Types of studies

We will include randomised controlled trials (RCTs) comparing the efficacy of different proton pump inhibitors (PPIs) in patients with an adequate diagnosis of functional dyspepsia (any validated criteria such as Rome I, II, III or Lancet Working Group) (Colin‐Jones 1988; Drossman 1999; Drossman 2006). We will not include cluster‐randomised trials and we will only include cross‐over studies if the results are available before the cross‐over, so that the study can be evaluated as a parallel‐group study.

Types of participants

We will consider patients over 16 years, of both genders, with a diagnosis of functional dyspepsia (functional or non‐ulcer dyspepsia) according to any well‐defined criteria (such as Rome I, II, III or Lancet Working Group), with a normal upper gastrointestinal endoscopy and with upper gastrointestinal symptoms including epigastric pain/discomfort. We will exclude patients with other gastrointestinal conditions, such as peptic ulcer, organic dyspepsia and reflux disease. If a study includes populations with different conditions, we will only consider patients with functional dyspepsia.

Types of interventions

We will include trials comparing oral administration of any dose of any PPI available (omeprazole, esomeprazole, pantoprazole, lansoprazole, dexlansoprazole or rabeprazole) with placebo, H₂‐receptor antagonists, prokinetics, antiacids or mucosal‐protecting agents. We will consider a combination of treatments in either intervention or control groups only if the combination of treatment is present for both groups.

Types of outcome measures

We will measure outcomes according to the cut‐off for each scale used. We will measure outcomes as continuous (mean score pre‐ and post‐treatment) and dichotomous (improved or not improved).

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We will conduct a literature search to identify all published and unpublished randomised controlled trials.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 consider publications regardless of language and publication status to avoid biases. We will translate the non‐English language papers and fully assess them for potential inclusion in the review as necessary. We will only include data from abstracts if we are able to obtain further details from the investigators.

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

• Cochrane Central Register of Controlled Trials (CENTRAL) (current issue) (Appendix 1);

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

• EMBASE (1988 to present); and

• CINAHL (1982 to present)."

We propose using different search terms; i.e. for MEDLINE, we will identify patients with dyspepsia with the medical subject heading (MeSH) and text term 'dyspepsia', together with text words for symptoms of dyspepsia such as 'indigestion', 'early adj5 satiety' and 'Symptom$ adj5 score$', according to the previous publication (Moayyedi 2011). We will combine these terms using the set operator 'AND' with terms for studies that have evaluated an active or control intervention. We previously identified these using MeSH terms for omeprazole and proton pump, together with text words for all PPIs, H₂‐receptor antagonists, prokinetics, antacids and mucosal‐protecting agents.

Searching other resources

We will perform handsearching of healthcare journals and conference proceedings. We will check the reference lists of all primary studies and review articles for additional references. We will contact the authors of identified trials 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 from eligible trials in PubMed (http://www.ncbi.nlm.nih.gov/pubmed) and report the date this was done within the review.

We will also conduct a search of ClinicalTrials.gov.

We will make efforts to identify unpublished studies. We will search the grey literature (e.g. conference reports, technical reports and dissertations) using SIGLE. EAGLE (the European Association for Grey Literature Exploitation) has closed the SIGLE (System for Information on Grey Literature) database, which was one of the most widely used databases of grey literature. Details of the search strategy used for each database have been published previously (Moayyedi 2011; Talley 2005).

Selection of studies

We will use the specially designed reference management software Reference Manager to collect and manage citations (Reference Manager 2014). 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.

To ensure that we identify all eligible studies, two authors (MIP and YY) will independently screen the titles, abstracts and selected trials according to the inclusion and exclusion criteria and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will document study selection or exclusion and create a list of studies to be included in the analysis. We will resolve any disagreement through discussion or, if required, we will consult third person (PM). At this initial stage we will include studies where there is disagreement or where it is difficult to decide whether or not a study should be included.

We will identify studies in which patients with an adequate diagnosis of functional dyspepsia (any valid criteria for functional dyspepsia with a normal upper gastrointestinal endoscopy) were randomised to receive any type of PPI versus another treatment or placebo. We will consider and record the general characteristics and outcomes of each study using a screening form. We will specify the instructions on how to complete the form in a manual. The screening form will record the title, author, date, study design (only RCTs were included), population characteristics, intervention and control treatment duration, as well as outcomes according to the PICO question. We will provide a section for general comments, for any screener considerations and future discussion. After development, we will pilot the form on the first five studies included in the list and make changes if necessary. We will identify and remove duplicate studies at this initial stage. We will combine the results of the title and abstract screening performed by the authors, and document and discuss decisions about inclusion in the final full‐text screening list.

To ensure that inclusion and exclusion criteria are properly interpreted and selection bias is minimised, two different review authors (MIP and YY) will perform the screening of the full texts. For papers in languages other than English, we will use a translator from The Cochrane Collaboration with experience in systematic reviewing and medicine. Information regarding the study inclusion and exclusion criteria will be provided to the translator, for them to assess whether the paper meets the criteria for inclusion. Should a paper meet the inclusion criteria, we will ask the translator to extract data on the pre‐defined data extraction form. The two authors will be provided with the full‐text journal articles and translations to perform the screening. We will collect the full‐text screening data in an Excel sheet and compare the results. We will calculate the level of agreement after each step: title and abstract screening, full‐text screening and data extraction using Kappa statistics for categorical data (GraphPad), and raw agreement for continuous data. We will report raw agreement as a percentage and Kappa as fair agreement (К = 0.4 to 0.59), good agreement (0.6 to 0.74) or excellent agreement (≥ 0.75). We will also calculate weighted Kappa statistics in the first and second steps to give 'partial credit to partial agreement'.

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. Two review authors (MIP and YY) 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 location, study setting, withdrawals, date of study.

2. Participants: N, mean age, age range, gender, severity of condition, diagnostic criteria, baseline lung function, smoking history, inclusion criteria, exclusion criteria.

3. Interventions: intervention, comparison, concomitant medications, excluded medications.

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 (MIP and YY) will independently extract outcome data from the included studies. We will note in the 'Characteristics of included studies' table if outcome data were reported in an unusable way. We will resolve disagreements by consensus or by involving a third person (PM). One review author (MIP) will copy across the data from the data collection form into Review Manager (RevMan) 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. A second review author will spot‐check study characteristics for accuracy against the trial report.

We will collect blinding information by individually identifying the person blinded. If this information is not reported, we will record the study as 'single‐blind' (implying that probably only the study participants were blinded), 'double‐blind' (implying that the study participants, healthcare providers, data collectors and assessors were blinded but not the data analysts) or 'triple‐blind' (implying that the data analysts were also blinded).

If any information is missing at the end of data extraction process, we will contact the authors of the trials to recover the specific study design, population, intervention, control or outcomes data, in addition to the information provided by the screening form. We will record data on authors, settings (primary, secondary or tertiary care) and funding source (industry‐sponsored, grant‐sponsored, investigator‐funded). We will include information on the following outcomes on the form: global symptoms and independent symptoms related to functional dyspepsia (epigastric pain, distension, early satiety, postprandial fullness, belching, reflux‐like), as well as quality of life and adverse events. We will detail common adverse events (such as such as diarrhoea, intolerance, nausea, headaches). We will include the number of patients exposed to treatment and control, their demographic characteristics (age, sex and ethnicity) and the type of PPI, dose and period of treatment. We will record patient demographics, treatment outcomes and adverse events as mean (standard deviation (SD)), n/N or % when applicable. We will also collect on the form information to assess possible risk of bias (randomisation, concealment, blinding of participants and outcome assessors, incomplete outcome data, selective reporting and other biases). 

Assessment of risk of bias in included studies

Two review authors (MIP and YY) 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). We will resolve any disagreement by discussion or by involving a third assessor (PM). 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 and provide a quote from the study report together with a justification for our judgement in the 'Risk of bias' table for each study. 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 patient‐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 of the studies that contributed to that outcome.

We will enter the data related to risk of bias into RevMan 5 (RevMan 2012) and construct the 'Risk of bias' tables. We will generate two figures with the RevMan software:

1. a 'Risk of bias' graph, which illustrates the proportion of studies complying with each of the judgements ('low', 'high' and 'unclear' risk of bias); and

2. a 'Risk of bias' summary, which represents all of the judgements in a cross‐tabulation of study by entry.

In order to translate the quality assessment into clinical practice, we will use the GRADE system and develop a 'Summary of findings' table. We will define the strength of recommendation as 'strong' or 'weak' depending on benefits versus risks associated with treatment and the quality of the evidence. We will grade the quality of evidence as high, moderate, low or very low with regard to study limitations, consistency, directness, precision and publication bias for each study.

Measures of treatment effect

We will analyse dichotomous data as risk ratio (RR) and continuous data as mean difference (MD) or standardised mean difference (SMD). 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 report information regarding the study population follow‐up (patients enrolled and randomised) as the data collected from discontinued patients over the total number of patients for each arm (n/N). We will collect and report the total number of participants with and without symptoms related to dyspepsia in each arm at each time point (before and after treatment) as a number over the total sample population (n/N) in each arm.  We will report the comparison of binary data as a RR with an associated 95% confidence interval (CI), an absolute risk reduction (ARR) or the number needed to treat to benefit (NNTB) with associated 95% CI, or the Chi² with associated P value.

We will collect continuous outcome data (dyspepsia score and quality of life) in three different ways:

1. Unit of measurement or, if unit of measurement cannot be reported (i.e. visual analogue scale), we will consider the data to be unit‐less.

2. Measure of central tendency: mean, median, mode.

3. Measure of variance, such as standard deviation, standard error, interquartile range or 95% CI. In the event that we are not provided with the raw data, we will collect the reported analysis.

We will collect change scores (the difference between scores before and after intervention) for comparison.

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 in which trialists indicate that 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. drug A versus placebo and drug B versus placebo) must be entered into the same meta‐analysis, we will halve the control group to avoid double‐counting.

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 an abstract only). We will contact study investigators whenever possible to request missing data. If this is not possible, or data are not provided, we will consider that patients with missing data did not have the outcome of interest. We will perform sensitivity analyses to assess robustness of the results relative to reasonable changes in the assumptions that are made.

We will address the potential impact of missing data on the findings of the meta‐analysis in the 'Discussion' section.

Assessment of heterogeneity

Heterogeneity in systematic reviews can occur because of artefactual or real differences in treatment effects across the different studies included in the review (Tett 2013), and the reasons behind it should be carefully investigated. We will consider all EPICOT components, as well as internal validity issues (such as compliance, co‐intervention, randomisation) in the analysis. Possible sources of heterogeneity could be related to the criteria considered for the functional dyspepsia definition and differences in the demographics of the included population: time, duration and dose of PPI; undetected co‐intervention and differences in outcomes measurements. To address the most important possible sources of heterogeneity, we will perform subgroup analysis.

We will assess statistical heterogeneity with both the I² statistic and the Chi² test. An I² value of 0% indicates no observed heterogeneity and larger values denote heterogeneity. We will consider heterogeneity significant when the I² is greater than 25% or there is a P value of less than 0.01 for the Chi² test.

We will use the I² statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity we will explore it with the pre‐specified subgroup analysis. 

Assessment of reporting biases

We will attempt to contact study authors and ask 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 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. In the graph, the effect estimates will be shown on the horizontal scale and the measure of study size on the vertical axis. Asymmetric funnel plots will suggest small study effects, publication bias, delayed publication (time lag), selective reporting outcome or even differences in methodological quality. We will perform statistical test of the funnel plot using the approach proposed by Egger et al (Egger 1997): a linear regression of the intervention effect estimates on their standard errors (SE), weighting by 1/(variance of the intervention effect estimate (Cochrane Handbook 2011). The test can be interpreted by considering the vertical line: the more the slope moves from vertical, the greater the association between intervention effect and SE.

Data synthesis

In order to be able to combine the results, we will consider some possible differences before performing the meta‐analysis. For qualitative evidence, we will create a summary table of reviewed studies using the GRADEpro software (GRADEpro). We will provide data regarding study type, comparison, study quality and number of patients involved.

We will create a forest plot of the meta‐analysis for quantitative synthesis.

We will address differences in the research question, population, intervention, comparators, outcomes and methodology. We will include different comparators (placebo or other active comparators such as H₂‐receptor antagonists, antiacids or prokinetics) in the analysis. However, we will separate studies with different comparators into different subgroups for their analysis. 

For quantitative analysis, we will perform a meta‐analysis using RevMan 5 (RevMan 2012). We will calculate a summary statistic for each study in order to describe the observed intervention effect. In the case of dichotomous outcomes, we will calculate a RR and for continuous data we will calculate a MD. When different instruments have been used, we will use the SMD. We will calculate a summary (pooled) intervention effect estimate as a weighted average of the intervention effects estimated in the individual studies. We will choose the weights to reflect the amount of information that each study contains.

For the combination of intervention effect estimates across studies, we will assume that the studies are not all estimating the same intervention effect, but estimating intervention effects that follow a distribution across studies. We will therefore consider a random‐effects model meta‐analysis to be adequate (Kwok 2013). However, since the correct selection of the model is controversial, we will also perform a fixed‐effect model analyses and compare the results of both. In the event that these models have similar results, we will consider that the chances of heterogeneity being present across the studies is low. Otherwise, if the results are different, we will consider the random‐effects model to be the most appropriate for the reasons previously described.

To communicate the strength of evidence against the null hypothesis of no intervention effect, we will use measures of dispersion (such as standard error) to derive a confidence interval and a P value.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses to reveal any effect that might explain any heterogeneity:

1. Treatment duration (less than four weeks versus greater than four weeks).

2. Dose (standard dose versus low dose; table of standard doses).

3. PPI subtype.

4. H. pylori status (H. pylori‐negative versus H. pylori‐positive).

5. Risk of bias (low versus unclear versus high risk of bias).

6. Geographical location (e.g. Western versus Asian studies).

7. Trial funding sources (industry‐sponsored versus non‐industry‐sponsored studies).

We will assess statistically significant differences between subgroups with the I² statistic and Borenstein, to test for subgroup interactions.

Sensitivity analysis

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

1. abstract inclusion;

2. eligibility criteria (inclusion of open‐label studies); and

3. fixed‐effect versus random‐effects models.

We will report the results from the sensitivity analyses in a summary table.