Types of studies

We will include studies if they are randomised controlled trials (RCTs). We require full journal publication, with the exception of online clinical trial results and summaries of otherwise unpublished clinical trials and abstracts with sufficient data for analysis. In the case of cross‐over trials, only the first period of the trial will be analysed. There will be no limitation with respect to the length of follow‐up.

We will exclude studies that were non‐randomised, case reports and clinical observations.

Types of participants

Studies will include trials involving adult patients according to the definition in the studies (usually ≧ 18 years of age), with a confirmed diagnosis of cancer, irrespective of type and stage of cancer and gender. We will include both patients with solid cancer and patients with haematological malignancies. We will include trials that included patients receiving moderately or highly emetogenic chemotherapy according to the latest Antineoplastic Agents Emetic Risk Classification (Jordan 2017; Roila 2016). As this classification has changed over the years (e.g. anthracycline and cyclophosphamide combination is nowadays classified as highly emetogenic instead of moderately emetogenic), we will use this classification to asses the emetogenic risk of one specific chemotherapeutic agent, irrespective of the emetogenic risk the study authors applied (see section Description of the condition). We will perform separate analyses for populations receiving moderately emetogenic and highly emetogenic chemotherapy, according to the latest definition by MASCC/ESMO (Jordan 2017; Roila 2016). We assume that patients who fulfil the inclusion criteria are equally eligible to be randomised to any of the interventions we plan to compare.

We will exclude trials including participants not receiving the same risk levels of emetogenic chemotherapies, which do not provide subgroup data for each emetogenic risk group. We will exclude trials evaluating participants at risk for radiotherapy‐induced nausea and vomiting. We will exclude trials evaluating participants at risk of vomiting and nausea due to their underlying disease.

Types of interventions

Nowadays, recommended antiemetics for prophylaxis of CINV caused by moderately or highly emetogenic chemotherapy are:

• 5‐Hydroxytryptamine‐3 (5‐HT₃) receptor antagonists with dexamethasone, solely, or combined with;

• Neurokinin‐1 (NK₁) receptor antagonist.

Combinations of these interventions at any dose and by any route will be compared to each other in a full network. We will include all RCTs comparing in at least two study arms the intervention of interest, either 5‐Hydroxytryptamine‐3 (5‐HT₃) receptor antagonists with dexamethasone or 5‐Hydroxytryptamine‐3 (5‐HT₃) receptor antagonists with dexamethasone combined with Neurokinin‐1 (NK₁) receptor antagonist) (see Figure 1 for a full network of direct comparisons). In case we identify additional, new drugs belonging to the above mentioned drug classes which are not mentioned in Figure 1, we will include these trials. We will explicitly state in the review that we identified further drugs of interest.

Figure 1

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Network of direct comparisons of interest. All drugs and drug combinations are combined with dexamethasone. Strength of the line represents number of RCTs.

We will analyse prophylaxis for cancer patients administered moderately emetogenic or carboplatin‐based chemotherapy or highly emetogenic chemotherapy separately. We assume that any participant that meets the inclusion criteria is, in principle, equally likely to be randomised to any of the eligible interventions. We plan to group interventions by evaluating different drug doses together as one drug of interest, according to the product characteristics.

We will exclude trials evaluating solely treatment of nausea and vomiting, meaning that the drug is not given before administering chemotherapeutic agents to prevent CINV, but once nausea or vomiting appears. Antimetic agents to treat CINV might be the same agents as for prevention of CINV, but to include clinically homogenous trials to answer the research question, we will focus on prophylaxis only.

Types of outcome measures

We will include all trials fitting the inclusion criteria mentioned above, irrespective of reported outcomes. We will estimate the relative ranking of the competing interventions according to each of the following outcomes.

Electronic searches

We will search the following databases without language restrictions. As at least one intervention arm will include at least one 5‐Hydroxytryptamine‐3 (5‐HT₃) receptor antagonist, which has been mentioned first in 1988 for the treatment of chemotherapy‐induced emesis (Carmichael 1988), we will restrict our search from 1988 to present. Only trials that compare at least two of the drug combinations mentioned above are eligible. We will search for all possible comparisons formed by the interventions of interest.

• The Cochrane Central Register of Controlled Trials (CENTRAL) (via the Cochrane Library, latest issue)

• MEDLINE (via Ovid, 1988 to present)

• Embase (via Ovid, 1988 to present)

Medical subject headings (MeSH) or equivalent and text word terms will be used. There will be no language restrictions. Searches will be tailored to individual databases. The search strategy for CENTRAL is in Appendix 1.

Searching other resources

In addition, we will search the following databases/sources.

• Conference proceedings of annual meetings of the following societies will be searched if they are not included in CENTRAL (1988 to present):

  • American Society of Clinical Oncology (ASCO);

  • European Society of Medical Oncology (ESMO);

  • Multinational Association of Supportive Care in Cancer (MASCC).

• Databases of ongoing trials:

• • metaRegister of controlled trials (mRCT) (www.controlled‐trials.com/mrct);

  • clinicaltrials.gov (www.clinicaltrials.gov);

  • WHO International Clinical Trials Registry Platform (ICTRP) (http://apps.who.int/trialsearch/).

• We will check reference lists of reviews and retrieved articles for additional studies and we will perform citation searches on key articles.

• We will contact experts in the field for unpublished and ongoing trials.

• We will contact authors where necessary for additional information.

Selection of studies

Two review authors will independently screen the results of the search strategies for eligibility for this review by reading the abstracts using Covidence software (Covidence systematic review software). We will code the abstracts as either 'retrieve' or 'do not retrieve'. In the case of disagreement or if it is unclear whether we should retrieve the abstract or not, we will obtain the full‐ text publication for further discussion. Independent review authors will eliminate studies that clearly do not satisfy the inclusion criteria, and obtain full‐text copies of the remaining studies. Two review authors will read these studies independently to select relevant studies, and in the event of disagreement, a third author will adjudicate. We will not anonymise the studies before assessment. We will include a Preferred Reporting Items for Systematic Reviews and Meta‐Analyses (PRISMA) flow chart in the full review that will show the status of identified studies (Moher 2009) as recommended in Part 2, Section 11.2.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will include studies in the review irrespective of whether measured outcome data are reported in a ‘usable’ way.

Data extraction and management

Two review authors will extract data using a standardised data extraction form developed in Covidence (Covidence systematic review software). If the authors are unable to reach a consensus, we will consult a third review author for final decision. If required, we will contact the authors of specific studies for supplementary information (Higgins 2011a). After agreement has been reached, we will enter data into Review Manager (RevMan 2014). We will extract the following information.

• General information: Author, title, source, publication date, country, language, duplicate publications.

• Quality assessment: Sequence generation, allocation concealment, blinding (participants, personnel, outcome assessors), incomplete outcome data, selective outcome reporting, other sources of bias.

Moreover, we will extract the following information which may act as effect modifier.

• Study characteristics: Trial design, aims, setting and dates, source of participants, inclusion/exclusion criteria, comparability of groups, subgroup analysis, statistical methods, power calculations, treatment cross‐overs, compliance with assigned treatment, length of follow‐up, time point of randomisation.

• Participant characteristics: Age, gender, ethnicity, number of participants recruited/allocated/evaluated, participants lost to follow‐up, cancer type and stage, additional diagnoses, type and intensity of antineoplastic therapy, emetogenic risk, other patient‐specific prognostic factors e.g. pregnancy, motion sickness, alcohol intake.

• Interventions: Type and dosage of antiemetic agents, duration of prophylaxis, duration of follow‐up.

• Outcomes: Complete control of nausea (acute and delayed phase, overall), complete control of vomiting (acute and delayed phase, overall), on‐study mortality, quality of life, adverse events. Where possible, we will extract data at the arm level, not summary effects.

• Notes: Sponsorship/funding for trial and notable conflict of interest of review authors.

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.

Assessment of risk of bias in included studies

This section is taken from the PaPaS template for protocols.

Two review authors will independently assess risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c) and adapted from those used by the Cochrane Pregnancy and Childbirth Group, with any disagreements resolved by discussion. We will complete a 'Risk of bias' table for each included study using the 'Risk of bias' tool in RevMan (RevMan 2014).

We will assess the following for each 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 (method used to generate sequence not clearly stated). Studies using a non‐random process (e.g. odd or even date of birth; hospital or clinic record number) will be excluded.

• 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 randomisation; consecutively numbered sealed opaque envelopes); unclear risk of bias (method not clearly stated). Studies that do not conceal allocation (e.g. open list) will be excluded.

• 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). Studies that were not double‐blinded are considered to have high risk of bias.

• 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). Studies where outcome assessment was not blinded will be considered as having a high risk of bias.

• Selective reporting (checking for reporting bias). We will assess whether primary and secondary outcome measures were pre‐specified and whether these were consistent with those reported: low risk of bias ( study protocol is available and all of the study’s pre‐specified (primary and secondary) outcomes that are of interest in the review have been reported in the pre‐specified way, or the study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were pre‐specified); unclear risk of bias (insufficient information to permit judgement of ‘low risk’ or ‘high risk'); high risk of bias (not all of the study’s pre‐specified primary outcomes have been reported or one or more primary outcomes is reported using measurements, analysis methods or subsets of the data that were not pre‐specified or one or more reported primary outcomes were not pre‐specified or one or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis, or the study report fails to include results for a key outcome that would be expected to have been reported for such a study).

• 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 (< 10% of participants did not complete the study and/or used ‘baseline observation carried forward’ analysis); unclear risk of bias (used 'last observation carried forward' analysis); high risk of bias (used 'completer' analysis).

• Size of study (checking for possible biases confounded by small size). We will assess studies as being at low risk of bias (≥ 200 participants per treatment arm); unclear risk of bias (50 to 199 participants per treatment arm); high risk of bias (< 50 participants per treatment arm).

Measures of treatment effect

Unit of analysis issues

Dealing with missing data

As suggested in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b), we will take the following steps to deal with missing data.

Whenever possible, we will contact the original investigators to request relevant missing data. If the number of participants evaluated for a given outcome is not reported, we will use the number of participants randomised per treatment arm as the denominator. If only percentages but no absolute number of events are reported for binary outcomes, we will calculate numerators using percentages. If estimates for mean and standard deviations are missing, we will calculate these statistics from reported data whenever possible, using approaches described in Chapter 7.7 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). If standard deviations are missing and we are not able to calculate them from reported data, we will calculate values according to a validated imputation method (Furukawa 2006). If data are not reported numerically but graphically, we will estimate missing data from figures. We will perform sensitivity analyses to assess how sensitive results are to imputing data in some way. We will address in the Discussion section the potential impact of missing data on findings of the review.

Assessment of heterogeneity

Assessment of reporting biases

In pairwise comparisons with at least 10 trials, we will examine the presence of small‐study effects graphically by generating funnel plots. We will use linear regression tests (Egger 1997) to test for funnel plot asymmetry. A P value less than 0.1 will be considered significant for this test (Sterne 2011). We will examine the presence of small‐study effects for the primary outcome only. Moreover, we will search study registries, to identify completed, but not published trials.

Data synthesis

Subgroup analysis and investigation of heterogeneity

We will use the test for interactions to test for subgroup differences. The following subgroup analysis will be conducted, if appropriate:

• type of chemotherapy (carboplatin versus other moderately emetogenic chemotherapy);

• drug dosage;

• route of administration (intravenous (IV) versus oral);

• cancer type;

• patient‐specific prognostic factors (e.g. younger age, female sex, alcohol intake, history of vomiting pregnancy, motion sickness).

Sensitivity analysis

To test the robustness of the results, we will conduct fixed‐effect pairwise and network meta‐analyses. We will report the estimates of the fixed‐effect only if they show a difference to the random‐effects model. We will explore the influence of quality components with regard to low and high risk of bias.