Types of studies

We included RCTs comparing the efficacy of different PPIs in people with an adequate diagnosis of FD (any validated criteria such as Rome I, II, III, IV or Lancet Working Group) (Colin‐Jones 1988; Drossman 1999; Drossman 2006; Stanghellini 2016). We included cross‐over studies only if the results were available before the cross‐over, so that the study could be evaluated as a parallel‐group study. We excluded cluster‐randomized trials.

Types of participants

We considered studies involving people aged over 16 years, of both genders, with a diagnosis of FD according to any well‐defined criteria (such as Rome I, II, III, IV or Lancet Working Group; Table 1), with a normal upper gastrointestinal endoscopy and with upper gastrointestinal symptoms including epigastric pain/discomfort. We excluded studies involving participants with other gastrointestinal conditions, such as peptic ulcer, organic dyspepsia and reflux disease. If a study included populations with different conditions, we only considered people with FD.

Types of interventions

We included trials comparing oral administration of any dose of any PPI available (omeprazole, esomeprazole, pantoprazole, lansoprazole, dex‐lansoprazole or rabeprazole; for doses see Table 2) with placebo, H2RAs or prokinetics. We considered a combination of treatments in either intervention or control groups only if the combination of treatment was present in both groups. We considered therapy of at least two weeks' duration. We recorded and compared the time of the intervention and follow‐up.

Types of outcome measures

We measured outcomes as continuous (mean score pre‐ and post‐treatment) and dichotomous (improved or not improved). We measured the number of events in each group for adverse events.

Electronic searches

We conducted a literature search to identify all published and unpublished RCTs. We considered studies regardless of language and publication status to avoid biases. We translated the non‐English language papers and fully assessed them for potential inclusion in the review as necessary. We only included data from abstracts if we were able to obtain further details from the investigators. We searched the following electronic databases for potential studies:

• the Cochrane Library (to May 2017) (Appendix 2);

• MEDLINE (OvidSP) (1946 to May 2017) (Appendix 3);

• Embase (OvidSP) (1974 to May 2017) (Appendix 4).

The Cochrane Library databases include Cochrane Database of Systematic Reviews (CDSR), Cochrane Central Register of Controlled Trials (CENTRAL), Cochrane Methodology Register (CMR), Database of Abstracts of Reviews of Effects (DARE), Health Technology Assessment Database (HTA) and NHS Economic Evaluation Database (EED). The search strategies were constructed by using a combination of subject headings and text words relating to dyspepsia and PPIs.

Searching other resources

We performed handsearching of healthcare journals and conference proceedings (i.e. Digestive Diseases Week, United European Gastroenterology Week). We checked the reference lists of all primary studies and review articles for additional references. We contacted the authors of identified trials and ask them to identify other published and unpublished studies. We contacted manufacturers and experts in the field. We searched for errata or retractions from eligible trials in PubMed (www.ncbi.nlm.nih.gov/pubmed) and reported the date this was done within the review. We also conducted a search of ClinicalTrials.gov for clinical trials. We made efforts to identify unpublished studies. We searched the grey literature (e.g. conference reports, technical reports and dissertations) using SIGLE (Appendix 5)). EAGLE (the European Association for Grey Literature Exploitation) has closed the SIGLE (System for Information on Grey Literature; www.opengrey.eu/) database, which was one of the most widely used databases of grey literature.

Selection of studies

We used Review Manager 5 to collect and manage citations (Reference Manager 2014). We identified and excluded duplicates and collate multiple reports of the same study, so that each study, rather than each report, was the unit of interest in the review. We recorded the selection process in sufficient detail to complete a PRISMA flow diagram (Figure 1).

Figure 1

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Study flow diagram.

To ensure that we identified all eligible studies, two review authors (MIP and YY) independently screened the abstracts and selected trials according to the inclusion and exclusion criteria. We documented study selection or exclusion and created a list of studies to be included in the analysis (see Characteristics of included studies table). We resolved any disagreement through discussion or consultation with a third review author (PM). At this initial stage, we included studies where there was disagreement or where it was difficult to decide whether a study should be included.

We identified studies in which participants with an adequate diagnosis of FD (any valid criteria for FD with a normal upper gastrointestinal endoscopy) were randomized to receive any type of PPI versus another prespecified treatment or placebo. We considered and recorded the general characteristics and outcomes of each study using a screening form. We piloted the form on the first five studies included in the list and made changes if necessary. The screening form recorded the title, author, date, study design (only RCTs were included), population characteristics, intervention and control treatment duration, and outcomes according to the PICO question (population (P), intervention (I), comparison (C) and outcome(s) (O)). We provided a section for general comments, for any review author considerations and future discussion. We identified and removed duplicate studies at this initial stage.

We combined the results of the title and abstract screening performed by the review authors and document and discussed decisions about inclusion in the final full‐text screening list. To ensure that inclusion and exclusion criteria were properly interpreted and selection bias was minimized, three different review authors (AH, MIP and YY) performed the screening of the full texts. For papers in languages other than English, we requested translation by a translator from Cochrane with experience in systematic reviews and medicine. If the paper met the inclusion criteria, we asked the translator to extract data on the predefined data extraction form. The two review authors received the full‐text journal articles and translations to perform the screening. We collected the full‐text screening data in an Excel sheet and compared the results. We calculated 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 reported 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 or greater).

Data extraction and management

We used a standard data collection form for study characteristics and outcome data, which was piloted on five studies. Three review authors (AH, MIP and YY) extracted the following study characteristics from included studies.

• Methods: study design, total duration of study and run‐in, number of study centres and location, study setting, withdrawals, date of study.

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

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

• Outcomes: primary and secondary outcomes specified and collected, time points reported.

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

Two review authors (MIP and AH) independently extracted outcome data from the included studies. We noted in the Characteristics of included studies table if outcome data were reported in an unusable way. We resolved disagreements by consensus or by involving a third review author (PM). One review author (MIP) copied across the data from the data collection form into Review Manager 5 (RevMan 2014). Two review authors (YY and PM) double‐checked that the data were entered correctly by comparing the study reports with how the data were presented in the systematic review.

We collected blinding information by individually identifying the person blinded. If this information was not reported, we recorded 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 was missing at the end of data extraction process, we contacted the authors of the trials to recover the specific information. We included information on the following outcomes on the form: global symptoms, QoL and adverse events. We detailed common adverse events (such as such as diarrhoea, intolerance, nausea, headaches). We recorded participant demographics, treatment outcomes and adverse events as mean (standard deviation (SD)), n/N or % when applicable. We also collected information to assess possible risk of bias (randomization, concealment, blinding of participants and outcome assessors, incomplete outcome data, selective reporting and other biases).

Assessment of risk of bias in included studies

Three review authors (AH, MIP and YY) independently assessed the risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

We assessed the risk of bias according to the following domains: random sequence generation; allocation concealment; blinding of participants and personnel; blinding of outcome assessment; incomplete outcome data; selective outcome reporting and other bias. We graded 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 summarized the 'Risk of bias' judgements across different studies for each of the domains listed. We considered blinding separately for different key outcomes where necessary, for example, for unblinded outcome assessment, risk of bias for all‐cause mortality may be very different from a participant‐reported pain scale). Where information on risk of bias related to unpublished data or correspondence with a trialist, we noted this in the 'Risk of bias' table.

When considering treatment effects, we took into account the risk of bias of the studies that contributed to that outcome. We entered the data related to risk of bias into Review Manager 5 (RevMan 2014) and construct the 'Risk of bias' tables. We generated two figures with the Review Manager 5 software: a 'Risk of bias' summary, which represents all the judgements in a cross‐tabulation of study by entry and a 'Risk of bias' graph, which illustrates the proportion of studies complying with each of the judgements (low, high and unclear risk of bias).

Measures of treatment effect

We analyzed dichotomous data as risk ratio (RR) and continuous data as mean difference (MD) or standardized mean difference (SMD). We reported information regarding the study population follow‐up (participants enrolled and randomized) as the data collected from discontinued participants over the total number of participants for each arm (n/N). We reported the total number of participants with 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 reported the comparison of binary data as an RR with an associated 95% confidence interval (CI), and the NNTB. The number needed to treat was calculated according to the following formula: NNTB = 100/ARR and ARR = 100 × ACR × (1 ‐ RR), where ARR was the absolute risk reduction and ACR was the assumed control risk (Higgins 2011). Standardized MD (SMD) was used to pool post‐treatment quality scores from different studies, since different scales were used to assess QoL. However,post‐treatment scores and change from baseline scores from different quality scales were not pooled as final values and change scores should not be combined as standardized mean differences (Deeks 2011).

We collected continuous outcome data in three different ways:

• unit of measurement or, if unit of measurement could not be reported (i.e. visual analogue scale), we considered the data to be unit‐less;

• measure of central tendency: mean, median, mode;

• measure of variance, such as SD, standard error (SE), interquartile range or 95% CI.

If we were not provided with the raw data, we collected the reported analysis.

We collected change scores (the difference between scores before and after intervention) for comparison. We compared the final values of post‐treatment scores when change scores were not available. We undertook meta‐analyses only where this was meaningful (i.e. if the treatments, participants and the underlying clinical question were 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 noted that the data were skewed and considered the implication of this. Where multiple trial arms were reported in a single trial, we included only the relevant arms. If two comparisons (e.g. drug A versus placebo and drug B versus placebo) needed to be entered into the same meta‐analysis, we halved the control group to avoid double‐counting.

Unit of analysis issues

The unit of analysis was the individual participant included in the studies. We analyzed cross‐over studies as parallel‐group study only if the results were available before the cross‐over.

Dealing with missing data

We contacted investigators or study sponsors to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study was identified as an abstract only). We contacted study investigators whenever possible to request missing data. If this was not possible, or data were not provided, we considered that participants with missing data did not have the outcome of interest. We performed sensitivity analyses to assess robustness of the results relative to reasonable changes in the assumptions that were made.

We addressed 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 considered all EPICOT components (evidence, population, intervention, comparison, outcome and time stamp), as well as internal validity issues (such as compliance, cointervention and randomization) in the analysis.

We preidentified potential sources of heterogeneity that could be related to the criteria considered for the FD definition and differences in the demographics of the included population: time, duration and dose of PPI; undetected cointervention and differences in outcomes measurements. To address the most important possible sources of heterogeneity, we performed subgroup analysis.

We assessed 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 considered that heterogeneity might be not important when the I² statistic was between 0% and 40%; moderate heterogeneity when between 30% and 60%; substantial heterogeneity when between 50% and 90% and considerable heterogeneity when greater than 75%; or there was a P value of less than 0.1 for the Chi² test (Higgins 2011).

Assessment of reporting biases

We attempted to contact study authors and asked them to provide missing outcome data. Where this was not possible, and the missing data were thought to introduce serious bias, we explored the impact of including such studies in the overall assessment of results by a sensitivity analysis.

If we could pool more than 10 trials, we created and examined a funnel plot to explore possible publication biases. In the graph, the effect estimates were shown on the horizontal scale and the measure of study size on the vertical axis. Asymmetric funnel plots suggested small‐study effects, publication bias, delayed publication (time lag), selective reporting outcome or even differences in methodological quality. Egger's test was used for detecting significant funnel plot asymmetry (RevMan 2014).

Data synthesis

To be able to combine the results, we considered some possible differences before performing the meta‐analysis. We created a forest plot of the meta‐analysis for quantitative synthesis. We addressed differences in the research question, population, intervention, comparators, outcomes and methodology. We included different comparators (placebo or other active comparators such as H2RAs or prokinetics) in the analysis. However, we separated studies with different comparators into different subgroups for their analysis. For quantitative analysis, we performed a meta‐analysis using Review Manager 5 (RevMan 2014). We calculated a summary statistic for each study to describe the observed intervention effect. In the case of dichotomous outcomes, we calculated an RR and for continuous data we calculated an MD. When outcomes were assessed by different instruments, we used the SMD when possible. We calculated a summary (pooled) intervention effect estimate as a weighted mean of the intervention effects estimated in the individual studies. We chose the weights to reflect the amount of information that each study contained. For the combination of intervention effect estimates across studies, we assumed that the studies were not all estimating the same intervention effect, but estimating intervention effects that followed a distribution across studies. We therefore considered a random‐effects model meta‐analysis to be adequate (Kwok 2013). However, since the correct selection of the model is controversial, we also performed a fixed‐effect model analysis and compared the results of both. If these models had similar results, we considered that the chances of heterogeneity being present across the studies were low. Otherwise, if the results were different, we considered the random‐effects model as the most appropriate for the reasons previously described. To communicate the strength of evidence against the null hypothesis of no intervention effect, we used measures of dispersion (such as SE) to derive a CI and a P value.

Subgroup analysis and investigation of heterogeneity

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

• treatment duration (less than four weeks versus four weeks and versus greater than four weeks);

• dose (standard‐dose versus low‐dose of PPI);

• PPI subtype;

• H pylori status (H pylori‐negative versus H pylori‐positive);

• presence of reflux, defined as abnormal 24‐hour pH study (pH less than 4 for more than 4% of the 24‐hour recording versus pH less than 4 for less than 4% of the 24‐hour recording);

• risk of bias (low versus unclear versus high risk of bias);

• geographical location (e.g. western versus eastern studies);

• trial funding sources (industry‐sponsored versus non‐industry‐sponsored studies).

We assessed differences between subgroups with the I² statistic to test for subgroup interactions.

Sensitivity analysis

We performed sensitivity analyses using different summary statistics (RR versus odds ratio (OR)) and meta‐analytic models (fixed‐effect versus random‐effects), to assess the robustness of our results.