COMPARATIVE EFFICACY AND SAFETY OF PHARMACOTHERAPIES FOR ALCOHOL WITHDRAWAL: A SYSTEMATIC REVIEW AND NETWORK META-ANALYSIS

Abstract

Background and Aims

There have been few head-to-head clinical trials of pharmacotherapies for alcohol withdrawal (AW). We, therefore, aimed to evaluate the comparative performance of pharmacotherapies for AW.

Methods

Six databases were searched for randomized clinical trials through November 2021. Trials were included after a blinded review by two independent reviewers. Outcomes included incident seizures, delirium tremens, AW severity scores, adverse events, dropouts, dropouts from adverse events, length of hospital stay, use of additional medications, total benzodiazepine requirements, and death. Effect sizes were pooled using frequentist random-effects network meta-analysis models to generate summary ORs and Cohen’s d standardized mean differences (SMDs).

Results

Across the 149 trials, there were 10 692 participants (76% male, median 43.5 years old). AW severity spanned mild (n = 32), moderate (n = 51), and severe (n = 66). Fixed-schedule chlormethiazole (OR, 0.16; 95% CI, 0.04–0.65), fixed-schedule diazepam (OR, 0.16; 95% CI, 0.04–0.59), fixed-schedule lorazepam (OR = 0.19; 95% CI, 0.08–0.45), fixed-schedule chlordiazepoxide (OR = 0.21; 95% CI, 0.08–0.53), and divalproex (OR = 0.22; 95% CI, 0.05–0.86) were superior to placebo at reducing incident AW seizures. However, only fixed-schedule diazepam (OR, 0.19; 95% CI, 0.05–0.76) reduced incident delirium tremens. Oxcarbazepine (d = −3.69; 95% CI, −6.21 to −1.17), carbamazepine (d = −2.76; 95% CI,−4.13 to −1.40), fixed-schedule oxazepam (d = −2.55; 95% CI, −4.26 to −0.83), and γ-hydroxybutyrate (d = −1.80; 95% CI, −3.35 to −0.26) improved endpoint Clinical Institute Withdrawal Assessment for Alcohol-Revised scores over placebo. Promazine and carbamazepine were the only agents significantly associated with greater dropouts because of adverse events. The quality of evidence was downgraded because of the substantial risk of bias, heterogeneity, inconsistency, and imprecision.

Conclusions

Although some pharmacotherapeutic modalities, particularly benzodiazepines, appear to be safe and efficacious for reducing some measures of alcohol withdrawal, methodological issues and a high risk of bias prevent a consistent estimate of their comparative performance.

INTRODUCTION

The symptoms of alcohol withdrawal (AW)—one diagnostic criterion for alcohol use disorder (AUD)—include anxiety, insomnia, tremors, hallucinations, seizures, and delirium tremens (DTs) [1]. The prevalence of AW in the general population is low (<5% in United States [US] adults in 1995), but much higher among those admitted for detoxification and rehabilitation for AUD (up to 86%) [2, 3]. Untreated AW is potentially fatal, and the mortality rate among those experiencing severe withdrawal is as high as 30% to 50% [4]. Although most AW is uncomplicated, depending on AW severity, patients may need hospitalization [5].

AW management is multimodal, involving fluid and electrolyte repletion [6, 7] and thiamine supplementation to prevent Wernicke-Korsakoff syndrome [4]. However, these do not treat AW per se. Pharmacotherapies play a crucial role in relieving immediate AW symptoms, preventing complications (such as seizures and DTs) [8], and may help prevent the return to alcohol use. Choosing a pharmacological treatment for AW is a complex decision that must factor in medication efficacy and safety.

Previous AW guidelines have recommended several classes of medications for acute AW [4, 9–13], primarily benzodiazepines (BZDs), with some role for anticonvulsants, beta-blockers, calcium channel blockers, and clonidine [4, 10]. Although most agents recommended in these guidelines have randomized controlled trial (RCT) evidence showing superiority over placebo, these agents’ comparative performance is less clear. For example, although there is good evidence of BZDs efficacy over placebo for a range of AW outcomes, there are fewer head-to-head comparisons across medications [14]. Therefore, in some cases, medications for AW are sometimes used based on retrospective studies and controlled trials without placebo or no medication arms. Furthermore, because AW treatment is not perfectly effective, because some patients will experience sedation or progression to DTs or seizures, clinicians continue to seek better remedies.

Newer statistical methods enable indirect treatment comparisons in the absence of head-to-head trials, including network meta-analysis (NMA) [15–17], which allows the simultaneous comparison of multiple treatments and comparators for the same condition, so long as there is a close similarity of compared trials [18]. NMAs can synthesize the available direct and indirect evidence, estimate the comparative benefits and risks of specific treatments, and guide clinical practice [19–21]. NMAs can also include pharmacotherapies from controlled trials without placebo or no medication arms in a comparative effectiveness analysis, especially phenobarbital.

The objectives of this systematic review and NMA are to evaluate the comparative efficacy, safety, and acceptability of AW pharmacotherapies. We hypothesized that BZDs would show the most consistent efficacy and safety across treatments given their established presence in AW treatment and practice guidelines.

METHODS

Protocol and registration

We registered our study protocol with the PROSPERO database of systematic reviews (CRD42020208946). We adhered to the Preferred Reporting Items for Systematic Reviews and Meta-analyses (PRISMA) for NMAs [22], reported in our supplementary checklist (Appendix 1). Because this study was a secondary analysis of published data, we did not seek ethics approval.

Eligibility criteria

We defined our study eligibility using the populations-interventions-comparators-outcomes study design (PICO) framework:

1. Population: we restricted eligibility to alcohol-dependent adult patients (age 18+) diagnosed experiencing acute AW per the Diagnostic and Statistical Manual of Mental Disorders (DSM), International Classification of Diseases (ICD), or other criteria. We included all patients regardless of symptom severity, comorbidity, age, gender, nationality, setting of care, or prior treatment history.

2. Interventions: experimental interventions included any pharmacological agent used to treat AW, including benzodiazepines, anticonvulsants, beta-blockers, barbiturate, calcium-channel blockers, gabapentinoids, antipsychotics, and others. Control interventions included placebo, other pharmacological interventions, or nonpharmacological/behavioral interventions (e.g. reassurance, low lights, quiet room/few interruptions, repeat assessments, and observation), given that NMA allows simultaneous comparison of different treatments.

3. Outcomes: we considered a range of efficacy, safety, acceptability, and secondary outcomes, defined below.

4. Studies: RCT or controlled clinical trials evaluate AW pharmacotherapies’ efficacy, safety, and overall risk–benefit.

Types of outcome measures

Efficacy outcomes

Efficacy outcomes include (i) alcohol withdrawal seizures as number of subjects experiencing seizures; (ii) alcohol withdrawal delirium as number of subjects experiencing delirium; and (iii) alcohol withdrawal symptoms as measured by prespecified scales (as the Clinical Institute Withdrawal Assessment of Alcohol Scale, Revised [CIWA-Ar] score).

Safety outcomes

Safety outcomes include (i) adverse events as the number of subjects experiencing at least one adverse event; (ii) dropouts; and (iii) dropouts because of adverse events.

Secondary outcomes

Secondary outcomes include (i) additional medication needed (referred to as PRN medication, or pro re nata); (ii) length of stay in hospital or intensive care (as a surrogate for AW duration; (iii) total benzodiazepine requirements (using lorazepam equivalents); and (iv) death.

Information sources and search

We consulted with a research librarian and searched six electronic databases (PubMed, MEDLINE, EMBASE, Cochrane, CINAHL, and PsycINFO) from their inception to December 2020, with an updated search in November 2021 (Appendix 2). We also searched clinical trial registries for ongoing, unpublished studies and the bibliographies of included studies, conference proceedings, and guidelines to supplement the electronic search and guide the present review. Finally, we cross-referenced our data against 35 previous AW pharmacotherapy reviews [5, 12, 23–55].

Study selection

Two authors (A.B. and M.D.) independently screened the titles and abstracts of all publications obtained through the search strategy using Covidence, a web-based systematic review manager [56, 57]. We obtained the full-text articles for all potentially eligible studies, and the same two authors independently assessed for review inclusion. We resolved discrepancies by consensus.

Data collection process

We extracted relevant PICOS characteristics and appraised the study-level risk of bias using piloted forms in Covidence before transferring to a Microsoft Excel spreadsheet. Extracted variables included population characteristics (sample size, age, and sex), intervention and comparator group details (name of medication, dose, frequency, and route of administration), outcome reporting, and study design indices (trial type, duration, location, blinding, and randomization).

The geometry of the network

We explored network geometry by graphic network plots, where each treatment represented a “node” and lines between nodes represent direct comparisons between treatment pairs.

Risk of bias within included studies

Two authors (A.B. and M.D.) independently appraised the risks of bias in each study using the Cochrane Collaboration tool for randomized controlled trials [58], which considers randomization, allocation concealment, blinding, selective reporting, and attrition. We assigned low, high, or unclear grades to each domain.

Summary measures

For continuous outcomes [3, 8, 9], we calculated the summary mean difference (MD) or standardized mean difference (SMD), with the uncertainty in each treatment comparison (against placebo) expressed by its 95% CI. In cases of missing standard deviations from baseline to the end of treatment, we imputed the standard deviation at the end of treatment for each group, per previous Cochrane methods [34]. For dichotomous outcomes [1, 2, 4–7, 10], we calculated the OR and its corresponding 95% CI. SMDs of 0.2, 0.5, and 0.8 correspond to small, medium, and large effect sizes [59]. Negative Cohen’s d (SMDs) or ORs <1 show that the treatment reduced the parameter of interest relative to the control [59, 60]. Although the majority of RCTs included in this review had a duration of 7 days or less, consistent with the conceptualization of ‘acute’ alcohol withdrawal, a minority of studies involved longer follow-up (e.g. up to 28 days). Unless otherwise indicated, all summary measures were for total differences from the comparator condition over the entire course of treatment. However, we extracted data as close to the 7-day mark for all studies to improve consistency across trials (e.g. for the 28-day studies, we extracted outcomes at the 7-day mark).

Planned methods of analysis

Per previous NMAs [20, 61–68], we used the netmeta package from R Studio (version 3.5.1) to conduct a frequentist NMA assuming a jointly randomizable network where participants were equally likely to be randomized to any treatment [17, 18, 69, 70]. For total benzodiazepine requirements (outcome 9), per Holleck et al. [49], we converted all benzodiazepines to lorazepam equivalents by dividing oxazepam doses by 15, chlordiazepoxide by 25, and diazepam by 5 [71–73]. We extracted all outcomes using the intention-to-treat principles from each study [18]. We used a random-effects model for all indirect comparisons. We also estimated P-scores, which are treatment rankings that take into account the effect size point estimate and precision (width of the 95% CI). P-scores measure the mean extent of certainty that a treatment is better than the competing treatments [74].

Assessment of inconsistency, risk of bias across studies, and additional analyses

To determine the NMA goodness of fit, we assessed transitivity (the extent of network heterogeneity) and consistency (the degree of agreement between direct and indirect comparisons [75]. To measure transitivity, we measured ττ2 (the total variation) and I2 (the percentage of ττ2 not because of random error), with I2 of at least 50% as statistical heterogeneity [76, 77]. Given the sparse data matrix for some treatment comparisons, we did not calculate other heterogeneity and inconsistency indices because they were not meaningful. We investigated publication bias graphically using funnel plots (plot of the effect size against the standard error) for each outcome that had at least four studies [78]. We tested funnel plot asymmetry using Egger’s rank correlation test when there were at least 10 studies [79]. We also incorporated principles from the GRADE framework to evaluate the strength of evidence, accounting for heterogeneity, precision, risk of study-level bias, and sample size. After graphical inspection of each NMA, we assessed the effect of treatment setting by restricting the network model to studies taking place in inpatient settings. We also excluded studies using combination or adjunctive therapies, which could introduce heterogeneity compared to monotherapy regimens.

RESULTS

Study selection

We identified 1980 unique reports from all electronic databases and excluded 1798 studies based on title and abstract. The remaining 182 articles were retrieved in full-text for more detailed evaluation, from which 149 RCTs met inclusion criteria (Figure 1).

FIGURE 1.

Preferred reporting items for systematic reviews and meta-analyses (PRISMA) flowchart of study selection process

Study characteristics

Given the large yield (n = 149) of studies meeting inclusion criteria, we provide detailed study characteristics in Appendix 4, which includes a breakdown of each study included in each NMA. Critical study features are summarized here. Across the 149 trials, there were 10 692 participants (76% male, median 43.5 years old). AWS severity spanned mild (n = 32), moderate (n = 51), and severe (n = 66). The most encountered medications (number of trials, dose range) were chlordiazepoxide (n = 31; 60–400 mg), chlormethiazole (n = 25; 1152–6000 mg), diazepam (n = 23; 30–100 mg), lorazepam (n = 22; 2–10 mg), and carbamazepine (n = 14; 600–1500 mg). Most treatments were provided as monotherapy (n = 114), whereas a minority involved adjunctive strategies (n = 23), combination treatments (n = 5), or internal comparisons between two formulations of the same benzodiazepine (n = 7; e.g. symptom-triggered vs fixed-schedule lorazepam). Most RCTs occurred in the United States (n = 51) and used either operationalized (n = 63) or DSM criteria (n = 64). Most studies occurred in inpatient settings (n = 118), whereas a minority took place in outpatient settings (n = 16), emergency departments (n = 8), or intensive care units (n = 7). The median RCT duration was 6 days (range: 1–28 days).

Risk of bias within studies

Although most studies were double-blinded (68%), the extent to which individual RCTs adequately described their methods was highly variable (Appendix 4). For example, 58% of RCTs did not sufficiently describe their randomization methods (e.g. computer-generated, block, or stratification), and 64% did not mention how they allocated treatment. Participant attrition across trials ranged from 0% to 62% (median: 7%). Only 40% of RCTs reported their funding sources. Overall, the risk of bias was moderate to high across most studies.

Results of individual studies and synthesis of results

Efficacy outcomes

Fixed-schOR,edule chlormethiazole (OR, 0.16; 95% CI, 0.04–0.65), fixed-schedule diazepam (OR, 0.16; 95% CI, 0.04–0.59), fixed-schedule lorazepam (OR = 0.19; 95% CI, 0.08–0.45), fixed-schedule chlordiazepoxide (OR = 0.21; 95% CI, 0.08–0.53), and divalproex (OR = 0.22; 95% CI, 0.05–0.86) were superior to placebo at reducing incident AW seizures (Figure 2(a)). However, only fixed-schedule diazepam (OR = 0.19; 95% CI, 0.05–0.76) reduced incident DTs (Figure 2(b)). Oxcarbazepine (d = −3.69; 95% CI, −6.21 to −1.17), carbamazepine (d = −2.76; 95% CI, −4.13 to −1.40), fixed-schedule oxazepam (d = −2.55; 95% CI, −4.26 to −0.83), and γ-hydroxybutyrate (GHB) (d = −1.80; 95% CI, −3.35 to −0.26) improved endpoint CIWA-Ar scores over placebo (Figure 2(c)).

FIGURE 2.

Forest plots depicting network meta-analyses syntheses for incident alcohol withdrawal seizures (a), delirium tremens (b), and reduced severity of alcohol withdrawal symptoms (c). All pharmacotherapies were compared with placebo using a random-effects frequentist network meta-analysis model.

For the treatment ranking score, treatments at the top of the plots have a higher ranking. OR indicates odds ratio; SMD, standardized mean difference; PBO, placebo, DTs, delirium tremens, AWS, alcohol withdrawal symptoms. All other definitions appear in the Abbreviations Table (Supporting Information S1). P-scores represent rankings, with the agent at the top of the plot having the most evidence for the analyzed outcome

Safety and acceptability outcomes

Promazine and carbamazepine were the only agents significantly associated with greater dropouts because of adverse events (Appendix 5). Halazepam, chlordiazepoxide, GHB, pregabalin, tiagabine, and chlormethiazole were associated with a reduced overall number of dropouts over placebo; however, promazine and ethanol were the only agents significantly associated with greater dropouts (Appendix 5). Promazine and carbamazepine were the only agents significantly associated with greater dropouts because of adverse events (Appendix 5).

Secondary outcomes

Symptom-triggered chlordiazepoxide, symptom-triggered diazepam, symptom-triggered alprazolam, diazepam, propranolol, adjunctive lamotrigine, chlordiazepoxide, topiramate, lorazepam, and adjunctive baclofen were associated with a reduced proportion of participants requiring additional AW pharmacotherapy against placebo, with ORs ranging from 0.01 (95% CI, 0.00–0.14) for symptom-triggered chlordiazepoxide to 0.12 (95% CI, 0.12) for adjunctive baclofen (Appendix 5). In addition, symptom-triggered diazepam, symptom-triggered lorazepam, symptom-triggered chlordiazepoxide, fixed-schedule lorazepam, fixed-schedule phenobarbital, adjunctive dexmedetomidine, and fixed-schedule chlordiazepoxide reduced the overall length of hospital stay significantly over placebo, with mean reductions of 250 hours (95% CI, 320–180) for symptom-triggered diazepam to 16 hours (95% CI, 30–1) for fixed-schedule chlordiazepoxide (Appendix 5). Phenobarbital, symptom-triggered lorazepam, symptom-triggered chlordiazepoxide, adjunctive dexmedetomidine, diazepam, and symptom triggered alprazolam all reduced total benzodiazepine doses (in lorazepam equivalents) against placebo, with effect sizes ranging from d = −23.00 (95% CI, −39.94 to −6.06) for phenobarbital to −6.18 (95% CI, −12.34 to −0.02) for symptom-triggered alprazolam (Appendix 5). Finally, none of the investigated agents demonstrated efficacy for reducing mortality (Appendix 5).

Assessment of inconsistency, risk of bias across studies, and additional analyses

Heterogeneity was only significant (I2 > 50%) for two continuous outcomes: total benzodiazepine requirements (I2 = 75.6%) and AW symptom severity on the CIWA-Ar scale (I2 = 91.6%). The risk of publication bias was deemed low for all 10 outcomes (Appendix 5). In addition, sensitivity analyses conducted by restricting samples to inpatient settings or monotherapy regimens alone did not identify significantly different patterns from the crude findings.

DISCUSSION

Summary of main results

The present review included 149 studies with 10 692 participants, spanning six decades of AW research. Although our review identified several evidence-based pharmacological strategies for AW, BZDs were the only agents showing consistent efficacy across efficacy, safety, acceptability, and secondary outcome measures. To that end, the only agent demonstrating efficacy for reduced DTs was diazepam, whereas no medication reduced the overall number of deaths.

Benzodiazepines

Across prior reviews, BZDs are the most extensively studied class of AW pharmacotherapies [5, 24, 26, 32, 34, 35, 38, 39, 43, 47, 49, 50, 80]. Meta-analyses from 1997 [23] and 1999 [24] demonstrated efficacy for BZDs over placebo and alternative treatments for seizures and DTs without significant adverse events or dropouts. Compared to non-BZDs, two Cochrane reviews from 2010 [32] and 2011 [35] identified non-significant trends favoring BZDs for seizures, DTs, adverse events, dropouts, global AW improvement, and RCT quality was low to very low for most included studies. A 2019 review found that symptom-triggered BZDs reduced the total duration of AW treatment and the total BZD dose requirements against fixed-schedule regimens [49].

Barbiturates

In the present review, five trials involved phenobarbital, finding similar efficacy for AW as gabapentin, lorazepam, valproate, or barbital [81–85]. Only one trial was placebo-controlled, finding that a single dose of phenobarbital with lorazepam-guided AW management reduced admissions to the intensive care unit.

Anticonvulsants

Previous reviews have explored anticonvulsants as alternatives to BZDs for AW, including valproate, carbamazepine, and oxcarbazepine [27, 34, 86]. However, compared to BZDs, there is less anticonvulsant data, and most comparisons between anticonvulsants and other drugs have been nonsignificant [34]. Although divalproex was associated with reduced incident AW seizures, we did not find evidence that anticonvulsants reduced DTs. Instead, they were associated with more adverse events and discontinuations because of adverse events. Based on these data, there is no suggestion that anticonvulsants have a role in managing moderate to severe withdrawal.

Chlormethiazole and GHB

The sedative-hypnotic chlormethiazole has been used widely in managing AW outside of North America [87]. However, its greater side effect burden, narrower therapeutic window, and potential withdrawal with abrupt discontinuation have lessened enthusiasm for its use [88]. An alternative GABAergic agent, GHB, has preliminary evidence for treating AW. In the present NMA, GHB reduced CIWA-Ar scores and was associated with reduced dropouts from placebo. As well, previous reviews indicate that a dose of 50 mg can effectively reduce AW symptoms over a placebo [33, 35, 40, 46].

Adrenergic agents

Selective α2-adrenergic agonists, including clonidine, dexmedetomidine, and lofexidine, and beta-blockers, like propranolol, have efficacy in managing AW because of their ability to suppress adrenergic hyperactivity [23]. However, we did not find consistent evidence for these agents regarding safety or efficacy outcomes in the present NMA.

Other glutamatergic agents

The glutamatergic agents lamotrigine, memantine, and topiramate have preliminary efficacy in AW [27, 34]. However, we did not find evidence favoring these agents in the present NMA.

Gabapentinoids

Although gabapentin and pregabalin confer some benefits in mild AW, the extent of evidence to support their use, particularly over BZDs, is limited. A previous meta-analysis of 10 gabapentin RCTs found preliminary efficacy in reducing AW symptoms [47]. However, the original meta-analysis estimates pooled all designs (i.e. observational studies with RCTs). Furthermore, when only RCTs were appraised, the corresponding effect sizes were not significant [47]. Therefore, the current NMA did not find evidence of efficacy with gabapentin for AW.

Baclofen

Although early case reports showed baclofen could reduce AW symptoms [25, 26], subsequent reviews could not conclude the efficacy and safety of baclofen for AW because of insufficient and very low-quality evidence [30, 80, 89, 90]. Methodological issues, such as the small number of studies, unclear outcome reporting, and different baseline characteristics in control and experimental groups, further decrease the evidence’s strength. The present NMA also failed to find evidence to support baclofen’s efficacy or safety in AW management.

Nitrous oxide

A previous review showed improvement with nitrous oxide for AW (RR = 1.35); however, the limited extent of adverse event reporting was an issue [29]. Although nitrous oxide may be efficacious for mild-to-moderate AW, there was a lack of solid evidence due primarily to the small sample sizes of the individual RCTs (n = 212 participants total). The present NMA failed to find evidence for the efficacy or safety of nitrous oxide.

Strengths and limitations

To our knowledge, the present NMA is the most comprehensive review of AW pharmacotherapies. Given the abundance of single-treatment RCTs and the shortage of head-to-head RCTs, NMAs can provide a novel knowledge synthesis of the available data.

However, our study also has limitations. First, although NMA is a powerful tool for comparative effectiveness research, some of our evidence relied on indirect treatment comparisons, which are more susceptible to bias than head-to-head comparisons. Yet, for most outcomes, available indices suggested consistency between direct and indirect evidence. Second, for a subset of pharmacotherapies (e.g. phenobarbital, individual anticonvulsants, and some antipsychotics), the availability of few RCTs and the use of small samples create imprecise and potentially underpowered estimates. However, this is one of the reasons for conducting an NMA in the first place, because it can pool small sample sizes to boost statistical power. Third, although we pooled studies regardless of treatment setting, AW severity, and comorbidity status to maximize power, our overall findings are less generalizable to specific settings or clinical populations and speak more to the efficacy of the treatments themselves. However, sensitivity analyses conducted by restricting samples to inpatient settings or monotherapy regimens alone did not identify significantly different patterns than the crude findings. Fourth, heterogeneity in the exposure (varying dosage of scheduled and as-needed medication), outcomes, setting (measured in the ED, inpatient units, and outpatient settings), and duration of treatment also limits the comparability across studies. However, given the lack of standardized protocols for RCTs investigating AW, this heterogeneity was, to a certain extent, unavoidable and not a specific limitation of this review. We used the random-effects model to estimate effect sizes across studies for a few reasons, as informed by evidence-based healthcare standard methodology [91]. First, we wanted results to apply beyond the included studies. Second, we did not assume a common, fixed parameter and hypothesized that different studies estimated different parameters, because studies were different from a clinical and methodological point of view. Finally, we wanted to create a meta-analysis summary effect to estimate the mean distribution of true effects. However, given the lack of standardized protocols for trials investigating AW, this heterogeneity was, to a certain extent, unavoidable and not a specific limitation of this review. Finally, we did not present inconsistency indices from the analyses because the data matrix for several treatments was sparse. Although comparability is particularly important for NMA, because of the transitivity assumption, the indices would have been non-significant because of the spares data matrix. Given this challenge, we compared our estimates to those of previous reviews, and our findings are fairly consistent with prior studies.

We may have missed relevant RCTs despite an extensive search, given the publication bias in two of our secondary outcomes. Although we did not detect network-level publication bias for most other outcomes, individual pharmacotherapies may have been subject to publication bias. As most review participants were middle-age males, our findings are less generalizable to other groups.

CONCLUSIONS

This NMA, although confirming the efficacy and safety of BZDs, uncovers substantial limitations in our knowledge regarding AW treatment. Several critical areas of limited knowledge are as follows. First, there are simply too few high-quality trials to establish safety and efficacy for medications other than BZDs and combinations of drugs. Second, there are too few high-quality comparative efficacy trials comparing BZDs to other medicines (in circumstances where the risk for serious outcomes is high, placebo-controlled trials would not be ethical and where risk is very low, neither feasible nor relevant). Third, we need high-quality trials in specific settings that address outcomes important in such settings. For example, in severe AW in intensive care unit settings, the risk for poor outcomes of AW (seizures, DTs, and death) is the risk of complications from medication treatments (from over-and prolonged sedation). In the case of outpatient management, medication can reduce AW symptoms and facilitate the transition to alcohol abstinence. In this setting, medications with lower risks of adverse events beyond the symptomatic AW period and higher chances of transitioning to AUD treatment are preferred. Finally, regarding clinical practice, treatment should be limited to medications with the best efficacy and safety; if additional medications (instead of or in addition to BZDs) are perceived to be needed in clinical circumstances, those should be subjected to future clinical trials.