Types of studies

This review will include randomized controlled trials (RCTs) only. We will not include quasi‐randomized studies or non‐randomized studies due to the risk of bias inherent in such designs.

Types of participants

We will include adults (aged 18 years or over) who receive an intravenous opioid in the acute care setting. Any intravenous opioids will be eligible for inclusion (e.g. morphine, hydromorphone, fentanyl, sufentanil, tramadol). We define the acute care setting as the ED or an urgent care clinic.

Types of interventions

The intervention will consist of antiemetic medication given via any route (e.g. oral, sublingual, intramuscular, intravenous) prophylactically with the intention of preventing opioid‐induced nausea and vomiting. We will complete analyses for outcomes by antiemetic medication class:

• serotonin receptor antagonists;

• dopamine receptor antagonists;

• neurokinin receptor antagonists;

• corticosteroids;

• histamine receptor antagonists; and

• anticholinergics.

The comparators will consist of placebo or standard care without an antiemetic agent.

Types of outcome measures

We will include studies that meet the above inclusion criteria and assess the following outcomes. We selected a time period of enrollment to ED discharge or hospital admission because prior research in opioids for ED pain management recommended a longer time period to ensure adequate assessment of adverse events (Rainer 2000). Avoiding nausea and vomiting throughout acute treatment is important to facilitate disposition from the ED.

Electronic searches

The Cochrane Pain, Palliative, and Supportive Care Review Group's Information Specialist will search the following electronic databases for randomized controlled trials. There will be no restrictions on language or year of publication.

• Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library (latest issue)

• MEDLINE Ovid (1946 to present)

• Embase Ovid (1980 to present)

• Google Scholar (initial 200 articles) (Bramer 2017)

The strategy that will be used to search MEDLINE can be found in Appendix 1. The Information Specialist will amend this where necessary to search the other databases listed.

Searching other resources

We will search www.clinicaltrials.gov and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/) for ongoing trials. In addition, we will check reference lists of reviews and retrieved articles for additional studies, and perform citation searches on key articles. We will contact experts in the field for unpublished and ongoing trials; we define experts as the primary or corresponding authors of identified studies for inclusion. We will contact study authors for additional information where necessary.

Selection of studies

Two review authors (MG, JNC) will independently determine eligibility of each study identified by the search. Independent review authors will eliminate studies that clearly do not satisfy inclusion criteria, and obtain full copies of the remaining studies. Two review authors (MG, JNC) will read these studies independently to select relevant studies, and in the event of disagreement, a third author will adjudicate (GDP). We will not anonymize the studies in any way before assessment. We will include a PRISMA flowchart in the full review which will show the status of identified studies (Moher 2009). We will include studies in the review irrespective of whether they report measured outcome data in a 'usable' way.

Data extraction and management

Two review authors (MG, GDP) will independently extract data using a standard piloted form and check for agreement before entry into Review Manager (Review Manager 2020). In the event of disagreement, a third author will adjudicate (JNC). We will collate multiple reports of the same study, so that each study rather than each report is the unit of interest in the review. We will collect characteristics of the included studies in sufficient detail to populate a table of 'Characteristics of included studies' in the full review. We will extract the following information.

Assessment of risk of bias in included studies

Two authors (MG, GDP) will independently assess risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and will resolve any disagreements by discussion. We will complete a 'Risk of bias' table for each included study using the 'Risk of bias' tool in RevMan (Review Manager 2020).

We will assess the following biases for each included study.

• Random sequence generation (checking for possible selection bias). We will assess the method used to generate the allocation sequence as:

• • low risk of bias (any truly random process, e.g. random number table; computer random number generator);

  • unclear risk of bias (insufficient detail about the method of randomization to be able to judge the generation as 'low' or 'high' risk of bias);

• Allocation concealment (checking for possible selection bias). The method used to conceal allocation to interventions prior to assignment determines whether intervention allocation could have been foreseen in advance of (or during) recruitment, or changed after assignment. We will assess the methods as:

• • low risk of bias (e.g. telephone or central randomization; consecutively numbered sealed opaque envelopes);

  • unclear risk of bias (insufficient detail about the method of randomization to be able to judge the generation as 'low' or 'high' risk of bias);

• Blinding of participants and personnel (checking for possible performance bias). We will assess the methods used to blind study participants and personnel from knowledge of which intervention a participant received. We will assess methods as:

• • low risk of bias (study states that it was blinded and describes the method used to achieve blinding, such as identical tablets matched in appearance or smell, or a double‐dummy technique);

  • unclear risk of bias (study states that it was blinded but does not provide an adequate description of how it was achieved);

• Blinding of outcome assessment (checking for possible detection bias). We will assess the methods used to blind study participants and outcome assessors from knowledge of which intervention a participant received. We will assess the methods as:

• • low risk of bias (study has a clear statement that outcome assessors were unaware of treatment allocation, and ideally describes how this was achieved);

  • unclear risk of bias (study states that outcome assessors were blind to treatment allocation but lacks a clear statement on how it was achieved);

• Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data). We will assess the methods used to deal with incomplete data as:

• • low risk of bias (no missing outcome data; reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring is unlikely to be introducing bias); missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; missing data have been imputed using 'baseline observation carried forward’ analysis);

  • unclear risk of bias (insufficient reporting of attrition/exclusions to permit a judgement of ‘low risk’ or ‘high risk’ [e.g. number randomized not stated, no reasons for missing data provided, or the study did not address this outcome]);

• Selective reporting (checking for reporting bias). We will assess reporting biases due to selective outcome reporting. We will judge studies as:

• • low risk of bias (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]);

  • unclear risk of bias (insufficient information available to permit a judgement of ‘low risk’ or ‘high risk’);

Measures of treatment effect

We will use the risk ratio (RR) to measure treatment effects for dichotomous data (presence of vomiting, presence of nausea, number of participants requiring rescue medication, adverse events). For continuous data (number of vomiting episodes, nausea severity), we will calculate treatment effects using the mean difference (MD), or use the standardized mean difference (SMD) if studies used different scales to measure the same outcome. We will report all treatment effects with 95% confidence intervals (CIs) and use forest plots to present the data. We will report the number needed to treat for an additional beneficial outcome (NNTB) or for an additional harmful outcome (NNTH).

Unit of analysis issues

Identifying cluster‐randomized or cross‐over trials is of low likelihood based on historical findings from a similar review on this topic (Simpson 2011), but we will include them given inclusion criteria are met. We will analyze cluster‐randomized and cross‐over randomized trials using generic inverse‐variance methods (Higgins 2020).

For cluster‐randomized trials, we will seek direct estimates of the effect from an analysis that accounted for the cluster design. Where the analysis in a cluster‐randomized trial does not account for the cluster design, we will use the approximately correct analysis approach presented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020).

For cross‐over design RCTs, we consider that the intervention is likely to have carry‐over effects. Therefore, we will use data only from the first period and analyze the data as a parallel‐group trial, as outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2020). Where cross‐over RCTs include more than two groups, we will pool data for antiemetic arms (serotonin antagonists or dopamine antagonists) into a single treatment group. Cross‐over RCTs with dichotomous outcomes require more complicated methods, and the authors will consult with a statistician (Elbourne 2002). 

Dealing with missing data

We will use intention‐to‐treat (ITT) data to minimize the impact of unknown information due to study participant attrition. We will contact investigators to verify missing study characteristics and missing numerical outcome data. For continuous data reported without standard deviations, we will impute standard deviations from available reported variances using standard errors, confidence intervals, t statistics, or P values. If a study does not report variances, we will impute missing standard deviations using the average from included studies. We will further assess outcome data including imputed values via sensitivity analysis.

Assessment of heterogeneity

To assess heterogeneity of pooled studies, we will assess the Chi² test and I² statistic. For the Chi² test, we will use N‐1 degrees of freedom and consider a P value less than 0.10 to indicate statistically significant heterogeneity (i.e. variation in effect estimates beyond chance). We will use the I² statistic to classify heterogeneity as follows:

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity; and

• 75% to 100%: considerable heterogeneity.

Assessment of reporting biases

We will assess funnel plots; where asymmetry exists, we will consider small study effects and non‐reporting biases as explanations for the asymmetry (Higgins 2011). We will explore additional explanations of funnel plot asymmetry, including inflated effects in smaller studies, true heterogeneity, artefactual causes, and chance (Egger 1997). Lastly, we will consider missing outcome data, and will contact study authors in such instances.

Data synthesis

We will pool outcomes using a random‐effects model, chosen irrespective of the assessment of statistical heterogeneity, to address clinical differences unexplained through our investigation of heterogeneity. We will account for clinical heterogeneity, as necessary, via subgroup analyses. We will pool adverse events for analysis and will measure events per participant (i.e. a participant experiencing more than one adverse event will be treated as a single event).

Subgroup analysis and investigation of heterogeneity

We will use a subgroup analysis to explore sources of heterogeneity, if it exists (I² statistic greater than 59%). We will conduct subgroup analysis only for the primary outcome measure. A priori, the authors decided a subgroup analysis will take into account treatment setting (ED versus other setting, e.g. urgent care clinic), based on the rationale that participants treated in an ED may present with more severe pain conditions and associated nausea. Additionally, we will perform subgroup analyses by drug within each medication class to inform clinicians of efficacy and safety. We will compare subgroups with each other using the difference in effects between subgroups approach presented in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2020).

We will treat our subgroup analysis as observational comparisons because participants will likely not be randomized into the subgroups. As such, we will measure treatment effects using risk difference (RD).

Sensitivity analysis

We will perform sensitivity analyses to examine the impact of excluding studies that are industry‐funded or unpublished, and studies we deem to be at high risk of bias according to the 'Risk of bias' summary.

Summary of findings and assessment of the certainty of the evidence

Two review authors (MG, JNC) will independently rate the certainty of the body of evidence for the outcomes. We will use the GRADE system to rank the certainty of the evidence using GRADE software (GRADEpro GDT 2015), and the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2020).

The GRADE approach uses five considerations (study limitations [risk of bias], unexplained heterogeneity and inconsistency of effect, imprecision, indirectness, and publication bias) to assess the certainty of the body of evidence for each outcome. The GRADE system uses the following criteria for assigning grade 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 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.

The GRADE system considers study design as a marker of certainty. Randomized controlled trials are considered to be high‐certainty evidence and can be downgraded for important limitations. Observational trials are considered low‐certainty evidence and can be upgraded for strengths (Schünemann 2013).

We will decrease the grade rating if we identify the following:

• serious or very serious study limitations;

• serious or very serious inconsistency of results;

• serious or very serious uncertainty about directness;

• serious or very serious imprecision;

• probability of reporting bias.