Primary outcomes

• All‐cause mortality.

• Serious adverse events. Serious adverse events correspond to Grade III or above of the Clavien‐Dindo classification, the only validated system for classifying postoperative complications (Dindo 2004). We will classify the following postoperative complications as serious adverse events: post‐intraoperative cholangiography acute pancreatitis; and bile duct injury during cholecystectomy, confirmed radiologically by intraoperative cholangiography, if diagnosed intraoperatively. Common bile duct injury suspected at postoperative follow‐up (at three months or six months) is to be confirmed by ERCP or magnetic resonance cholangiopancreatography. Classification of bile duct injury will be according to Strasberg and further stratified from type A to type E, which are subdivided into E1 to E5, according to the Bismuth classification system (Strasberg 1995). Other serious post‐operative complications such as acute cholangitis, bile leak, biliary strictures, intra‐abdominal abscess, secondary cirrhosis, haemorrhage requiring reoperation, and biloma will also be considered as serious adverse events.

• Health‐related quality of life: measured by any validated general or specific tool such as the 36‐item Short Form (SF‐36) (SF‐36 1994) and Gastrointestinal Quality of Life Index (GIQLI 1995).

We will analyse each primary outcome separately, including each component of serious adverse events.

Secondary outcomes

• Non‐serious adverse events: may include non‐serious local and systemic postoperative complications: wound infection (according to Surgical Site Infection Criteria ‐ Center for Disease Control and Prevention (Berríos‐Torres 2017), or incision haematoma. Systemic complications: pneumoperitoneum‐related (carbon dioxide embolism, vasovagal reflex, cardiac arrhythmias, hypercarbic acidosis), nausea or vomiting, diarrhoea, or lung atelectasis if they do not lead to hospitalisation or prolongation of hospitalisation.

• Pain: right upper abdomen, right shoulder, and incision pain (at trocar sites and subcostal incision), as provided by trial authors.

• Common bile duct stones:

• • if detected intraoperatively: we will consider intraoperative cholangiography as the diagnostic method. We are aware that this outcome is inherently biased, likely to occur more often in the control group;

  • if detected postoperatively: suspected by clinical signs and symptoms such as jaundice, right upper abdominal pain, back pain, nausea or vomiting, and confirmed by serum chemistry analysis (gamma‐glutamyltransferase greater than 37 U/L, alkaline phosphatases greater than 95 U/L, alanine aminotransferase greater than 40 U/L, aspartate aminotransferase greater than 40 U/L, total bilirubin greater than 1.2 mg/dL) plus image study calculi demonstration: ultrasound, magnetic resonance cholangiopancreatography, or ERCP. It is important to consider and, to differentiate, that after at least a two year symptom‐free interval following cholecystectomy, there is a probability of primary common bile duct stones (Saharia 1977).

We will analyse the outcomes separately, considering each time point. We will primarily base our conclusions at maximum follow‐up.

Allocation sequence generation

• Low risk of bias: the study authors performed sequence generation using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice were adequate if an independent person not otherwise involved in the study perform them.

• Unclear risk of bias: the study authors did not specify the method of sequence generation.

• High risk of bias: the sequence generation method was not random. We will only include such studies for assessment of harms.

Allocation concealment

• Low risk of bias: the participant allocations could not have been foreseen in advance of, or during, enrolment. A central and independent randomisation unit controlled allocation. The investigators were unaware of the allocation sequence (e.g. if the allocation sequence was hidden in sequentially numbered, opaque, and sealed envelopes).

• Unclear risk of bias: the study authors did not describe the method used to conceal the allocation so the intervention allocations may have been foreseen before, or during, enrolment.

• High risk of bias: it is likely that the investigators who assigned the participants knew the allocation sequence. We will only include such studies for assessment of harms.

Blinding of participants and personnel

• Low risk of bias: any of the following: no blinding or incomplete blinding, but the review authors judged that the outcome was not likely to be influenced by lack of blinding; or blinding of participants and key study personnel ensured, and it was unlikely that the blinding could have been broken.

• Unclear risk of bias: any of the following: insufficient information to permit judgement of 'low risk' or 'high risk;' or the trial did not address this outcome.

• High risk of bias: any of the following: no blinding or incomplete blinding, and the outcome was likely to be influenced by lack of blinding; or blinding of key study participants and personnel attempted, but likely that the blinding could have been broken, and the outcome was likely to be influenced by lack of blinding.

Blinding of outcome assessment

• Low risk of bias: any of the following: no blinding of outcome assessment, but the review authors judged that the outcome measurement was not likely to be influenced by lack of blinding; or blinding of outcome assessment ensured, and unlikely that the blinding could have been broken.

• Unclear risk of bias: any of the following: insufficient information to permit judgement of 'low risk' or 'high risk;' or the trial did not address this outcome.

• High risk of bias: any of the following: no blinding of outcome assessment, and the outcome measurement was likely to be influenced by lack of blinding; or blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement was likely to be influenced by lack of blinding.

Incomplete outcome data

• Low risk of bias: missing data were unlikely to make treatment effects depart from plausible values. The study used sufficient methods, such as multiple imputation, to handle missing data.

• Unclear risk of bias: there was insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias on the results.

• High risk of bias: the results were likely to be biased due to missing data.

Selective outcome reporting

• Low risk of bias: the trial reported the following predefined outcomes: mortality, serious adverse events, and surgical‐related morbidity. If the original trial protocol was available, the outcomes should have been those called for in that protocol. If the trial protocol was obtained from a trial registry (e.g. www.ClinicalTrials.gov), the outcomes sought should have been those enumerated in the original protocol if the trial protocol was registered before or at the time that the trial was begun. If the trial protocol was registered after the trial was begun, we will not consider those outcomes to be reliable.

• Unclear risk of bias: the study authors did not report all predefined outcomes fully, or it was unclear whether the study authors recorded data on these outcomes or not.

• High risk of bias: the study authors did not report one or more predefined outcomes.

For‐profit bias

• Low risk of bias: the trial appeared free of industry sponsorship or other type of for‐profit support that could manipulate the trial design, conductance, or trial results.

• Unclear risk of bias: the trial may or may not have been free of for‐profit bias as the trial did not provide any information on clinical trial support or sponsorship.

• High risk of bias: the trial was sponsored by industry or received another type of for‐profit support.

Other bias

• Low risk of bias: the trial appeared free of other factors that could put it at risk of bias.

• Unclear risk of bias: the trial may or may not have been free of other factors that could put it at risk of bias.

• High risk of bias: there were other factors in the trial that could put it at risk of bias.

Overall risk of bias

We will assess overall risk of bias in the trials as:

• low risk of bias: if all the bias domains described in the above paragraphs are classified as low risk of bias;

• high risk of bias: if one or more of the bias domains described in the above paragraphs are classified as 'unclear risk of bias' or 'high risk of bias.'

We will assess the domains 'Blinding of outcome assessment,' 'Incomplete outcome data,' and 'Selective outcome reporting' for each outcome. Thus, we will be able to assess the bias risk for each outcome in addition to each trial.

We will base our primary conclusions and our presentation in the 'Summary of findings' table on the results of our primary outcomes at low risk of bias.

We will resolve disagreements by discussion or by consulting a third review author (DM). We will have two assessors (Marcelo Linhares, Diego Kleinubing) and one adjudicator (Rachel Riera).

Dealing with missing data using sensitivity analysis

If trials report only per protocol analysis results, we will include missing data by considering participants as treatment failures or treatment successes by imputing them according to the following two scenarios:

• 'extreme case' analysis favouring the experimental intervention ('best‐worst' case scenario): none of the participants who dropped out from the experimental group experienced the outcome, but all the participants who dropped out from the control group experienced the outcome; including all randomised participants in the denominator.

• 'extreme case' analysis favouring the control ('worst‐best' case scenario): all participants who dropped out from the experimental group, but none of the participants who dropped out from the control group experienced the outcome; including all randomised participants in the denominator.

We will perform the two sensitivity scenario analyses only for our primary outcomes.

Meta‐analysis

We will perform the meta‐analyses using Review Manager 5 (RevMan 2014), and according to the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

We will present the results of dichotomous outcomes of individual trials as RR with 95% CI and the results of the continuous outcomes as MD with 95% CI. We will apply both fixed‐effect model (Demets 1987) and random‐effects model (DerSimonian 1986) meta‐analyses. If there are statistically significant discrepancies in the results (e.g. one giving a significant intervention effect and the other no significant intervention effect), we will report the more conservative point estimate analysis (Jakobsen 2014). The more conservative point estimate is the estimate closest to zero effect. If the two point estimates are equal, we will use the estimate with the widest CI as our main result of the two analyses. We will consider a P value of 0.025 or less, two‐tailed, as statistically significant if the required information size is reached due to our three primary outcomes at six‐months' follow‐up (Jakobsen 2014). We will use an eight‐step procedure to assess if the thresholds for significance are crossed (Jakobsen 2014). We will present heterogeneity using the I² statistic (Higgins 2002). We will present the results of the individual trials and meta‐analyses in the form of forest plots.

Where data are only available from one trial, we will use Fisher's exact test for dichotomous data (Fisher 1922) and Student's t‐test for continuous data (Student 1908) to present the results in a narrative way.

Trial Sequential Analysis

We will examine apparently significant beneficial and harmful intervention effects and neutral effects with Trial Sequential Analyses to evaluate if these apparent effects could be caused by random error (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010; Thorlund 2011; TSA 2011; Wetterslev 2017).

We will use Trial Sequential Analysis as cumulative meta‐analyses are at risk of producing random errors due to sparse data and repetitive testing of the accumulating data (Wetterslev 2008). To minimise random errors, we will calculate the required information size (i.e. the number of participants needed in a meta‐analysis to detect or reject a certain intervention effect) (Wetterslev 2008). The required information size calculation should also account for the diversity present in the meta‐analysis (Wetterslev 2008; Wetterslev 2009; Wetterslev 2017).

In our meta‐analysis, the diversity‐adjusted required information size for dichotomous outcomes will be based on the event proportion in the control group; assumption of an a priori relative risk reduction of 20% or the relative risk reduction observed in the included trials at low risk of bias; a risk of type I error of 2.5% due to three primary outcomes (Jakobsen 2014); a risk of type II error of 10%; and the observed diversity of the included trials in the meta‐analysis (Castellini 2016). We will also calculate and report the Trial Sequential Analysis‐adjusted CI (Thorlund 2011). The underlying assumption of Trial Sequential Analysis is that testing for significance may be performed each time a new trial is added to the meta‐analysis. We will add the trials according to the year of publication, and, if more than one trial has been published in a year, we will add trials alphabetically according to the last name of the first author.

On the basis of the diversity‐adjusted required information size, trial sequential monitoring boundaries will be constructed (Thorlund 2011). These boundaries will determine the statistical inference one may draw regarding the cumulative meta‐analysis that has not reached the required information size. If the cumulative Z‐curve crosses the trial sequential monitoring boundary for benefit or harm before the diversity‐adjusted required information size is reached, firm evidence may perhaps be established and further trials may turn out to be superfluous. In contrast, if the boundary is not surpassed, it is most probably necessary to continue doing trials to detect or reject a certain intervention effect. That can be determined by assessing if the cumulative Z‐curve crosses the trial sequential monitoring boundaries for futility.

A more detailed description of Trial Sequential Analysis can be found at www.ctu.dk/tsa/ (Thorlund 2011).

'Summary of findings' tables

We will assess confidence in the evidence using GRADE criteria (Atkins 2004) and using GRADEpro software (GRADEpro 2008). We will assess all our review primary and secondary outcomes using the five factors referring to limitations in the study design and implementation of included studies that suggest the quality of the evidence: risk of bias; indirectness of evidence (population, intervention, control, outcomes); unexplained heterogeneity or inconsistency of results (including problems with subgroup analyses); imprecision of results (wide CIs and as evaluated with our Trial Sequential Analyses) (Jakobsen 2014); and a high probability of publication bias. We will define the levels of evidence as 'high,' 'moderate,' 'low,' or 'very low'. We will follow the recommendations of Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). These grades are defined as follows.

• High certainty: this research provides a very good indication of the likely effect; the likelihood that the effect will be substantially different is low.

• Moderate certainty: this research provides a good indication of the likely effect; the likelihood that the effect will be substantially different is moderate.

• Low certainty: this research provides some indication of the likely effect; however, the likelihood that it will be substantially different is high.

• Very low certainty: this research does not provide a reliable indication of the likely effect; the likelihood that the effect will be substantially different is very high.