Experimental group

We will include any type of beta‐blockers, both administered as intravenous therapy and as oral administration, as experimental intervention (non‐selective beta‐blockers (propranolol, oxprenolol, sotalol, timolol); selective beta₁‐blockers (metoprolol, bisoprolol, acebutolol, atenolol, esmolol); and beta‐blockers which are combined alpha‐ and non‐selective beta‐blockers (carvedilol)) commenced in the acute or subacute phase of myocardial infarction.

Control group

We will accept placebo or no intervention as control interventions.

Co‐interventions

We will accept any co‐intervention (medical therapy as well as revascularisation strategy) provided they are intended to be delivered similarly to the experimental and the control groups.

Primary outcomes

• All‐cause mortality.

• Major cardiovascular event defined as a composite outcome consisting of either cardiovascular mortality (defined by trialists) or myocardial infarction (defined by trialists). Additionally, we will assess cardiovascular mortality and myocardial infarction separately as secondary outcomes (see below).

• Serious adverse event defined as any untoward medical occurrence that: resulted in death, was life‐threatening, was persistent, led to significant disability, prolonged hospitalisation, or jeopardised the participant (ICH‐GCP 1997).

Secondary outcomes

• Quality of life measured on any valid scale, such as the Short‐Form (36) Health Survey (SF‐36) (Ware 1992).

• Angina measured on any valid scale, such as the Canadian Cardiovascular Angina Score (CCS) (Campeau 1976).

• Cardiovascular mortality.

• Myocardial infarction.

We will narratively report adverse events, presenting them in a table.

We will estimate all outcomes at two different follow‐ups.

• Outcomes assessed at the follow‐up time point closest to one month after randomisation (this will be the follow‐up time point of primary interest).

• Outcomes assessed at maximum follow‐up.

We chose one‐month follow‐up as our primary follow‐up time point because the possible effects of beta‐blockers needs some time to show (one month), and the follow‐up period is not too long so other factors unrelated to the given trial affecting the outcomes might decrease the statistical power, i.e. the results are 'diluted' by events (e.g. traffic accidents) unrelated to the trial.

Overall risk of bias

• Low risk of bias: the outcome result will be classified as at overall 'low risk of bias' only if all of the bias domains described in the above paragraphs are classified as at low risk of bias.

• High risk of bias: the outcome result will be classified as at 'high risk of bias' if any of the bias risk domains described above are classified as at 'unclear' or 'high risk of bias'.

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 on the results of our primary outcomes with low risk of bias.

Dichotomous outcomes

We will calculate risk ratios (RR) with 95% confidence intervals (CI) and TSA‐adjusted CIs (Thorlund 2011) for dichotomous outcomes.

Continous outcomes

We will calculate the mean differences (MD) with 95% CIs and TSA‐adjusted CIs (Thorlund 2011) for continuous outcomes. We will use the standardised mean difference when the trials all assess the same outcome but measure it in a variety of ways (e.g. different scales) (Higgins 2011).

Dichotomous outcomes

If included studies have used rigorous methodology (i.e. reporting on outcomes for all participants or multiple imputation to deal with missing data), we will use these data in our primary analysis (Sterne 2009), otherwise we will use the last observation carried forward to handle missing data or if the proportion of dropouts are less than 5%. We will not impute missing values for any outcomes in our primary analysis.

Continous outcomes

If included studies have used rigorous methodology (i.e. reporting on outcomes for all participants or multiple imputation to deal with missing data), we will use these data in our primary analysis (Sterne 2009), otherwise we will use the last observation carried forward to handle missing data or if the proportion of dropouts are less than 5%. We will not impute missing values for any outcomes in our primary analysis. If standard deviations (SD) are not reported, the SDs will be calculated using data from the trial if possible. We will not use intention‐to‐treat data if the original report did not contain such data.

In our sensitivity analysis for dichotomous and continuous outcomes, we will impute data, see below and Sensitivity analysis.

Best‐worst and worst‐best case scenarios

To assess the potential impact of the missing data for dichotomous outcomes, we will perform the two following sensitivity analyses.

1. 'Best‐worst' case scenario: it will be assumed that all participants lost to follow‐up in the experimental group survived, had no serious adverse event, had no cardiovascular event, and had no adverse events; and all those with missing outcomes in the control group have not survived, had a serious adverse event, had a cardiovascular event, and had adverse events.

2. 'Worst‐best' case scenario: it will be assumed that all participants lost to follow‐up in the experimental group did not survive, had a serious adverse event, had a cardiovascular event, and had adverse events; and all those with missing outcomes in the control group survived, had no serious adverse event, had no cardiovascular event, and had no adverse events.

Results from both scenarios will be presented in our publication.

To assess the potential impact of missing SDs for continuous outcomes, we will perform the following sensitivity analysis.

1. Where SDs are missing and not possible to calculate, we will impute SDs from trials with similar populations and low risk of bias. If no such trials can be found, we will impute SDs from trials with a similar population. As the final option we will impute SDs from all trials.

Meta‐analysis

We will accept both end scores and change from baseline scores analysing continuous outcomes. If both end scores and change from baseline scores are reported then we will use end scores. If only change values are reported the results will be analysed together with end scores (Higgins 2011a).

We will undertake this systematic review according to the recommendations stated in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) and according to Jakobsen 2014 and Keus 2010. We will use the statistical software Review Manager 5 (RevMan 2014) provided by Cochrane to meta‐analyse data. We will use Stata (Stata 2015) in case of zero‐event trials, where Review Manager 5 zero‐event handling (replacing 0 with a constant of 0.5) is not sufficient (e.g. in cases with skewed number of participants between groups, which we will handle with reciprocal zero‐event handling according to Sweeting 2004, and in case metaregression (post hoc) is needed).

Assessment of significance

We will assess our intervention effects with both random‐effects model meta‐analyses (DerSimonian 1986) and fixed‐effect model meta‐analyses (DeMets 1987). We will use the more conservative point estimate of the two (Jakobsen 2014). The more conservative point estimate is the estimate closest to no effect. If the two estimates are equal, the estimate with the widest confidence interval will be used. We use three primary outcomes and we will therefore consider a P value less than P ≤ 0.025 as statistically significant (Jakobsen 2014). We will use the eight‐step procedure to assess if the thresholds for significance are crossed or not (Jakobsen 2014). We use four secondary outcomes and we will therefore consider a P value less than P ≤ 0.02 for the secondary outcomes (Jakobsen 2014). We will use the eight‐step procedure to assess if the thresholds for significance are crossed or not (Jakobsen 2014).

We will include all studies in our analyses, and conduct a sensitivity analysis with studies at low risk of bias. If the results are similar we will base our primary conclusions at the time point closest to one month on the overall analysis. If they differ, we will base our primary conclusions on studies with a low risk of bias.

We will present a table describing the types of serious adverse events in each trial.

Trial Sequential Analysis (TSA)

Cumulative meta‐analyses are at risk of producing random errors due to sparse data and multiple testing of accumulating data (Brok 2008; Brok 2009; Higgins 2011a; Pogue 1997; Thorlund 2009; Wetterslev 2008); therefore TSA (CTU 2011) can be applied to assess and control this risk (http://www.ctu.dk/tsa/) (Thorlund 2011). Similar to a sample size calculation in a randomised controlled trial, TSA calculates the required information size for the meta‐analysis (that is the number of participants needed in a meta‐analysis to detect or reject a certain intervention effect) in order to minimise random errors (Wetterslev 2009). The required information size takes into account the event proportion in the control group, the assumption of a plausible relative risk reduction, and the heterogeneity of the meta‐analysis (Turner 2013; Wetterslev 2009). TSA enables testing for significance to be conducted each time a new trial is included in the meta‐analysis. On the basis of the required information size, trial sequential monitoring boundaries can be constructed. This enables one to determine the statistical inference concerning cumulative meta‐analysis that has not yet reached the required information size (Wetterslev 2008).

Firm evidence for benefit or harms may be established if the trial sequential monitoring boundary is crossed before reaching the required information size, in which case further trials may turn out to be superfluous. In contrast, if the boundary is not surpassed one may conclude that it is necessary to continue with further trials before a certain intervention effect can be detected or rejected. Firm evidence for lack of the postulated intervention effect can also be assessed with TSA. This occurs when the cumulative Z‐score crosses the trial sequential monitoring boundaries for futility.

For dichotomous outcomes we will estimate the required information size based on the proportion of participants with an outcome in the control group, a relative risk reduction of 10%, an alpha of 2.5% for primary outcomes and 2.0% for secondary outcomes, a beta of 10%, and a variance suggested by the trials in a random‐effects meta‐analysis (diversity‐adjusted required information size) (Jakobsen 2014; Wetterslev 2009). In case there is some evidence of effect of the intervention, a supplementary TSA will use the limit of the confidence interval closest to 1.00 as the anticipated intervention effect (Jakobsen 2014). Additionally, we will calculate TSA‐adjusted confidence intervals.

For continuous outcomes we will estimate the required information size based on the standard deviation observed in the control group of trials with low risk of bias or lower risk of bias and a minimal relevant difference of SD / 2 for continuous outcomes, an alpha of 2.0%, a beta of 10%, and a diversity suggested by the trials in the meta‐analysis (Jakobsen 2014; Wetterslev 2009). In case there is some evidence of effect of the intervention, as a supplementary TSA we will use the limit of the confidence interval closest to 0.00 as the anticipated intervention effect (Jakobsen 2014). Additionally, we will calculate TSA‐adjusted confidence intervals.

Summary of findings

We will use the GRADE system (Guyatt 2008) to assess the quality of the body of evidence associated with each of the primary outcomes (all‐cause mortality, major cardiovascular events, and serious adverse events), quality of life and angina in our review constructing 'Summary of findings' (SoF) tables using the GRADEpro GDT software (ims.cochrane.org/revman/other‐resources/gradepro) and the TSA‐adjusted CI for statements of precision or imprecision (Jakobsen 2014). The GRADE approach appraises the quality of a body of evidence based on the extent to which one can be confident that an estimate of effect or association reflects the item being assessed. The quality measure of a body of evidence considers within study risk of bias, the directness of the evidence, heterogeneity of the data, precision of effect estimates, and risk of publication bias. We will include all studies in our analyses, and conduct a sensitivity analysis with studies at low risk of bias. If the results are similar we will base our primary SoF tables and primary conclusions on the overall analysis. If they differ, we will base our primary SoF and primary conclusions on studies with a low risk of bias.