Endoscopic versus surgical palliation for malignant distal bile duct obstruction
Abstract
This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:
To assess the benefits and harms of endoscopic versus surgical palliation for malignant distal bile duct obstruction.
Background
Malignant biliary obstruction is a frequent complication in people with advanced tumour diseases; the most commonly met complication is due to carcinoma of the head of the pancreas. Less common causes for malignant biliary obstruction include carcinoma of the ampulla of Vater, bile duct, and duodenum. Pancreatic tumours are the seventh most common cause for cancer‐related death in the western world (Ferlay 2013). Worldwide, there were 338,000 people newly diagnosed in 2012 (2% of the total), and in Europe that figure was 104,000 (Ferlay 2013). Up to 70% of them have some degree of biliary obstruction at the time of their initial diagnosis (Kruse 2010). At one year, the survival rate of pancreatic cancer in the UK was reported to be 20.2% (Cancer Research UK 2014) and biliary obstruction predicts decreased survival times (Afshar 2014).
The best potential cure for malignant biliary obstruction is complete surgical resection (Ahrendt 2001; Lazaridis 2005). Unfortunately, majority of people with advanced tumours are not good candidates for such curative therapy and may benefit only from palliative therapy (Sarr 1982; Gudjonsson 1987). Median survival of such people undergoing palliative therapy is higher than in people without biliary drainage (Farley 1995; Chang 1998; Berr 2004).
The aims of palliation in these people are to restore biliary flow to relieve the obstructive cholestasis and its associated symptoms such as pruritus, cholangitis, and pain; to avoid liver failure due to progressive biliary obstruction; and to improve quality of life and cost‐effectiveness, and reduce procedure‐related complications and hospital stays (Chahal 2006).
Description of the condition
Clinical manifestations of malignant distal bile duct obstruction are obstructive jaundice, pruritus, malabsorption, cholangitis, liver, and renal dysfunction. Prolonged bile duct obstruction usually results in malabsorption and consequent progressive malnutrition, recurrent biliary infection (cholangitis), and hepatic dysfunction. Therefore, the majority of unresectable cancers with distal bile duct obstruction require relief of jaundice and other symptoms. Relief of obstructive jaundice improves nutritional status and quality of life. Biliary drainage can be achieved non‐surgically by placement of a biliary stent (endoscopic or percutaneous) or surgically by performing a biliary bypass.
Description of the intervention
Endoscopic intervention
Endoscopic intervention involves the insertion of endobiliary prosthesis using a therapeutic side viewing endoscope under fluoroscopic guidance (Scott 2009). The procedure is called 'endoscopic retrograde cholangiopancreatography,' and this can be performed under sedation or general anaesthesia. Endoscopic biliary drainage is widely performed using plastic (Teflon and polyethylene) stents.
Another type of stent is the self‐expandable metallic stents. Self‐expandable metallic stents have been shown to be better than plastic stents for palliation. One Cochrane Review evaluated nine randomised clinical trials that compared the stent materials. This showed a risk ratio for recurrent biliary obstruction of 0.48, favouring metal over plastic stents (Moss 2006).
Surgical palliation
Biliary enteric bypass includes cholecystojejunostomy, choledochojejunostomy, or choledochoduodenostomy. Palliative surgery is either a single bypass for bile duct obstruction or a double bypass for bile duct and gastric outlet obstruction. The most commonly performed biliary bypass technique is a choledochojejunostomy with either a side‐to‐side or an end‐to‐side anastomosis to the jejunum.
How the intervention might work
Biliary drainage increases quality of life and can be achieved non‐surgically by placement of a biliary stent (endoscopic or percutaneous), or surgically by performing a biliary bypass.
Sarr 1982 reported that surgical biliary bypass was associated with longer survival and a better quality of life in people with malignant bile duct obstruction. Later, Ballinger 1994 observed that biliary stent insertion provided complete relief of jaundice and other symptoms including pruritus, dyspeptic symptoms, and loss of appetite. Currently, palliation of malignant bile duct obstruction is achieved by surgical bypass, biliary endoprosthesis insertion via endoscopy, percutaneous transhepatic approach, or a combined procedure.
In the past, surgical biliary drainage was generally preferred (Watanapa 1992). However, the success rate of cholecystojejunostomy to relieve obstructive jaundice was lower than that for choledochojejunostomy. According to Sarfeh 1988, which is the only randomised clinical trial comparing open cholecystojejunostomy and choledochojenunostomy; cholecystojejunostomy is technically more difficult but preferred over choledochojenunostomy due to the lower rate of recurrent jaundice and cholangitis, and a better patency of the bypass. Short‐term morbidity, mortality, and length of hospital stay were higher in people who underwent cholecystoenterostomy compared to choledochoenterostomy.
Some observational studies have reported that in the subgroup of unresectable ampullary carcinomas, surgical palliation provides better long‐term results than endoscopic palliation (Nieveen van Dijkum 2003, Nieveen van Dijkum 2005). They often require double bypass for biliary and gastric outlet obstruction (Nuzzo 2004).
In contrast, several randomised clinical trials have shown advantages of endoscopic stenting over surgical bypass, although 'long‐term survivors' could clearly benefit from palliative surgery by precluding the need for stent exchanges necessitated by stent clogging (Shepard 1988; Andersen 1989; Smith 1994). Benefits of endoscopic stent insertion include shorter length of hospital stay, and lower procedure‐related morbidity and mortality.
Complications of stent placement include the short‐term complications related to endoscopic retrograde cholangiopancreatography such as bleeding, pancreatitis, cholangitis, and perforation. Recurrent episodes of jaundice and cholangitis caused by stent occlusion require repeated hospital admission and is a drawback of endoscopic palliation. There are also delayed complications related to stent placement such as stent occlusion (up to 40%), recurrent cholangitis, stent migration, and stent fracture. Another disadvantage of stent treatment is the potential for duodenal obstruction caused by tumour growth. Plastic stents are associated with complications such as migration and occlusion. In comparison with plastic stents, self‐expandable metallic stents has been shown to have a longer patency than that of plastic stents, but they cannot be removed after placement (Kaassis 2003).
Why it is important to do this review
Evidence from randomised clinical trials on endoscopic versus surgical palliation for malignant distal bile duct obstruction is inconsistent, with a paucity of well‐conducted systematic reviews.
Smith 1994 reported a higher procedure‐related mortality rate after bypass compared with stenting, while one meta‐analysis concluded that more treatment sessions were required after stent placement than after surgery (Taylor 2000). A 2006 review concluded that surgical treatment of biliary obstruction in unresectable pancreatic cancer is associated with higher early morbidity, longer hospital stay, and probably higher initial mortality rate, with better long‐term results. The authors also concluded that endoscopic treatment was associated with a lower initial mortality and morbidity, but more frequently led to late biliary complications and re‐interventions due to clotting of the stent, infection, and gastric outlet obstruction (Gouma 2006).
One meta‐analysis found no difference in procedural success, with observed better outcomes for endoscopy therapy in relation to complication‐related mortality, and overall 30 day‐mortality (Alves de Lima 2015). However, this meta‐analysis did not follow Cochrane systematic review standards. One of the limitations was inclusion of cohort studies in its meta‐analysis and a lack of a predefined protocol.
Economic issues must be considered, and metallic stents, due to their high cost, should probably be reserved for people who might really benefit from the intervention (Cotton 1992). Therefore, prediction of survival becomes a critical issue. Biliary self‐expanding metal stents are placed if expected survival is more than six months, whereas plastic stents are used if expected survival is less than six months(Srikureja 2005). As survival is related to a long‐term quality of life (Crippa 2008), the we believe it is worthwhile to systematically investigate the potential benefits and harms of endoscopic versus surgical palliation for malignant distal bile duct obstruction.
Objectives
To assess the benefits and harms of endoscopic versus surgical palliation for malignant distal bile duct obstruction.
Methods
Criteria for considering studies for this review
Types of studies
Randomised clinical trials, irrespective of blinding, publication status, country of origin, and language.
If, during the selection of trials, we identify observational studies (i.e. quasi‐randomised studies, cohort studies, or patient reports) that report adverse events caused by or associated with the interventions in our review, we will include these studies for a review of the adverse events. We will not specifically search for observational studies, which is a known limitation of our systematic review.
Types of participants
Adults (aged 18 years or over) who were diagnosed with distal bile duct obstruction due to periampullary tumours who are not qualified for other radical treatment procedures.
We will exclude from this review people with jaundice related to intrahepatic cholestasis or obstruction.
Types of interventions
We will compare endoscopic intervention versus surgical bypass. Certain anaesthesiological, antibiotic, and perioperative procedures may be connected to the interventions. We will allow such differences as being parts of the two approaches.
Endoscopic intervention
Endoscopic intervention involves the insertion of an endobiliary prosthesis using a therapeutic side‐viewing endoscope under fluoroscopic guidance (Scott 2009). The procedure is called 'endoscopic retrograde cholangiopancreatography,' and this can be performed under sedation or general anaesthesia. Endoscopic biliary drainage is widely performed using plastic (Teflon and polyethylene) stents. Another type of stent is the self‐expandable metallic stent.
Surgical bypass
Surgical bypass includes cholecystojejunostomy, choledochojejunostomy, or choledochoduodenostomy. The palliative surgery is either a single bypass for bile duct obstruction or a double bypass for bile duct and gastric outlet obstruction. The most commonly performed biliary bypass technique is a choledochojejunostomy with either a side‐to‐side or an end‐to‐side anastomosis to the jejunum. These procedures are usually performed under general anaesthesia.
We do not expect cointerventions; however, if such trials are identified, we will consider their inclusion.
Types of outcome measures
Primary outcomes
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All‐cause mortality at 30 days and maximal follow‐up.
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Serious adverse events. We will use the International Conference on Harmonisation Guidelines for Good Clinical Practice's (ICH‐GCP 1997) definition of a serious adverse event, that is, any untoward medical occurrence that results in death, is life threatening, requires hospitalisation or prolongation of existing hospitalisation, results in persistent or significant disability or incapacity, or is a congenital anomaly or birth defect. We will consider all other adverse events as non‐serious (see below).
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Health‐related quality of life as described by the authors.
Secondary outcomes
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Technical failure of biliary drainage.
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Recurrent cholangitis or jaundice or both.
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Mortality due to procedural complications.
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Complications (e.g. gastric outlet obstruction).
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Need for repeat procedures.
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Non‐serious adverse events.
Search methods for identification of studies
Electronic searches
We will search The Cochrane Hepato‐Biliary Group Controlled Trials Register (Gluud 2017), Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library, MEDLINE Ovid, Embase Ovid, LILACS (Bireme), Science Citation Index Expanded (Web of Science), and Conference Proceedings Citation Index ‐ Science (Web of Science) (Royle 2003). We will apply no language limitations. Preliminary search strategies with the expected time spans of the searches are provided in Appendix 1.
We do not have immediate access to Chinese, Russian, and Japanese databases. However, we hope that at the review stage, we may be able to retrieve search results from these databases through the Cochrane Hepato‐Biliary Group Information Specialist.
Searching other resources
We will contact experts and main manufacturers of endoscopic stents to ask for unpublished randomised trials. We will identify additional trials by handsearching the reference lists of included trials and systematic reviews, meta‐analyses, and health‐technology assessment reports.
We will search online trial registries such as ClinicalTrial.gov (clinicaltrials.gov/), European Medicines Agency (EMA) (www.ema.europa.eu/ema/), World Health Organization International Clinical Trial Registry Platform (www.who.int/ictrp), the Food and Drug Administration (FDA) (www.fda.gov), and medical device company sources for ongoing or unpublished trials.
Data collection and analysis
We will summarise data following the recommendations of Cochrane (Higgins 2011a) and the Cochrane Hepato‐Biliary Group Module (Gluud 2017). We will collect and utilise the most detailed numerical data that might facilitate similar analyses of included studies. We will perform the analyses using Review Manager 5 (RevMan 2014).
Selection of studies
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Level 1 screening: two review authors (LLL and II) will independently review titles and abstracts of the studies identified through the electronic databases, and in parallel, they will determine the study eligibility according to the inclusion and exclusion criteria, described in the Criteria for considering studies for this review section. If there is disagreement about study relevance, they will reach consensus with a third review author (SKC).
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Level 2 screening: two review authors (LLL and II) will independently obtain and review the full‐text publications selected at level 1, and in parallel, they will determine the study eligibility according to the inclusion and exclusion criteria described in the Criteria for considering studies for this review section. If there is disagreement about study relevance, they will reach consensus with a third review author (SKC).
The review authors will include an adapted PRISMA flow diagram of study selection for the review (Moher 2009).
Data extraction and management
For studies that fulfil the inclusion criteria, two review authors (LLL and II) will independently extract relevant population, intervention, characteristics, and risk of bias components using standard data extraction templates. If we identify multiple publications, we will extract the most comprehensive data for analysis of benefits and harms from all publications related to a randomised clinical trial. We will collect only data on harms from all the remaining and relevant publications. We will present the reported data on harms in a tabular or narrative way under the 'Results' section of the review, but we will not mix these data with the data on harms obtained from the included randomised clinical trials. We will discuss the limitations ensued from the collected data on harm from studies not related to the randomised clinical trials in the 'Discussion' section. We will be very cautious when extracting data from identified abstracts, posters, and grey literature as often these publications are unfinished reports. We will resolve disagreements by discussion, or, when required, by consulting other review authors (KCJ and SKC).
We will extract the following information for each eligible trial:
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study design;
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study population: total number enrolled, characteristics, age, comorbidities, previous treatment;
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sample size calculation performed or not;
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sample size reached or not;
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type of experimental intervention and control;
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outcome data, related to primary and secondary outcomes, and toxicity of interventions;
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results about outcomes reported.
Assessment of risk of bias in included studies
Two review authors (LL, II) will independently assess the risk of bias of each included trial according to the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a), the Cochrane Hepato‐Biliary Group Module (Gluud 2017), and methodological studies (Schulz 1995; Moher 1998; Kjaergard 2001; Wood 2008; Lundh 2012; Savovic 2012a; Savovic 2012b). We will use the following definitions in the assessment of risk of bias.
Allocation sequence generation
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Low risk of bias: the sequence generation was achieved using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice are adequate if performed by an independent person not otherwise involved in the trial.
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Unclear risk of bias: the method of sequence generation was not specified.
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High risk of bias: the sequence generation method was not random.
Allocation concealment
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Low risk of bias: the participant allocations could not have been foreseen in advance of, or during, enrolment. Allocation was controlled by a central and independent randomisation unit. The allocation sequence was unknown to the investigators (e.g. if the allocation sequence was hidden in sequentially numbered, opaque, and sealed envelopes).
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Unclear risk of bias: the method used to conceal the allocation was not described so that intervention allocations may have been foreseen in advance of, or during, enrolment.
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High risk of bias: the allocation sequence was likely to be known to the investigators who assigned the participants.
Blinding of participants and personnel
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Low risk of bias: either of the following: no blinding or incomplete blinding, but the review authors judge that the outcome was not likely to be influenced by lack of blinding (mortality); or blinding of participants and key study personnel ensured, and it was unlikely that the blinding could have been broken.
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Unclear risk of bias: either of the following: insufficient information to permit judgement of 'low risk' or 'high risk;' or the trial did not address this outcome.
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High risk of bias: either 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 assessors
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Low risk of bias: either of the following: no blinding of outcome assessment, but the review authors judge that the outcome measurement was not likely to be influenced by lack of blinding (mortality); or blinding of outcome assessment ensured, and unlikely that the blinding could have been broken.
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Unclear risk of bias: either of the following: insufficient information to permit judgement of 'low risk' or 'high risk'; or the trial did not address this outcome.
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High risk of bias: either 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
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Low risk of bias: missing data were unlikely to make treatment effects depart from plausible values. Sufficient methods, such as multiple imputation, were employed to handle missing data.
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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.
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High risk of bias: the results were likely to be biased due to missing data
Selective outcome reporting
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Low risk of bias: the trial reported the following predefined outcomes: all‐cause mortality and number of participants with serious adverse events. 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 had begun, those outcomes will not be considered to be reliable.
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Unclear risk of bias: not all predefined outcomes were reported fully, or it was unclear whether data on these outcomes were recorded or not.
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High risk of bias: one or more predefined outcomes were not reported.
For‐profit bias
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Low risk of bias: the trial appeared to be free of industry sponsorship (medical device) or other type of for‐profit support that may manipulate the trial design, conductance, or results of the trial.
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Unclear risk of bias: the trial may or may not be free of for‐profit bias as no information on clinical trial support or sponsorship was provided.
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High risk of bias: the trial was sponsored by endoscopy device manufacturers or had received other type of for‐profit support.
Other bias
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Low risk of bias: the trial appeared to be free of other bias issues that could put it at risk of bias.
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Unclear risk of bias: the trial may or may not have been free of other issues that could put it at risk of bias.
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High risk of bias: there were other issues in the trial that could put it at risk of bias.
We will judge trials to be at a low risk of bias if they are assessed as having a low risk of bias in all the above domains. We will judge trials to be at a high risk of bias if they are assessed as having an unclear or high risk of bias in one or more of the above domains.
We will resolve any differences in opinion through discussion, and in the case of unsettled disagreements, a third review author will adjudicate.
Measures of treatment effect
Dichotomous outcomes
If outcomes are reported as dichotomous data, we will calculate the risk ratios (RR) with 95% confidence interval (CI) from meta‐analysis and Trial Sequential Analysis‐adjusted CI, or hazard ratio (HR) when appropriate (e.g. time to death).
Continuous outcomes
Where outcomes are measured as continuous data, we will compare the mean differences (MD) in change scores with 95% CIs, depending on the data available. If standard deviations or standard errors are not available, we will attempt to extract P values, t‐values, and CIs to impute standard deviations and standard errors. If authors have used different scales to measure similar outcomes, we will use standardised mean differences (SMD) with 95% CIs.
Unit of analysis issues
For each included trial, we will determine whether the unit of analysis is appropriate for the unit of randomisation and the design of each study (i.e. whether the number of observations matches the number of 'units' that were randomised (Deeks 2011). It is unlikely that we will find cluster‐randomised trials because this design is uncommon in this therapeutic field. If we include a cluster‐randomised trial, we will use the intraclass correlation coefficient (ICC) to convert trials to their effective sample size before incorporating them into the meta‐analysis, as recommended in the Cochrane Handbook for Systematic Review of Interventions (Higgins 2011b). Where the ICC is not provided, we will use values for ICCs available in the published literature (Campbell 2000).
Studies with multiple treatment groups
In the primary analysis, we will combine results across all eligible intervention groups (endoscopic retrograde cholangiopancreatography performed using Teflon and polyethylene stents or self‐expandable metallic stent and compare them with the combined results across all eligible control arms (i.e. surgical bypass), making single, pair‐wise comparisons. Where such a strategy prevents investigation of potential sources of heterogeneity, we will analyse each eligible intervention separately (against a common control group), but we will divide the sample size for common comparator arms proportionately across each comparison (Higgins 2011b). This simple approach will allow the use of standard software (including Review Manger 5) (RevMan 2014) and prevent inappropriate double‐counting of participants.
Dealing with missing data
We will carry out the outcome analyses, as far as possible, on an intention‐to‐treat basis, meaning that we will attempt to include all participants randomised to each group in the analyses, regardless of whether they received the allocated intervention or not. We will describe missing data and dropouts/attrition for each study in the 'Risk of bias' table and discuss the extent to which the missing data could alter the results/conclusions of the review. Where necessary, we will contact the corresponding authors to obtain any unreported data, such as group means and standard deviations, details of dropouts, and details of intervention received by the control group. In trials with a large proportion of missing data (more than 20%), we will assess the sensitivity of any primary meta‐analyses to missing data using the strategy recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will base analysis on the total number of randomised participants, irrespective of how the original study authors analysed the data. This will involve imputing outcomes for the missing participants based on consideration of what the event rates might have been in the missing data. We will then compare the results of the meta‐analyses with imputed data with the original analyses. We will discuss any discordances among ourselves.
Dealing with missing data using sensitivity analysis
We will attempt to obtain relevant missing data from authors whenever we lack important numerical data such as number of screened or randomised participants, or lack of data regarding the performance of intention‐to‐treat analyses, or data on as‐treated or per‐protocol participant analyses to perform our analyses as thoroughly as possibly. We will investigate attrition rates (e.g. dropouts, losses to follow‐up, and withdrawals).
Regarding the primary outcomes, we will include participants with incomplete or missing data in sensitivity analyses by computing them according to the following scenarios (Hollis 1999):
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Extreme‐case analysis favouring the experimental intervention ('best‐worse' case scenario: none of the dropouts/participants lost from the intervention arm, but all the dropouts/participants lost from the control arm experienced the outcome, including all randomised participants in the denominator.
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Extreme‐case analysis favouring the control ('worst‐best' case scenario): all dropouts/participants lost from the intervention arm, but none from the control arm experienced the outcome, including all randomised participants in the denominator.
Assessment of heterogeneity
We will assess clinical heterogeneity by comparing the distribution of important participant factors between trials (e.g. age, severity, recurrence), and trial factors (randomisation concealment, blinding of outcome assessment, losses to follow‐up, treatment type, cointerventions). We will identify heterogeneity by visual inspection of the forest plots, using a standard Chi² test, and a significance level of 0.1. We will assess statistical heterogeneity by examining the I² statistics (Deeks 2011), which describe the proportion of variation in point estimates due to variability across studies rather than sampling error. We will classify an I² value greater than 50% as substantial and discuss the result accordingly (Deeks 2011). In addition, we will employ a Chi² test of homogeneity to determine the strength of evidence that heterogeneity is genuine. We will explore clinical variation across studies by comparing the distribution of important participant factors in the trials (e.g. age), and trial factors (randomisation concealment, blinding of outcome assessment, losses to follow‐up, treatment drug, and cointerventions).
Assessment of reporting biases
To minimise the risk of publication bias, we will attempt to obtain the results of any unpublished trials to compare findings extracted from published reports with results from other sources (including drug regulatory agencies and correspondence). If there are more than 10 trials grouped in a comparison, we will assess whether reporting biases are present using funnel plots to investigate any relationship between effect estimates and study size/precision, as recommended in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).
Data synthesis
We will perform statistical analyses according to the statistical guidelines in the latest version of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).
Meta‐analysis
We will perform meta‐analyses according to the recommendations of Cochrane (Higgins 2011a). We will use random‐effects model (DerSimonian 1986) and fixed‐effect model (DeMets 1987) meta‐analyses. In the case of statistically different results between the two models, we will report the results of both models. Otherwise, we will present the results with one of the two models. We will use Review Manager 5 software for our analyses (RevMan 2014). We will express binary outcomes using RR with 95% CI, and the results of the continuous outcomes as MD with 95% CI.
Trial Sequential Analysis
Traditional meta‐analyses are prone to random errors due to sparse data and repetitive testing of accumulating data. Trial Sequential Analysis (Thorlund 2011; TSA 2011) is a methodology used to control for random errors in a meta‐analysis that helps critical appraisal of the effect of an intervention on a given outcome (Wetterslev 2008). Trial Sequential Analysis is a methodology that combines a required information size calculation (cumulated sample sizes of trials to prove or disprove a certain intervention effect) with the threshold of statistical significance. In a single randomised trial, it is essential to estimate the number of events and participants needed to make a reliable statistical inference (i.e. the sample size gives the study sufficient power (1 ‐ β (the risk of type II error) to accept or reject a certain intervention effect at a chosen risk of α (type I error). To control for the risks of random errors due to sparse data and multiplicity, we will perform Trial Sequential Analysis for the primary and secondary outcomes (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2009; Wetterslev 2009; Thorlund 2010). For dichotomous outcomes, we will estimate the required information size based on the proportion of participants with an outcome in the control group, a relative risk reduction of 20%, an α (type I error) of 5% for both primary and secondary outcomes, a β (type II error) of 10% (power 90%), and a variance suggested by the trials in a random‐effects meta‐analysis (diversity‐adjusted required information size) (Wetterslev 2009; Jakobsen 2014).
For continuous outcomes such as health‐related quality of life, we will estimate the required information size based on the standard deviation observed in the control group of trials with low risk of bias or lower risk of bias and a clinically relevant MD equal to standard deviation/2. For continuous outcomes, we will consider an α of 2.0%, a β of 10%, and a diversity suggested by the trials in the meta‐analysis (Wetterslev 2009; Jakobsen 2014; Wetterslev 2017).
Subgroup analysis and investigation of heterogeneity
Large numbers of subgroup analyses may lead to misleading conclusions (Yusuf 1991; Oxman 1992). These analyses will be exploratory as they involve non‐experimental (cross‐study) comparisons and we will treat any conclusions with caution. We plan to perform the following subgroup analyses.
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Trials at low risk of bias compared to trials at high risk of bias.
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Types of endoscopic biliary drainage: plastic (Teflon and polyethylene) stents or self‐expandable metallic stent.
Sensitivity analysis
We will conduct sensitivity analyses to establish whether findings are sensitive to restricting the analyses to studies judged to be at low risk of bias for all‐cause mortality and recurrent cholangitis or jaundice or both.
To explore the influence of imputation of missing data on the intervention effect size, we will conduct the sensitivity analyses as described under Dealing with missing data.
'Summary of findings' tables
To rate the quality of the evidence, we will create 'Summary of findings' tables on all outcomes using GRADEpro (GRADEpro GDT) and we will implement the Trial Sequential Analysis results in the GRADE assessment, especially in the assessment of imprecision.
We will assess five factors referring to limitations in 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.' These grades are defined as follows.
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High certainty: this research provides a very good indication of the likely effect; the likelihood that the effect will be substantially different is low.
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Moderate certainty: this research provides a good indication of the likely effect; the likelihood that the effect will be substantially different is moderate.
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Low certainty: this research provides some indication of the likely effect; however, the likelihood that it will be substantially different is high.
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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.
