Abstract
Background
There are ongoing concerns regarding pharmaceutical opioid‐related harms, including overdose and dependence, with an associated increase in treatment demand. People dependent on pharmaceutical opioids appear to differ in important ways from people who use heroin, yet most opioid agonist treatment research has been conducted in people who use heroin.
Objectives
To assess the effects of maintenance opioid agonist pharmacotherapy for the treatment of pharmaceutical opioid dependence.
Search methods
We updated our searches of the following databases to January 2022: the Cochrane Drugs and Alcohol Group Specialised Register, CENTRAL, MEDLINE, four other databases, and two trial registers. We checked the reference lists of included studies for further references to relevant randomised controlled trials (RCTs).
Selection criteria
We included RCTs with adults and adolescents examining maintenance opioid agonist treatments that made the following two comparisons.
1. Full opioid agonists (methadone, morphine, oxycodone, levo‐alpha‐acetylmethadol (LAAM), or codeine) versus different full opioid agonists or partial opioid agonists (buprenorphine) for maintenance treatment.
2. Full or partial opioid agonist maintenance versus non‐opioid agonist treatments (detoxification, opioid antagonist, or psychological treatment without opioid agonist treatment).
Data collection and analysis
We used standard Cochrane methods.
Main results
We identified eight RCTs that met inclusion criteria (709 participants). We found four studies that compared methadone and buprenorphine maintenance treatment, and four studies that compared buprenorphine maintenance to either buprenorphine taper (in addition to psychological treatment) or a non‐opioid maintenance treatment comparison.
We found low‐certainty evidence from three studies of a difference between methadone and buprenorphine in favour of methadone on self‐reported opioid use at end of treatment (risk ratio (RR) 0.49, 95% confidence interval (CI) 0.28 to 0.86; 165 participants), and low‐certainty evidence from four studies finding a difference in favour of methadone for retention in treatment (RR 1.21, 95% CI 1.02 to 1.43; 379 participants). We found low‐certainty evidence from three studies showing no difference between methadone and buprenorphine on substance use measured with urine drug screens at end of treatment (RR 0.81, 95% CI 0.57 to 1.17; 206 participants), and moderate‐certainty evidence from one study of no difference in days of self‐reported opioid use (mean difference 1.41 days, 95% CI 3.37 lower to 0.55 days higher; 129 participants). There was low‐certainty evidence from three studies of no difference between methadone and buprenorphine on adverse events (RR 1.13, 95% CI 0.66 to 1.93; 206 participants).
We found low‐certainty evidence from four studies favouring maintenance buprenorphine treatment over non‐opioid treatments in terms of fewer opioid positive urine drug tests at end of treatment (RR 0.66, 95% CI 0.52 to 0.84; 270 participants), and very low‐certainty evidence from four studies finding no difference on self‐reported opioid use in the past 30 days at end of treatment (RR 0.63, 95% CI 0.39 to 1.01; 276 participants). There was low‐certainty evidence from three studies of no difference in the number of days of unsanctioned opioid use (standardised mean difference (SMD) −0.19, 95% CI −0.47 to 0.09; 205 participants). There was moderate‐certainty evidence from four studies favouring buprenorphine maintenance over non‐opioid treatments on retention in treatment (RR 3.02, 95% CI 1.73 to 5.27; 333 participants). There was moderate‐certainty evidence from three studies of no difference in adverse effects between buprenorphine maintenance and non‐opioid treatments (RR 0.50, 95% CI 0.07 to 3.48; 252 participants).
The main weaknesses in the quality of the data was the use of open‐label study designs, and difference in follow‐up rates between treatment arms.
Authors' conclusions
There is very low‐ to moderate‐certainty evidence supporting the use of maintenance agonist pharmacotherapy for pharmaceutical opioid dependence. Methadone or buprenorphine did not differ on some outcomes, although on the outcomes of retention and self‐reported substance use some results favoured methadone. Maintenance treatment with buprenorphine appears more effective than non‐opioid treatments.
Due to the overall very low‐ to moderate‐certainty evidence and small sample sizes, there is the possibility that the further research may change these findings.
Plain language summary
Opioid maintenance medicines for the treatment of dependence on opioid pain medicines
Key messages
1. Methadone may keep more people in treatment than buprenorphine.
2. People reported less opioid use with methadone than buprenorphine, although when testing urine for opioid use there was no difference between groups.
3. Buprenorphine maintenance probably keeps more people in treatment and may be better at helping people reduce opioid use than non‐opioid treatments.
What is dependence on opioid pain medicines?
Use of pharmaceutical opioids (medicines that are used to treat pain) has increased dramatically in some parts of the world since the mid‐1990s. With the increased use, there has been increasing numbers of people seeking treatment for dependence (addiction) on pharmaceutical opioids. Currently, most treatment guidelines are based on research that was conducted in people who were dependent on heroin (a highly addictive opioid). People who use pharmaceutical opioids may differ from people who use heroin in important ways, such as having a higher prevalence of chronic pain and mental health symptoms.
What did we want to find out?
This review sought to compare different opioid agonist maintenance treatments (i.e. treatments such as methadone or buprenorphine that are given for at least 30 days to help the person to reduce their unsanctioned medicine use) for the treatment of pharmaceutical opioid dependence. We also compared results from maintenance treatment to short‐term treatments such as detoxification (removal of the drug from the body) or psychological treatments (e.g. talking therapy, counselling).
What did we do?
We examined the scientific literature up to January 2022. We identified eight randomised controlled trials (studies where people were allocated at random to one of two or more treatment or control conditions) involving 709 adults and adolescents who were dependent on pharmaceutical opioids. Seventy percent of the people in the studies were male, and had an average age of 32.0 years. The average duration of the studies comparing different opioid maintenance treatments (four studies that compared methadone to buprenorphine) was 21 weeks, and the average duration of studies comparing a maintenance treatment (four studies with buprenorphine maintenance) to detoxification, an opioid antagonist, or psychological treatment was 14 weeks. Seven of the eight studies were conducted in the USA, with one study from Iran.
The main outcomes we examined were opioid use and leaving treatment early.
The National Institutes of Health (USA) funded seven studies, with one study not reporting the funding source. Five studies reported that a pharmaceutical company provided the medicine.
What did we find?
We found that when comparing methadone with buprenorphine maintenance treatments, methadone may keep more people in treatment than buprenorphine. People on methadone may report less opioid use than people on buprenorphine, although when testing urine for opioid use there was no difference between methadone and buprenorphine. When comparing buprenorphine maintenance to other non‐opioid treatments such as detoxification, opioid antagonists like naltrexone, or psychological treatments, buprenorphine probably keeps more people in treatment, and may be better at helping people reduce opioid use.
What were the limitations of the evidence?
Overall, the evidence was of low to moderate quality. All studies put people into treatment groups randomly, but the participants and researchers knew which medication the participants were taking, which could bias the results and lower the quality of the evidence. In some studies, many people did not finish the study, leading to a meaningful amount of missing data which may bias the results. In some studies, there were more missing results in one arm of the study than the other. Most of the studies were similar in design and results were collected in a way that allowed them to compare the main outcomes of opioid use and number of people completing the study.
How up to date is this evidence?
The evidence is current to January 2022.
Summary of findings
Summary of findings 1. Full opioid agonists versus different full opioid agonists or partial opioid agonists (methadone versus buprenorphine) for maintenance.
| Full opioid agonists versus different full opioid agonists or partial opioid agonists (methadone versus buprenorphine) for maintenance | ||||||
| Patient or population: people dependent on pharmaceutical opioids Intervention: methadone Comparison: buprenorphine | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect (95% CI) | No of participants (studies) | Certainty of the evidence (GRADE) | Comments | |
| Risk with buprenorphine | Risk with methadone | |||||
|
Illicit opioid use assessed with: days of unsanctioned opioid use at end of study period Scale: 0–30 Follow‐up: mean 24 weeks |
The mean opioid use was 2.92 days | The mean opioid use in the intervention group was 1.41 days lower (3.37 lower to 0.55 higher) | MD −1.41 (−3.37 to 0.55) | 129 (1 RCT) | ⊕⊕⊕⊝ Moderatea | — |
|
Illicit opioid use assessed with: positive urine drug screen for opioids at end of treatment |
Study population | RR 0.81 (0.57 to 1.17) | 206 (3 RCTs) | ⊕⊕⊝⊝ Lowa,b | 1 study coded missing urine drug screens as positive; however, they conducted sensitivity analyses and results were unchanged if this assumption was not made (Saxon 2013). For 1 study, half of the participants in the methadone arm had switched to buprenorphine (the comparator condition), limiting the ability to assess the effect of methadone on substance use, in addition to concerns relating to high attrition and small sample size (Neumann 2020). | |
| 430 per 1000 | 348 per 1000 (245 to 503) | |||||
| Low | ||||||
| 250 per 1000 | 203 per 1000 (143 to 293) | |||||
| High | ||||||
| 440 per 1000 | 356 per 1000 (251 to 515) |
|||||
|
Illicit opioid use assessed with: self‐reported opioid use at the end of the study period Follow‐up: mean 24 weeks |
Study population | RR 0.49 (0.28 to 0.86) | 165 (3 RCTs) | ⊕⊕⊝⊝ Lowa,b | For 1 study, half of the participants in the methadone arm had switched to buprenorphine (the comparator condition), limiting the ability to assess the effect of methadone on substance use, in addition to concerns relating to high attrition and small sample size (Neumann 2020). | |
| 387 per 1000 | 190 per 1000 (108 to 333) | |||||
|
Retention assessed with: proportion of participants retained in treatment Follow‐up: mean 20 weeks |
Study population | RR 1.21 (1.02 to 1.43) | 379 (4 RCTs) | ⊕⊕⊝⊝ Lowa,c | — | |
| 615 per 1000 | 745 per 1000 (628 to 880) | |||||
| Adverse effects | 83 per 1000 | 37 per 1000 (7 to 199) |
RR 0.45 (0.09 to 2.41) | 206 (3 RCTs) | ⊕⊕⊝⊝ Lowa,b | — |
| *The risk in the intervention group (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). CI: confidence interval; RCT: randomised controlled trial; RR: risk ratio. | ||||||
| GRADE Working Group grades of evidence High certainty: we are very confident that the true effect lies close to that of the estimate of the effect. Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different. Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect. Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect. | ||||||
aDowngraded one level for risk of bias: all studies were open label, and one study presented limited information meaning that we were unable to assess risk of bias. bDowngraded one level for imprecision: two studies had small samples with low follow‐up rates (Neumann 2013; Neumann 2020). cDowngraded one level for clinical heterogeneity: for Ahmadi 2003, the population consisted of people who injected buprenorphine. There was no evidence of a difference when the meta‐analyses included only results from Neumann 2013, Neumann 2020, and Saxon 2013.
Summary of findings 2. Full or partial opioid agonist maintenance versus placebo, detoxification only or psychological treatment (buprenorphine maintenance compared to taper or treatment as usual).
| Full or partial opioid agonist maintenance versus non‐opioid treatment condition (buprenorphine maintenance compared to detoxification, opioid antagonist or psychological treatment) | ||||||
| Patient or population: pharmaceutical opioid dependent people Intervention: opioid agonist Comparison: non‐opioid comparison (detoxification, opioid antagonist or psychological treatment) | ||||||
| Outcomes | Anticipated absolute effects* (95% CI) | Relative effect (95% CI) | No of participants (studies) | Certainty of the evidence (GRADE) | Comments | |
| Risk with non‐opioid treatment | Risk with opioid agonist | |||||
| Days of unsanctioned opioid use (as number of days/30 or days/7) Follow‐up: mean 11 weeks | The mean days of unsanctioned opioid use was 2.16 days | The mean days of unsanctioned opioid use in the intervention group was 0.19 standard deviation days lower (0.47 lower to 0.09 higher) | SMD 0.19 (−0.47 to 0.09) | 205 (3 RCTs) | ⊕⊕⊝⊝ Lowa,b | — |
| Self‐reported opioid use at treatment completion Follow‐up: mean 14 weeks | Study population | RR 0.63 (0.39 to 1.01) | 276 (4 RCTs) | ⊕⊝⊝⊝ Very lowa,b,c | There was some heterogeneity in results in populations (i.e. non‐treatment seeking), and indirect nature of substance use outcomes in D'Onofrio 2015. When we removed Woody 2008 from the analysis, there was a difference in favour of buprenorphine maintenance (RR 0.71, 95% CI 0.54 to 0.93; I2 = 0%; 3 studies, 249 participants). | |
| 522 per 1000 | 329 per 1000 (204 to 527) | |||||
| Opioid use assessed with urine drug screens Follow‐up: mean 14 weeks | Study population | RR 0.66 (0.52 to 0.84) | 270 (4 RCTs) | ⊕⊕⊝⊝ Lowa,b | — | |
| 537 per 1000 | 354 per 1000 (279 to 451) | |||||
| Retention: proportion of participants retained in treatment Follow‐up: mean 11 weeks | Study population | RR 3.02 (1.73 to 5.27) | 333 (4 RCTs) | ⊕⊕⊕⊝ Moderated | — | |
| 260 per 1000 | 785 per 1000 (450 to 1000) | |||||
| Adverse events | 195 per 1000 | 98 per 1000 (14 to 679) |
RR 0.50 (0.07 to 3.48) | 252 (3 RCTs) | ⊕⊝⊝⊝ Very lowa,e,f | 1 study used protective transfers as adverse events (Fiellin 2014). |
| *The risk in the intervention group (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI). CI: confidence interval; RCT: randomised controlled trial; RR: risk ratio; SMD: standardised mean difference. | ||||||
| GRADE Working Group grades of evidence High certainty: we are very confident that the true effect lies close to that of the estimate of the effect. Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different. Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect. Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect. | ||||||
aDowngraded one level for risk of bias: studies were open label, there were differences in retention between groups resulting in differences in missing data on some variables. bDowngraded one level for indirectness: one study examined different methods of referral to treatment in non‐treatment‐seeking people who presented to hospital. Substance use was an indirect outcome of the study. cDowngraded one level for heterogeneity: there was substantial heterogeneity (I2 = 52%), but there was evidence of a difference in favour of buprenorphine maintenance when Woody 2008 was removed. dDowngraded one level for heterogeneity: there was substantial heterogeneity (I2 = 73%). When D'Onofrio 2015 was removed, based on statistical and clinical heterogeneity, heterogeneity was no longer significant, though moderate heterogeneity remained, and there remained an effect favouring buprenorphine maintenance (RR 3.66, 95% CI 2.11 to 6.32, I2 = 47%). eDowngraded one level for heterogeneity: there was considerable heterogeneity (I2 = 83%). When Lee 2018 was removed, heterogeneity was no longer evident (I2 = 0%) and there was evidence of a difference favouring buprenorphine maintenance having fewer adverse events (RR 0.19, 95% CI 0.06 to 0.57). fDowngraded one level for heterogeneity in how studies measured adverse events.
Background
Globally, extramedical opioid use is a major cause of excess mortality due to non‐communicable diseases, overdose, infectious diseases, and injuries, much of which is preventable (Larney 2020). In the USA, pharmaceutical opioid use contributes to approximately one‐third of opioid‐related deaths (Mattson 2021). High rates of pharmaceutical opioid use have been described in Canada (Fischer 2012), although more recently the largest number of deaths has been driven by a rise in illicit fentanyl use (Belzak 2018). Although other countries are yet to reach the magnitude of problems seen in the USA and Canada, there is evidence of increased pharmaceutical opioid use and harms. One global review identified that pharmaceutical opioid diversion, non‐medical use, and injection were considerable problems in the USA, South Asia, South East Asia, and some European countries (Degenhardt 2007). In Europe, increases in non‐medical use of prescription opioids and related harms are also documented, with notably large increases in oxycodone use in France, and increases in pharmaceutical opioid problems in Germany and the Nordic regions (Chenaf 2019). There have been increasing reports of use and harms with pharmaceutical opioids in Australia, with most opioid‐related deaths and hospitalisations currently related to prescription opioids, though this has stabilised in recent years (Australian Institute of Health and Welfare 2018; Man 2021). The number of emergency department admissions from pharmaceutical opioids continues to be greater than with heroin, though heroin dependence remains the main opioid people seek treatment for (Lam 2020; Nielsen 2015a). In other parts of the world, and in particular lower‐income countries, there is a paucity of data to describe the prevalence of dependence to pharmaceutical opioids (Ellerstrand 2017).
Description of the condition
The non‐medical use and dependence upon pharmaceutical drugs has been described as a major health problem. Opioid dependence is a chronic relapsing condition with significant cost to human life (Grella 2011; Hser 2001). One estimation was that more than 40 million people were using opioids in 2017 (Degenhardt 2019), though the proportion using pharmaceutical opioids is not well documented. Estimates of the number of people who are prescribed opioids who develop problematic use range from 1% to 81%, and estimates for those who go on to develop dependence vary from 0.1% to 34% (Chou 2015; Klimas 2019a; Vowles 2015). This variability may in part be explained by whether data were based on clinical follow‐up and screening of all patients versus database studies that relied on diagnostic codes in administrative data sets (the latter likely underestimating opioid dependence) (Klimas 2019a).
The definition of opioid dependence, according to the World Health Organization (WHO) International Classification of Diseases, 10th edition (ICD‐10) is the presence of three or more of the following six features simultaneously at any one time in the past year: 1. a strong desire or sense of compulsion to take opioids; 2. difficulties in controlling opioid use; 3. presence of withdrawal on ceasing opioids; 4. development of tolerance to the effects of opioids; 5. neglecting pleasures or interests because of opioid use; and 6. persistent opioid use despite clear evidence of harmful consequences (WHO 2004).
A range of factors has been associated with the development of dependence upon prescription opioids including being prescribed higher doses, concurrent mental health conditions, younger age and male sex (Campbell 2015; Cragg 2019; Klimas 2019a).
Description of the intervention
Opioid agonist treatments were established for the treatment of heroin dependence (Clark 2002; Faggiano 2003; Mattick 2009; Mattick 2014). The two main opioid agonist treatments that are most widely available are methadone and buprenorphine. Both of these treatments are well established to reduce mortality in people with opioid dependence (Sordo 2017).
Methadone is well established as a treatment and has a strong evidence base demonstrating its effectiveness in reducing mortality and substance use, improving physical and mental health outcomes, reducing criminal activity, reducing HIV risk and risk behaviours (Amato 2005; Caplehorn 1996; Gowing 2011; Gowing 2012; Gowing 2013; Mattick 2014).
Methadone is a synthetic μ‐opioid agonist, and an N‐methyl‐D‐aspartate (NMDA) antagonist. It has a half‐life of 24 to 36 hours and has close to 100% oral bioavailability. Methadone is generally given as a single daily dose in the treatment of opioid dependence. Methadone doses of 60 mg to 100 mg are more effective in retaining people in treatment compared with lower doses (Faggiano 2003). Methadone can cause severe adverse effects including fatal respiratory depression, so due to its safety profile, it is sometimes considered a second‐line treatment (Bruneau 2018).
Buprenorphine is a partial opioid agonist, having a lower intrinsic activity at the opioid receptor, but, due to its high affinity for the opioid receptor, buprenorphine has antagonist actions, blocking the effect of other opioids. Buprenorphine has a favourable safety profile due to its ceiling on respiratory effects (Walsh 1994), with mortality in treatment appearing to be relatively less common with buprenorphine compared with methadone in naturalistic study designs in Australia and France (Auriacombe 2001; Degenhardt 2009). Buprenorphine has poor oral bioavailability, and is available in sublingual formulations for the treatment of opioid dependence. Due to its pharmacological properties, buprenorphine may be given as larger doses every second or third day (Amass 2000).
Levo‐alpha‐acetylmethadol (LAAM) was concluded to be more effective than methadone for reducing heroin use (Clark 2002), but it is currently not commercially available. Other therapies such as slow‐release oral morphine have also been explored (Klimas 2019b).
How the intervention might work
Opioid agonist treatment, also known as opioid maintenance treatment, involves prescribing a stable dose of an opioid medication, such as methadone or buprenorphine to remove the need to take opioids non‐medically. Most of the original research into opioid maintenance treatment involves prescribing a legal opioid such as methadone or buprenorphine for at least one to 12 months to treat illicit opioid (e.g. heroin) dependence. The provision of a regular dose of a legal opioid treatment enables a reduction in illicit or unsanctioned opioid use, with improvements in health and social stability. The dose of the medication is adjusted to a level that reduces withdrawal and craving without causing excessive sedation. Regular dosing maintains a fairly constant blood level, so that the sense of euphoria or intoxication usually associated with opioid use (either illicit or prescribed) is lessened. Maintenance treatment decreases the frequency and intensity of the cycle of intoxication and withdrawal, allowing the patient to address the associated issues necessary for recovery.
Psychosocial support provided in conjunction with medication can help to address the psychological health and social problems that can be associated with opioid use, and therefore help to improve quality of life and prevent premature mortality (WHO 2009).
Psychosocial support can be delivered in various ways to address individual patient needs in relation to their psychological health and social environment (which can include basic assistance with obtaining food or shelter, monitoring progress in treatment over time and goal setting, to structured psychological treatments such as contingency management, cognitive behavioural therapy or group counselling).
Opioid agonist treatment works by provision of a regular dose of μ‐opioid agonist that binds at the μ‐opioid receptor, alleviating opioid withdrawal symptoms. Providing a stable dose of opioid agonist has been demonstrated in people who use illicit opioids to lead to numerous health and social benefits for opioid‐dependent people, specifically though reducing illicit opioid use (Amato 2005; Mattick 2009; Mattick 2014), HIV risk behaviour (Gowing 2011), HIV seroconversion (MacArthur 2012), and criminality (Amato 2005; Mattick 2009). Among studies primarily with people who use illicit opioids, opioid agonist treatment has been confirmed to improve physical and mental health, and social functioning (Mattick 2009; Mattick 2014; Padaiga 2007), and reduce mortality (Sordo 2017).
Why it is important to do this review
Opioid agonist treatment is commonly initiated as a first‐line treatment for people with pharmaceutical opioid dependence. However, much of the evidence base for the use of pharmacotherapy in opioid dependence was derived from studies conducted primarily or exclusively with heroin‐dependent samples. People who use pharmaceutical opioids (i.e. prescription opioids and opioids that are available without a prescription in some countries such as codeine) have been described in the literature to be a population with a number of characteristics that differ from people who use heroin, including being more likely to be employed, less likely to use drugs by injection, and having a higher prevalence of physical and mental health comorbidities (Brands 2004; Fischer 2008; Moore 2007; Nielsen 2011; Nielsen 2015a). How these characteristics may impact on treatment outcomes is not well understood. Further, studies that have compared treatment outcomes for people who use pharmaceutical opioids and heroin have had mixed results, with some studies finding better treatment outcomes for people using pharmaceutical opioids, and other studies finding no difference (Banta‐Green 2009; McCabe 2013; Nielsen 2013; Nielsen 2015b).
Pharmaceutical opioid dependence is stabilised in the USA and increased in some other countries around the world (Australian Institute of Health and Welfare 2018; Chenaf 2019; Mattson 2021). Establishing an evidence base for treatment of prescription opioid dependence is therefore timely and critical. A systematic review conducted in 2016 determined that there were similar outcomes for people who are opioid dependent with methadone and buprenorphine, and better outcomes with maintenance opioid agonist treatment compared to short‐term treatments or psychological treatments only (Nielsen 2016). This is an update of that review, and summarises the evidence from randomised controlled trials (RCTs) to inform clinicians about the evidence for using opioid agonist treatments for pharmaceutical opioid dependence.
Objectives
To assess the effects of maintenance agonist pharmacotherapy for the treatment of pharmaceutical opioid dependence.
Methods
Criteria for considering studies for this review
Types of studies
Randomised controlled trials (RCTs).
Types of participants
We included studies with people who were assessed by study staff to meet the criteria for opioid dependence as per Diagnostic and Statistical Manual of Mental Disorders, 4th edition (DSM‐IV), ICD‐10, meet Diagnostic and Statistical Manual of Mental Disorders, 5th edition (DSM‐5) criteria for opioid use disorder, or meet other validated criteria for pharmaceutical opioid dependence as assessed by a clinician (i.e. a population meeting criteria for 'addiction' rather than just physiological neuro‐adaptation in the absence of other behaviours suggesting dependence).
We did not include people who were solely taking pharmaceutical opioids in the context of opioid substitution treatment (e.g. studies of people who were already in methadone treatment) as dependent on pharmaceutical opioids. Where participants were reported to be 'opioid dependent', as opposed to specifically dependent on pharmaceutical opioids, the main opioid used prior to treatment entry must have been a pharmaceutical opioid. We excluded studies examining opioid treatments for pain and not for the treatment of opioid dependence.
Where study populations were not exclusively comprised of people who were dependent upon pharmaceutical opioids, at least 80% of the study participants must have reported pharmaceutical opioids as their primary substance of use for the parent study data to be included in the analysis. Where subpopulations of pharmaceutical opioid‐dependent people did not comprise 80% of the study population, we requested study data, with only participants meeting the above criteria (i.e. dependent on pharmaceutical opioids, or opioid dependent with the main opioid used being a pharmaceutical opioid) included in the analysis. We contacted study authors where necessary to confirm levels of use of pharmaceutical opioids. Studies with mixed populations of opioid‐dependent people must have recruited at least 10 people who were dependent on pharmaceutical opioids for re‐analyses of data to be included in the review.
Types of interventions
We included studies of maintenance opioid agonist treatments, where maintenance was defined as at least 30 days of opioid agonist treatment. We included trials that made the following comparisons:
full opioid agonists (methadone, morphine, oxycodone, LAAM or codeine) versus different full opioid agonists or partial opioid agonists (buprenorphine) for maintenance treatment;
full or partial opioid agonist maintenance versus placebo, detoxification only or psychological treatment (without opioid agonist treatment).
Types of outcome measures
Outcome measures were not considered as part of the eligibility criteria.
Primary outcomes
Illicit opioid use, as measured by: days of unsanctioned opioid use at the end of the intervention period.
Illicit opioid use at end of treatment completion (defined as point prevalence of opioid use at end of treatment by self‐report and with urine drug screen).
Retention.
Adverse effects (participants experiencing any adverse event or serious adverse event).
Secondary outcomes
Pain, assessed by validated scales such as the Brief Pain Inventory (Cleeland 1991), and the McGill Pain Questionnaire (Melzack 1975).
Risk behaviours (injecting, sexual, polydrug use, overdoses or hospital admissions).
Aberrant opioid‐related behaviours (e.g. seeing multiple doctors for extra opioid medication, lost medication, unauthorised dose escalations).
Employment.
Quality of life, as assessed by validated scales such the World Health Organization Quality of Life (WHOQOL) or WHOQOL‐BREF (WHO 1997).
Physical health, as assessed by validated scales such as the 36‐item Short Form (SF‐36) (Ware 1992).
Psychological health, as assessed by validated scales such as the SF‐36 (Ware 1992), Kessler Psychological Distress Scale (K10) (Kessler 2002), or Depression and Anxiety Stress Scale (DASS) (Lovibond 1995).
Outcomes were either self‐reported or objectively measured.
Search methods for identification of studies
All searches included non‐English language literature (Lefebvre 2022). We found no studies in languages other than English.
Electronic searches
For this update, we revised all our search strategies in line with current Cochrane Drugs and Alcohol Group practices. We searched the following databases up to 28 January 2022:
Cochrane Drugs and Alcohol Group's Specialised Register of Trials; 2020;
the Cochrane Central Register of Controlled Trials (CENTRAL, Issue 1, 2022);
MEDLINE (January 1946 to 28 January 2022);
Embase (Ovid) (January 1974 to 28 January 2022);
CINAHL (EBSCOhost) (1982 to 28 January 2022);
ISI Web of Science (1900 to 28 January 2022);
PsycINFO (Ovid) (1806 to 28 January 2022);
ClinicalTrials.gov (clinicaltrials.gov; searched 28 January 2022);
WHO International Clinical Trials Registry Platform (ICTRP; trialsearch.who.int/; searched 28 January 2022).
We developed a search strategy to retrieve references relating to the pharmacological treatment of pharmaceutical opioid dependence. This strategy was adapted to each of the databases listed below (Appendix 1).
Details of the previous search strategies are available in Nielsen 2016.
Searching other resources
We search abstracted databases including the National Institute on Drug Abuse/College on Problems of Drug Dependence (NIDA/CPDD) abstracts.
We searched the reference lists of all relevant papers to identify further studies, in addition to contacting the authors of all included studies to enquire if there were other relevant published or unpublished studies (Lefebvre 2022). All searches included English and non‐English language literature.
Data collection and analysis
Selection of studies
One review author checked the titles and abstracts identified by the above searches. We requested the full text of each potentially relevant article, and two review authors independently assessed the studies for inclusion (Li 2022). Where the two review authors were unable to reach agreement following their independent review of the full text, a third review author assessed the studies to assist in reaching consensus.
Data extraction and management
Two review authors independently extracted data using a data collection form, with a third review author involved where there was disagreement to assist in reaching consensus.
We extracted information about the number of participants treated; drug and dosing regimen; study design; study duration and follow‐up; and outcomes listed at including pain, substance use measures, treatment retention, risk behaviours, employment, quality of life, physical and psychological health, and adverse events (participants experiencing any adverse event, or serious adverse event) from each study and recorded them on a data extraction sheet.
We attempted to collect and utilise the most detailed numerical data that might have facilitated similar analyses of included studies. Where 2 × 2 tables or means and standard deviations were unavailable, we used effect estimates (e.g. odds ratios, regression coefficients), confidence intervals (CI), test statistics (e.g. t, F, Z, Chi2) or P values in the analyses (see also Measures of treatment effect).
Assessment of risk of bias in included studies
We performed the risk of bias assessment for RCTs using the criteria recommended by the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). This comprises a two‐part tool addressing seven specific domains, namely sequence generation and allocation concealment (selection bias), blinding of participants and providers (performance bias), blinding of outcome assessor (detection bias), incomplete outcome data (attrition bias), selective outcome reporting (reporting bias) and other sources of bias. The first part of the tool involves describing what was reported to have happened in the study. The second part of the tool involves assigning a judgement relating to the risk of bias for that entry, in terms of low, high or unclear risk. To make these judgements, we used the criteria indicated by the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), adapted to the addiction field. See Appendix 1 for details.
The tools addressed the domains of sequence generation and allocation concealment (avoidance of selection bias) by a single entry for each study.
We considered blinding of participants, personnel and outcome assessor (avoidance of performance bias and detection bias) separately for objective outcomes (e.g. retention, substance use measured by urine drug screens, employment) and subjective outcomes (e.g. pain, risk behaviours, adverse effects, aberrant opioid related behaviours, quality of life, physical health and psychological health).
We considered incomplete outcome data (avoidance of attrition bias) for all outcomes except for retention, which is often the primary outcome measure in trials on addiction.
Measures of treatment effect
Where possible, we expressed the treatment effect for each dichotomous outcome as a risk ratio (RR) with 95% CI (Higgins 2022). Where there was a comparable consistent outcome measure (e.g. days of opioid use), we expressed the treatment effect for each continuous outcome as a mean difference (MD) with 95% CIs. Where there was variability in outcome measure (e.g. quality of life scales, risk behaviour measures or pain scales), we expressed the treatment effect for each continuous outcome as a standardised mean difference (SMD) with 95% CIs.
Unit of analysis issues
For trials with multiple treatment arms, we combined groups to allow single pair‐wise comparisons (Higgins 2022).
Dealing with missing data
Where there appeared to be an important amount of missing data, we described the possible effects of the missing data in the Discussion and summary of findings tables.
Assessment of heterogeneity
We considered clinical heterogeneity (variability in the participants, interventions and outcomes studied) and methodological heterogeneity (variability in study design and risk of bias), which we discussed in the summary of findings tables (Deeks 2022).
We conducted meta‐analysis where studies were sufficiently homogeneous in terms of participants, interventions and outcomes to provide a meaningful summary. Where this was not the case, and the heterogeneity of the included studies precluded a meta‐analysis being performed, we described the relevant studies separately.
To assess heterogeneity, initially we inspected the results graphically. A P value of the test lower than 0.10 or an I2 statistic of at least 50% indicated significant statistical heterogeneity.
Assessment of reporting biases
If sufficient studies were included in meta‐analyses (i.e. more than 10), we planned to use funnel plots (plots of the effect estimate from each study against the standard error) to assess the potential for publication bias related to the size of the trials.
Data synthesis
We summarised the key findings of studies descriptively before considering if studies were appropriate for quantitative meta‐analysis. We contacted study authors where we required additional information to enable inclusion of studies in meta‐analyses.
We undertook statistical analysis using Review Manager Web (Review Manager Web).
We combined the outcomes of the individual trials through meta‐analysis where possible (depending on the comparability of interventions and outcomes between trials) using of a random‐effects model as variability was expected between the studies. Where meta‐analysis was not possible, we reported a narrative synthesis of the findings.
Subgroup analysis and investigation of heterogeneity
We planned to perform subgroup analysis to explore potential sources of heterogeneity with the following subgroups:
with and without chronic pain;
with and without a history of heroin use;
with and without a history of injecting drug use;
with and without mental health problems.
Sensitivity analysis
Where the effect of a decision on the outcome of the review was uncertain (e.g. the decision to include or exclude a study remained unclear, or the impact of unavailable data on the findings was uncertain), we conducted a sensitivity analysis (Deeks 2022) with the results described in text.
To incorporate risk of bias assessment in the review process, we planned to plot intervention effect estimates for different outcomes stratified for risk of bias for each item and to perform sensitivity analysis, excluding studies at a high risk of bias; however, we found insufficient numbers of studies to warrant this process for the two planned comparisons. For future updates of this review, if differences in results are present among studies at different risk of bias, we will perform sensitivity analysis, excluding studies at a high risk of bias. We will also perform subgroup analysis for studies at a low and unclear risk of bias.
Where there was significant heterogeneity, we excluded studies that contributed to heterogeneity to determine if the exclusion of these studies would change our conclusions (Deeks 2022). Results of these analyses were reported as sensitivity analysis.
Summary of findings and assessment of the certainty of the evidence
We assessed the overall certainty of the evidence for the primary outcomes (illicit opioid use, retention and adverse effects) using the GRADE system, which grades the certainty of the evidence that takes into account issues related to internal validity and to external validity, such as directness, consistency, imprecision of results and publication bias (GRADE 2004; Guyatt 2008; Guyatt 2011). We presented the main findings of the review in the summary of findings tables, which present results in a transparent and simple tabular format. In particular, the tables provide key information concerning the certainty of evidence, the magnitude of effect of the interventions examined and the sum of available data on the main outcomes (Schünemann 2021).
The GRADE system uses the following criteria for assigning grades of evidence.
High: we are very confident that the true effect lies close to that of the estimate of the effect.
Moderate: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.
Low: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.
Very low: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.
Grading is decreased for the following reasons.
Serious (−1) or very serious (−2) limitation to study quality.
Important inconsistency (−1).
Some (−1) or major (−2) uncertainty about directness.
Imprecise or sparse data (−1).
High probability of reporting bias (−1).
Results
Description of studies
See Characteristics of included studies table.
Results of the search
We identified 11,884 studies through the electronic and other searches. After removing duplicates, 9308 titles and abstracts remained. We examined the full text or contacted study authors (or both) for 131 records, excluding 82 records at this stage, with an additional three records that were identified as ongoing studies, leaving 46 records representing eight studies to be included in the analysis (see Figure 1). Several full texts that were reviewed indicated studies had recruited populations of 'opioid‐dependent people' without specifying the primary opioid used (e.g. whether the participant was dependent on a pharmaceutical opioid, heroin or opium). In each of these papers, where the full text did not explicitly indicate that the participants were dependent on pharmaceutical opioids, the review authors (SN, BL) contacted the study authors to determine if the study met eligibility criteria with respect to the opioid used being a pharmaceutical opioid (Li 2022). We included studies where the primary opioid of concern was clearly identified as a pharmaceutical opioid or where the study population included at least 10 participants who were dependent on pharmaceutical opioids and data were available to enable analyses of the study data only for those participants who were dependent on pharmaceutical opioids. Where authors were unable to provide further information on the primary drug of concern (other than being an opioid), or where we received no response, we excluded the study.
1.
Study flow diagram.
Included studies
We identified eight RCTs that met the inclusion criteria (709 participants). Four studies compared methadone and buprenorphine (Ahmadi 2003; Neumann 2013; Neumann 2020; Saxon 2013), and four studies compared buprenorphine maintenance to buprenorphine taper (in addition to psychological treatment) (Fiellin 2014; Woody 2008), brief intervention and referral to treatment (D'Onofrio 2015), or the opioid antagonist naltrexone (Lee 2018). The mean duration of the trials was 123 days (17.6 weeks).
Seven studies were conducted in an outpatient setting. One study recruited participants who were admitted to hospital, with one group randomised to commence buprenorphine as an inpatient while the other two groups offered a brief intervention and treatment referral information (D'Onofrio 2015). Neumann 2013 and Neumann 2020 recruited populations of people with chronic non‐cancer pain and opioid dependence. All other studies recruited participants with dependence on pharmaceutical opioids, and one study specifically recruited participants who were injecting buprenorphine (Ahmadi 2003).
Data from four studies represent a re‐analysis of parent studies to include only data from participants who were dependent on pharmaceutical opioids; three studies provided data for analyses through the Clinical Trials Network (CTN) data share website (Lee 2018; Saxon 2013; Woody 2008), and for one study, the study statistician provided the data for participants who were dependent on pharmaceutical opioids (D'Onofrio 2015). Fiellin 2014 also provided additional data to facilitate analyses with comparable outcome measures across the studies. Data for three studies were drawn directly from the published papers (Ahmadi 2003; Neumann 2013; Neumann 2020), supplemented by data reported on ClinicalTrials.gov for Neumann 2020.
Seven studies were conducted in the USA and one study was conducted in Iran (Ahmadi 2003). Seven studies recruited adults, and one study examined young people aged 15 to 21 years (Woody 2008).
Overall, the participants in the studies were 70.3% male and had a mean age of 32.0 years. The mean duration of the studies comparing different opioid maintenance treatments (four studies that compared methadone to buprenorphine) was 17.4 weeks, and the mean duration of studies comparing a maintenance treatment (three studies with buprenorphine maintenance) to detoxification, antagonist or psychological treatment was 13.6 weeks.
Excluded studies
Of the studies that we excluded during full‐text review, we excluded eight studies because all participants received the same opioid agonist (or partial agonist) medication, meaning that no comparison was possible: one study of buprenorphine for prescription opioid dependence because the study was an adaptive study design where the randomised trial component compared adjunctive counselling to standard care, and all participants received buprenorphine (resulting in there being no non‐opioid agonist comparison group) (Weiss 2011). Fiellin 2006; Ghalehney 2018; Gordon 2017; Gordon 2018; and Gordon 2019 described that all participants received buprenorphine, hence there was no non‐agonist arm for comparison. Chopra 2009 also examined different psychosocial adjunct treatments where all participants received buprenorphine. Both groups received methadone in Kim 2015.
One study contained prescription opioid‐dependent people in their population, but the number was too small (e.g. two or three participants) to permit meaningful analyses of the prescription opioid‐dependent participants across different treatment conditions (Liebschutz 2013). Two further studies recruited pharmaceutical opioid‐dependent participants to the study; we requested data to perform analyses for only those dependent on pharmaceutical opioids, but they were unavailable (Ling 2010; Rosenthal 2013).
Four studies were excluded due to not using the intervention of interest (i.e. did not administer maintenance opioid agonists, Amass 1994; Marsch 2016; Sigmon 2013; Stitzer 1983). Five studies had the wrong study design, as they were either not RCTs (Batki 1998; Bazazi 2017; Gossop 2001; Hoffmann 2014), or did not randomise the opioid condition as part of the study design (Watkins 2017).
Three articles were review articles or commentaries (Anon 2015; Bahji 2018; Raleigh 2017)
The remainder of the excluded studies had populations of opioid‐dependent people primarily using heroin, or we were unable to contact the author to confirm if the populations included people with pharmaceutical opioid dependence (see Excluded studies).
Studies awaiting classification
There are no studies awaiting classification.
Ongoing studies
There are three ongoing studies (Gordon 2021; Seval 2021; Socias 2018).
Risk of bias in included studies
Figure 2 and Figure 3 present a summary of the assessed risk of bias for each of the included studies.
2.
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
3.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study.
Allocation
All included studies were RCTs. For two studies, the method of sequence generation was unclear (Ahmadi 2003; Saxon 2013), and for five studies, the method of allocation concealment was unclear (Ahmadi 2003; Lee 2018; Neumann 2013; Neumann 2020; Saxon 2013). The remaining studies had low risk of random sequence or allocation bias. No studies had high risk of selection bias.
Blinding
None of the studies were double‐blind (most were described as open‐label studies), with all studies having either a high or unknown risk of performance and detection bias for subjective outcomes, and an unknown or high risk of performance bias for objective outcomes. Most studies had a low risk of detection bias on objective outcomes such as retention.
Incomplete outcome data
All studies reported data on retention. One study was at high risk of attrition bias as participants could switch treatments, and in one arm, 50% of the sample had switched from methadone to buprenorphine, and had greater loss‐to‐follow‐up in the buprenorphine arm (Neumann 2020). Three studies had differences in the number of participants retained and followed up across treatment arms, which introduced a high risk of attrition bias (D'Onofrio 2015; Fiellin 2014; Lee 2018). One study was at unclear attrition bias as it only presented data on treatment completer; however, the rates of retention were comparable for the two arms, reducing the likelihood that this would introduce bias (Neumann 2013). One study only reported retention with no other outcome data and was at unclear risk (Ahmadi 2003). Two studies were at low risk of bias (Saxon 2013; Woody 2008).
Selective reporting
Six studies had a low risk of reporting bias, with prospectively published protocols available or prospective clinical trial registration including describing main outcome measures or data published on open access websites, or a combination of these (D'Onofrio 2015; Lee 2018; Neumann 2013; Neumann 2020; Saxon 2013; Woody 2008). One study was at unclear risk of reporting bias as it had non‐primary outcomes that were registered and not reported, though these were unlikely to introduce bias (Fiellin 2014). One study reported only one outcome measure, retention and was at high risk of reporting bias (Ahmadi 2003).
Other potential sources of bias
One study did not report the funding source (Ahmadi 2003), and five studies reported that a pharmaceutical company provided the medicine (D'Onofrio 2015; Fiellin 2014; Lee 2018; Saxon 2013; Woody 2008).
Effects of interventions
See Table 1 and Table 2. We presented results for the two main comparisons:
opioid agonists versus other opioid agonists (or partial agonists) for maintenance treatment;
full or partial opioid agonists versus placebo, detoxification, opioid antagonist or psychological treatment (without maintenance agonist treatment).
The results in the summary of findings tables include the primary outcomes measures of opioid use, retention in treatment and adverse effects. Included studies provided data on the outcomes of opioid use, treatment retention, pain, risk behaviours, adverse effects, physical health and psychological health.
Full opioid agonists versus different full opioid agonists or partial opioid agonists
We found four studies comparing methadone versus buprenorphine (with or without naloxone) (Ahmadi 2003; Neumann 2013; Neumann 2020; Saxon 2013). We found no studies examining opioids agonists other than methadone or buprenorphine.
Primary outcomes
Illicit opioid use
We found moderate‐certainty evidence of no difference in days of unsanctioned opioid use (MD −1.41 days, 95% CI −3.37 to 0.55; 1 study, 129 participants; Analysis 1.1).
1.1. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 1: Days of illicit opioid use
We found low‐certainty evidence of no difference in point prevalence use at the end of treatment (urine‐analysis results) (RR 0.81, 95% CI 0.57 to 1.17; 3 studies, 206 participants; Analysis 1.2).
1.2. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 2: Opioid‐positive urine drug screen at treatment completion
We found low‐certainty evidence of a difference in point prevalence use at the end of treatments (self‐reported) in favour of methadone (RR 0.49, 95% CI 0.28 to 0.86; 2 studies, 165 participants; Analysis 1.3).
1.3. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 3: Self‐reported substance use (end of treatment)
Retention
We found low‐certainty evidence of a difference in favour of methadone for retention (number of participants retained at end of treatment) (RR 1.21, 95% CI 1.02 to 1.43; 4 studies, 379 participants; Analysis 1.4). When we conducted a sensitivity analysis to consider clinical heterogeneity, as the population in Ahmadi 2003 consisted of people who injected buprenorphine (a different population from the other three studies), there was no evidence of a difference between methadone and buprenorphine in retention (RR 1.10, 95% CI 0.92 to 1.30).
1.4. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 4: Retention
Adverse effects
We found low‐certainty evidence of no difference in adverse events between methadone and buprenorphine (RR 1.13, 95% CI 0.66 to 1.93; 3 studies, 206 participants; Analysis 1.5). Neumann 2013 described self‐reported side‐effects from study medications (no further details), and Saxon 2013 had a small number of documented serious adverse events (with no further details available). Neumann 2020 reported non‐medical use of study medication (methadone).
1.5. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 5: Adverse effects
Secondary outcomes
Pain
There was no evidence of a difference in pain using different measures (improvement from baseline pain, pain using a 100‐mm visual analogue scale (VAS), and mean bodily pain as measured by the SF‐36 (SMD −0.12, 95% CI −0.73 to 0.50; 3 studies, 163 participants; Analysis 1.6).
1.6. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 6: Pain
Risk behaviours
There was no evidence of a difference in risk behaviours (RR 0.52, 95% CI 0.02 to 12.64; 1 study, 170 participants; Analysis 1.7).
1.7. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 7: Risk behaviours
Aberrant opioid‐related behaviours
None of the studies reported aberrant opioid‐related behaviours.
Employment
None of the studies reported on employment.
Quality of life
None of the studies reported an overall quality of life score.
Physical health
There was no evidence of a difference in mean physical functioning (SF‐36) (MD 1.28, 95% CI −3.83 to 6.39; 1 study, 127 participants; Analysis 1.8).
1.8. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 8: Physical health
Psychological health
There was no evidence of a difference in mental health functioning (SF‐36 and Beck Depression Inventory) (SMD −0.08, 95% CI −0.42 to 0.26; 2 studies, 137 participants; Analysis 1.9).
1.9. Analysis.
Comparison 1: Full opioid agonists versus different full opioid agonists or partial opioid agonists, Outcome 9: Psychological health
Full or partial opioid agonist maintenance versus non‐opioid treatment condition (buprenorphine maintenance compared to detoxification, opioid antagonist or psychological treatment)
We found four studies comparing buprenorphine maintenance treatment to a non‐opioid agonist control condition (D'Onofrio 2015; Fiellin 2014; Lee 2018; Woody 2008). We found no studies that compared opioid agonist treatment other than buprenorphine to a non‐opioid agonist control condition.
Primary outcomes
Illicit opioid use
We found low‐certainty evidence of no difference on the outcome of days of self‐reported unsanctioned opioid use (reported as mean days in past 7 or 30 days: SMD −0.19, 95% CI −0.47 to −0.09; 3 studies, 205 participants; Analysis 2.1).
2.1. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 1: Days of illicit opioid use (7 or 30 days)
We found low‐certainty evidence of a difference in favour of buprenorphine maintenance treatment for lower point prevalence of opioid use at the end of treatment as determined by urinalysis (RR 0.66, 95% CI 0.52 to 0.84; 4 studies, 270 participants; Analysis 2.2).
2.2. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 2: Opioid positive (per urine drug screen, last week of treatment maintenance)
We found very low‐certainty evidence of no difference for point prevalence of self‐reported opioid use at the end of treatment (RR 0.63, 95% CI 0.39 to 1.01; 4 studies, 276 participants; Analysis 2.3). We conducted a sensitivity analysis to address the substantial heterogeneity (I2 = 52%). When we removed Woody 2008 from the analysis due to statistical heterogeneity, there was a difference in favour of buprenorphine maintenance (RR 0.71, 95% CI 0.54 to 0.93; I2 = 0%; 3 studies, 249 participants).
2.3. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 3: Self‐reported opioid use at treatment completion (past 30 days)
Retention
We found moderate‐certainty evidence of a difference in favour of buprenorphine maintenance for treatment for retention (RR 3.02, 95% CI 1.73 to 5.27; 4 studies, 333 participants; Analysis 2.4). We conducted a sensitivity analysis to address the substantial heterogeneity (I2 = 73%). When we removed D'Onofrio 2015 from the analysis due to statistical and clinical heterogeneity, there remained a difference favouring buprenorphine maintenance (RR 3.66, 95% CI 2.11 to 6.32; I2 = 47%), although moderate heterogeneity was still present.
2.4. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 4: Retention
Adverse effects
We found very low‐certainty evidence of no difference in adverse events (RR 0.50, 95% CI 0.07 to 3.48; 3 studies, 252 participants; Analysis 2.5). The three studies measured outcomes differently, one study reported protective transfer (Fiellin 2014); one study had data available on serious adverse events (Woody 2008); and one study had data available on adverse events and serious adverse events (Lee 2018). We conducted sensitivity analysis to address the considerable heterogeneity (I2 = 83%). When we removed Lee 2018, there was a difference between buprenorphine maintenance and non‐opioid treatment approaches in favour of buprenorphine maintenance with fewer adverse events (RR 0.19, 95% CI 0.06 to 0.57; 2 studies, 166 participants).
2.5. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 5: Adverse events
Lee 2018 indicated no evidence of a difference in adverse events between buprenorphine maintenance and naltrexone maintenance. Woody 2008 found fewer adverse events with buprenorphine maintenance (RR 31.08, 95% CI 12.40 to 49.76).
Secondary outcomes
Pain
There was no evidence of a difference between the proportion of participants who reported 'moderate' to 'extreme' pain or discomfort at the end of treatment (RR 0.74, 95% CI 0.35 to 1.56; 2 studies, 102 participants; Analysis 2.6). There was substantial heterogeneity (I2 = 55%); however, results of the individual studies also indicated no evidence of a difference between buprenorphine maintenance and the comparison condition.
2.6. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 6: Pain (moderate to extreme pain)
Risk behaviours
There was no evidence of a difference in events of risk behaviour (RR 0.92, 95% CI 0.25 to 3.40; 3 studies, 177 participants; Analysis 2.7).
2.7. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 7: Risk behaviours
Aberrant opioid‐related behaviours
None of the studies reported aberrant opioid‐related behaviours.
Employment
None of the studies reported on employment.
Quality of life
None of the studies reported an overall quality of life measure.
Physical health
Two studies examined physical health on a 100‐point self‐reported VAS at the end of treatment. One study comparing injectable naltrexone to buprenorphine found no evidence of a difference in physical health (MD 0.80, 95% CI −7.68 to 9.28). There was considerable heterogeneity with the meta‐analysis (I2 = 88%), so results of these two studies were not pooled.
Psychological health
There was no evidence of a difference in proportions of participants reporting 'moderate' to 'extreme' anxiety and depression at the end of treatment (RR 1.02, 95% CI 0.70 to 1.50; 2 studies, 102 participants; Analysis 2.9). There was no evidence of a difference in depression as measured using the Hamilton Depression Scale between buprenorphine maintenance and naltrexone (RR −0.40, 95% CI −2.8 to 2.00; 1 study, 65 participants; Analysis 2.10).
2.9. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 9: Psychological health (moderate to extremely anxious or depressed)
2.10. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 10: Psychological health (continuous)
Discussion
Summary of main results
The identified studies compared methadone versus buprenorphine maintenance treatment (four studies), and buprenorphine maintenance treatment versus detoxification, opioid antagonist or psychological treatment (without maintenance agonist treatment); two studies where the comparison was buprenorphine taper, one study where the comparison was naltrexone, and one study where the control condition was brief intervention and referral. In total, the review included eight studies with 709 participants.
The certainty of the evidence was generally low to moderate with all studies being RCTs that were not double‐blind (see Table 1; Table 2). Sample sizes were generally small, from 19 to 204 participants, with the two smallest studies also having high rates of attrition. The meta‐analyses included data for the primary outcomes of opioid use, retention and adverse effects.
There was low‐certainty evidence of a difference in self‐reported opioid use in favour of methadone, and no evidence of a difference in opioid use as measured by opioid‐positive urine drug tests between methadone and buprenorphine. There was low‐certainty evidence of a difference in retention in favour of methadone, which was no longer significant when we considered heterogeneity in the clinical populations.
For buprenorphine maintenance compared with non‐opioid treatments (detoxification, opioid antagonist or other psychological treatment in the absence of maintenance opioid pharmacotherapy), low‐ to moderate‐certainty evidence favoured maintenance buprenorphine treatment with opioid‐positive urine tests and with greater retention in treatment. These findings suggest that where retention and opioid use outcomes are important to patient and clinician, there appear to be advantages in maintenance opioid agonist treatment over non‐opioid agonist treatment approaches.
Overall completeness and applicability of evidence
There was enough consistency in the way the studies collected and reported primary outcome measures to enable pooling data.
Ahmadi 2003 contributed just under one‐third of the sample size, and represented a population of people who injected buprenorphine. As such, the population in this study may differ from the populations of the other two studies, and from the most common populations of pharmaceutical opioid dependence who may seek treatment. Sensitivity analyses confirmed that the exclusion of this study changed the overall result of the meta‐analyses on the outcome of retention, which was the only outcome reported in that study.
A limitation to generalisability is study location. Seven of the eight studies were conducted in the USA, making it difficult to know how these findings may apply to people who are dependent on pharmaceutical opioids in other settings.
Quality of the evidence
The studies in this review were generally either small, or the sample size was small once the population was restricted to only people who were dependent on pharmaceutical opioids. Two studies had larger sample sizes; Saxon 2013 (170 participants in the analyses of only people who were dependent upon pharmaceutical opioids) and Ahmadi 2003 (204 participants, although this study reported only one outcome). No studies had high risk of selection bias, though none of the studies were double‐blind. Six studies had low risk of reporting bias. See Figure 2 and Figure 3.
Missing data introduced the potential for bias in opioid use outcome measures. Two small studies had high rates of attrition, and also allowed patient cross‐over into the other treatment arm, making interpretation of results difficult (Neumann 2013; Neumann 2020).
One studies had the primary outcome of 'enrolment in addiction treatment 30 days after randomisation', as the study was examining commencing buprenorphine maintenance treatment as an inpatient versus two other conditions where participants received a brief intervention and referral to addiction treatment (we combined these two other non‐buprenorphine groups in the present analyses) (D'Onofrio 2015). As such, the evidence from this study on opioid use outcomes could be considered indirect as the study did not directly aim to reduce opioid use. The study population was also not treatment seeking. Finally, data for four studies were from existing larger studies of opioid‐dependent people, rather than from studies specifically developed to examine the effectiveness of these interventions for pharmaceutical opioid‐dependent people (D'Onofrio 2015; Lee 2018; Saxon 2013; Woody 2008).
Potential biases in the review process
There is the possibility that studies with negative findings on pharmacotherapy may be less likely to be published, which could potentially favour the finding of published studies that demonstrate an effect of pharmacotherapy treatments. We found no conference abstracts of unpublished studies to confirm or suggest that this was the case.
Agreements and disagreements with other studies or reviews
The finding of a difference in retention between methadone and buprenorphine is consistent with findings reported in studies of predominantly people dependent on heroin, where Mattick 2014 found evidence in favour of methadone retaining more participants in treatment.
Findings were consistent with a larger adaptive study design that also appeared to favour longer periods of buprenorphine treatment, with poorer outcomes following buprenorphine taper among pharmaceutical opioid‐dependent people (Weiss 2011).
Authors' conclusions
Implications for practice.
There was low‐certainty evidence favouring maintenance agonist pharmacotherapy with methadone over buprenorphine for pharmaceutical opioid dependence on some outcomes. It is possible that methadone treatment may support increased retention in treatment, though the difference between the treatments was small, and was no longer evident once heterogeneity was considered. There was low‐certainty evidence favouring methadone on self‐reported substance use. There was no difference on this outcome using the objective measure of urine drug screens. Due to the safety profile of methadone, and its restricted availability in some settings, other clinician or treatment system factors may also inform the choice of pharmacotherapy for patients, including patient preference, safety and availability of medications.
Maintenance treatment with buprenorphine may be more effective than detoxification, opioid antagonist or psychological treatments.
Due to the overall low‐ to moderate‐certainty evidence and smaller sample sizes, there is the possibility that the further research may change these findings.
Implications for research.
Given the high prevalence of chronic pain among people who are dependent upon pharmaceutical opioids (Lusted 2013; Voon 2017), larger studies are needed to examine outcomes for people with pain and opioid dependence. In the current review, only two small studies with high attrition rates examined outcomes among people with concurrent pain and opioid dependence (Neumann 2013; Neumann 2020). In addition, the inclusion of standardised measures of pain severity and pain interference as secondary outcomes measures in randomised controlled trials of opioid treatments would support meta‐analysis in the future (Turk 2008). Studies that specifically recruit pharmaceutical opioid‐dependent people will add to the evidence base that is currently formed in large part by secondary data analyses from previously completed clinical trials.
What's new
| Date | Event | Description |
|---|---|---|
| 5 September 2022 | New citation required and conclusions have changed | Review has been updated |
| 5 September 2022 | New search has been performed | Review updated |
History
Protocol first published: Issue 5, 2014 Review first published: Issue 5, 2016
Acknowledgements
We thank Mary Kumvaj and Zuzana Mitrova for their assistance in developing the search strategy and running the searches for the original review, and the review update, respectively; and Philip Claire and Dr Ting Xia for assistance with data analyses in the original review and the update, respectively. We acknowledge Louisa Degenhardt for her assistance in screening articles for the updated review. We thank the following people who contributed to the original 2016 review: Louisa Degenhardt, Linda Gowing, Cheyanne Kehler and Nicholas Lintzeris.
We would also like to thank the following peer reviewers for their comments: Jan Klimas (University of British Columbia) and Anees Bahji (University of Calgary) for the review manuscript.
Appendices
Appendix 1. Criteria for risk of bias assessment
| Item | Judgement | Description |
| Random sequence generation (selection bias) |
Low risk | The investigators describe a random component in the sequence generation process such as: random number table; computer random number generator; coin tossing; shuffling cards or envelopes; throwing dice; drawing of lots; minimisation. |
| High risk | The investigators describe a non‐random component in the sequence generation process such as: odd or even date of birth; date (or day) of admission; hospital or clinic record number; alternation; judgement of the clinician; results of a laboratory test or a series of tests; availability of the intervention. | |
| Unclear risk | Insufficient information about the sequence generation process to permit judgement of low or high risk. | |
| Allocation concealment (selection bias) |
Low risk | Investigators enrolling participants could not foresee assignment because 1 of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based, and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes. |
| High risk | Investigators enrolling participants could possibly foresee assignments because 1 of the following methods was used: open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards (e.g. if envelopes were unsealed or non‐opaque or not sequentially numbered); alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure. | |
| Unclear risk | Insufficient information to permit judgement of low or high risk. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement. | |
| Blinding of participants and providers (performance bias): objective outcomes |
Low risk | No blinding or incomplete blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding. Blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken. |
| High risk | No blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding or blinding of key study participants and personnel attempted, but likely that the blinding could have been broken, and the outcome is likely to be influenced by lack of blinding. | |
| Unclear risk | Insufficient information to permit judgement of low or high risk. | |
| Blinding of participants and providers (performance bias): subjective outcomes |
Low risk | Blinding of participants and providers and unlikely that the blinding could have been broken. |
| High risk | No blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding. Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken, and the outcome is likely to be influenced by lack of blinding. |
|
| Unclear risk | Insufficient information to permit judgement of low or high risk. | |
| Blinding of outcome assessor (detection bias): subjective outcomes |
Low risk | No blinding of outcome assessment, but the review authors judge that the outcome measurement is not likely to be influenced by lack of blinding Blinding of outcome assessment ensured, and unlikely that the blinding could have been broken. |
| High risk | No blinding of outcome assessment, and the outcome measurement is likely to be influenced by lack of blinding. Blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement is likely to be influenced by lack of blinding. |
|
| Unclear risk | Insufficient information to permit judgement of low or high risk. | |
| Incomplete outcome data (attrition bias): for all outcomes except retention |
Low risk |
No missing outcome data. Reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias). Missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups. For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk not enough to have a clinically relevant impact on the intervention effect estimate. For continuous outcome data, plausible effect size (difference in means or standardised difference in means) among missing outcomes not enough to have a clinically relevant impact on observed effect size. Missing data have been imputed using appropriate methods. All randomised participants are reported/analysed in the group they were allocated to by randomisation irrespective of non‐compliance and co‐interventions (intention to treat). |
| High risk | Reason for missing outcome data likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in intervention effect estimate. For continuous outcome data, plausible effect size (difference in means or standardised difference in means) among missing outcomes enough to induce clinically relevant bias in observed effect size. 'As‐treated' analysis done with substantial departure of the intervention received from that assigned at randomisation. |
|
| Unclear risk | Insufficient information to permit judgement of low or high risk (e.g. number randomised not stated, no reasons for missing data provided; number of dropout not reported for each group). | |
| Selective reporting (reporting bias) |
Low risk | The study protocol is available and all of the study's prespecified (primary and secondary) outcomes that are of interest in the review have been reported in the prespecified way. The study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were prespecified (convincing text of this nature may be uncommon). |
| High risk | Not all of the study's prespecified primary outcomes have been reported ≥ 1 primary outcomes is reported using measurements, analysis methods, or subsets of the data (e.g. subscales) that were not prespecified ≥ 1 reported primary outcomes were not prespecified (unless clear justification for their reporting is provided, such as an unexpected adverse effect) ≥ 1 outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis. The study report fails to include results for a key outcome that would be expected to have been reported for such a study. |
|
| Unclear risk | Insufficient information to permit judgement of low or high risk. |
Appendix 2. Search strategies 2022
Cochrane Drugs and Alcohol Group (CDAG) Specialised Register of Trials
Searched: 2015 to 28 January 2022
#1 (((prescript* OR prescrib* OR pharmaceutical) NEAR (opioid* OR opiate*))) AND INREGISTER
#2 (opiate* OR opioid*):XDI AND INREGISTER
#3 ((buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or opiate* or opioid* or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) NEAR2 (abuse* or abusing or addict* or misus* or depend*)) AND INREGISTER
#4 #2 OR #3
#5 #1 AND #4
#6 2015 TO 2022:YR AND INREGISTER
#7 #5 AND #6
Cochrane Central Register of Controlled Trials (CENTRAL)
Searched: Issue 1, 2022
#1 MeSH descriptor: [Opioid‐Related Disorders] explode all trees
#2 MeSH descriptor: [Substance Abuse, Intravenous] explode all trees
#3 ((buprenorphine OR dihydromorphine OR diamorphine OR hydromorphone OR methadone OR morphine OR opioid* OR opiate* OR oxycodone OR oxymorphone OR fentanyl OR levorphanol OR pethidine OR meperidine) NEAR/3 (abuse* OR abusing OR addict* OR misus* OR depend* OR disorder*)):ti,ab
#4 ((non NEXT medical OR nonmedical) NEAR (use* or using or misuse* or abus* or dependence* or dependent* or addict*)):ti,ab 165
#5 #1 OR #2 OR #3 OR #4
#6 ((prescript* OR prescrib* OR pharmaceutical) NEAR (opioid* OR opiate*)):ti,ab,kw
#7 MeSH descriptor: [Prescription Drugs] explode all trees
#8 MeSH descriptor: [Narcotics] this term only
#9 MeSH descriptor: [Analgesics, Opioid] explode all trees
#10 #5 and #9
#11 ((buprenorphine OR dihydromorphine OR diamorphine OR hydromorphone OR methadone OR morphine OR oxycodone OR oxymorphone OR fentanyl OR levorphanol OR pethidine OR meperidine) NEAR/2 (abuse* OR abusing OR addict* OR misus* OR depend* )):ti,ab
#12 #10 OR #11 with Publication Year from 2015 to present, in Trials
Ovid MEDLINE(R)
Searched: 2015 to 28 January 2022
1 exp Opioid‐Related Disorders/
2 Substance Abuse, Intravenous/
3 ((buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or opioid* or opiate* or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) adj3 (abuse* or abusing or addict* or misus* or depend* or disorder*)).tw.
4 ((non‐medical or nonmedical) adj2 (use* or using or misuse* or abus* or dependence* or dependent* or addict*)).ti,ab.
5 1 or 2 or 3 or 4
6 ((prescript* or prescrib* or pharmaceutical) adj3 (opioid* or opiate*)).mp.
7 exp Prescription Drugs/
8 exp Analgesics, Opioid/
9 Narcotics/
10 6 or 7 or 8 or 9
11 5 and 10
12 ((buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) adj2 (abuse* or abusing or addict* or misus* or depend*)).tw.
13 11 or 12
14 Opiate Substitution Treatment/
15 (opioid agonist* adj2 (therap* or treatment*)).mp.
16 (maintenance adj2 (therapy or treatment)).mp.
17 (MMT or BMT or OST or OAT).ti,ab.
18 (methadone or buprenorphine or codeine or morphine or LAAM or oxycodone).mp.
19 14 or 15 or 16 or 17 or 18
20 13 and 19
21 randomized controlled trial.pt.
22 controlled clinical trial.pt.
23 random*.ab.
24 placebo.ab.
25 clinical trials as topic.sh.
26 random allocation.sh.
27 trial.ti.
28 21 or 22 or 23 or 24 or 25 or 26 or 27
29 exp animals/ not humans.sh.
30 28 not 29
31 20 and 30
32 limit 31 to yr="2015 ‐Current"
Ovid Embase
Searched: 2015 to 28 January 2022
1 exp opiate addiction/
2 intravenous drug abuse/
3 ((buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or opioid* or opiate* or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) adj3 (abuse* or abusing or addict* or misus* or depend* or disorder*)).tw.
4 ((non‐medical or nonmedical) adj2 (use* or using or misuse* or abus* or dependence* or dependent* or addict*)).ti,ab.
5 1 or 2 or 3 or 4
6 ((prescript* or prescrib* or pharmaceutical) adj3 (opioid* or opiate*)).mp.
7 prescription drug/ and exp addiction/
8 Prescription Drug Misuse/
9 exp narcotic agent/ and exp addiction/
10 6 or 7 or 8 or 9
11 5 and 10
12 ((buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) adj2 (abuse* or abusing or addict* or misus* or depend*)).tw.
13 11 or 12
14 opiate substitution treatment/
15 (opioid agonist* adj2 (therap* or treatment*)).mp.
16 (maintenance adj2 (therapy or treatment)).mp.
17 (MMT or BMT or OST or OAT).ti,ab.
18 buprenorphine/
19 methadone treatment/ or maintenance therapy/
20 ((methadone or buprenorphine or codeine or morphine or LAAM or oxycodone) and (therap* or treatment* or mainten* or program*)).tw.
21 14 or 15 or 16 or 17 or 18 or 19 or 20
22 Clinical‐Trial/ or Randomized‐Controlled‐Trial/ or Randomization/ or Single‐Blind‐Procedure/ or Double‐Blind‐Procedure/ or Crossover‐Procedure/ or Prospective‐Study/ or Placebo/
23 (((clinical or control or controlled) adj (study or trial)) or ((single or double or triple) adj (blind$3 or mask$3)) or (random$ adj (assign$ or allocat$ or group or grouped or patients or study or trial or distribut$)) or (crossover adj (design or study or trial)) or placebo or placebos).ti,ab.
24 22 or 23
25 13 and 21
26 24 and 25
27 limit 26 to yr="2015 ‐Current"
Ovid PsycINFO
Searched: 2015 to 28 January 2022
1 exp Drug Dependency/ or exp Drug Abuse/ or exp Drug Withdrawal/ or exp Drug Addiction/
2 addiction/
3 ((narcotic$ or opiate$ or opioid$ or morphin$) adj3 (misuse or abuse$ or addict$ or depend$)).ti,ab.
4 1 or 2 or 3
5 ((opioid* or opiat*) adj3 analges*).ti,ab.
6 narcotic agonists/ or narcotic drugs/ or apomorphine/ or meperidine/ or methadone/ or tramadol/ or analgesic drugs/
7 exp Morphine/ or exp Analgesia/ or exp Analgesic Drugs/
8 prescription drugs/
9 ((prescript* or prescrib* or pharmaceutical) adj3 (opioid* or opiate*)).ti,ab.
10 5 or 6 or 7 or 8 or 9
11 4 and 10
12 animals/ not (animals/ and human$.mp.)
13 (animal/ or animals/) not ((animal/ and human/) or (animals/ and humans/))
14 (animal not (animal and human)).po.
15 random$.mp.
16 trial.mp.
17 groups.mp.
18 placebo.mp.
19 exp Clinical Trials/
20 or/15‐19
21 20 not (12 or 13 or 14)
22 11 and 21
23 limit 22 to yr="2015 ‐Current"
EBSCO CINAHL
Searched: 2015 to 28 January 2022
S28 S21 AND S27
S27 S22 OR S23 OR S24 OR S25 OR S26
S26 "Opiate Substitution Treatment"
S25 TX (methadone or buprenorphine or codeine or morphine or LAAM or oxycodone)
S24 TI ( (MMT or BMT or OST or OAT) ) OR AB ( (MMT or BMT or OST or OAT) )
S23 TX (maintenance N2 (therapy or treatment))
S22 TX (agonist* N2 (therap* or treatment*))
S21 S10 AND S19
S20 S10 AND S19
S19 S11 OR S12 OR S13 OR S14 OR S15 OR S16 OR S17 OR S18
S18 TI placebo* or AB placebo*
S17 TI random* allocat* or AB random* allocat*
S16 MH "Random Assignment"
S15 AB ( singl* or doubl* or trebl* or tripl* ) and AB ( blind* or mask* )
S14 TI ( singl* or doubl* or trebl* or tripl* ) and TI ( blind* or mask* )
S13 TI clinic* N1 trial* or AB clinic* N1 trial*
S12 PT Clinical trial
S11 MH "Clinical Trials+"
S10 S3 AND S9
S9 S4 OR S5 OR S6 OR S7 OR S8
S8 TX (prescript* or prescrib* or pharmaceutical) N3 (opioid* or opiate*)
S7 (MH "Drugs, Prescription")
S6TX (analges* N6 (opioid* or opiate*))
S5 MH "Analgesics, Opioid+"
S4 (MH "Narcotics+")
S3 S1 OR S2
S2 TX (buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or opioid* or opiate* or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) N3 (abuse* or abusing or addict* or misus* or depend* or disorder*)
S1 (MH "Substance Use Disorders+")
Web of Science (Clarivate Analytics)
Searched: 2015 to 28 January 2022
TS= clinical trial* OR TS=research design OR TS=comparative stud* OR TS=evaluation stud* OR TS=controlled trial* OR TS=follow‐up stud* OR TS=prospective stud* OR TS=random* OR TS=placebo* OR TS=(single blind*) OR TS=(double blind*)
TS=((buprenorphine or dihydromorphine or diamorphine or hydromorphone or methadone or morphine or opioid* or opiate* or oxycodone or oxymorphone or fentanyl or levorphanol or pethidine or meperidine) NEAR/3 (abuse* or abusing or addict* or misus* or depend*) )
TS=((opioid* or opiat*) near/2 analges*)
TS=((prescript* or prescrib* or pharmaceutical) NEAR/3 (opioid* or opiate*) )
#5 OR #4 OR #3
#6 AND #2 AND #1
Indexes=SCI‐EXPANDED, SSCI, A&HCI, CPCI‐S, CPCI‐SSH, ESCI Timespan=2015‐2022
Data and analyses
Comparison 1. Full opioid agonists versus different full opioid agonists or partial opioid agonists.
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
|---|---|---|---|---|
| 1.1 Days of illicit opioid use | 1 | 129 | Mean Difference (IV, Random, 95% CI) | ‐1.41 [‐3.37, 0.55] |
| 1.2 Opioid‐positive urine drug screen at treatment completion | 3 | 206 | Risk Ratio (M‐H, Random, 95% CI) | 0.81 [0.57, 1.17] |
| 1.3 Self‐reported substance use (end of treatment) | 3 | 165 | Risk Ratio (M‐H, Random, 95% CI) | 0.49 [0.28, 0.86] |
| 1.4 Retention | 4 | 379 | Risk Ratio (M‐H, Random, 95% CI) | 1.21 [1.02, 1.43] |
| 1.5 Adverse effects | 3 | 206 | Risk Ratio (M‐H, Random, 95% CI) | 1.13 [0.66, 1.93] |
| 1.6 Pain | 3 | 163 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.12 [‐0.73, 0.50] |
| 1.7 Risk behaviours | 1 | 170 | Risk Ratio (M‐H, Random, 95% CI) | 0.52 [0.02, 12.64] |
| 1.8 Physical health | 1 | 127 | Mean Difference (IV, Random, 95% CI) | 1.28 [‐3.83, 6.39] |
| 1.9 Psychological health | 2 | 137 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.08 [‐0.42, 0.26] |
Comparison 2. Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only.
| Outcome or subgroup title | No. of studies | No. of participants | Statistical method | Effect size |
|---|---|---|---|---|
| 2.1 Days of illicit opioid use (7 or 30 days) | 3 | 205 | Std. Mean Difference (IV, Random, 95% CI) | ‐0.19 [‐0.47, 0.09] |
| 2.2 Opioid positive (per urine drug screen, last week of treatment maintenance) | 4 | 270 | Risk Ratio (M‐H, Random, 95% CI) | 0.66 [0.52, 0.84] |
| 2.3 Self‐reported opioid use at treatment completion (past 30 days) | 4 | 276 | Risk Ratio (IV, Random, 95% CI) | 0.63 [0.39, 1.01] |
| 2.4 Retention | 4 | 333 | Risk Ratio (M‐H, Random, 95% CI) | 3.02 [1.73, 5.27] |
| 2.5 Adverse events | 3 | 252 | Risk Ratio (M‐H, Random, 95% CI) | 0.50 [0.07, 3.48] |
| 2.6 Pain (moderate to extreme pain) | 2 | 102 | Risk Ratio (M‐H, Random, 95% CI) | 0.74 [0.35, 1.56] |
| 2.7 Risk behaviours | 3 | 177 | Risk Ratio (M‐H, Random, 95% CI) | 0.92 [0.25, 3.40] |
| 2.8 Physical health | 2 | Mean Difference (IV, Random, 95% CI) | Totals not selected | |
| 2.9 Psychological health (moderate to extremely anxious or depressed) | 2 | 102 | Risk Ratio (M‐H, Random, 95% CI) | 1.02 [0.70, 1.50] |
| 2.10 Psychological health (continuous) | 1 | 65 | Mean Difference (IV, Random, 95% CI) | ‐0.40 [‐2.80, 2.00] |
2.8. Analysis.
Comparison 2: Full or partial opioid agonist maintenance versus placebo, antagonist, detoxification or psychological treatment only, Outcome 8: Physical health
Characteristics of studies
Characteristics of included studies [ordered by year]
Ahmadi 2003.
| Study characteristics | ||
| Methods | Open label randomised controlled trial | |
| Participants | Participants had reported daily buprenorphine injection for ≥ 6 months 80% had a history of heroin or opium dependence prior to buprenorphine injection 100% male Mean age 31.2 years (range 17–53 years) No current use of substances reported |
|
| Interventions | Oral methadone 50 mg (n = 68) Sublingual buprenorphine 5 mg (n = 68) Oral naltrexone 50 mg (n = 68) For 12 weeks |
|
| Outcomes | Retention | |
| Notes | No other outcome measures reported. A second publication appeared to report findings from the same study. Included only the first publication on the study. Funding for the study not reported. | |
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Unclear risk | Insufficient information provided to enable assessment. |
| Allocation concealment (selection bias) | Unclear risk | Insufficient information provided to enable assessment. |
| Blinding of participants and personnel (performance bias) Objective outcomes | Unclear risk | Insufficient information provided to enable assessment. |
| Blinding of outcome assessment (detection bias) Objective measures | Unclear risk | Insufficient information provided to enable assessment. |
| Incomplete outcome data (attrition bias) All outcomes | Unclear risk | Insufficient information provided to enable assessment. |
| Selective reporting (reporting bias) | High risk | Information was only reported on retention. |
Woody 2008.
| Study characteristics | ||
| Methods | Open‐label randomised controlled trial of buprenorphine (+ naloxone) maintenance compared with buprenorphine detoxification | |
| Participants | Opioid dependent youths aged 15–21 years Analyses from unpublished data reported represents only those participants (n = 53) who reported that a pharmaceutical opioid was their main drug problem Mean age of participants reporting pharmaceutical opioid as a main drug problem 20.0 (SD 1.3) years 64% male |
|
| Interventions | Sublingual buprenorphine–naloxone maintenance + weekly individual and group counselling (n = 27) for 12 weeks Sublingual buprenorphine detoxification for 14 days in addition to weekly individual and group counselling for 12 weeks (n = 26) |
|
| Outcomes | Primary outcome: opioid‐positive urine tests at weeks 4, 8 and 12 | |
| Notes | All outcomes reported in this analysis were for week 8 as buprenorphine taper began in week 9, meaning at week 12 participants were no longer in maintenance treatment. Disclosures: quote: "Dr Woody reported being a member of the RADARS [Researched Abuse, Diversion and Addiction‐Related Surveillance] postmarketing study external advisory group whose job is to assess abuse of prescription medications. Denver Health administers RADARS and Abbott, Cephalon, Endo, Pricara/Ortho‐McNeil, Purdue Pharma, and Shire subscribe to its data. Dr Woody reported that Ortho‐McNeil and Purdue Pharma funded similar work by him prior to his joining RADARS. Dr Woody reported that Schering‐Plough, the European distributor for buprenorphine‐naloxone, funded his travel costs to meetings in Sweden and Finland in June 2008 to present data from this study. Dr Bogenschutz reported receiving research funding from Forest and Lilly and having a confidentiality agreement with Lilly. Dr Forman reported being a faculty member at the University of Pennsylvania and co‐principal investigator with Dr Woody on the Delaware Valley Node of the NIDA Clinical Trials Network until December 2005 when he joined Alkermes. Dr Patkar reported being a consultant to Bristol‐Meyers Squibb, GlaxoSmithKline, and Reckitt Benckiser and being on the speakers' bureau for and receiving honoraria from Bristol‐Meyers Squibb, Forest, GlaxoSmithKline, Janssen, Jazz Pharmaceuticals Lundbeck, McNeil Consumer & Specialty Inc, Organon, and Pfizer. Dr Publicker reported having been a speaker for Cephalon, Forest, and Reckitt Benckiser. Dr McNicholas reported having conducted training programs to certify physicians in the use of buprenorphine. Her expenses have been paid by unrestricted grants to universities that were often provided by Reckitt Benckiser. Dr Fudala reported having been employed by the University of Pennsylvania and Philadelphia VA Medical Center from 1991 until he joined Reckitt Benckiser in June 2005 and reported having been a consultant to Johnson & Johnson and Purdue Pharma." Study supported by the NIDA and Reckitt Benckiser provided medication for the study |
|
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Quote: "Randomization occurred through an automated 24‐hour service at the Veterans Affairs Cooperative Studies Program in Perry Point, Maryland, that was programmed to randomise patients separately by site." |
| Allocation concealment (selection bias) | Low risk | Quote: "Randomization occurred through an automated 24‐hour service at the Veterans Affairs Cooperative Studies Program in Perry Point, Maryland, that was programmed to randomise patients separately by site." Central randomisation procedures, condition could not be foreseen by staff. |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | High risk | Quote: "Research assistants likely know group assignments because the study was not blinded." Open‐label study |
| Blinding of participants and personnel (performance bias) Objective outcomes | High risk | Quote: "Research assistants likely know group assignments because the study was not blinded." Open‐label study |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Detection bias is unlikely to influence results for objective measures such as retention. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | Quote: "Research assistants likely know group assignments because the study was not blinded." Open‐label study. |
| Incomplete outcome data (attrition bias) All outcomes | Low risk | Investigators used multiple statistical approaches to examine the impact of missing data on their results, and it appears the results of these analyses did not alter the results of the study findings. Quote: "A pattern‐mixture model was used to assess the impact of missing data on urine test results. Pattern mixture models extend the basic repeated measures by including a variable that describes the main patterns of missing data as a main effect and an interaction with other variables (week and group). Significant interactions with the missing data indicator on the main variables suggest that its effects differ across levels of missing data and that missing data may not be ignorable. Following suggested guidelines, we used time of last data provision (a categorical variable representing week 4, 8, or 12) as the missing variable. Another approach often taken is to impute missing tests as positive. If results obtained for the original and imputed models differ substantially, missing data may not be ignorable. Both methods were used to evaluate the effects of data on the primary outcome wherein missing urine test results were counted as opioid positive. A GEE [generalised estimating equation] model that ignored missing data showed a marginal group × time interaction (P = .09). While not attaining the usual 5% significance, it likely reflected a lack of power for interaction effects rather than constant treatment effects at each time point." "Because there were no interactions pertaining to dropout time, results suggested that missing data were not invalidating the group effect." |
| Selective reporting (reporting bias) | Low risk | Protocol and data were available on an open access CTN datashare website. |
Saxon 2013.
| Study characteristics | ||
| Methods | Open‐label randomised controlled trial of methadone vs buprenorphine | |
| Participants | Reported analyses of unpublished data only for participants who used only pharmaceutical opioids in the 30 days prior to the study (n = 170) 61% (n = 104) men Mean age 34.4 (SD 10.1) years at baseline 83% white with no difference between randomisation groups on demographic characteristics Participants who were randomised to the buprenorphine group were less likely to report a history of heroin use (odds ratio 0.47, 95% confidence interval 0.25 to 0.88) Past year dependence on other substance was: alcohol 7% (n = 11), cannabis 7% (n = 12), cocaine 8% (n = 14), amphetamines 7% (n = 11), sedatives 7% (n = 12) |
|
| Interventions | Oral methadone (n = 66) Sublingual buprenorphine (n = 104) 24 weeks in a flexible dose schedule |
|
| Outcomes | Primary outcome of parent study: liver function at 24 weeks | |
| Notes | Financial interests disclosed. Quote: "Andrew Saxon: Paid consultant to Reckitt Benckiser Pharmaceuticals; Walter Ling: Paid consultant to Reckitt Benckiser Pharmaceuticals; R. Douglas Bruce: Research grant support from Gilead Sciences, Inc., Merck & Co., Bristol Myers Squibb, Boehringer Ingelheim, Reckitt Benckiser Pharmaceuticals, Abbott Laboratories, Pfizer, Inc., and honorarium from Reckitt Benckiser Pharmaceuticals; Yuliya Lokhnygina: Paid consultant to Johnson & Johnson." Reckitt Benkiser provided some initial advice on the study design and supplied Suboxone. The main study funding came from the NIDA through the CTN. |
|
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Unclear risk | Study stated randomisation, no additional information reported on sequence generation. |
| Allocation concealment (selection bias) | Unclear risk | Method of concealment not described. |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | High risk | Study reported as open label. |
| Blinding of participants and personnel (performance bias) Objective outcomes | High risk | Study reported as open label. |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Detection bias was unlikely to influence results for objective measures such as retention. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | Study reported as open label. |
| Incomplete outcome data (attrition bias) All outcomes | Low risk | Figure 1 of the publication indicated that there were more missing data from the buprenorphine group; however, in the subanalyses, retention was comparable across the groups suggesting that this was less likely to influence the results presented in this review. |
| Selective reporting (reporting bias) | Low risk | Study protocol was available and expected results were reported. Further, study data available on the CTN datashare website. |
Neumann 2013.
| Study characteristics | ||
| Methods | Open‐label randomised controlled trial | |
| Participants | 54 men and women aged ≥ 18 years with well‐documented chronic non‐malignant pain related to the spine or a large joint (e.g. hip, knee, shoulder) and an "addiction to prescription opioids" (defined as DSM‐IV‐TR for 'opioid dependence') 54% (n = 29) men Mean age 38.3 (SD 9.7) years 7 participants reported cocaine use at baseline and 20 (36%) had a urine drug test that was positive for any other drug at baseline |
|
| Interventions | Sublingual buprenorphine/naloxone 4–16 mg/1–4 mg/day (experimental group) (n = 26) Oral methadone tablets 10–60 mg/day (active comparator group) (n = 28) Doses divided 1–4 times daily |
|
| Outcomes | Pain and opioid use | |
| Notes | Results reported for treatment completers only. Study supported, in part, by a grant from the NIDA. Conflicts of interest were not reported in the manuscript. |
|
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Participants were randomised into 1 of 2 groups that were predetermined by drawing lots using a 3:3 ratio block randomisation procedure. |
| Allocation concealment (selection bias) | Unclear risk | Method of concealment not described. |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | High risk | This was an open‐label trial without a placebo and a control group. The outcomes might have been different, if a placebo had been used and the treatment conditions were masked to the participants, to the clinicians who provided care, and to the investigators who collected the follow‐up data. |
| Blinding of participants and personnel (performance bias) Objective outcomes | High risk | This was an open‐label trial without a placebo and a control group. The outcomes might have been different, if a placebo had been used and the treatment conditions were masked to the participants, to the clinicians who provided care, and to the investigators who collected the follow‐up data. |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Detection bias was unlikely to influence results for objective measures such as retention. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | This was an open‐label trial without a placebo and a control group. The outcomes might have been different, if a placebo had been used and the treatment conditions were masked to the participants, to the clinicians who provided care, and to the investigators who collected the follow‐up data. |
| Incomplete outcome data (attrition bias) All outcomes | Unclear risk | Analyses only for completers; however, missing data balanced across the 2 groups (n = 15/28 missing for methadone group and n = 13/26 missing for buprenorphine group), 13 completers in each group. |
| Selective reporting (reporting bias) | Low risk | Outcomes were consistent with those prospectively reported on ClinicalTrials.gov (NCT00879996). |
Fiellin 2014.
| Study characteristics | ||
| Methods | Open label clinic‐based trial of buprenorphine taper compared to buprenorphine maintenance | |
| Participants | Prescription opioid‐dependent people 58% male Mean age 30.35 (SD 9.16) years 12% (n = 13) reported cocaine abuse at baseline |
|
| Interventions | Buprenorphine (sublingual) stabilisation for 6 weeks followed by 3‐week taper (n = 57) Maintenance buprenorphine (sublingual) (n = 56) for 14 weeks |
|
| Outcomes | Illicit opioid use, retention and re‐initiation of buprenorphine treatment | |
| Notes | Quote: "Dr Fiellin has received honoraria for serving on expert advisory boards to monitor for diversion, misuse, and abuse of buprenorphine for Pinney Associates and ParagonRx and has received honoraria from the American Society of Addiction Medicine to serve as the medical director of the Physician Clinical Support Systems for Buprenorphine and Primary Care and from the American Academy of Addiction Psychiatry to serve as a consultant to the Physician Clinical
Support Systems for Buprenorphine and Opioids. Drs Schottenfeld and Moore received support from the Connecticut Mental Health Center, State of
Connecticut. Dr Barry has received compensation for expert testimony addressing addiction and pain. No other disclosures were reported." Funding received from NIDA and a pharmaceutical company, Reckitt‐Benckiser Pharmaceuticals, provided buprenorphine through the NIDA |
|
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Quote: "After the induction and stabilization period, patients were randomly assigned in a 1:1 ratio to receive taper or maintenance therapy (each described below). An urn randomisation procedure under the control of an investigator (B.A.M.) who was not involved with enrolment or assessment for eligibility was used to ensure that the groups were similar with regard to current cocaine abuse and urine samples with findings negative for opioids and cocaine at the time of randomisation." |
| Allocation concealment (selection bias) | Low risk | Quote: "Treatment allocation was communicated by an investigator not involved in assessment for eligibility or randomization who notified each patient of his or her treatment assignment in a sequential manner." |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | High risk | Quote: "Open label randomized clinical trial." |
| Blinding of participants and personnel (performance bias) Objective outcomes | High risk | Quote: "Open label randomized clinical trial." |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Objective outcomes unlikely to be influenced by detection bias. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | Quote: "Open label randomized clinical trial." |
| Incomplete outcome data (attrition bias) All outcomes | High risk | Quote: "Patients in the taper group provided fewer urine samples than those in the maintenance group (57.3% vs 78.2%; P = .001). The results regarding the patient‐reported frequency of illicit opioid use are based on 1044 assessments of the 1582 total possible assessments (66.0%) had all patients remained in treatment for the entire 14‐week trial. Patients in the taper group completed fewer patient‐reported assessments than those in the maintenance group (56.9% vs 76.3%; P < .001)." |
| Selective reporting (reporting bias) | Unclear risk | ClinicalTrials.gov indicated some measures that were collected were not included in the primary outcome paper (e.g. reductions in HIV risk, patient satisfaction, costs of services). The main outcomes that would be expected to be reported in a study of this type were included in the main outcome paper, suggesting that this may not have represented bias. |
D'Onofrio 2015.
| Study characteristics | ||
| Methods | Open‐label randomised controlled trial of opioid‐dependent people presenting at emergency departments | |
| Participants | Unpublished data for participants where a pharmaceutical opioid was the primary opioid used (n = 82) included in analysis Main study recruited participants who were 75% male with mean age of 31.4 (SD 10.6) years Data on other substance use for the subset who used pharmaceutical opioids not available |
|
| Interventions | Referral to addiction treatment (n = 31) Brief intervention and referral to addiction treatment (n = 24) Brief intervention and commenced on sublingual buprenorphine as an inpatient with sufficient take‐home daily doses provided to ensure participants had adequate medication until a scheduled appointment in the hospital's primary care centre, within 72 hours. Buprenorphine doses were 8 mg on day 1 and 16 mg on days 2 and 3. Clinic‐based buprenorphine treatment was provided for 10 weeks by physicians and nurses using established procedures with visits ranging from weekly to twice monthly based on clinical stability |
|
| Outcomes | Primary outcome: engagement in addiction treatment on the 30th day following randomisation Secondary outcomes collected at 30 days: self‐reported number of days of illicit opioid use in the past 7 days, urine toxicology for illicit opioid use, HIV risk‐taking behaviour and use of addiction treatment services |
|
| Notes | Quote: "The study was supported by grant 5R01DA025991 from the National Institute on Drug Abuse (NIDA), and Reckitt‐Benckiser Pharmaceuticals provided buprenorphine through NIDA." Dr Fiellin reported having received honoraria from Pinney Associates (quote) "for serving on an external advisory board monitoring the diversion and abuse of buprenorphine." |
|
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Quote: "A computerized stratified randomization procedure under the control of an investigator (M.C.C.) who was not involved with enrolment or assessment for eligibility was used to ensure that the groups were balanced with regard to sex, cocaine use in the last 30 days, and primarily prescription opioid or heroin use." |
| Allocation concealment (selection bias) | Low risk | Quote: "A computerized stratified randomization procedure under the control of an investigator (M.C.C.) who was not involved with enrolment or assessment…" |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | Unclear risk | Quote: "Data on all outcomes were collected by research associates not involved in the patients' ED [emergency department] care." Not enough details were available to assess risk (i.e. just because the participants were not aware of the care in the emergency department did not mean that they were not aware of the study treatment). |
| Blinding of participants and personnel (performance bias) Objective outcomes | Unclear risk | Quote: "Data on all outcomes were collected by research associates not involved in the patients' ED [emergency department] care." Not enough details were available to assess risk (i.e. just because the participants were not aware of the care in the emergency department did not mean that they were not aware of the study treatment). |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Detection bias unlikely to influence assessment of objective measures. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | High risk of bias in an unblinded study for subjective measures. |
| Incomplete outcome data (attrition bias) All outcomes | High risk | For the main outcome paper, most data would not have been affected by attrition due to the statistical methods used. Quote: "We used the mixed‐models procedure repeated measures linear models to evaluate the differences between baseline and 30‐day follow‐up in the number of days per week of illicit opioid use, HIV risk behaviors, and inpatient addiction services across the study groups. This analytical approach uses all available data on each randomized patient; therefore, all study patients, including those with missing data, were included in the analyses; no imputations were required." This suggests that for the main outcome paper low risk would exist; however, authors reported that there were more missing data for the non‐opioid agonist group, suggesting analyses presented in this review may be affected by attrition bias |
| Selective reporting (reporting bias) | Low risk | All measures prospectively reported on ClinicalTrials.gov were reported in the main outcome paper, in addition to those that would be expected in this type of study. |
Lee 2018.
| Study characteristics | ||
| Methods | Open‐label randomised controlled trial | |
| Participants | Aged ≥ 18 years, spoke English, had DSM‐5 opioid‐use disorder, and had used non‐prescribed opioids (illicit or pharmaceutical) in the past 30 days Analyses from unpublished data represented only those participants who reported only pharmaceutical opioid use in the 30 days prior to treatment (n = 86) Mean age of participants reporting pharmaceutical opioid use 34.4 (SE 1.5) years 84% were men |
|
| Interventions | 24 weeks of sublingual buprenorphine‐naloxone 8–24 mg (n = 46) Extended‐release naltrexone intramuscular injection 380 mg (n = 46) |
|
| Outcomes | Primary outcome: time to a relapse event | |
| Notes | Financial interests disclosed. Quote: "All authors report grant or contract funding from the National Institute of Drug Abuse (NIDA) for this study. JDL and JR received other research support from NIDA and National Institute on Alcohol Abuse and in‐kind study drug from Alkermes for another trial. EVN Jr received other research support from NIDA, Brainsway, Braeburn Pharma, and Alkermes, unpaid consulting fees from Alkermes, and consulting fees from the University of Arkansas. MF received other research support from Alkermes, US World Meds, MediaRez, and the Laura and John Arnold Foundation, and consulting fees from Alkermes and US World Meds. SR received other research support from NIDA, the Heffter Research Institute, Council on Spiritual Practices, and the Sarlo Foundation, and travel support from the Multidisciplinary Association for Psychedelic Studies. All other authors declare no competing interests. Reckitt Benkiser provided some initial advice on the study design and supplied Suboxone." Main study funding came from the NIDA through the CTN |
|
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Quote: "We used a web‐based permuted block design with random equally weighted block sizes of four and six for randomisation." |
| Allocation concealment (selection bias) | Unclear risk | Quote: "We used a web‐based permuted block design with random equally weighted block sizes of four and six for randomisation." No further information on allocation concealment. |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | High risk | Quote: "This open‐label trial involved no masking of treatment or outcomes." |
| Blinding of participants and personnel (performance bias) Objective outcomes | High risk | Quote: "This open‐label trial involved no masking of treatment or outcomes." |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Detection bias is unlikely to influence results for objective measures such as retention. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | Quote: "This open‐label trial involved no masking of treatment or outcomes." |
| Incomplete outcome data (attrition bias) All outcomes | High risk | There was a lower rate of retention in the naltrexone arm, and rates of follow‐up for data collection on some outcomes was lower in the naltrexone group, which may have introduced bias, with poorer treatment outcomes for those who were not retained (or able to be started) on treatment reported in the main study. Quote: "First, it was more difficult to start XR‐NTX [extended‐release naltrexone] treatment than BUP‐NX [buprenorphine‐naloxone] treatment: 28% dropped out of treatment before XR‐NTX induction versus only 6% before BUP‐NX induction. Second, nearly all induction failures had early relapse." |
| Selective reporting (reporting bias) | Low risk | Study protocol was available and expected results were reported. Further, study data are available on datashare website. |
Neumann 2020.
| Study characteristics | ||
| Methods | Prospective open‐label randomised controlled trial | |
| Participants | Men and women aged 18–64 years with postsurgical chronic non‐malignant back pain and failed back surgery syndrome due to past spinal surgery and opioid dependence confirmed using the DSM‐IV‐TR for opioid dependence and Drug Abuse Screening Test score > 4 Mean age 41.1 years 31.5% men |
|
| Interventions | Oral methadone tablets 30–60 mg/day in 3–4 times daily divided doses (n = 9) Sublingual buprenorphine/naloxone 8 mg/2 mg to 16 mg/4 mg in 2–4 times daily doses (n = 10) for 6 months |
|
| Outcomes | Primary outcome: analgesia Secondary outcomes: retention, self‐reported functioning, cravings, depression and self‐reported substance use |
|
| Notes | Research supported by an R03 NIH grant (5R03DA029768) awarded to RDB. Authors reported no potential conflicts of interest. Study enrolment ceased early due to suspected non‐medical use of study medication (planned enrolment was for n = 63 in each arm). Data from the published paper and ClinicalTrials.gov were used. | |
| Risk of bias | ||
| Bias | Authors' judgement | Support for judgement |
| Random sequence generation (selection bias) | Low risk | Quote: "The participants were randomized into one of two groups that were pre‐determined by drawing lots using a 3:3 ratio, block randomization procedure." |
| Allocation concealment (selection bias) | Unclear risk | Limited information on random sequence generation (quote) "was kept concealed and was referred to by the research associate at each enrolment." |
| Blinding of participants and personnel (performance bias) Subjective Outcomes | High risk | Open‐label study. Quote: "Participants and treatment providers were not blinded to the conditions." |
| Blinding of participants and personnel (performance bias) Objective outcomes | High risk | Open‐label study. Quote: "Participants and treatment providers were not blinded to the conditions." |
| Blinding of outcome assessment (detection bias) Objective measures | Low risk | Detection bias was unlikely to influence results for objective measures such as retention. |
| Blinding of outcome assessment (detection bias) Subjective measures | High risk | Open‐label study. Quote: "Participants and treatment providers were not blinded to the conditions." |
| Incomplete outcome data (attrition bias) All outcomes | High risk | Of the 19 enrolled participants, 10 participants (52.6%) completed the study, with higher rates of follow‐up in the methadone arm. |
| Selective reporting (reporting bias) | Low risk | Outcomes were consistent with those prospectively reported on ClinicalTrials.gov (NCT01559454). |
CTN: Clinical Trials Network; DSM‐IV‐TR: Diagnostic and Statistical Manual of Mental Disorders 4th Edition Text Revision; DSM‐5: Diagnostic and Statistical Manual of Mental Disorders 5th Edition; n: number of participants; NIDA: National Institute on Drug Abuse; SD: standard deviation; SE: standard error.
Characteristics of excluded studies [ordered by study ID]
| Study | Reason for exclusion |
|---|---|
| Amass 1994 | No opioid maintenance condition as per definition of maintenance in protocol |
| Anglin 2007 | Participants were heroin dependent |
| Anon 2015 | Commentary/editorial |
| Bahji 2018 | Review article |
| Batki 1998 | Not a randomised controlled trial |
| Bazazi 2017 | Wrong study design |
| Brinkley‐Rubinstein 2018 | Unable to confirm eligibility of population |
| Cameron 2006 | Unable to determine if participants were dependent on pharmaceutical opioids |
| Chandra 2019 | Unable to confirm eligibility – no response from author |
| Chopra 2009 | All participants received buprenorphine (i.e. not randomised to different opioid agonists, and no non‐agonist group), randomised to different conditions of contingency management to promote abstinence from illicit opioid use |
| Cook 2021 | Wrong patient population |
| Cushman 2015 | Wrong patient population |
| Cushman 2016 | Wrong patient population |
| Eder 1998 | Participants were primarily heroin dependent |
| Fiellin 2006 | All groups received buprenorphine, i.e. there was no non‐agonist comparison group |
| Fischer 1999 | Participants were primarily heroin dependent |
| Fudala 2003 | Participants were primarily heroin dependent |
| Ghalehney 2018 | Wrong comparator |
| Gordon 2017 | Wrong comparator |
| Gordon 2018 | Wrong comparator |
| Gordon 2019 | Wrong comparator |
| Gossop 2001 | Not a randomised controlled trial design |
| Gruber 2008 | Participants were primarily using heroin |
| Haight 2019 | Wrong patient population |
| Hoffmann 2014 | Observational study (not a randomised controlled trial) |
| Johnson 1992 | Participants were primarily using heroin |
| Johnson 1995 | Participants were primarily using heroin |
| Johnson 2000 | Participants were primarily using heroin |
| Kakko 2003 | Participants were primarily using heroin |
| Karp‐Gelernter 1982 | Participants were primarily using heroin |
| Kelly 2020 | Wrong patient population |
| Kim 2015 | Wrong comparator |
| Kranzler 2021 | Wrong patient population |
| Kristensen 2005 | Subanalyses of participants who used only pharmaceutical opioids was not possible, though it was confirmed that there were participants who used a combination of heroin and pharmaceutical opioids |
| Kunøe 2016 | Wrong patient population |
| Laffont 2018 | Wrong patient population |
| Latif 2019a | Wrong patient population |
| Latif 2019b | Wrong patient population |
| Liebschutz 2013 | Too few participants (< 10) were using only pharmaceutical opioid, precluding meaningful comparisons |
| Ling 1996 | Participants were primarily using heroin |
| Ling 1998 | Participants were primarily using heroin |
| Ling 2010 | Data not available to perform analyses on only those participants who were dependent on pharmaceutical opioids |
| Ling 2019 | Unable to confirm primary opioid used by participants |
| Longshore 2005 | Participants were primarily using heroin |
| Maremmani 1999 | Unable to confirm if population met inclusion criteria from information available |
| Marsch 2016 | Wrong intervention |
| McKenzie 2012 | Participants were primarily using heroin |
| Mokri 2016 | Wrong patient population |
| Montoya 2004 | Participants were primarily using heroin |
| Ngaimisi 2017 | Wrong patient population |
| Oleskowicz 2021 | Wrong population (unable to confirm study population were pharmaceutical opioid‐dependent) |
| Petitjean 2001 | Full text described sample in terms of their heroin use, unable to confirm with authors if any participants were primarily pharmaceutical opioid‐dependent people |
| Piralishvili 2015 | Unclear if participants were dependent only on pharmaceutical opioids |
| Raleigh 2017 | Review article |
| Reimer 2011 | Participants were primarily using heroin |
| Robertson 2006 | Published paper did not indicate the primary opioid used by study participants, unable to confirm with study authors |
| Rosenthal 2013 | Data not available to perform analyses on only those participants who were dependent on pharmaceutical opioids |
| Sees 2000 | Participants were described as primarily using heroin. Unable to confirm with study authors if there were any pharmaceutical opioid‐dependent participants recruited |
| Shava 2018 | Wrong patient population |
| Sigmon 2013 | Study was not of maintenance opioid treatment (all participants received different duration taper) |
| Sigmon 2015 | Wrong study design |
| Sigmon 2016 | Unable to confirm eligibility – no response from author |
| Solli 2018a | Wrong patient population |
| Solli 2018b | Wrong patient population |
| Solli 2019 | Wrong patient population |
| Stein 2020 | Unable to confirm eligibility – no response from author |
| Stitzer 1983 | All participants received detoxification, no maintenance comparison |
| Strain 1996 | Participants were primarily using heroin |
| Strang 2000 | Participants were primarily using heroin |
| Streck 2018 | Unable to confirm eligibility – no response from author |
| Tanum 2017a | Wrong patient population |
| Tanum 2017b | Wrong patient population |
| Tanum 2017c | Wrong patient population |
| Tanum 2018a | Wrong patient population |
| Tanum 2018b | Wrong patient population |
| Tanum 2018c | Wrong patient population |
| Tanum 2019 | Wrong patient population |
| Tennant 1982 | Study design was not a randomised controlled trial |
| Uehlinger 1998 | Unable to confirm if any participants were dependent on pharmaceutical opioids |
| Wang 2019 | Wrong patient population |
| Watkins 2017 | Wrong intervention |
| Weiss 2011 | All participants received buprenorphine (no non‐buprenorphine control group). Participants were randomised to receive enhanced counselling vs standard care |
Characteristics of ongoing studies [ordered by study ID]
Gordon 2021.
| Study name | Extended release naltrexone versus extended release buprenorphine with individuals leaving jail |
| Methods | Type 1 hybrid effectiveness‐implementation RCT |
| Participants | Adult inmates at participating jails meeting DSM‐5 criteria of moderate or severe opioid‐use disorder at the time of incarceration |
| Interventions | Extended‐release buprenorphine or extended‐release naltrexone |
| Outcomes | Primary outcome: pharmacotherapy adherence (6 months after release) as number of monthly injections received (0–6) Secondary outcomes: number of illicit opioid positive urine drug screen results (1–7, 12 months); self‐reported illicit opioid use (baseline, 1–7, 12 months); number of fatal and non‐fatal overdose events (baseline, 1–7, 12 months); patient‐reported outcomes measurement information system (baseline, 1–7, 12 months); risk assessment battery (baseline, 1–7, 12 months); HIV risk behaviours, total score 40 (range 0–1); number of days committed crime (20 crimes) (baseline, 1–7, 12 months); time to rearrest (12 months) (days to arrest); time to re‐incarceration (12 months) (days to re‐incarceration) |
| Starting date | 28 October 2020 |
| Contact information | Michael S Gordon, DPA 410‐837‐3977 ext 251 mgordon@friendsresearch.org |
| Notes |
Seval 2021.
| Study name | Design and methods of a multi‐site randomized controlled trial of an integrated care model of long‐acting injectable buprenorphine with infectious disease treatment among persons hospitalized with infections and opioid use disorder |
| Methods | Randomised control trial |
| Participants | 200 adult hospitalised with severe bacterial or viral infections related to opioid use dependence |
| Interventions | Long‐acting buprenorphine |
| Outcomes | Primary outcome: proportion of participants enrolled in effective medication for opioid use disorder at 12 weeks after randomisation Secondary outcomes: relapse to opioid use, adherence to infectious disease treatment, infection morbidity and mortality, and drug overdose |
| Starting date | August 2020 |
| Contact information | Sandra.springer@yale.edu |
| Notes |
Socias 2018.
| Study name | Optimizing patient centered‐care: a pragmatic randomized control trial comparing models of care in the management of prescription opioid misuse (OPTIMA) study |
| Methods | Randomised controlled trial |
| Participants | People with prescription opioid‐use disorder |
| Interventions | Methadone and buprenorphine naloxone |
| Outcomes | Primary outcome: opioid use Secondary outcomes: retention, medication adherence, adverse effects and participant satisfaction and patient engagement |
| Starting date | 7 October 2017 |
| Contact information | Didier Jutras Aswad, Canadian Research Initiative in Substance Misuse |
| Notes |
DSM‐5: Diagnostic and Statistical Manual of Mental Disorders, 5th edition; RCT: randomised controlled trial.
Differences between protocol and review
We had originally intended to include any studies with pharmaceutical opioid‐dependent people in analyses if they could provide data for only those participants who were dependent on pharmaceutical opioids. When completing the original review in 2016, on contacting authors, we became aware that some studies had only recruited very small numbers (e.g. two or three participants) of people who were dependent on pharmaceutical opioids, preventing meaningful analyses. For this reason, we added the criterion that at least 10 people must have been recruited who were dependent on pharmaceutical opioids to warrant re‐analyses of the data for those people.
We did not produce funnel plots to examine risk of bias because there were not enough studies identified.
We found insufficient number of studies to perform subgroup analysis.
When we updated the review in 2022, we reclassified adverse events as a primary outcome.
Additional sensitivity analyses that were not outlined in the protocol were conducted to address statistical heterogeneity.
Louisa Degenhardt, Linda Gowing, Cheyanne Kehler and Nicholas Lintzeris left the review author team and Wai Chung Tse joined the team.
Contributions of authors
| Draft the protocol | SN, Louisa Degenhardt (LD), Nicholas Lintzeris (NL), Linda Gowing (LG) |
| Develop and run the search strategy | SN, BL, LD, Cheyanne Kehler (CK) |
| Obtain copies of studies | SN, BL, WCT |
| Select which studies to include (2 people) | SN, BL, LD, WCT |
| Extract data from studies (2 people) | SN, WCT |
| Enter data into Review Manager Web | SN |
| Carry out the analysis | SN, WCT |
| Interpret the analysis | SN, WCT |
| Draft the final review | SN, BL, WCT |
| Update the review | SN, WCT, BL |
Sources of support
Internal sources
No sources of support provided
External sources
-
SN is supported by a National Health and Medical Research Council (NHMRC) research fellowships (#1163961), Australia
Funding is from the national (Australian) Health and Medical Research Council, representing competitive funding from the Australian Government that is independently peer‐reviewed.
Declarations of interest
SN and BL are named investigators on an implementation trial of buprenorphine depot funded by Indivior, which was not eligible for inclusion in this review. SN and BL did not receive funding for their work on the study neither did they have control over the funds that were received by another institution. That company has no role in the conception of, or decision to submit, this review. SN and BL have received untied educational grants for unrelated work from Seqirus. SN is funded by a National Health and Medical Research Council (NHMRC) fellowship. The NHMRC has no interest in the outcome of the review that could lead to a real or perceived conflict of interest.
WCT: none.
New search for studies and content updated (conclusions changed)
References
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