Types of studies

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 We will include studies reported as full text, studies published as abstract only, and unpublished data.

Types of participants

We will include adults undergoing transhiatal oesophagectomy for oesophageal cancer (squamous cell carcinoma or adenocarcinoma). While we will exclude people undergoing oesophagectomy for oesophageal strictures not amenable for endoscopic treatment whenever possible, we will include trials in which no separate outcome data for people undergoing oesophagectomy for oesophageal cancers are available provided that oesophagectomy for other causes is less than 10% of participants included in the trial.

Types of interventions

We will include trials comparing laparoscopic transhiatal oesophagectomy with open transhiatal oesophagectomy provided that the only difference between the randomised groups is the use of laparoscopic or open method of access to the abdomen. We will exclude trials comparing thoracoscopic oesophagectomy with open transthoracic oesophagectomy or trials comparing minimally invasive approaches with open approach for performing McKeown's procedure.

Types of outcome measures

Electronic searches

We will conduct a literature search to identify all published and unpublished RCTs. The literature search will identify potential studies in all languages. We will translate any 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:

1. the Cochrane Central Register of Controlled Trials (CENTRAL; to present) (Appendix 1);

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

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

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

We will also conduct a search of ClinicalTrials.gov (ClinicalTrials.gov; Appendix 5) and the World Health Organization ‐ International Clinical Trials Registry Platform (WHO ICTRP; www.who.int/ictrp/en/; 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 We will contact authors of identified trials and ask them to identify other published and unpublished studies.

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 within the review.

Selection of studies

Two review authors (trained research assistants or students or colleagues of K Gurusamy) will independently screen titles and abstracts for inclusion all the potential studies we identify as a result of the search and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports and two review authors (research assistants or students or colleagues of K Gurusamy) 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 disagreements through discussion or, if required, we will consult third person (K Gurusamy). 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 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 study characteristics from included studies and detail them in a 'Characteristics of included studies' table. We will extract the following study characteristics:

1. methods: study design, total duration study and run in, number of study centres and location, study setting, withdrawals, date of study;

2. participants: number, mean age, age range, gender, tumour stage, tumour location, histological subtype, performance status, American Society of Anesthesiologists (ASA) status (ASA 2014), inclusion criteria, exclusion criteria;

3. interventions: intervention, comparison, 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 are reported multiple times for the same time point (e.g. short‐term health‐related quality of life is reported at six weeks and three months), we will chose the later time point (i.e. three months) for data extraction. For time‐to‐event outcomes, we will extract data to calculate the natural logarithm of the hazard ratio (HR) and its standard error using the methods suggested by Parmar et al. (Parmar 1998).

We will include all randomised participants for medium‐term and long‐term outcomes (e.g. mortality or quality of life) and this will not be conditional upon the short‐term outcomes (e.g. being alive at three months or having a low or high quality‐of‐life index at three months).

We will note in the 'Characteristics of included studies' table if outcome data are reported in an unusable way. We will resolve disagreements by consensus or by involving a third person (K Gurusamy). One review author (K Gurusamy) will copy across the data from the data collection form into the Review Manager 5 (RevMan 2012). 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.

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). We will resolve any disagreements by discussion or by involving a third person (K Gurusamy). We will assess the 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 risk of bias and provide a quote from the study report together with a justification for our judgement in the 'Risk of bias' table. We will summarise the risk of bias judgements across different 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 from a participant‐reported pain scale). Where information on risk of bias relates 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 the studies that contribute to that outcome.

Measures of treatment effect

We will analyse dichotomous data as risk ratio (RR) and continuous data as mean difference (MD) when the outcome is reported or converted to the same units in all the trials (e.g. hospital stay, time to return to work) or standardised mean difference (SMD) when different scales are used for 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, explain the direction to the reader, and report where the directions were reversed if this was necessary. We will calculate the rate ratio (RaR) for outcomes such as adverse events and serious adverse events, where it is possible for the same person to develop more than one adverse event (or serious adverse event). If the authors have calculated the RaR of adverse events (or serious adverse events) in the intervention versus control based on Poisson regression, we will obtain the RaR by the Poisson regression method in preference to RaR calculated based on the number of adverse events (or serious adverse events) during a certain period. We will calculate the HR 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 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 when 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.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. laparoscopic oesophagectomy method 1 versus open oesophagectomy and laparoscopic oesophagectomy method 2 versus open oesophagectomy) 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 the laparoscopic oesophagectomy method 1 and laparoscopic oesophagectomy method 2 and compare it with open oesophagectomy. We will perform a sensitivity analysis to determine if the results of the two methods of dealing with multi‐arm trials lead to different conclusions

Unit of analysis issues

The unit of analysis will be individual participants undergoing transhiatal oesophagectomy. We do not anticipate finding any cluster‐randomised trials for this comparison but if we do identify cluster‐randomised trials, we will obtain the effect estimate adjusted for the clustering effect. If this is not available, we will perform a sensitivity analysis excluding the trial from the meta‐analysis as the variance of the effect estimate unadjusted for cluster effect is less than the actual variance that is adjusted for cluster‐effect giving inappropriately more weight to the cluster RCT in the meta‐analysis.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. 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 mean from median (i.e. consider median as the mean) and standard deviation from standard error, interquartile range, or P values according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), but assess the impact of including such studies as indicated in a sensitivity analysis. If we are unable to calculate the standard deviation from 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 MD and shift the effect towards no effect for SMD.

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 Cochrane Handbook for Systematic Reviews of Interventions (greater than 50% to 60%; Higgins 2011), we will explore it by pre‐specified subgroup analysis. 

Assessment of reporting biases

We will attempt to contact study authors asking them to provide missing outcome data. Where this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results using 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). We will consider a P value less than 0.05 statistically significant reporting bias.

Data synthesis

We will perform analyses using Review Manager 5 (RevMan 2012). We will calculate the 95% confidence intervals for the treatment effect.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses:

1. different histological types (squamous cell carcinoma and adenocarcinoma);

2. different cancer stages;

3. different locations (upper third, middle third, lower third);

4. people with different anaesthetic risk (ASA I (a healthy person) or II (a person with mild systemic disease) versus ASA III or more (a person with severe systemic disease or worse);

5. different body mass index (BMI) (health weight (BMI 18.5 to 25) versus overweight or obese (BMI 25 or greater).

We will use all the primary outcomes in subgroup analyses.

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

Sensitivity analysis

We will perform sensitivity analysis 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 (other than blinding of surgeon) classified as unclear or high);

2. excluding trials in which either mean or standard deviation, or both are imputed;

3. excluding cluster RCTs in which the adjusted effect estimates are not reported;

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