Types of studies

All experimental or interventional studies, without any limitation in type and details, that studied the effectiveness of three classes of drugs (antacids, sucralfate and bismuth salts) in the improvement of either individual or global dyspepsia.

Types of participants

We will include all participants over 18 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 , IV or Lancet Working Group) .

Studies that included other gastrointestinal diseases, such as peptic ulcer, organic dyspepsia and reflux disease will be excluded.

This may be confirmed by checking if upper gastrointestinal endoscopy or any other diagnostic modality was performed in participant recruitment for the study.

If a study included populations with different conditions, we will only include participants with functional dyspepsia.

Participants in the trials that did not have any positive findings at endoscopy or barium study, symptoms of hiatus hernia, less than five gastric erosions or mild duodenitis will be included. We will include all participants, naive or with a history of treatment of FD and we will include all types of participant that were recruited in studies such as participants in primary care, secondary or tertiary care, or convenience sample.

Types of interventions

We will include trials comparing oral administration of any dose of any available drug (antacids, sucralfate and bismuth salts) with placebo.

Types of outcome measures

Outcomes in FD may be measured by an ordinal or dichotomous (improved/not improved) scale. In ordinal measures, such as the five‐point Likert scale, we will assume that they are continuous measures or variables and, for interpretation, we will use standardized mean differences.

In ordinal scales with a variety of answers, we will assume that scores above the mean are improved and those lower than the mean are not improved.

Electronic searches

We will conduct a comprehensive literature search to identify all published and unpublished randomised controlled trials with no language restriction. We will search the following electronic databases to identify potential studies:

• Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library) Appendix 1;

• MEDLINE 1966 to present Appendix 2; and

• Embase 1980 to present Appendix 3.

Independent reviewers also will conduct a search for ongoing trials on the ClinicalTrials.gov (clinicaltrials.gov) and World Health Organization International Clinical Trials Registry Platform (WHO ICTRP) (apps.who.int/trialsearch). For grey literature we will search in SIGLE (System for Information on Grey Literature in Europe) (www.cf.ac.uk/insrv/eresources/databases/sigle.html) and New York Academic of Medline Library Grey literature collection (www.nyam.org/library/pages/grey_literature_report).

Searching other resources

We will handsearch the published abstracts from the conference proceedings in United European Gastroenterology Week (published in Gut) from 2005 to 2016. We will handsearch references cited in studies found by the above search to identify further relevant trials.

Selection of studies

Two independent reviewers will screen the titles and abstracts of papers to assess the eligibility for inclusion in the review. 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 a third person (PA). Information on study design, participant characteristics, measurement of FD, adjustment for potential confounders, and estimates of associations will be extracted independently by two reviewers. Discrepancies will be resolved by discussion. We will estimate the agreement level for all steps: title, abstract and full‐text screening and data extraction by discussion and reach a consensus.

We will use Endnote to collect and manage citations. Since there may be several published papers with the same result, we will exclude duplicate and similar results and collate all results. Process of study selections will be presented in PRISMA diagram form and we will clarify the characteristics of excluded studies.

Data extraction and management

Data will be extracted independently using a standard form (which has been piloted by at least one study) by two reviewers to record study characteristics and outcome data. Consensus will be used for inconsistencies between authors. All numeric data from tables, graphs or figures will be confirmed by a second reviewer. In the case of missing data in the included studies, investigators will be contacted (by email, letter and/or fax, phone) to prepare the missing information.

Two review authors will extract the following study characteristics from the 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: number of participants, mean age, age range, gender, severity of condition, diagnostic criteria, inclusion criteria, exclusion criteria.

3. Interventions: intervention, comparison, concomitant medications, excluded medications (with or without placebo) and duration of treatment and follow‐up time.

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

Notes: Funding for trial, notable conflicts of interest of trial authors, name of the author, year of publication, location/country and ethics approval.

Assessment of risk of bias in included studies

Methodological quality will be assessed independently by at least two review authors according to the Cochrane Handbook for Systematic Reviews of Interventions and Cochrane Review guidelines, for each key outcome variable. Review authors will independently assess the risk of bias within each included study based on the following domains with ratings of ‘Yes’ (low risk of bias); ‘No’ (high risk of bias) and ‘Unclear’ (uncertain risk of bias):

• Sequence generation;

• Allocation concealment;

• Blinding (we will collect blinding information by individually identifying the person blinded: single‐blind, double‐blind and triple‐blind);

• Incomplete outcome data;

• Selective outcome reporting.

We will use RevMan software for creation of a 'risk of bias' table. Also, we will create two types of figures with RevMan software for clarifying the risk of bias:

1. A ’Risk of bias’ graph, which demonstrates the proportion of studies complying with each of the judgments (’low’, ’high’ and ’unclear’ risk of bias); and

2. A ’Risk of bias’ summary, which shows all of the judgments in a cross‐tabulation of study by entry.

Measures of treatment effect

Analysis of dichotomous data will be recorded as risk ratio (RR) and continuous data as mean difference (MD) or standardized mean difference (SMD). Comparison of binary data will be reported 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 test 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. If raw data are not accessible, we will report the individual study analysis.

Continuous data measures will be collected after treatment. Change scores will also be collected (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. If the study reported median or inter‐quartile range, it is reasonable to assume that the data were skewed. If we suspect the data is skewed, we will exclude studies that do not contain mean and standard deviation; otherwise, median and interquartile range will be used instead of mean and standard deviation, respectively. Where several intervention arms were included in a single study, we will consider only the relevant arms. If two arms of trial were compared to a single placebo group, but reported separately in the text, to avoid double counting in a single meta‐analysis, we will halve the placebo number.

Unit of analysis issues

To reduce the possibility of unit of analysis error, we will take into account the level at which randomisation occurred.

If we face trials with cluster randomizations, we may include each participant as a case in general analysis, but we will mention the detail of such a study in the results and we will conduct a sensitivity analysis to assess the validity of the data. In cross‐over trials, we will consider each part of the study as a parallel arm if a washout period was conducted.

Dealing with missing data

In the first instance, authors will be contacted to provide missing data or clarification of data from included studies (e.g. when a study is identified as an abstract only). Missing data and drop‐outs or attrition or both will be assessed for each included study, and the extent to which the results/conclusions of the review could be altered by the missing data will be assessed and discussed.

Assessment of heterogeneity

Clinical heterogeneity will be assessed by comparing the distribution of important participant factors between trials (e.g. administered dose of drugs, duration of administration of all three drugs), and trial factors (randomization concealment, blinding of outcome assessment, losses to follow‐up, treatment type, cointerventions). Within‐ and between‐study heterogeneity will be assessed using Cochran’s Q‐statistic and the heterogeneity test will be used to assess the null hypothesis that all studies evaluated the same effect. The effect of heterogeneity is quantified using the I² statistic which provides a measure of the degree of inconsistency between studies. If we identify substantial heterogeneity, we will explore it with the prespecified subgroup analysis. We will assess heterogeneity by the I² statistic where values of 0% to 40%, 30% to 60%, 50% to 90%, and 75% to 100% will be considered as representing low, moderate, substantial and high level of heterogeneity, respectively.

Assessment of reporting biases

Funnel plots (estimated differences in treatment effects against their standard error) will be drawn if sufficient (10 or more) studies are found. We will perform a statistical test of the funnel plot using this approach (Egger Test).

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.

We will provide data regarding study type, comparison, study quality and number of participants involved. We will create a forest plot of the meta‐analysis for quantitative synthesis. We will include different comparators (placebo or other active comparators such as H2‐receptor antagonists, or prokinetics). However, we will separate studies with different comparators into different subgroups for their analysis. For quantification of calculations, a meta analysis will be performed using RevMan 5 (RevMan 2012). We will use appropriate statistical methods (Curtin 2002) to combine the parallel and cross‐over trials. A summary statistic will be calculated for each trial in order to describe the observed intervention effect. For 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. A random‐effects model will be used. Meta‐regression or sub‐group analysis will be used in the case of statistical heterogeneity. We will perform analyses with a fixed‐effect model in order to test for heterogeneity. P values less than 0.05 will be considered statistically significant. All statistical tests will be two‐sided.

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. People suffering from functional dyspepsia according to different definitions (e.g. Rome III, Rome II criteria) (ROME criteria).

2. People suffering from functional dyspepsia by category subtype (e.g. epigastric pain type versus postprandial distress type).

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

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

5. Naive versus treatment‐experienced.

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

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

8. Different control groups (placebo, H2‐receptor antagonists, antacids, prokinetics).

Sensitivity analysis

Sensitivity analyses will be conducted to assess the impact of the study quality. A sensitivity analysis compares studies fulfilling the 'quality' criteria compared to the inclusion of all studies regardless of quality and asks the question, 'Are the findings robust to the decisions made in the process of obtaining them?' This involves the removal of studies that meet certain criteria (e.g. poor‐quality, commercial sponsorship, conference abstract) to determine the effect of their inclusion on the overall result. This will be undertaken by including:

1. Only those with low risk of selection bias (associated with sequence generation or allocation concealment);

2. Only those with low risk of performance bias (associated with issues of blinding);

3. Only those with low risk of attrition bias (associated with completeness of data).

4. Fixed‐effect versus random‐effects models.