Types of studies

We will include all RCTs or quasi‐RCTs (“a trial in which randomisation is attempted but subject to potential manipulation, such as allocating participants by day of the week, date or birth, or sequence of entry into trial”) (CCCRG 2016).

We will include studies reported as full text, those published in abstract form only, and unpublished data, with no restrictions on blinding, publication status, or language.

Types of participants

We will include people with pancreatic cancer, diagnosed using any validated criteria, irrespective of gender, age, or ethnicity.

We will use the following inclusion criteria:

1. clinical presentation (medical history, physical examination, and information from imaging, chemical, histological, and cellular studies) compatible with pancreatic cancer;

2. steatorrhoea (see Background for definition).

We will include studies conducted in any healthcare setting.

We will exclude studies involving combined populations (i.e. people with pancreatic cancer along with those with chronic pancreatitis, cystic fibrosis, or any other people suffering from other diseases causing PEI) if they do not report results for individuals with pancreatic cancer separately.

Types of interventions

We will include the following types of study.

1. Studies comparing PERT (single‐ or multi‐enzyme preparations, various coating methods (e.g. enteric or non‐enteric coatings) different pharmacological forms) versus placebo or no treatment.

2. Studies comparing PERT versus fat restriction.

We will include studies investigating opiate usage as a cointervention provided that this is not a part of the randomised treatment, keeping in mind that it may hide the effects of exocrine insufficiency, which could complicate the detection and treatment of malabsorption (Imrie 2010); however, when opiates are used in one or more of the groups and not in others (treatment or control groups) we will exclude the study.

As mentioned above, we will include studies comparing PERT with fat restriction, which is a treatment for steatorrhoea. We will include trials that do not compare PERT with fat restriction, but which include the use of fat restriction in all groups; however, when fat restriction is used in one or more of the groups and not in others (treatment or control groups), we will exclude the study.

Types of outcome measures

Electronic searches

We will conduct a literature search to identify all published and unpublished RCTs. We will construct the search strategies by using a combination of subject headings and text words relating to pancreatic cancer, steatorrhoea, and PERT. A preliminary search testing suggests that only a very small number of studies has been published that mention terms related to pancreatic cancer, steatorrhoea, and PERT (< 50 hits in MEDLINE). As we want to review all identified references including reviews, we will not apply a RCT filter on this search combination. To further increase the literature search sensitivity, we will also search any RCT that used terms related to pancreatic cancer and PERT in the abstract even if these studies do not mention terms relating to steatorrhoea in the abstract. We will apply the standard Cochrane search strategy filter for identifying RCTs to this supplemental search because a large of number of hits are found (> 1000 in MEDLINE). Hence, the final search strategy will combine terms related to: (pancreatic cancer AND steatorrhoea AND pancreatic enzyme therapy) OR (pancreatic cancer AND pancreatic enzyme therapy AND RCT filter). Will will not use an RCT filter for the search in the Cochrane Library (pancreatic cancer AND pancreatic enzyme therapy). We will apply no language restrictions. We will translate 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

• CINAHL (Cumulative Index to Nursing and Allied Health Literature; 1982 to present) (Appendix 5).

We will also conduct a search of ClinicalTrials.gov and the World Health Organization International Clinical Trials Registry Platform (www.who.int/ictrp/en/).

Searching other resources

We will handsearch the published abstracts from the conference proceedings published in Digestive Disease Week and United European Gastroenterology Week from 2011 to 2018. We will handsearch the references cited in studies found by the above search to identify further relevant studies. We will check the reference lists of all primary studies and review articles for additional references.  We will contact authors of identified studies and ask them to identify other published and unpublished studies. We will also contact manufacturers and experts in the field.

We will search for errata or retractions for any eligible studies and for studies that are not indexed by MEDLINE in PubMed (www.ncbi.nlm.nih.gov/pubmed) prior to publication of the review and report the date this was done within the review.

Selection of studies

Four review authors (YHN, YA, YAD, and FA) will independently screen the titles and abstracts of 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/publications and four review authors (YHN, YA, YAD, and FA) will independently screen the full text and identify studies for inclusion, and identify and record reasons for exclusion of any ineligible studies. We will resolve any disagreement through discussion or, if required, we will consult another review author (NAH). 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 a 'Characteristics of excluded studies' table.

Data extraction and management

We will use a standard data collection form for study characteristics and outcome data, adapted from the Cochrane Upper Gastrointestinal and Pancreatic Diseases website (Resources for Authors), which we will pilot on at least one study in the review. Four review authors (YHN, YA, YAD, and HAS) will extract study characteristics from included studies. 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, and date of study.

2. Participants: number, age range, mean age, gender, severity of condition, diagnostic criteria, inclusion criteria, and exclusion criteria.

3. Interventions: intervention (routes of delivery (e.g. oral or intravenous delivery), doses (e.g. amount or intensity of each treatment, frequency of delivery), timing (e.g. before, during, or after a meal), pharmacological form, length of treatment, comparisons, concomitant medications (antacids, etc.), excluded medications (when opiates are used in one or more of the groups and not in others (treatment or control groups)), excluded treatment (when fat restriction is used in one or more of the groups and not in others (treatment or control groups)).

4. Outcomes: primary and secondary prespecified and collected outcomes at different time points.

5. Notes: funding source of the study and potential conflicts of interest of the study authors.

Four review authors (YHN, YAD, YA, FA) will independently extract outcome data from included studies. We will note in a 'Characteristics of included studies' table whether outcome data were reported in an unusable way. We will resolve disagreements by consensus or by involving another review author (NAH). One review author (YA) will copy across the data from the data collection form into Review Manager 5 (RevMan 5) (RevMan 2014). Each review author (YHN, YAD, YA, FA) will double check that the data are entered correctly by comparing the study reports with the data presented in the systematic review. A review author (NAH) will spot‐check study characteristics for accuracy against the study report.

Assessment of risk of bias in included studies

Four review authors (YHN, YA, YAD, and HAS) will independently assess the risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Any disagreement will be resolved by discussion or by involving a fifth review author (NAH). For individually randomised studies we will assess the risk of bias according to the following domains.

Measures of treatment effect

We will analyse dichotomous variables (e.g. improvement in steatorrhoea, reductions in symptoms and improvements in fat‐soluble vitamin deficiency‐related diseases) using risk ratios with 95% confidence intervals. For continuous variables (e.g. measuring weight change, malabsorption, abdominal pain and costs) we will calculate mean differences with 95% confidence intervals. We will use standardised mean differences with 95% confidence intervals for quality of life or any other continuous variable if studies used different scales. We will ensure that higher scores for continuous outcomes have the same meaning for each particular outcome, explain the direction to the reader, and report where the directions were reversed, if this was necessary. For count outcomes, such as the number of adverse events, we will calculate the rate ratios with 95% confidence intervals.

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

A common way that trialists indicate the presence of skewed data is the reporting of medians and interquartile ranges. When we encounter this we will note that the data are skewed and consider the implications of this.

Unit of analysis issues

The unit of analysis will be the individual participant with pancreatic cancer suffering from steatorrhoea.

We will consider special issues in the analysis of studies with non‐standard designs as follows.

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 published in abstract form only).

For dichotomous variables we will perform an intention‐to‐treat analysis whenever possible, which will include all participants randomised to a study irrespective of what happened subsequently (Higgins 2011; Lewis 1993; Newell 1992). This will involve imputing outcomes for the missing participants and we will assume that all missing participants did not experience the desired outcome (reduction in steatorrhoea and related symptoms). If this is not possible, we will conduct a per‐protocol analysis (an analysis of the results of only those participants who completed the study and who complied with (or received some of) their allocated intervention (in this review, PERT)) (Higgins 2011); we will, however, assess the impact of the worst‐ and best‐case scenarios on the results in the sensitivity analysis. For continuous outcomes, we will perform an available‐case analysis. If we are unable to obtain the necessary 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, interquartile range, or P values, according to guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011); we will, however, assess the impact of including such studies using 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 studies included in the outcome, being fully aware that this method of imputation will decrease the weight of a study in a meta‐analysis of mean differences and will shift the effect estimate towards no effect for standardised mean differences. We will assess the impact of including such studies using a sensitivity analysis.

Assessment of heterogeneity

We will test heterogeneity using:

1. the Chi² test, with significance set at P < 0.1;

2. the I² statistic (Higgins 2003), which can be interpreted as the percentage of variation observed between the studies that is attributable to between‐study differences rather than sampling error (chance) (Higgins 2011); we will consider an I² statistic greater than 50% as indicative of high‐level heterogeneity. We will recognise that there is uncertainty in the I² statistic when there are few studies in a meta‐analysis;

3. Tau², which represents an estimate of the between‐study variance in a random‐effects meta‐analysis (Higgins 2011). If Tau² is similar to the treatment effect we will conclude that the heterogeneity is very high.

If we find high levels of heterogeneity (I² > 50%, or Tau² is similar to the treatment effect) for our primary outcomes, we will explore possible sources of heterogeneity using the sensitivity and subgroup analyses described below.

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 studies, we will create and examine a funnel plot to explore possible publication biases.

We will consider reporting biases (publication, time lag, duplicate publication, location, citation, language, and outcome reporting) at all points of both the data analysis and the interpretation. If sufficient numbers of RCTs are found in a particular field, attempts will be made to analyse the studies for publication bias using funnel plots, bearing in mind that publication bias does not necessarily cause asymmetry (Egger 1997; Macaskill 2001). We will consider a P value of less than 0.05 statistically significant for reporting bias.

Data synthesis

We will perform the analysis using RevMan 2014. We will use both a fixed‐effect model and a random‐effects model for the analysis. For subgroup analyses, if the studies are found to be homogeneous (in terms of age, diagnostic subtype, intervention type, intervention duration) we will use a fixed‐effect model; if they are found to be heterogeneous we will perform a random‐effects model. In case of discrepancies between the two models, we will report both results.

• We will summarize dichotomous (binary) variables (e.g. proportion of participants who develop side effects) using risk ratios.

• We will summarize continuous data using the mean difference when studies use the same scale. We will use the standardised mean difference to measure the difference between groups in studies that use different scales

• We will summarize ordinal outcomes data and scales as dichotomous data for short scales and continuous data for long scales

• When studies have a multifactorial design comparing multiple intervention groups, we will extract data and assign them to the relevant intervention group. We will treat each intervention group independently within our analysis

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

• PERT in participants with unresectable or resectable cancers prior to the Whipple procedure as one group versus participants after the Whipple procedure as another group. This is because the procedure is greatly invasive and its malabsorption consequences could be a result of many factors other than the loss of pancreatic enzymes.

• Coadministration of antacids and various PERT preparations versus various PERT preparations alone, to allow for the change in pH level in the stomach associated with antacids that could affect PERT efficacy (Vecht 2006).

• Different administration schedules (before, with, or after meals), to allow for their effect on the therapeutic efficacy of PERT, considering that the change in the timing of the arrival of PERT with chymus in the duodenum could affect PERT efficacy (Dominguez‐Munoz 2005).

• Doses of 25,000 or lower lipase units per main meal versus doses of more than 25,000 lipase units per main meal (Struyvenberg 2017).

We will use steatorrhoea as the outcome in subgroup analyses.

We will use the formal statistical test for heterogeneity across subgroups based on the random‐effects model to test for subgroup interactions (Borenstein 2008) and we will use caution in the interpretation of subgroup analyses, as advised in Section 9.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will compare the magnitude of the effects between the subgroups by assessing the overlap of the confidence intervals of the summary estimate (non‐overlap of the confidence intervals indicates statistical significance).

Sensitivity analysis

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

• excluding studies at unclear or high risk of bias (one or more of the 'Risk of bias' domains classified as unclear or high, including: methods used for randomisation, allocation to interventions, blinding or missing data);

• excluding those at unclear or high risk of bias for sequence generation (e.g. quasi‐RCTs);

• making different hypotheses on any imputed data (e.g. excluding studies in which either means or standard deviations, or both are imputed);

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

• excluding studies published in abstract form only;

• excluding studies of low statistical power;

• excluding unpublished studies;

• excluding studies funded by industry;

• comparing summary statistics (risk ratios versus odds ratios) by calculating a risk ratio for the desired outcome (no steatorrhoea and malabsorption after PERT therapy); if the risk ratio is close to one, we will compare this with the odds ratio to analyse sensitivity;

• comparing meta‐analysis modelling (fixed‐effect versus random‐effects);

• evaluating the influence of missing data on the results (intention‐to‐treat analysis versus per‐protocol analysis);

• performing a best‐case, worst‐case type analysis in which all missing participants in one arm are assumed to have had the outcome of interest and all missing participants in the other arm are assumed to have not had the outcome, and vice‐versa.

We will report the results from the sensitivity analyses in a summary table and produce a summary table detailing decisions made during the process of conducting the review and the potential impact of these decisions on the findings. We will address significant decisions in the 'Discussion' section of the review.