Types of studies

We will consider randomised controlled trials (RCTs), as they are considered the gold standard for clinical questions of interventions. We will include RCTs reported as full text, as abstract only and as unpublished data.

We will not include cluster‐randomised, cross‐over design, and quasi‐randomised controlled trials since these study designs could either lead to an undesirable risk of bias or be unjustifiable given the nature of the intervention.

Types of participants

We will consider RCTs involving adults (16 years and older) with a diagnosis of Helicobacter pylori (H. pylori) infection, and confirmed by urea breath test, stool antigen test, endoscopic biopsies with rapid urease reaction, histology, or culture.

Types of interventions

We will include RCTs that compared triple clarithromycin‐based therapy, composed of (i) PPI standard* or double standard dose twice daily plus (ii) clarithromycin 500 mg twice daily plus (iii) amoxicillin 1 g twice daily or metronidazole 500 mg twice daily for 14 days versus any of the following regimens:

• Bismuth quadruple therapy composed of (i) PPI standard dose twice daily plus (ii) bismuth subcitrate 120 mg to 300 mg or 420 mg or bismuth subsalicylate 300 mg or 524 mg four times daily plus (iii) tetracycline 500 mg four times daily.

• Clarithromycin‐based concomitant therapy composed of (i) PPI standard dose twice daily plus (ii) clarithromycin 500 mg twice daily plus (iii) amoxicillin 1 g twice daily plus (iv)

• Clarithromycin‐based sequential therapy, in which the first sequence is composed of (i) PPI standard dose plus (ii) amoxicillin 1 g twice daily for 5 days followed by a second sequence composed of (i) PPI standard dose plus (ii) clarithromycin 500 mg twice daily plus (iii) either metronidazole 500mg twice daily or tinidazole 500 mg twice daily for additional 5 days ‐ completing a total of 10 days.

• Clarithromycin‐based hybrid therapy, in which the first sequence is composed of (i) PPI standard dose plus (ii) amoxicillin 1 g twice daily for 7 days followed by a second phase composed of (i) PPI standard dose plus (ii) amoxicillin 1 g twice daily plus (iii) clarithromycin 500 mg twice daily plus (iv) either metronidazole 500 mg twice daily or tinidazole 500 mg twice daily for additional 7 days ‐ completing a total of 14 days.

*Standard dose of PPI includes one of the oral daily options: lansoprazole 30 mg, omeprazole 20 mg, pantoprazole 40 mg, rabeprazole 20 mg or esomeprazole 20 mg.

Types of outcome measures

We will consider the outcomes detailed below. Reporting of the primary and/or secondary outcomes listed here will not be an inclusion criterion for the review. We will contact trial authors if a trial has not reported their eradication rates.

Electronic searches

We will conduct a literature search to identify all published or unpublished RCTs that fulfil our eligibility criteria. The literature search will identify potential studies in all languages, with no limits as to the year of publication. 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) (via Ovid) (Appendix 1)

• MEDLINE (1946 to present) (via Ovid) (Appendix 2)

• Embase (1974 to present) (via Ovid) (Appendix 3)

• CINAHL (1982 to present)

• LILACS (1982 to present)

Searching other resources

We will check reference lists of all primary studies and review articles for additional references. We will contact authors of identified trials and ask them to identify other published and unpublished studies. We will also contact manufacturers and experts in the field, asking them for additional published or unpublished trials. We will check the articles citing the identified studies in order to find additional references.

We will search for errata or retractions from eligible trials on PubMed and report the date this was done within the review. We will search the grey literature databases and clinical trials registers below.

Selection of studies

Two review authors (RRV, LESF) will independently screen titles and abstracts on Covidence in order to identify and include all potential studies, which will be labelled as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. We will retrieve the full‐text study reports/publications, and two review authors (RRV, LESF) will independently screen the full text and identify studies for inclusion and identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement by consulting a third review author (RR or RLP). 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

Two review authors (RRV, PM) will extract study characteristics from the included studies. We will use the Covidence electronic form, based on the Cochrane standard data collection form, which will be tested a priori on at least one study in the review. We will extract the following study characteristics.

1. Miscellaneous details of the study: report title, year of publication, author contacts, and publication type (abstract or full report).

2. Methods: aim of study, study design, unit of allocation, start and end dates, duration of participation, and ethical approval.

3. Participants: population description, setting, inclusion criteria, exclusion criteria, age, method of recruitment, informed consent obtained, total number randomised, baseline imbalances, withdrawals and exclusions, gender, race/ethnicity, underlying indication for treatment, diagnostic criteria, subgroups measured and reported, and other relevant sociodemographics.

4. Interventions: number randomised in each group, dose, duration of treatment period, timing, delivery, co‐interventions, and compliance.

5. Outcomes: primary and secondary outcomes specified and collected, time points measured, outcome definition, person measuring/reporting, unit of measurement, scales, imputation of missing data.

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

Two review authors (RRV, LESF) will independently extract outcome data from included studies. We will note in the 'Characteristics of included studies' table if outcome data are reported in an unusable way. We will resolve disagreements by consensus, or by involving a third person (RR or RLP). One review author (RRV) will cross‐copy the data from the data collection form into the Review Manager file. We will double‐check that the data is entered correctly by comparing the study reports with how the data are presented in the systematic review. A second review author (LESF) will spot‐check study characteristics for accuracy against the trial report.

Assessment of risk of bias in included studies

Two review authors (RRV, RLP) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019). Any disagreement will be resolved by discussion or by involving a third person (RR OR LESF). We will assess the risk of bias according to the following domains (sources of bias).

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 sources of bias.

We will judge each potential source of bias as high, low or unclear and provide a quote from the study report together with a justification for our judgment from the 'Risk of bias' table. We will judge the following domains separately for different outcomes: blinding of participants and personnel, blinding of outcome assessment, and Incomplete outcome data.

Measures of treatment effect

We will analyse dichotomous data (eradication rates, occurrence of adverse events) as risk ratios (RRs) providing 95% confidence intervals (CIs) for the results. 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 is necessary.

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 that trialists indicate when 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 implications.

Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons are present (e.g. drug A versus placebo and drug B versus placebo), then they must be entered into the same meta‐analysis, we will halve the control group to avoid double‐counting.

Unit of analysis issues

The unit of analysis will be the individual, with a single measurement of each outcome for each participant being collected and analysed.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing outcome data whenever it is possible (e.g. when a study is identified as abstract only). If we cannot obtain the outcome data, we plan to analyse whether the missing data is "not missing at random" or "missing at random". If the data is judged to be "not missing at random", we will input the missing data with replacement values, treating these as if they were observed (e.g. imputing an assumed outcome such as assuming all were poor outcomes). If the data is judged to be "missing at random" we will analyse only the available data, i.e. ignoring the missing data (Higgins 2019).

We intend to perform sensitivity analyses to assess how sensitive results are to reasonable changes in the assumptions that are made. Furthermore, we will address the potential impact of missing data on the findings of the review in the Discussion section (Higgins 2019).

Assessment of heterogeneity

We will assess clinical, methodological and statistical heterogeneity among the included trials. We will use the Chi² test (P < 0.10 indicates signIficant heterogeneity) and the I² statistic to measure statistical heterogeneity among the trials in each meta‐analysis Higgins 2003). If we identify substantial heterogeneity, we will explore it by prespecified subgroup analysis. We will consider an I² value greater than 50% as substantial heterogeneity (Higgins 2011). We will use the random‐effects model for meta‐analyses, provided we expect clinical and methodological heterogeneity between studies, using Review Manager software version 5.3 ( Review Manager 2014).

We will use the Inverse Variance for Heterogeneity (IVHET) model proposed by Doi 2015 and colleagues in a sensitivity analysis. This method is a variation of random‐effects and fixed‐effects models. Inverse Variance for Heterogeneity keeps the weight of the studies as a fixed‐effects model does, allowing a wider confidence interval as a random‐effects model does. In practice, we have the same point estimate as a fixed‐effects model, but wider confidence intervals than fixed‐effects, except when heterogeneity is zero. We will use the STATA package software version 15.1 (StataCorp 2017) for this purpose.

Assessment of reporting biases

We will attempt to contact study authors, asking them to provide missing outcome data. When this is not possible, and the missing data are thought to introduce serious bias, the impact of including such studies in the overall assessment of results will be explored by excluding the study in a sensitivity analysis.

If we are able to pool 10 or more trials, we will create and examine funnel plots to explore possible publication biases.

Data synthesis

We will combine the results across studies, undertaking a random‐effect model meta‐analysis for dichotomous and continuous outcomes by default, as we expect some clinical heterogeneity among them.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses for the primary outcomes.

1. Level of clarithromycin resistance: Regions with high clarithromycin resistance (>15%), versus regions of high (>15%) dual clarithromycin and metronidazole resistance, versus regions with low clarithromycin resistance (<15%) (Malfertheiner 2017).

2. Type of PPI used, considering the pharmacokinetic differences: Pantoprazole has faster action and maintains higher concentration levels over a longer period of time than omeprazole and lansoprazole (Shin 2013). Rabeprazole has proven superior to omeprazole and lansoprazole in urease inhibition (Barth 2002). There is also an omeprazole isomer that shows better stability and greater potential than omeprazole (Hu 2017). The main enzyme in the metabolism of PPIs is CYP2C19, and the effects of PPIs depend on cytochrome P450 and CYP2C19. CYP2C19 polymorphism is highly varied among different ethnic populations and its genotype is a key factor for H. pylori eradication in patients using triple therapy with omeprazole or lansoprazole, and has no significant effect on triple therapy with rabeprazole or esomeprazole (Kuo 2014).

3. Type of test used to assess eradication: urea breath test, versus stool antigen test, versus endoscopic methods. In terms of analysing the diagnostic tests, the urease breath test is the most recommended for its high sensitivity and specificity because it is expected to have the best results. The stool antigen test also has high sensitivity and specificity, as long as the monoclonal antibody‐based ELISA method is used. The endoscopic urease test method has a higher chance of false‐negatives, especially in patients with gastrointestinal bleeding, or in those that have been using bismuth and/or an antibiotic for less than four weeks, as well as those that have been using a PPI for less than two weeks (Malfertheiner 2017). We will use the outcome of successful eradication rate in subgroup analysis.

Sensitivity analysis

We will perform sensitivity analysis, defined a priori, to assess the robustness of our conclusions for the primary outcomes, excluding:

• trials with a high or unclear risk of bias for at least one RoB domain.

• trials with missing data judged as "not missing at random", in which we inputted the missing data with replacement values (computing as poor outcomes).

We will perform an additional sensitivity analysis using the Inverse Variance for Heterogeneity (IVHET) model proposed by Doi 2015 and colleagues. This method keeps the weight of the studies as a fixed‐effect model does, allowing a wider confidence interval as a random‐effects model does. In practice, we have the same point estimate than FE model, but wider confidence intervals than FE, except when heterogeneity is zero. We will use the STATA package software version 15.1(StataCorp 2017) for this purpose.

Summary of findings and assessment of the certainty of the evidence

We will create a 'Summary of findings' table adding all the outcomes stated under 'Types of outcome measures' for each comparison of clinical interest.

Two review authors (LESF, RRV) will independently assess the certainty of the evidence. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to evaluate the certainty of a body of evidence as it relates to the studies, which contributes data to the synthesis of each outcome. We will report the certainty of evidence as either high, moderate, low, or very low as described in Section 8.5 and 8.7, and Chapters 11 and 12, of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019). We will use GRADEpro software to create 'Summary of findings' tables (GRADEprofiler). We will justify all decisions to downgrade the certainty of the evidence by the use of footnotes and present useful comments for readers when necessary.