Types of studies

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 We will include studies reported as full text, those published as abstract only, and unpublished data.

Types of participants

We will include adults with acute pancreatitis irrespective of the severity (mild, moderately severe, or severe acute pancreatitis) or the type of acute pancreatitis (acute interstitial oedematous pancreatitis or necrotising pancreatitis). However, if there is any evidence of inconsistency (see Data synthesis), we will perform a separate meta‐analysis for interventions for mild pancreatitis separately from moderately severe or severe pancreatitis. This is because mild pancreatitis has no local or systemic complications and combining participants with mild and severe acute pancreatitis in the same network meta‐analysis may violate the transitivity assumption (the assumption that the participants included in the different studies with different treatments can be considered to be a part of a multi‐arm randomised controlled trial ‐ i.e., they should be reasonably similar in characteristics).

Types of interventions

We will include trials comparing any pharmacological intervention mentioned above with another pharmacological intervention mentioned above, with placebo, or with no intervention, provided that the only difference between the randomised groups is the pharmacological intervention or interventions being assessed. We will combine the different somatostatin analogues (such as somatostatin or octreotide) as a single treatment, but will consider the remaining interventions such as gabexate mesilate, aprotinin, ulinastatin, nafamostat, vitamin C, selenium, lexipafant, steroids, tumour necrosis factor‐alpha (TNF‐α) antibody, probiotics, and antibiotics as different interventions. We will assess a combination of drugs as a separate treatment.

Types of outcome measures

Electronic searches

We will conduct a literature search to identify all published and unpublished randomised controlled trials. The literature search will identify potential studies in all languages. We will translate the 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:

• Cochrane Central Register of Controlled Trials (CENTRAL) (Appendix 2);

• MEDLINE (1966 to present) (Appendix 3);

• EMBASE (1988 to present) (Appendix 4); and

• Science Citation Index (1982 to present) (Appendix 5).

We will also conduct a search of ClinicalTrials.gov (Appendix 6) and World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (Appendix 7).

Searching other resources

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

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

Selection of studies

Two review authors (trained research assistants or students or colleagues of KG) will independently screen titles and abstracts of all the potential studies we identify through the searches, and will 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 will independently screen them and identify studies for inclusion; they will identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion or, if required, will consult the lead author (KG). 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 contact the investigators of trials of unclear eligibility. We will record the selection process in sufficient detail to complete a PRISMA 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, which has been piloted on at least one study in the review. Two review authors (research assistants or students or colleagues of KG) 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 (N), mean age, age range, gender, severity and type of acute pancreatitis, inclusion criteria, exclusion criteria

3. Interventions: intervention, comparison, concomitant interventions, number of participants randomised to each group

4. Outcomes: primary and secondary outcomes specified and collected, time points reported. For binary outcomes, we will obtain the number of participants with events and the number of participants included in the analysis in each group. For continuous outcomes, we will obtain the unit or scale of measurement, mean, standard deviation, and the number of participants included in the analysis for each group. For count outcomes, we will obtain the number of events and number of participants included in the analysis in each group. For time‐to‐event outcomes, we will obtain the proportion of people with events, the average duration of follow‐up of participants in the trial, and the number of participants included in the analysis for each group

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

Two review authors (research assistants or students or colleagues of KG) will independently extract outcome data from included studies. If outcomes were reported at multiple time points, we will extract the data for all time points. We will obtain information on the number of participants with adverse events (or serious adverse events) and the number of such events where applicable. We will extract all information on costs using the currency reported by the trial authors, and will convert this to US dollars at the conversion rates on the day of the analysis. We will extract data for every trial arm that is an included intervention. If outcome data are reported in an unusable way, we will attempt to contact the trial authors and try to obtain usable data. If we are unable to obtain usable data despite this, we will summarise the unusable data in an appendix. We will resolve disagreements by consensus or by involving the lead author (KG). One review author (KG) will copy across the data from the data collection form into the Review Manager 5 file. 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 KG) 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 assessor (KG). 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 potential bias.

We will grade each potential source of bias as high, low or unclear, 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 than for a participant‐reported pain scale. Where information on risk of bias relates to unpublished data or to correspondence with a trial author, we will note this in the 'Risk of bias' table. We will present the risk of bias in each pair‐wise comparison in separate tables.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome by a sensitivity analysis.

Measures of treatment effect

For dichotomous variables (short‐term mortality, proportion of participants with adverse events, requirement for additional interventions), we will calculate the odds ratio (OR) with 95% credible interval (CrI). For continuous variables, such as length of hospital stay, ICU stay, time to return to normal activity, time to return to work, and costs, we will calculate the mean difference (MD) with 95% CrI. We will use standardised mean difference (SMD) with 95% CrI for quality of life if different scales were used. For count outcomes such as the number of adverse events, we will calculate the rate ratio (RaR) with 95% CrI. For time‐to‐event data, such as long‐term mortality, we will use the hazard ratio (HR) with a 95% CrI.

A common way that trial authors indicate when they have skewed data is by reporting medians and interquartile ranges. When we encounter this, we will report the median and interquartile range in a table.

Unit of analysis issues

The unit of analysis will be individual participants with acute pancreatitis. We do not anticipate 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 from the report or from the trial authors, we will not include the trial in the meta‐analysis.

In multi‐arm trials, the models account for the correlation between trial‐specific treatment effects from the same trial.

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). For binary, count, and time‐to‐event outcomes, we will perform an intention‐to‐treat analysis whenever possible (Newell 1992). If this is not possible, we will perform an available‐case analysis but will assess the impact of 'best‐best', 'best‐worst', 'worst‐best', and 'worst‐worst' scenario analyses on the results for binary outcomes. For continuous outcomes, we will perform an available‐case analysis. If we are unable to obtain the information from the investigators or study sponsors, we will impute the mean from the median (i.e., consider the median as the mean) and the standard deviation from the standard error, inter‐quartile range, or P values according to the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), but 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, inter‐quartile range, or P values, we will impute the standard deviation as the highest standard deviation in the remaining trials included in the outcome, being fully aware that this method of imputation will decrease the weight of the studies in the meta‐analysis of mean difference and will shift the effect estimate towards no effect for standardised mean difference. We will then assess the impact of including such studies by sensitivity analysis.

Assessment of heterogeneity

We will assess the heterogeneity in each pair‐wise comparison by assessing the Higgins I² (Higgins 2003), the Chi² test with significance set at a P value less than 0.10, and by visual inspection. We will also use the τ² (tau‐squared) statistic to measure heterogeneity among the trials in each analysis. τ² (tau‐squared) statistic provides a measure of the variability of the effect estimate across studies in a random‐effects model (Higgins 2011). If the τ² is similar to the treatment effect (natural logarithm of treatment effect for ratios), one may conclude that the heterogeneity is very high. If we identify substantial heterogeneity, we will explore it by meta‐regression. 

Assessment of reporting biases

We will attempt to contact trial authors, asking them to provide missing outcome data. Where this is not possible, and if we think that the missing data may introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis. 

If we are able to pool more than 10 trials for a specific comparison, 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 of < 0.05 will be considered statistically significant reporting bias.

Data synthesis

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. In general, we favour performing a meta‐analysis, and will clearly highlight the reason for not performing one if we decide against it. We will conduct network meta‐analyses to compare multiple interventions simultaneously for each of the primary and secondary outcomes. Network meta‐analysis combines direct evidence within trials and indirect evidence across trials (Mills 2012).

We will obtain a network plot to ensure that the trials are connected by treatments using Stata/IC 11 (StataCorp LP) (see Appendix 8 for the Stata commands to be used). We will apply network meta‐analysis to each connected network. We will conduct a Bayesian network meta‐analysis using the Markov chain Monte Carlo method in WinBUGS 1.4. We will model the treatment contrast (e.g., log OR for binary outcomes, MD or SMD for continuous outcomes, rate ratio for count outcomes, HR for time‐to‐event outcomes) for any two interventions ('functional parameters') as a function of comparisons between each individual intervention and an arbitrarily selected reference group ('basic parameters') (Lu 2004). The reference group will combine placebo and no‐intervention. We will perform the network analysis as per the guidance from the NICE DSU documents (Dias 2013). Further details of the codes used and the technical details of how we will perform the analysis are shown in Appendix 9 and Appendix 10. In short, we will use three non‐informative priors, a burn in of 30,000 simulations to ensure convergence (we will use longer burn in if the models do not converge in 30,000 simulations), and obtain the posterior estimates after a further 100,000 simulations. We will run the fixed‐effect and random‐effects models (assuming homogeneous between‐trial variance across comparisons) for each outcome. We will choose the fixed‐effect model if it results in an equivalent or better fit (assessed by residual deviances, number of effective parameters, and deviance information criterion (DIC)) than the random‐effects model. A lower DIC indicates a better model fit. We will use the random‐effects model if it results in a better model fit as indicated by a DIC lower than that of the fixed‐effect model by at least three. In addition, we will perform a treatment‐by‐design random‐effects inconsistency model (Higgins 2012; White 2012). We will deem the inconsistency model to be better than the random‐effects consistency model (standard random‐effects network meta‐analysis model) if the model fit of the inconsistency model (as indicated by DIC) is at least three lower than the random‐effects consistency model.

For multi‐arm trials, one can enter the data from all the arms in a trial as: the number of people with events and the number of people exposed to the event, using the binomial likelihood and logit link for binary outcomes; the mean and standard error using the normal likelihood and identity link for continuous outcomes requiring calculation of the mean difference; the mean and standard error of the treatment differences using the normal likelihood and identity link for continuous outcomes requiring calculation of the standardised mean difference; the number of events and the number of people exposed to the event using the Poisson likelihood and log link for count outcomes; the follow‐up time in the study, number of people with the event and the number of people exposed to the event using the binomial likelihood and cloglog link for time‐to‐event outcomes. We will report the treatment contrasts (e.g., log ORs for binary outcomes, MDs for continuous outcomes, and so on) of the different treatments in relation to the reference treatment (i.e., combined placebo and no‐intervention), the residual deviances, number of effective parameters, and DIC for the fixed‐effect model and the random‐effects model for each outcome. We will also report the parameters used to assess the model fit (i.e., residual deviances, number of effective parameters, and DIC) for the inconsistency model for all the outcomes and the between‐trial variance for the random‐effects model (Dias 2012a; Dias 2012b; Higgins 2012; White 2012). If the inconsistency model results in a better model fit than consistency models, transitivity assumption is likely to be untrue and the effect estimates obtained may not be reliable. We will highlight such outcomes where the inconsistency model results in a better model fit than consistency models. We will then perform a separate network meta‐analysis for interventions for mild versus moderate or severe acute pancreatitis and assess the inconsistency again. If there is no evidence of inconsistency in the revised analysis, we will present the results of the analysis for mild and moderate or severe acute pancreatitis separately. If there is persistent evidence of inconsistency, we will present the results from the direct comparison in the 'Summary of findings' table.

The 95% CrIs of treatment effects (e.g., ORs for binary outcomes, MDs for continuous outcomes, and so on) are calculated in the Bayesian meta‐analysis, which is similar in use to the 95% confidence intervals in the frequentist meta‐analysis. These are the 2.5^th percentile and 97.5^th percentiles of the simulations. We will report the mean effect estimate and the 95% CrI for each pair‐wise comparison in a table. We will also estimate the probability that each intervention ranks at one of the possible positions, and will present this information in graphs. It should be noted that a less than 90% probability that the treatment is the best treatment is unreliable (i.e., one should not conclude that the treatment is the best treatment for that outcome if the probability of it being the best treatment is less than 90%) (Dias 2012a). We will also present the cumulative probability of the treatment ranks (i.e., the probability that the treatment is within the top two, the probability that the treatment is within the top three, etc.) in graphs. We will also plot the probability that each treatment is best for each of the different outcomes (rankograms) which are generally considered more informative (Dias 2012a; Salanti 2011).

We will also perform direct comparisons using the same codes. This will allow us to assess the heterogeneity in the comparisons and create the 'Summary of findings' table (see below).

In the presence of adequate data where authors report the outcomes of participants at multiple follow‐up time points, we will follow the methods suggested by Lu 2007 to perform the meta‐analysis.

Subgroup analysis and investigation of heterogeneity

We will assess the differences in the effect estimates between the following subgroups using meta‐regression for each source of heterogeneity (i.e., one analysis for each source of heterogeneity) with the help of the code shown in Appendix 6 when at least one trial was included in each subgroup. We will perform the subgroup analysis regardless of inconsistency, but the main purpose of subgroup analysis is to investigate heterogeneity and inconsistency.

1. Different types of acute pancreatitis (acute interstitial oedematous pancreatitis or necrotising pancreatitis).

2. Different severity of acute pancreatitis (mild pancreatitis versus moderate or severe acute pancreatitis).

3. Presence of persistent organ failure (mild or moderate acute pancreatitis versus severe acute pancreatitis).

4. Presence of infection (infected necrotising pancreatitis versus non‐infected necrotising pancreatitis).

We will calculate the interaction term (Dias 2012c). If the 95% CrI of the regression coefficient of the interaction term does not overlap zero, we will consider this statistically significant.

Sensitivity analysis

We will perform sensitivity analyses defined a priori to assess the robustness of our conclusions. These will involve:

1. Excluding trials at unclear or high risk of bias (one or more of the 'Risk of bias' domains classified as unclear or high).

2. Excluding trials in which either the mean or the standard deviation or both were imputed.

3. Imputation of binary outcomes under 'best‐best', 'best‐worst', 'worst‐best', and 'worst‐worst' scenarios.