Study design

We will conduct a systematic review of RCTs with meta-analysis and trial sequential analysis (TSA) and follow the recommendations by the Cochrane Collaboration [32] and the Preferred Reporting Items for Systematic Review and Meta-Analysis (PRISMA) statement [33].

Study registration

This protocol has been prepared according to the Preferred Reporting Items for Systematic Review and Meta-Analysis Protocols (PRISMA-P) guidelines [34] (checklist included as Additional file 1), and the review has been registered in the International Prospective Register of Systematic Reviews (PROSPERO) (https://www.crd.york.ac.uk/prospero/; registration number CRD42017055676).

Criteria for considering studies for this review

Types of studies

RCTs will be included regardless of publication source, status and language. Quasi-randomised trials and cross-over trials will be excluded.

Types of participants

Adult hospitalised acutely ill patients (as defined by the included trials) with high risk of gastrointestinal bleeding including (but not limited to) medical and surgical ICU patients, patients in intermediate care units, patients in coronary care facilities, neurosurgical patients (head and spine), cardiothoracic surgical patients, organ transplanted patients, major abdominal/vascular/orthopaedic (pelvis and hip) surgery, burn injured patients (incl. thermal injury), patients with active malignant haematological illness, patients with acute kidney injury, patients with acute hepatic failure, patients receiving high dose steroids (at least 0.3 mg/kg/day of prednisolone equivalent) and patients with sepsis.

Trials including children (as defined by the original trials) will be excluded unless data can be separately extracted for adults only.

Types of interventions

Experimental intervention: any type of PPI (omeprazole, lansoprazole, dexlansoprazole, esomeprazole, pantoprazole and rabeprazole) or H2RA (nizatidine, famotidine, cimetidine and ranitidine) in any dose, formulation, timing and duration

Control intervention: placebo or no prophylaxis

Types of outcome measures

Primary outcomes

All-cause mortality

Proportion of participants with one or more serious adverse event (SAE), defined as any untoward medical occurrence that resulted in death, was life-threatening or prolonged existing hospitalisation, resulted in persistent or significant disability or any important medical event, which may have jeopardised the patient [35]

Proportion of participants with ‘clinically important gastrointestinal bleeding’ as defined in the included trials (not including ‘overt GI bleeding’)

Secondary outcomes

Proportion of participants with C. difficile enteritis (yes/no), as defined in the included trials

Proportion of participants with myocardial infarction (yes/no), as defined in the included trials

Proportion of participants with hospital-acquired pneumonia (yes/no), as defined in the included trials

Quality-of-life (any continuous scale used in the included trials)

Assessment time points

All outcomes will primarily be assessed at the time point closest to 90 days. Secondly, we will assess all outcomes at the maximum time of follow-up.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases:

Cochrane Library

MEDLINE

EMBASE

Epistemonikos

Science Citation Index

BIOSIS

We will additionally search databases of ongoing trials including Clinical-Trials.gov (http://clinicaltrials.gov/), metaRegister of Controlled Trials (http://www.isrctn.com/page/mrct), the EU Clinical Trials register (https://www.clinicaltrialsregister.eu/) and the World Health Organization (WHO) International Clinical Trials Registry Platform Search Portal (http://apps.who.int/trialsearch/).

The tentative Medline search strategy is available in Additional file 2. To continuously identify newly published studies, we will apply PubMed’s ‘My NCBI’ (National Center for Biotechnology Information) email alert service. Before we submit the final review draft to an international peer-reviewed journal, we will perform an updated search on all specified databases. If we identify new trials, these will be assessed and if relevant incorporated in our review before submission of the final review draft. If we detect additional relevant keywords during any of the electronic or other searches, we will modify the electronic search strategies to incorporate these terms and document the changes.

Searching other resources

We will hand-search the reference list of relevant trials and other systematic reviews and meta-analyses on stress ulcer prophylaxis in adult hospitalised acutely ill patients.

Unpublished trials will be sought identified. Authors will be contacted for additional data if relevant.

Data collection and analysis

Selection of studies

Two review authors (SM, AG or CTA) will independently screen the abstract, title or both, of every record retrieved, to determine which trials should be assessed further. We will assess all potentially relevant articles as full text. We will resolve any discrepancies through consensus or recourse to a third review author (MHM). If resolving disagreement is not possible, the article will be added to those ‘awaiting assessment’ and we will contact study authors for clarification. We will present an adapted PRISMA flowchart of study selection [33]; see Additional file 3.

Data extraction and management

Two review authors (SM, AG or CTA) will independently extract information from each included trial using a predefined data extraction form. The extracted information will include trial characteristics (year of publication, duration, country), characteristics of the trial participants (inclusion criteria and exclusion criteria), type of intervention/control (name, dosing, duration and route of administration), type of control (name, dosing, duration and route of administration), outcomes and risk of bias.

In the event of duplicate publications, companion documents or multiple reports of a primary study, we will maximise yield of information by comparing all available data and use the most complete dataset aggregated across all known publications. In case of doubt, the publication reporting the longest follow-up associated with our primary or secondary outcomes will be given priority.

Assessment of risk of bias in included studies

We will assess the risk of systematic errors (bias) of the included trials according to the Cochrane Handbook [32]. The assessment will be performed independently by two authors (SM, AG or CA). Disagreements will be resolved by consensus upon consultation with a third author (MHM).

The following domains will be assessed: (1) random sequence generation, (2) allocation concealment, (3) blinding of participants and personnel, (4) blinding of outcome assessment, (5) incomplete outcome data, (6) selective reporting and (7) other bias, including baseline imbalance, early stopping and bias due to vested financial interest or academic bias. If one or more domains are judged as being high or unclear, we will classify the trial as having overall high risk of bias [32]. We will assess the domains ‘blinding of outcome assessment’, ‘incomplete outcome data’ and ‘selective outcome reporting’ for each outcome. Thus, we will be able to assess the bias risk for each result in addition to each trial.

We will base our primary conclusions as well as our presentation in the ‘Summary of findings table’ section on the results of our primary outcomes with low risk of bias.

The risk of bias will be depicted in a ‘risk of bias summary’ figure, reviewing the authors judgements (according to the Cochrane handbook [32]) about each included risk of bias item for each included study (red: high risk, green: low risk, yellow: unclear).

Measures of treatment effect

We will calculate relative risks (RRs) with 95% confidence intervals (CIs) and mean differences (MDs) with 95% CIs for dichotomous outcomes and continuous outcomes, respectively.

Dealing with missing data

The relevant authors will be sought contacted for missing outcome data. Sensitivity analysis using imputations of missing outcome data of dichotomous outcomes in best-worse and worse-best case scenarios will be performed assuming:

1) All patients lost to outcome assessment (follow-up) in the intervention group did not experience the outcome of interest, while all patients lost to outcome assessment (follow-up) in the control group did experience the outcome of interest. 2) All patients lost to outcome assessment (follow-up) in the intervention group did experience the outcome of interest, while all patients lost to outcome assessment (follow-up) in the control group did not experience the outcome of interest.

When analysing continuous outcomes with missing data, we will use imputations of missing outcome data in best-worse and worse-best case scenarios [36] assuming:

1) All patients lost to outcome assessment (follow-up) in the intervention group have an outcome being the group mean plus two standard deviations (SDs) of the group mean, and all patients lost to outcome assessment (follow-up) in the control group will be the group mean minus two SDs. 2) All patients lost to outcome assessment (follow-up) in the intervention group have an outcome being the group mean minus two SDs of the group mean, and all patients lost to outcome assessment (follow-up) in the control group will be the group mean plus two SDs.

Assessment of heterogeneity

Based on a previous systematic review and meta-analysis where statistical and clinical heterogeneity was limited, we plan to report pooled effect estimates [27]. We will primarily inspect forest plot for signs of statistical heterogeneity. We will secondly use D-squared and I-squared statistics to describe heterogeneity among the included trials. We will use and report a fixed-effect model if I-squared = 0 and use and report the results of both random-effects model and fixed-effect model if I-squared >0. We will report the most conservative estimate if the intervention effects differ in the two models and the broadest confidence interval if they concur [36].

Assessment of reporting bias

We will use a funnel plot to assess reporting bias if ten or more trials are included. For dichotomous outcomes, we will test asymmetry with the Harbord test [37]. For continuous outcomes, we will use the regression asymmetry test [38] and the adjusted rank correlation [39].

Data synthesis

We will use Review Manager Software (RevMan 5.3) as statistical software.

We will calculate summary estimates (conventional meta-analyses) as outlined above. We will use and report results based on the analysis of intention-to-treat populations if available.

Trial sequential analysis

We will conduct TSA in order to assess the risk of random errors [40,41,42]. Cumulative meta-analyses are at risk of producing random errors due to sparse data and multiple testing of accumulating data [32, 43,44,45,46,47,48,49,50]. TSA allows to estimate the required information size (the number of participants) needed to detect or reject an a priori pre-specified realistic intervention effect in a meta-analysis and the TSA-adjusted CIs [51, 52]. The required information size will take into account the event proportion in the control group, the assumption of a plausible RR reduction and the heterogeneity variance of the meta-analysis [52, 53]. We will use conservative estimations of the anticipated intervention effect estimates to reduce the risk of random error [36]. In brief, as we have three co-primary outcomes and four secondary outcomes, we will consider a P < 0.025 and P < 0.020 as statistically significant, respectively [35].

We will apply trial sequential monitoring boundaries according to an a priori 15% relative risk difference (reduction or increase), with a family-wise error rate (FWER) equal to an alfa of 5%, beta 90% and a control event proportion suggested by all the trials reporting the outcome in question. TSA-adjusted CIs will be provided [42].

Subgroup analysis and investigation of heterogeneity

We will use Chi-squared test to provide an indication of heterogeneity between trials, with P = 0.10 considered significant.

We plan to conduct the following subgroup analyses:

1. Comparing estimates of the pooled intervention effect in trials with overall low risk of bias vs. overall high risk of bias. Hypothesised direction of sub-group effect: increased beneficial intervention effect in the trials with overall high risk of bias 2. Comparing estimates of the pooled intervention effect in trials using PPI vs. H2RA. Hypothesised direction of sub-group effect: increased beneficial intervention effect in trials using PPI 3. Comparing estimates of the pooled intervention effect in trials using placebo vs. no treatment. Hypothesised direction of sub-group effect: increased beneficial intervention effect in trials using no treatment 4. Comparing estimates of the pooled intervention effect in the included subpopulations of adult hospitalised acutely ill patients. Hypothesised direction of sub-group effect: increased beneficial intervention effect in some subpopulations 5. Comparing estimates of the pooled intervention effect in ICU patients vs. non-ICU patients. Hypothesised direction of sub-group effect: increased beneficial intervention effect in ICU patients vs. non-ICU patients

Sensitivity analysis

We will conduct sensitivity analysis by performing empirical continuity adjustments in the zero event trials.

Summary of findings table

We will assess the overall quality of evidence for each outcome measure according to the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) approach [54]. In brief, we will downgrade the quality of evidence (our confidence in the effect-estimates) for an intervention for identified risks of bias, inconsistency (unexplained heterogeneity), indirectness (including other patient populations or use of surrogate outcomes), imprecision (wide confidence interval around the effect estimate) and publication bias. Accordingly, the overall quality of evidence will be rated ‘high’, ‘moderate’, ‘low’ or ‘very low’.