Types of studies

We will include randomised controlled trials. We will not consider quasi‐randomised, non‐randomised studies, cohort studies, case series, cross‐over trials or cluster‐randomised trials.

Types of participants

Participants with locally advanced or metastatic urothelial carcinoma of the bladder as determined by cross‐sectional imaging or confirmed by biopsy, or both, whose disease progressed during or following platinum‐containing chemotherapy (synonymous with second‐/third‐/fourth‐line therapy). We will not include participants receiving pembrolizumab as first‐line therapy.

Types of interventions

This review will focus on pembrolizumab (synonyms: MK‐3475, lambrolizumab, Keytruda). We plan to investigate the following comparisons of experimental intervention versus comparator intervention.

Types of outcome measures

We will not exclude trials because one or several of our primary or secondary outcomes were not reported in the publication. In cases where none of our primary or secondary outcomes has been reported we will not include this trial but will provide some basic information in an additional table.

Electronic searches

We will search the following sources.

• Databases of medical literature

  • Cochrane Central Register of Controlled Trials (CENTRAL; latest issue);

  • MEDLINE (via PubMed; 2000 onward to November 2017).

• Databases of ongoing trials

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

  • World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; apps.who.int/trialsearch/, 2000 to present).

This being an expedited, rapid review, we will limit our search to published studies and to the use of English as the language of publication. We will not search the databases and websites of institutions, such as pharmaceutical organisations, agencies and societies. We will start the search in 2000 as PD‐1/PD‐L1 blockade for tumour control, the underlying mechanism of action of tumor immunotherapy by PD‐L1 blockade, was first reported in 2002 (Iwai 2002).

Searching other resources

We will check the reference lists of all identified trials, relevant review articles, and current treatment guidelines for further literature but will not contact experts in the field, drug manufacturers or regulatory agencies for information on unpublished trials.

Selection of studies

We will use reference management software (Endnote 2011) to identify and remove potential duplicate records. Two review authors (VN, FK) will independently scan the abstract, title, or both, of the remaining records retrieved and will investigate all potentially relevant records as full text, map records to studies, and classify studies as included studies, excluded studies, studies awaiting classification, or ongoing studies using Covidence software (Covidence). We will resolve any discrepancies through consensus or recourse to a third review author (PD). We will document reasons for the exclusion of studies that may have reasonably been expected to be included in the review in a 'Characteristics of excluded studies' table. We will present an adapted PRISMA flow diagram showing the process of study selection (Liberati 2009).

Data extraction and management

For studies that fulfil the inclusion criteria, one review author (FK) will extract key participant and intervention characteristics using a data extraction form based on the recommendations of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). A second review author will check data entry (VN). We will resolve any disagreements by consensus or, if required, by consultation with a third review author (PD).

We will extract the following information.

• Study design;

• Study dates (if dates are not available then this will be reported);

• Study settings;

• Participant inclusion and exclusion criteria;

• Participant details, baseline demographics such as disease stage, age, gender, pretreatment;

• The number of participants by study/study arm;

• Details of relevant experimental and comparator interventions such as dose, route, frequency, and duration;

• Definitions of relevant outcomes, and method and timing of outcome measurement, as well as any relevant subgroups;

• Study methods such as treatment cross‐over, compliance with assigned treatment, length of follow‐up;

• Study funding sources;

• Declarations of interest by primary investigators.

We will provide information, including trial identifier, about potentially relevant ongoing studies in the table 'Characteristics of ongoing studies'. We will attempt to contact authors of included studies to obtain key missing data as needed.

We will extract outcome data relevant to this review as needed for the calculation of summary statistics and measures of variance. For dichotomous outcomes, we will attempt to obtain numbers of events per total number of included patients to enable the population of a 2 x 2 table, as well as summary statistics with corresponding measures of variance. For continuous outcomes, we will attempt to obtain means and standard deviations or the data necessary to calculate this information. For time‐to‐event outcomes, we will attempt to obtain hazard ratios (HRs) with corresponding measures of variance or the data necessary to calculate this information.

Assessment of risk of bias in included studies

One review author (FK) will assess the risk of bias in each included study and a second review author will check the data entry (VN). We will resolve disagreements by consensus, or by consultation with a third review author (PD).

For randomised controlled trials, we will assess the risk of bias using the Cochrane tool (Higgins 2011b). We will assess the following domains.

• Random sequence generation (selection bias);

• Allocation concealment (selection bias);

• Blinding of participants and personnel (performance bias);

• Blinding of outcome assessment (detection bias);

• Incomplete outcome data (attrition bias);

• Selective reporting (reporting bias);

• Other sources of bias.

We will judge risk of bias domains as 'low risk', 'high risk', or 'unclear risk' and will evaluate individual bias items as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). We will present a 'Risk of bias' graph to illustrate these findings.

For performance bias (blinding of participants and personnel) and detection bias (blinding of outcome assessment), we will evaluate the risk of bias separately for each outcome (Hróbjartsson 2013), but group outcomes as appropriate, as detailed below.

With regards to performance bias, we will judge outcomes as similarly susceptible to performance bias and will rate them as one group.

We will define the following endpoints as subjective outcomes in terms of susceptibility to detection bias and will rate them as one group.

• Quality of life;

• Progression‐free survival;

• Response rate;

• Treatment‐related mortality;

• Rate of serious AEs.

We will define the following endpoint as an objective outcome in terms of susceptibility to detection bias.

• Overall survival.

We will also assess attrition bias (incomplete outcome data) on an outcome‐specific basis, and will group outcomes with like judgements when reporting our findings in the 'Risk of bias' tables.

We will summarise the risk of bias across domains for each outcome in each included study, as well as across studies and domains for each outcome.

Measures of treatment effect

When at least two included trials are available for the comparison of a given outcome, we will try to express dichotomous data as a risk ratio (RR) or odds ratio (OR) with 95% confidence intervals (CIs). For continuous outcomes measured on the same scale we will estimate the intervention effect using the mean difference with 95% CIs. For continuous outcomes measuring the same underlying concept (e.g. health‐related quality of life) but using different measurement scales, we will calculate the standardised mean difference (SMD). We will express time‐to‐event data as HRs with 95% CIs or will use an indirect estimation method if HRs were not given (Parmar 1998; Tierney 2007).

Unit of analysis issues

The unit of analysis will be the individual participant. Should we identify trials with more than two intervention groups for inclusion in the review, we will handle these in accordance with guidance provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011c).

When arms cannot be pooled this way we will compare each arm with the common comparator separately. For pairwise meta‐analysis, we will split the ‘shared’ group into two or more groups with a smaller sample size, and include two or more (reasonably independent) comparisons. For this purpose, for dichotomous outcomes, both the number of events and the total number of participants will be divided up, and for continuous outcomes, the total number of participants will be divided up with unchanged means and standard deviations.

Dealing with missing data

We will obtain missing data from study authors, if feasible, and will perform intention‐to‐treat analyses if data are available; we will otherwise perform case analyses. We will investigate attrition rates (e.g. drop‐outs, losses to follow up, and withdrawals) and will critically appraise issues of missing data. We do not plan to impute missing data.

Assessment of heterogeneity

In the event of excessive heterogeneity unexplained by subgroup analyses, we will not report study results as the pooled effect estimate in a meta‐analysis but will provide a narrative description of the results of each study.

We will identify heterogeneity (inconsistency) through visual inspection of the forest plots to assess the amount of overlap of 95% CIs, and using the I² statistic, which quantifies inconsistency across studies to assess the impact of heterogeneity on the meta‐analysis (Higgins 2002; Higgins 2003); we will interpret I² as follows.

• 0% to 40%: may not be important;

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

• 50% to 90%: may indicate substantial heterogeneity;

• 75% to 100%: may indicate considerable heterogeneity.

When we find heterogeneity, we will attempt to determine possible reasons for it by examining individual study and subgroup characteristics.

Assessment of reporting biases

We will attempt to obtain study protocols to assess for selective outcome reporting.

If we include 10 studies or more investigating a particular outcome, we will use funnel plots to assess small study effects. Several explanations can be offered for the asymmetry of a funnel plot, including true heterogeneity of effect with respect to trial size, poor methodological design (and hence bias of small trials), and publication bias. We will therefore interpret results carefully (Sterne 2011).

Data synthesis

Unless there is good evidence for homogeneous effects across studies, we will summarise data using a random‐effects model (Wood 2008). We will interpret random‐effects meta‐analyses with due consideration of the whole distribution of effects. In addition, we will perform statistical analyses according to the guidelines contained in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). For dichotomous outcomes, we will use the Mantel‐Haenszel method; for continuous outcomes, we will use the inverse variance method; and for time‐to‐event outcomes, we will use the generic inverse variance method. We will use Review Manager software to perform analyses (Review Manager 2014).

Subgroup analysis and investigation of heterogeneity

We expect the following characteristics to potentially introduce clinical heterogeneity, and plan to carry out subgroup analyses with investigation of interactions.

• Performance status (Eastern Cooperative Oncology Group (ECOG) 0 or 1 versus ≥ 2);

• Time since last chemotherapy administration (< three months versus ≥ three months);

• Degree of pretreatment (second‐ versus third‐ versus fourth‐line or more);

• PDL‐1 tumour expression status (positive versus negative).

We will use the test for subgroup differences in Review Manager to compare subgroup analyses if there are sufficient studies (Review Manager 2014).

Sensitivity analysis

We plan to perform sensitivity analyses in order to explore the influence of the following factors (when applicable) on effect sizes.

• Restricting the analysis by taking into account risk of bias, by excluding studies at 'high risk' or 'unclear risk'.