Types of studies

We will include randomised controlled trials (RCTs) reported as full text, those published as abstract only and those with unpublished data.

Types of participants

We will include adults or children or both undergoing major upper gastrointestinal, liver and pancreatic surgery such as transhiatal oesophagectomy, gastrectomy (irrespective of whether a total or subtotal distal gastrectomy is performed), liver resection (irrespective of the number of segments resected and the aetiology), pancreatic resection (irrespective of whether a pancreaticoduodenectomy or a distal pancreatectomy is performed, and irrespective of whether the pylorus is preserved), pancreatic drainage procedures (for chronic pancreatitis) and open pancreaticojejunostomy or pancreaticogastrostomy for pseudocyst. We will exclude upper gastrointestinal, liver and pancreatic surgeries that are included in the British Association of Day Surgery Directory of Procedures (BADS 2012), including laparoscopic cholecystectomy or laparoscopic fundoplication, as patients are discharged on the same day when they have mobilised adequately.

Types of interventions

We will include trials comparing an enhanced recovery protocol with usual care, provided that the only difference between randomly assigned groups is the use of an enhanced recovery protocol. We will accept the definition proposed by Kehlet et al (Kehlet 1997), which requires inclusion of one or more of the following elements.

1. Preoperative information and teaching.

2. Decreased stress related to surgery.

3. Pain relief.

4. Exercise (early mobilisation).

5. Enteral nutrition.

6. Growth factors.

We will exclude trials comparing different enhanced recovery protocols. We will also exclude trials comparing laparoscopic and open surgeries, as the issues surrounding laparoscopic or open surgery are different for different procedures.

Types of outcome measures

Electronic searches

We will conduct a literature search to identify all published and unpublished randomised controlled trials.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

We will search the following electronic databases to identify potential studies.

1. Cochrane Central Register of Controlled Trials (CENTRAL) (Appendix 1).

2. MEDLINE (1966 to present) (Appendix 2).

3. EMBASE (1988 to present) (Appendix 3).

4. Science Citation Index (1982 to present) (Appendix 4).

We will also conduct a search of ClinicalTrials.gov (Appendix 5) and the World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (Appendix 6).

Searching other resources

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

We will search for errata or retractions from eligible trials on http://www.ncbi.nlm.nih.gov/pubmed and will report within the review the date this was done.

Selection of studies

Two review authors (trained research assistants or students or colleagues of K Gurusamy) will independently screen titles and abstracts for inclusion of all potential studies identified as a result of the search and will code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve.' We will retrieve full‐text study reports, and two review authors (research assistants or students or colleagues of K Gurusamy) will independently screen them, will identify studies for inclusion and will identify and record reasons for exclusion of ineligible studies. We will resolve disagreements through discussion or, if required, will consult a third person (K Gurusamy). We will identify and exclude duplicates and 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 record the selection process in sufficient detail to complete a PRISMA (Preferred Reporting Items for Systematic Reviews and Meta‐Analyses) flow diagram and a 'Characteristics of excluded studies' table.

Data extraction and management

We will use a standard data collection form for study characteristics and outcome data that has been piloted on at least one study in the review. Two review authors (research assistants or students or colleagues of K Gurusamy) will extract the following study characteristics from included studies.

1. Methods: study design, total duration of study and run‐in, number of study centres and locations, study settings, withdrawals, dates of study.

2. Participants: number (N), mean age, age range, gender, inclusion criteria, exclusion criteria.

3. Interventions: interventions, comparisons, concomitant interventions.

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

5. Notes: funding for trial, notable conflicts of interest of trial authors.

Two review authors (research assistants or students or colleagues of K Gurusamy) will independently extract outcome data from included studies. If outcomes were reported multiple times for the same time point, for example, if short‐term health‐related quality of life was reported at six weeks and at three months, the later time point (i.e. three months) will be chosen for data extraction. For time‐to‐event outcomes, we will extract data to calculate the natural logarithm of the hazard ratio and its standard error using the methods suggested by Parmar et al (Parmar 1998).

All randomly assigned participants will be included for medium‐ and long‐term outcomes (e.g. mortality, quality of life), and this will not be conditional upon short‐term outcomes (e.g. being alive at three months, having a low or high quality of life index at three months).

We will note in the 'Characteristics of included studies' table whether outcome data were reported in an unusable way. We will resolve disagreements by reaching consensus or by involving a third person (K Gurusamy). One review author (K Gurusamy) will copy data from the data collection form into the Review Manager file (Review Manager 2013). We will double‐check that data are entered correctly by comparing data in the study reports with data presented in the systematic review.

Assessment of risk of bias in included studies

Two review authors (research assistants or students or colleagues of K Gurusamy) will independently assess risk of bias for each study, using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Disagreements will be resolved by discussion or through involvement of a third assessor (K Gurusamy). We will assess risk of bias according to 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 bias.

We will grade each potential source of bias as high, low or unclear and will provide a quote from the study report together with a justification for our judgement in the 'Risk of bias' table. We will summarise risk of bias judgements across different studies for each of the domains listed. We will consider blinding separately for different key outcomes when necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be very different than for a patient‐reported pain scale). When information on risk of bias is related to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

When considering treatment effects, we will take into account the risk of bias for studies that contribute to those outcomes.

Measures of treatment effect

We will analyse dichotomous data as risk ratios and continuous data as mean differences when the outcome is reported or converted to the same units in all trials (e.g. hospital stay, time to return to work) or as standardised mean differences when different scales are used in measuring the outcome (e.g. quality of life). We will ensure that higher scores for continuous outcomes have the same meaning for the particular outcome, will explain the direction to the reader and will report when the directions were reversed if this was necessary. We will calculate rate ratios for outcomes such as adverse events and serious adverse events when it is possible for the same person to experience more than one adverse event (or serious adverse event). If the study authors have calculated the rate ratio of adverse events (or serious adverse events) for intervention versus control on the basis of Poisson regression, we will obtain the rate ratio by using the Poisson regression method in preference to the rate ratio calculated using the number of adverse events (or serious adverse events) reported during a specified period. We will calculate the hazard ratio for time‐to‐event outcomes such as long‐term mortality, long‐term recurrence and time to first adverse event (or serious adverse event).

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

Trialists commonly indicate when they have skewed data by reporting medians and interquartile ranges. When we encounter this, we will note that the data are skewed and will consider the implications of this.

When multiple trial arms are reported in a single trial, we will include only the relevant arms. When two comparisons (e.g. enhanced recovery protocol A vs standard care and enhanced recovery protocol B vs standard care) must be entered into the same meta‐analysis, we will halve the control group to avoid double counting. The alternative way of including such trials with multiple arms is to pool the results of enhanced recovery protocol A and enhanced recovery protocol B and compare them with standard care. We will perform a sensitivity analysis to determine whether results obtained using the two methods of dealing with multi‐arm trials lead to different conclusions.

Unit of analysis issues

The unit of analysis will be individual study participants undergoing major upper gastrointestinal, liver and pancreatic surgery. If cluster‐randomised trials are identified, we will obtain the effect estimate adjusted for the clustering effect. If this is not available, we will perform a sensitivity analysis by excluding the trial from the meta‐analysis, as the variance of the effect estimate unadjusted for cluster effect is less than the actual variance, which is adjusted for cluster effect, inappropriately giving more weight to the cluster RCT in the meta‐analysis.

Dealing with missing data

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

Assessment of heterogeneity

We will use the I² statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity as per the Cochrane Handbook for Systematic Reviews of Interventions (> 50% to 60%), we will explore this by performing prespecified subgroup analysis. 

Assessment of reporting biases

We will attempt to contact study authors to ask them to provide missing outcome data. When this is not possible, and the missing data are thought to introduce serious bias, the impact of including such studies in the overall assessment of results will be explored by a sensitivity analysis. 

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). A P value < 0.05 will be considered to show statistically significant reporting bias.

Data synthesis

We will perform analyses using RevMan 5.2 (Review Manager 2013).

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

1. Different surgeries (e.g. total or subtotal gastrectomy, distal gastrectomy, pancreaticoduodenectomy, distal pancreatectomy).

2. Different enhanced recovery protocols (according to the element that the enhanced recovery protocol is meant to address, for example, pain relief, nutrition).

3. Adults versus children.

4. Different methods of dealing with multi‐arm trials (please see Measures of treatment effect).

All primary outcomes will be used in the subgroup analysis.

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

Sensitivity analysis

We will perform sensitivity analysis as defined a priori to assess the robustness of our conclusions. This will involve:

1. excluding trials at unclear or high risk of bias (one of more of the risk of bias domains is classified as unclear or high);

2. excluding trials for which mean or standard deviation or both were imputed; and

3. excluding cluster RCTs for which adjusted effect estimates are not reported.