescents and young adults (aged 13-29 years by January 1, 2013) from a linkage38,39 of Swedish registers. The linkage data include nationwide information regarding dispensed prescriptions, inpatient hospitalizations, outpatient specialist care, criminal convictions, causes of death, and family relationships (eMethods in the Supplement).40 We included individuals who were prescription opioid naive by January 1, 2007. Prescription opioid–naive individuals who became 13 years of age after January 1, 2007, were included at their 13th birthday. Because prescription data were available from July 2005 onward, the cohort had 1.5 years or more of prescription opioid-free washout. eTable 1 in the Supplement details inclusion criteria. The Indiana University Institutional Review Board and the Regional Ethics Committee in Stockholm, Sweden, approved this study. Because the study used deidentified register data, informed consent was determined not to be necessary by the review boards. We analyzed data from March 30, 2019, to January 22, 2020. This study followed the Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) reporting guideline for cohort studies.
In this cohort, we used 3 designs to compare opioid recipients with nonrecipients (Table 1). Preliminarily, to facilitate comparisons with prior studies,33 we made demographically matched comparisons. We matched individuals who received opioids 1:1 to randomly selected nonrecipients on exact year and month of birth, sex, and county of residence at the start of eligibility. Second, we applied an active comparator design, which compared new opioid recipients with new recipients of prescription nonsteroidal anti-inflammatory drugs (NSAIDs).35,41,42 This approach adjusted for confounding from all factors shared across individuals initiating analgesic treatment with opioids and with NSAIDs (eg, indications for pain treatment), and we used inverse probability of treatment weighting to balance measured covariates.43 Third, we applied a co-twin control design, which compared sets of twins or larger sets of multiple birth individuals (eg, triplets).36 Comparing individuals within families adjusted for confounding from all measured and unmeasured genetic and environmental sources of twin and other multiple birth similarity.44,45
We defined prescription opioid initiation as the date of the first dispensed opioid analgesic. We included weak opioids (codeine, dextropropoxyphene, tramadol) but not cough and cold preparations, consistent with prior research (eTable 2 in the Supplement).16,31,46 We followed previous research methods to identify and exclude methadone and buprenorphine treatment of opioid use disorder from the analgesic definition.47,48 We defined dental prescriptions as those written by dentists working in clinics specializing in dentistry, jaw surgery, or oral surgery. For the active comparator design, we identified individuals initiating prescription NSAID therapy. NSAIDs have been used for this purpose previously18 and are recommended for acute dental analgesia.49
Consistent with prior register-based research,50-52 we examined an omnibus indicator of substance-related morbidity. Incidence was defined as the first International Statistical Classification of Diseases, Tenth Revision code diagnosis of or death by nontobacco substance use disorder or overdose, dispensed pharmacotherapy for alcohol use disorder, or conviction for substance-related crime (eTable 3 in the Supplement). To avoid criterion contamination from misclassified analgesia prescriptions, we did not include buprenorphine or methadone classified as pharmacotherapy for opioid use disorder in the outcome definition.47,48
We assessed a range of potential confounders, focusing on factors preceding opioid initiation that were possible contributors to the risk of substance-related morbidity (eTable 4 in the Supplement). Covariates included individual (demographics, mental health diagnoses, and psychoactive pharmacotherapies), maternal pregnancy related (birth order, smoking during pregnancy, and year of birth), parental (demographics, opioid prescription, mental health hospitalizations, violent and substance-related criminal convictions, and educational levels), and socioeconomic (parental cohabitation; within-year decile ranks16 of family income, defined as mean of available parental disposable incomes; and neighborhood deprivation53 at age 12 years) factors.
We used survival analysis because follow-up could end due to death, emigration, end of the study (December 31, 2013), or change in exposure condition (for the active comparator design and for nonrecipient co-twins and other co-multiple birth individuals in the co-twin control design).54 Follow-up time began the day after the first dispensed prescription or, for nonrecipients, an assigned date corresponding to their matched recipient’s or co-twin’s first prescription. The timescale was years since that index date. Substance-related morbidity registered on or before the index date was considered pre-existing. Using SAS, version 9.4 (SAS Institute Inc), we estimated hazard ratios (HRs) in Cox proportional hazards regression as well as Kaplan-Meier estimates of the 5-year cumulative incidence of substance-related morbidity as an index of absolute risk. We report 95% CIs corresponding to 2-sided significance tests at P < .05.
In the interest of transparency, we present estimates before and after excluding individuals with preexisting substance-related morbidity and including statistical covariates. We examined whether associations varied by opioid strength and immediate- vs extended-release formulation in stratified analyses. We also examined dental prescriptions specifically, although too few outcome-discordant multiple birth individuals (n = 21 in 10 families) received dental opioids to apply the co-twin control design.
For the demographically matched comparison and co-twin control design, we used stratified Cox proportional hazards regression. By allowing the baseline hazard function to vary across sets of twins or other multiple birth individuals, for example, this model adjusted for all factors that make twins in a pair similar to each other.55 Because only outcome-discordant sets provide the necessary within-set variability, these sets contribute to the stratified Cox proportional hazards regression models.
For the active comparator design, we weighted observations by the inverse of the predicted probability of their observed exposure (opioid or NSAID) conditional on their covariate values, which we estimated with logistic regression. We stabilized weights by multiplying them by the predicted probability of the exposure status not conditional on covariates.56 To address extreme values, we truncated weights at the first and 99th percentiles.57 Because the inverse probability of treatment weighting approach required complete data, we excluded all individuals with missing covariate values.
Sensitivity analyses explored the implications of definitions and technical decisions and included subgroups. First, we excluded criminal outcomes from the demographically matched comparison because few opioid studies have included those outcomes. Second, we excluded overdose outcomes58 to examine whether associations extended to other substance-related morbidity. Third, we excluded individuals whose initial prescriptions were for methadone or buprenorphine to ensure that misclassification of analgesics vs opioid use disorder treatments did not affect associations. Fourth, we examined whether associations differed by age at initiation. Fifth, we examined whether active comparator results varied as a function of truncating and stabilizing weights, estimating robust SEs, or including statistical covariates rather than weights.59 Sixth, we estimated unadjusted active-comparator associations without excluding cases with missing covariate values to examine whether the complete-case approach biased the results. Seventh, we included only twin pairs and then, where zygosity was known,60 monozygotic twins in the co-twin control analysis to further account for genetic confounding.
The included cohort from which each analytic design was derived comprised 1 541 862 individuals (747 929 [48.5%] female, 793 933 [51.5%] male). This cohort represented 93.2% of the original births and 97.1% of those alive who had not emigrated by the start of follow-up. Among the cohort, 193 922 individuals (12.6%) initiated opioid therapy by December 31, 2013 (median age at initiation, 20.9 years [IQR, 18.2-23.6 years]). Treatment in most individuals was initiated with codeine (56.3%) or tramadol (25.6%) (eTable 5 in the Supplement). The most common strong (ie, not weak) opioid was oxycodone (8.3%).
The demographically matched comparison included 186 034 singleton opioid recipients, with 1:1 matched nonrecipients. A total of 159 230 of the matched pairs (85.6%) had no preexisting substance-related morbidity (Table 2).
Among those without preexisting substance-related morbidity, the cumulative incidence of new substance-related morbidity within 5 years was 7.1% (95% CI, 6.9%-7.2%) for opioid recipients and 3.7% (95% CI, 3.6%-3.9%) for demographically matched nonrecipients (Figure). That is, opioid recipients had twice the hazard of incident substance-related morbidity (HR, 1.98; 95% CI, 1.91-2.07) (Table 3). eTable 6 in the Supplement details analytic samples. Because this comparison was a preliminary characterization of differences in substance-related morbidity, we adjusted for further confounding in the other designs.
After excluding 40 763 individuals (11.0%) with missing covariates, the active comparator design included 328 407 individuals (25.9% opioid recipients). Among them, 306 604 individuals (93.4%) had no preexisting substance-related morbidity (77 143 opioid recipients and 229 461 NSAID recipients).
Among individuals initiating analgesia treatment without preexisting substance-related morbidity, the inverse probability of treatment–weighted cumulative incidence of new substance-related morbidity was 6.2% (95% CI, 5.9%-6.5%) for opioid recipients and 4.9% (95% CI, 4.8%-5.1%) for NSAID recipients. That is, opioid recipients had a 29% relatively greater hazard of substance-related morbidity than did NSAID recipients (HR, 1.29; 95% CI, 1.23-1.35). eTable 4 in the Supplement reports how weighting balanced the measured covariates. Individuals initiating treatment with immediate-release weak opioids had a similarly greater hazard of substance-related morbidity relative to NSAID recipients (HR, 1.31; 95% CI, 1.25-1.37).
The co-twin control design comprised 6911 individuals in 3408 discordantly exposed families (97.2% of families were twin-pairs), among whom 6120 individuals (88.6%) were in sets of more than 1 person with no preexisting substance-related morbidity. Among twins or other multiple birth individuals without preexisting substance-related morbidity, the cumulative incidence of new substance-related morbidity was 5.9% (95% CI, 4.6%-7.1%) for opioid recipients and 4.2% (95% CI, 3.2%-5.2%) for nonrecipients. Adjusting for within-family covariates, opioid recipients had 43% relatively greater hazard of substance-related morbidity than did their nonrecipient co-twins or other multiple birth individuals (HR, 1.43; 95% CI, 1.02-2.01). eTable 7 in the Supplement details analytic samples. Multiple birth individuals initiating treatment with immediate-release weak opioids had similarly greater hazard of substance-related morbidity (HR, 1.40, 95% CI, 0.96-2.02), although the estimate was not statistically significant.
Relative to demographically matched nonrecipients, the 11 096 dental opioid recipients (57.5% female) had a nearly doubled hazard of incident substance-related morbidity (HR, 1.84; 95% CI, 1.55-2.17). Consistent with the overall results, this association was partially attenuated in the adjusted active comparator design. Among 17 438 dental initiators (52.1% female; 37.1% opioid recipients), hazard of incident substance-related morbidity was 33% relatively greater among opioid recipients than among NSAID recipients (HR, 1.33; 95% CI, 1.11-1.59).
Sensitivity analyses among those without preexisting substance-related morbidity largely supported the overall findings. First, the inclusion of criminal outcomes did not inflate the association; the demographically matched comparison was similar for noncriminal substance-related morbidity (HR, 2.08; 95% CI, 1.98-2.18). Second, associations persisted after excluding overdose outcomes, suggesting that they were not entirely driven by overdoses (eTable 7 in the Supplement). However, the co-twin control estimate was not statistically significant. Third, excluding those dispensed buprenorphine or methadone did not alter the active comparator association, and these prescriptions were minimal in the co-twin control design, suggesting that misclassified substance use disorder treatment did not bias the results (eTable 7 in the Supplement). Fourth, the associations remained moderate in magnitude among adolescents and young adults separately, albeit with statistically nonsignificant co-twin control associations (unadjusted because of limited sample size) (eTable 7 in the Supplement). Fifth, the active comparator association was virtually unchanged across technical specifications (eTable 7 in the Supplement). Sixth, the unadjusted active comparator association among all eligible individuals (HR, 1.41; 95% CI, 1.35-1.47) was similar to that for the complete case cohort (HR, 1.40; 95% CI, 1.34-1.47), suggesting that the complete covariate case approach did not meaningfully bias the results. Seventh, the adjusted co-twin control association persisted but was not statistically significant when excluding nontwin multiple birth individuals (eTable 7 in the Supplement). Although the unadjusted association appeared to attenuate among only monozygotic twins, the wide 95% CI illustrates the lack of precision, even without further adjustment (eTable 7 in the Supplement).
In this nationwide study of Swedish adolescents and young adults, opioid-prescription initiators had approximately doubled rates of incident substance-related morbidity relative to noninitiators. Use of active comparator and co-twin control designs to reduce confounding weakened but did not entirely attenuate this association: opioid initiation was associated with an approximately 30% to 40% relative increase in rates of substance-related morbidity. The results were maintained for individuals receiving opioids for dental indications and for those initiating therapy with immediate-release weak opioids.
Health care claims–based studies of adverse outcomes associated with opioid prescription have been inconclusive primarily because they have possessed uncertain generalizability, have lacked critical measures (eg, criminal justice outcomes), and have been subject to potential measured (eg, mental health and familial factors) and unmeasured (eg, shared genetic influences) confounders.10,12,13 Against this background, the present study represents what is, to our knowledge, a novel contribution in 3 domains. First, register-based data include virtually the whole Swedish population, so records are not dependent on insurance claims and include the entire socioeconomic range. Second, the data also included broader administrative information (eg, convictions and deaths).21 This breadth is beneficial for assessing substance-related morbidity (preexisting or subsequent), which frequently goes untreated.61 Third, this study used multiple designs to address measured and unmeasured confounders, including analgesia indications, individual and familial risk for substance-related morbidity, and other genetic and environmental factors. Although no observational study can entirely rule out residual confounding by indication, the limited effectiveness of measured covariates62 suggests that triangulating design-based approaches may be valuable for future opioid research as well.
Efforts are underway to reduce harms associated with opioid prescription.5,6 Studies have suggested that these harms may be substantial, even among those first initiating therapy.12,33,63 In the present study, increased risk of substance-related morbidity persisted in multiple designs, including among individuals initiating therapy with weaker opioids. Even so, after adjustment, the increase was smaller in relative and absolute terms than has been found in some previous studies. This pattern suggests that it may be appropriate to view opioid initiation not as a singular influence on risk, but rather as one likely contributor among multiple broader pathways to adverse opioid-related outcomes.3 Addressing substance-related morbidity requires accounting for other clinical and social factors in addition to analgesic prescription practices, and our results support the need for ongoing monitoring for mental health and substance use disorder among those receiving opioid therapy.5
Our results should be understood in the context of several limitations. First, each design had its own assumptions. The active comparator design cannot account for unmeasured factors that differentiate opioid and NSAID initiators and assumes no increased risk of substance-related morbidity due to NSAID initiation.42 The co-twin control design is susceptible to lower precision and bias from unmeasured within-family confounding and measurement error.64 This design additionally rules out processes shared across twin pairs that may nevertheless contribute to substance-related morbidity,65 such as household opioid availability following prescription to either twin.66 Consistent with previous studies,29,31 we could not entirely rule out confounding from characteristics of analgesia indications (eg, injury severity, pain-related impairment and distress) that may differentiate opioid recipients from NSAID recipients and co-twins and other multiple birth individuals. However, the comparable results across multiple designs may support the conclusions from this study. Second, although our measurement of substance-related morbidity included more data sources than have claims-based approaches, this measure likely captured only more severe outcomes (eg, convictions, deaths, and specialist treatment). In addition, given the ubiquity of polysubstance use and the shared genetic and neurobiological processes underlying opioid use disorder and other substance use disorders, we assessed morbidity involving diverse substances.34,67,68 Risks may differ for specific outcomes, such as opioid overdoses. Third, consistent with other health care record studies, we assessed initiation from dispensed prescriptions rather than those written by prescribers or taken by patients. Our results are therefore analogous to an intent-to-treat approach among recipients.69 Fourth, the generalizability of our results outside Sweden and after 2013 is unknown. Although pharmacologic mechanisms would not vary across countries or time and we found associations even for weaker opioids, differences in health care systems and broader factors may influence pathways to substance-related morbidity. However, opioid overdose–related mortality has also increased substantially in Sweden,2 and patterns of opioid prescription among those with substance use disorder appear similar in Sweden and the US.16,20
The results of this study do not rule out a nontrivial increase in risk of substance-related morbidity due to opioid initiation but suggest that this increase may be smaller than has been estimated in some previous studies. Understanding the situations in which opioid initiation may especially lead to risk of adverse outcomes is thus a necessary domain for continuing research.31 Initiation is only one aspect of the course of opioid therapy, and risk may vary as a function of treatment duration.29 To the extent that initiation can lead to long-term opioid therapy for some individuals,70 later treatment patterns may serve as potential contributors to any increase in risk associated with initiation.
Accepted for Publication: May 20, 2020.
Corresponding Author: Patrick D. Quinn, PhD, Department of Applied Health Science, School of Public Health, Indiana University, 1025 E Seventh St, Room 116, Bloomington, IN 47405 (email@example.com).
Published Online: August 10, 2020. doi:10.1001/jamapediatrics.2020.2539
Author Contributions: Dr Quinn had full access to all of the data in the study and takes responsibility for the integrity of the data and the accuracy of the data analysis.
Concept and design: Quinn, Fine, Rickert, Sujan, Franck, Larsson, D'Onofrio.
Acquisition, analysis, or interpretation of data: Quinn, Fine, Rickert, Sujan, Boersma, Chang, Franck, Lichtenstein, D'Onofrio.
Drafting of the manuscript: Quinn, Fine.
Critical revision of the manuscript for important intellectual content: All authors.
Statistical analysis: Quinn, Fine, Rickert, Sujan, Chang.
Obtained funding: Quinn, Sujan, Lichtenstein, Larsson, D'Onofrio.
Administrative, technical, or material support: Lichtenstein.
Supervision: Larsson, D'Onofrio.
Conflict of Interest Disclosures: Dr Larsson has served as a paid speaker for Shire and has received research grants from Shire, all outside the submitted work. No other disclosures were reported.
Funding/Support: Research reported in this publication was supported by the National Institute on Drug Abuse of the National Institutes of Health under awards R00DA040727 (Dr Quinn) and R01DA048042 (Dr D’Onofrio), in part, by the National Center for Advancing Translational Sciences of the National Institutes of Health under a Clinical and Translational Sciences Award (TL1TR001107; Dr Quinn; A. Shekhar, principal investigator), by the Swedish Research Council (grant 2018-02679; Dr D’Onofrio), and by a National Science Foundation Graduate Research Fellowship (1342962; Ms Sujan).
Role of the Funder/Sponsor: The funding organizations had no role in the design and conduct of the study; collection, management, analysis, and interpretation of the data; preparation, review, or approval of the manuscript; and decision to submit the manuscript for publication.
Disclaimer: The content is solely the responsibility of the authors and does not necessarily represent the official views of the National Institutes of Health or other funders.
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