Types of studies

As opposed to previously published reviews which included observational studies (Xiong 2013; Zong 2011), we included only randomised controlled trials (RCTs), with no restrictions on language. We included studies reported as full text, those published as abstract only, and unpublished data. We did not apply any restriction with respect to blinding status because blinding for surgeons and participants, which prevents detection and performance biases, is typically difficult in the case of surgical RCTs, although the degree of such biases is unknown (Probst 2016); however, the blinding status of assessors should be clarified (Speich 2017). We planned to include cluster‐RCTs when available. Clinical studies with a cross‐over design are impossible for the interventions in question.

Types of participants

We included adults aged 18 years and older with a diagnosis of gastric cancer who were undergoing robotic, laparoscopic, laparoscopy‐assisted, or open distal gastrectomy.

Types of interventions

We included studies comparing Roux‐en‐Y with Billroth‐I reconstruction. When a primary anastomosis was constructed, it could either be performed as an intracorporeal procedure (stapled or hand‐sewn) or an extracorporeal procedure (stapled or hand‐sewn). We did not specify types of stapling devices: we included both linear and circular stapling.

Types of outcome measures

We assessed the following outcomes. Reporting of the outcomes listed here was not considered as inclusion criteria for the review.

Electronic searches

We conducted a literature search to identify all published and unpublished RCTs. We placed no restrictions on the language of publication when searching the electronic databases. We translated non‐English language papers and assessed them thoroughly for potential inclusion in the review, as necessary.

We searched the following electronic databases up to 4 May 2021.

1. The Cochrane Library databases, and the Cochrane Central Register of Controlled Trials (CENTRAL; to 2020 Issue 4; Appendix 2) (via Ovid).

2. MEDLINE (1946 to 4 May 2021; Appendix 3) (via Ovid).

3. Embase (1974 to 4 May 2021; Appendix 4) (via Ovid).

We also searched PubMed (www.ncbi.nlm.nih.gov/pubmed) before completing the review to obtain records that were not yet indexed in Ovid MEDLINE.

Searching other resources

We checked the reference lists of all primary studies for additional references that our original electronic searches may have missed. We searched clinical trials registers for unpublished data and planned to send a comprehensive list of relevant articles to the first author of reports of the included studies to enquire as to any further relevant studies (Higgins 2021). We also contacted manufacturers and experts in the field to ask if they knew of any ongoing and unpublished trials. We searched for errata or retractions from eligible studies on PubMed (www.ncbi.nlm.nih.gov/pubmed) and reported the date this was done in the review. We performed a citation search in the Web of Science to obtain articles citing the included studies.

We searched the following registers and grey literature sources up to 4 May 2021.

Selection of studies

Two review authors (DN and RG) independently screened the titles and abstracts of all studies identified by our search, coding them as 'retrieve' (eligible, potentially eligible, or unclear) or 'do not retrieve'. We retrieved the full text of study reports or publications, and two review authors (DN and RG) independently screened the full text, identified studies for inclusion, and recorded reasons for exclusion of ineligible studies. Any disagreements were resolved through discussion or by consulting a third review author (NW) when necessary. We identified and excluded duplicates and collated multiple reports of the same study so that each study, rather than each report, was the unit of interest in the review. We recorded the selection process in sufficient detail to complete a PRISMA flow diagram and tabulated characteristics of excluded studies (Liberati 2009).

Data extraction and management

To determine study characteristics and outcome data, we used a standard data collection form that had been piloted on at least one study in the review. Two review authors (DN and RG) independently extracted the following study characteristics from included studies.

1. Methods: study design, number of study centres and location, study setting, withdrawals, date of study.

2. Participants: number, mean age, age range, gender, diagnostic criteria (for anastomotic leakage, bile reflux, and health‐related quality of life), inclusion and exclusion criteria.

3. Interventions: intervention, comparison.

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

5. Notes: funding for study, notable conflicts of authors participating in the study.

Two review authors (DN and RG) independently extracted outcome data from the included studies. We presented the characteristics of included studies in the ‘ Characteristics of included studies ’ tables, as well as whether data were reported in an unusable way. Any disagreements were resolved through discussion or by involving a third review author (NW) when necessary. One review author (DN) copied the data from the data collection form into the Review Manager 5 file (Review Manager 2020). We double‐checked that data had been entered correctly by comparing the study reports with the presentation of data in the review. A second review author (RG) spot‐checked study characteristics for accuracy against the study report.

Assessment of risk of bias in included studies

Two review authors (DN and RG) independently assessed the risk of bias of each study, according to the criteria in Table 8.5.d of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Any disagreements were resolved by discussion or by involving a third review author (NW) when necessary. We assessed the risk of bias based on the following domains.

1. Random sequence generation.

2. Allocation concealment.

3. Blinding of participants and personnel.

4. Blinding of outcome assessment.

5. Incomplete outcome data.

6. Selective outcome reporting.

7. Other potential bias (i.e. specific study design, deceptive study, co‐intervention, blinding of data assessors, baseline imbalance in participant characteristics, perioperative timing of randomisation, and the influence of funders).

We judged each potential source of bias as low, high, or unclear, and provided a quote from the study report and justification for our judgement in the risk of bias table.

We summarised the risk of bias judgements across studies for each of the domains listed. We considered 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 participant‐reported health‐related quality of life scale). Where information on risk of bias related to unpublished data or correspondence with a trialist, we noted this in the risk of bias table.

We took into account the risk of bias for studies that contributed to a given outcome as part of the GRADE methodology when considering treatment effects.

Measures of treatment effect

We analysed dichotomous data (incidence of anastomotic leakage, incidence of bile reflux, and postoperative morbidity) as a risk ratio (RR), and continuous data (health‐related quality of life, loss of body weight, and length of hospital stay) as a mean difference (MD) or standardised mean difference (SMD), using a 95% confidence interval (CI) in both cases. We ensured that higher scores for continuous outcomes had the same meaning for a particular outcome; explained the direction to the reader; and reported where the directions were reversed if this was necessary.

We deemed health‐related quality of life scores to be continuous (not arbitrarily categorised) and articulated them as SMDs with 95% CIs following the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021). We delineated a positive SMD as showing better effects for quality of life.

We undertook meta‐analyses only where this was meaningful, that is if the treatments, participants, and the underlying clinical question were similar enough for pooling to make sense. Considering substantial heterogeneity of surgical outcomes, we used the inverse‐variance random‐effects model unless the events were sparse.

Length of hospital stay is known to be skewed data in most cases. Although some studies ignored the skewness of data and reported mean and standard deviation (SD) for length of hospital stay, trials reporting medians and interquartile ranges (IQRs) only indicated the data were most likely to be skewed (Altman 1996). For studies that did not report mean and SD but did report median and IQRs, we assumed the median was similar to the mean, and IQRs were approximately 1.35 SDs (Higgins 2021). When median and range were reported, we calculated the mean and SD from the median, range, and sample size (Hozo 2005). We excluded these studies in a sensitivity analysis.

Unit of analysis issues

We planned to include cluster‐RCTs in the analysis along with individually randomised trials. We planned to adjust the sample sizes of cluster‐RCTs using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021), with an estimate of the intracluster correlation coefficient (ICC) derived from the trial if possible, or from a similar trial or a study of a similar population. If we used ICCs from other sources, we would report this and conduct a sensitivity analysis to investigate the effect of variation in the ICC. If we identified both cluster‐RCTs and individually randomised trials, we would synthesise the relevant information. We considered it reasonable to combine the results from both if there was little heterogeneity amongst the study designs, and interaction between the effect of intervention and the choice of randomisation unit was considered to be unlikely.

If we included multiple‐arm studies (e.g. comparison between Roux‐en‐Y, Billroth‐I and ‐II), we formed a pair‐wise comparison between Roux‐en‐Y and Billroth‐I reconstruction in the meta‐analysis, and excluded the other arms.

Dealing with missing data

We contacted investigators or study sponsors to verify key study characteristics and to obtain missing numerical data pertaining to outcomes as indicated (e.g. when a study was identified as abstract only). If we were unable to obtain information from investigators or study sponsors, we imputed the mean from the median (i.e. consider median as the mean) and the SD from the standard error, interquartile range, or P values, based on the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). When only the median and range were reported, we imputed the mean and the SD calculated from the median, range, and sample size (Hozo 2005). We assessed the impact of including such studies in a sensitivity analysis and indicated our results. When we were unable to calculate the SD from any numerical data including standard error, IQR, range, or P values, we imputed SD as the highest SD in the remaining studies included in the outcome, as it appears safe to borrow SDs from other studies (Furukawa 2006; Higgins 2021), being mindful of the fact that this method of imputation decreases the weight of the studies in the meta‐analysis of MD and shifts the effect towards no effect for SMD.

Assessment of heterogeneity

We used the I² statistic to measure heterogeneity amongst studies in each analysis (Higgins 2003); we considered that an I² of 30% to 60% may represent moderate heterogeneity, and that an I² greater than 60% may represent substantial heterogeneity (Higgins 2021). Furthermore, we explored heterogeneity by prespecified subgroup analyses (Higgins 2021), regardless of the measurement of I² statistics. We additionally assessed heterogeneity by evaluating whether there was good overlap of CIs by visual inspection of the forest plots.

Assessment of reporting biases

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

Data synthesis

We performed meta‐analyses based on the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions using Review Manager 5 (Higgins 2021; Review Manager 2020). We used a random‐effects model for analysis as we considered that the different studies estimated different, yet related intervention effects (DerSimonian 1986), especially pertaining to surgical outcomes.

Subgroup analysis and investigation of heterogeneity

We planned to carry out the following subgroup analyses.

1. Open resection versus laparoscopic resection versus others.

2. Early clinical‐stage gastric cancer (stage I) versus others according to the 15th edition of Japanese Classification of Gastric Carcinoma (JGCA 2017b).

We chose two characteristics for subgroup analyses: surgical approach and clinical stage. The rationale for the choice of characteristics was as follows: i) difference of surgical approach may affect the outcomes (Best 2016; Vinuela 2012); and ii) the difference of clinical stage alters the extent of lymph node dissection (JGCA 2017a), which may affect the outcomes.

If the study included laparoscopic and laparoscopy‐assisted cases between 0% and 30%, 31% and 70%, 71% and 100%, and an unknown proportion, we classified them as 'open (laparotomy) study', 'mixed study', 'laparoscopic study', and 'unknown approach study', respectively. If the study included stage I cases between 0% and 30%, 31% and 70%, 71% and 100%, and an unknown proportion, we classified them as 'advanced stage study', 'mixed study', 'early‐stage study', and 'unknown stage study', respectively.

We planned to use the following outcomes in subgroup analyses. To avoid multiplicity issues, we focused on a total of three outcomes that included the two primary outcomes and one of the secondary outcomes.

1. Health‐related quality of life after surgery (12 months postoperatively).

2. Loss of body weight (6 to 24 months postoperatively).

3. Incidence of anastomotic leakage (within 30 days postoperatively).

We used the formal statistical test for subgroup differences to test for subgroup interactions as described in Section 9.6.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021).

Sensitivity analysis

We performed an a priori sensitivity analysis to assess the robustness of our conclusions that involved exclusion of studies with high risk of bias in random sequence generation, studies with high risk of bias in allocation concealment, and studies with high risk of attrition bias. We performed additional sensitivity analyses by excluding studies that contained stage IV participants for the outcomes of health‐related quality of life and loss of body weight. We also performed additional sensitivity analyses by excluding studies that reported only median and range in length of hospital stay; excluding studies with unclear usage of the Clavien‐Dindo classification in overall morbidity; and using a fixed‐effect model for the outcome with sparse events (anastomotic leakage).

Summary of findings and assessment of the certainty of the evidence

We created a summary of findings table for the comparison Roux‐en‐Y versus Billroth‐I reconstruction with the following outcomes.

1. Health‐related quality of life (at the time point closest to 12 months postoperatively).

2. Incidence of anastomotic leakage (within 30 days postoperatively).

3. Loss of body weight (6 to 24 months after surgery).

4. Incidence of bile reflux (at time point closest to 12 months postoperatively).

5. Length of hospital stay (in days).

6. Postoperative morbidity (within 30 days after surgery).

We used the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the quality of the body of evidence based on studies that contributed data to the meta‐analyses for each outcome, classifying it as high, moderate, low, or very low. We used the methods and recommendations described in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions, employing GRADEpro GDT software (GRADEpro GDT; Higgins 2011). Two review authors (DN, NH) independently assessed the certainty of the evidence. We justified all decisions to downgrade or upgrade the certainty of evidence in the footnotes, providing comments to aid the reader's understanding of the review where necessary. We considered whether there was additional outcome information that was not incorporated into the meta‐analyses, noted this in the comments, and stated if it supported or contradicted the information obtained from the meta‐analyses.