Types of studies

We will include randomised controlled trials (RCTs). We will include studies reported as full text, those published as abstract only, and unpublished data. We will exclude quasi‐randomised trials (where the allocation is done on the basis of a pseudo‐random sequence, e.g. alternating odd or even hospital numbers or dates of birth), and non‐randomised studies (Reeves 2011).

Types of participants

We will include adults (irrespective of sex or race) who are diagnosed with any pancreatic/duodenal/periampullary disease requiring pancreatoduodenectomy.

Types of interventions

We will assess the following comparisons for people undergoing pancreatoduodenectomy.

• Duct‐to‐mucosa pancreaticojejunostomy versus any other type of pancreaticojejunostomy (e.g. invagination pancreaticojejunostomy, binding pancreaticojejunostomy)

• One type of duct‐to‐mucosa pancreaticojejunostomy versus a different type of duct‐to‐mucosa pancreaticojejunostomy (e.g. double layers versus triple layers)

We will include any additional interventions, provided they are not part of the randomised treatment.

Types of outcome measures

Electronic searches

We will conduct a literature search to identify all published and unpublished randomised controlled trials. The literature search will identify potential studies in all languages. We will translate the non‐English language papers and fully assess them for potential inclusion in the review as necessary.

We will search the following electronic databases for identifying potential studies.

• Cochrane Central Register of Controlled Trials (CENTRAL) (Appendix 2).

• MEDLINE (1966 to present) (Appendix 3).

• Embase (1988 to present) (Appendix 4).

• Science Citation Index Expanded (1982 to present) (Appendix 5).

Searching other resources

We will check the reference lists of all primary studies and review articles for additional references.  We will contact authors of identified trials and ask them to identify other published and unpublished studies. We will also contact experts in the field.

We will search for errata or retractions from eligible trials on PubMed (www.ncbi.nlm.nih.gov/pubmed) and report the date this was done in the review.

Selection of studies

Two review authors (SH, JX) will independently screen titles and abstracts for inclusion. All of the potential studies we identify as a result of the search will be coded them as either 'retrieve' (eligible, potentially eligible, or unclear) or 'do not retrieve'. We will retrieve the full text of potentially eligible studies and two review authors (SH, JX) will independently screen the full text, identify studies for inclusion, and identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion or, if required, we will consult a third author (YC). We will identify and exclude duplicates and 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 record the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table.

Data extraction and management

We will use a standardised data collection form for study characteristics and outcome data, which will be piloted on at least one study included in the review. Two review authors (XD, ZL) will independently extract the following information from the included studies.

• Methods: study design, total study duration and run‐in (the time period before entering a clinical trial, in which participants may discontinue or begin treatment), number of study centres and location, study setting, withdrawals, date of study.

• Participants: number (N), mean age, age range, gender, severity of condition, diagnostic criteria, inclusion criteria, exclusion criteria.

• Interventions: intervention, comparison.

• Outcomes: primary and secondary outcomes specified and collected, time points reported.

• Notes: funding for study, notable conflicts of interest of study authors.

Two review authors (XD, ZL) will independently extract outcome data from the included studies. We will note in the 'Characteristics of included studies' table if the study authors reported outcome data in an unusable way. We will resolve disagreements by consensus or by involving a third review author (YC). One review author (YC) will copy across the data from the data collection form into the Review Manager 5 file (Review Manager 2014). We will double‐check that the data are entered correctly by comparing the study reports with how the data are presented in the systematic review. A second review author will spot‐check study characteristics for accuracy against the trial report.

Assessment of risk of bias in included studies

Two review authors (YC, JG) will independently assess the risk of bias for each included study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion, or by involving a third review author (YC). We will assess the risk of bias according to the following domains.

• Random sequence generation.

• Allocation concealment.

• Blinding of participants and personnel.

• Blinding of outcome assessment.

• Incomplete outcome data.

• Selective outcome reporting.

• Other bias.

We will judge each study as being at high, low or unclear risk of bias for each domain. We will provide a quote from the study report and justification for our judgement in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgements across studies for each of the domains listed. We will consider blinding separately for different key outcomes where necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be very different than for a person‐reported pain scale). Where information on risk of bias relates to unpublished data or correspondence with a study author, we will note this in the 'Risk of bias' table. If we judge a trial to be at low risk of bias in all domains, we will consider it to be at low risk of bias overall. Otherwise, we will consider trials to be at high risk of bias (i.e. trials with unclear or high risk of bias for one or more domains). We will resolve any difference in opinion by discussion.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome, as part of the GRADE methodology.

Measures of treatment effect

We will analyse dichotomous data as risk ratios and continuous data as mean difference or standardised mean difference. We will ensure that higher scores for continuous outcomes have the same meaning for the particular outcome; we will also explain the direction of effect to the reader and report where the directions were reversed, if this was necessary.

We will undertake meta‐analyses only where this is meaningful, i.e. if the treatments, participants and the underlying clinical question are similar enough for pooling to make sense.

A common way that trialists indicate they have skewed data is by reporting medians and interquartile ranges. When we encounter this, we will note that the data are skewed and consider the implication of this. If the data are skewed, we will not perform a meta‐analysis, but will provide a narrative summary instead.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. drug A versus placebo and drug B versus placebo) must be entered into the same meta‐analysis, we will halve the control group to avoid double counting.

Unit of analysis issues

The unit of analysis will be individual participants undergoing pancreatoduodenectomy. We do not anticipate finding any cross‐over or cluster‐randomised trials for this comparison.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data as indicated (i.e. when a study is identified as abstract only). If we are unable to obtain the information from the investigators or study sponsors, we will impute the mean from the median (i.e. consider median as the mean) and the standard deviation from the standard error, interquartile range, or P values, according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will conduct a sensitivity analysis to assess the impact of including such studies. If we are unable to calculate the standard deviation from the standard error, interquartile range, or P values, we will impute standard deviation as the highest standard deviation in the remaining trials included in the outcome, fully aware that this method of imputation will decrease the weight of the studies in the meta‐analysis of mean difference, and shift the effect towards no effect for standardised mean difference.

Assessment of heterogeneity

We will describe the heterogeneity by using the Chi² test (Higgins 2011). A P value of less than 0.10 is considered to be significant heterogeneity. We will use the I² statistic to measure heterogeneity among the studies in each analysis (0% to 40%: might not be important; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity; 75% to 100%: considerable heterogeneity; Higgins 2003). If we identify substantial or considerable heterogeneity, we will explore it by prespecified subgroup analysis, and we will interpret summary effect measures with caution.

Assessment of reporting biases

If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible publication biases. We will use Egger's test to determine the statistical significance of the reporting bias (Egger 1997). We will consider a P value of less than 0.05 to be a statistically significant reporting bias.

Data synthesis

We will perform the meta‐analysis using Review Manager (Review Manager 2014). We will use a random‐effects model by default. For testing the robustness of our findings we will conduct a sensitivity analysis for primary outcomes, using the fixed‐effect model. In case of divergence between the two models, we will present both results; otherwise, we will present only results from the random‐effects model.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

• Pancreatoduodenectomy performed via laparotomy versus laparoscopy.

• Participants at high risk of POPF versus participants at low risk of POPF.

The following outcomes will be used in subgroup analyses.

• Postoperative pancreatic fistula.

• Postoperative mortality.

We will use the formal Chi² test for subgroup differences to test for subgroup interactions.

Sensitivity analysis

We will perform sensitivity analyses defined to assess the robustness of our conclusions. This will involve the following.

• Changing between fixed‐effect and random‐effects models.

• Changing between worst‐case and best‐case scenario analysis for missing data.

• Excluding studies in which the mean or standard deviation, or both, were imputed.

• Excluding studies that did not use International Study Group of Pancreatic Fistula (ISGPF) criteria (Bassi 2005; Bassi 2017).