Beta‐blockers for non‐acute treatment after myocardial infarction

Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the benefits and harms of beta‐blockers compared with placebo, beta‐blockers and co‐intervention compared with similar co‐intervention, and beta‐blockers compared to no treatment in people after myocardial infarction.

Background

Description of the condition

Cardiovascular disease is the number one cause of death globally (Cooper 2000; Lloyd‐Jones 2010; Nichols 2014; Rosamond 2008; Schmidt 2012). Ischaemic heart disease accounts for almost 50% of the disease burden of the cardiovascular diseases (Nichols 2014). According to the World Health Organization (WHO), 7.4 million people died from ischaemic heart disease in 2012 (WHO 2015).

Ischaemic heart disease is caused by different underlying mechanisms: (1) atherosclerotic plaque‐related obstruction of the coronary arteries; (2) focal or diffuse spasms of normal or plaque‐diseased arteries; (3) microvascular dysfunction; and (4) left ventricular dysfunction caused by acute myocardial necrosis or ischaemic cardiomyopathy (Montalescot 2013). Ischaemic heart disease increases the risk of stable angina pectoris (see below) and acute coronary syndrome (see below).

Stable angina pectoris is defined as episodes of reversible myocardial demand or supply mismatch, leading to ischaemia or hypoxia of the heart muscle. These processes lead to transient chest discomfort or pain which is precipitated by activities such as walking, emotion, or stress, with no to minimal symptoms at rest and with beneficial effect of sublingual nitroglycerin on the pain (Montalescot 2013).

Acute coronary syndrome is a collective term for: (1) unstable angina pectoris (chest pain during rest related to ischaemia or hypoxia of the heart muscle (Roffi 2015)); (2) non‐ST‐elevation myocardial infarction (NSTEMI); or (3) ST‐elevation myocardial infarction (STEMI) (Roffi 2015; Steg 2012). Myocardial infarction is caused by death of cardiac myocytes (myocardial necrosis) due to ischaemia (O'Gara 2013; Steg 2012). The clinical definition of myocardial infarction is elevated serum levels of cardiac biomarkers (cardiac‐specific troponins and the myocardial band (MB) isoenzyme of creatine kinase (CK‐MB) among others) and changes of the ST‐segment on an electrocardiogram (ECG) (STEMI and NSTEMI) or symptoms of cardiac ischaemia (Roffi 2015; Steg 2012).

The diagnosis of myocardial infarction is dependent on an elevation of the serum levels of cardiac‐specific troponin I, troponin T, or CK‐MB , among others (Roffi 2015; Steg 2012). However, these enzymes will often not be detectable before 8 to 24 hours after the first symptoms of the myocardial infarction occur. Beta‐blockers may accordingly be commenced as an intervention in people with suspected myocardial infarction or may be commenced as an intervention for people with a confirmed diagnosis of myocardial infarction at a later time.

The causes of myocardial infarction are generally divided into five main classes (Thygesen 2012):

• Type 1: spontaneous myocardial infarction related to atherosclerotic plaque rupture, ulceration, fissuring, erosion, or dissection with resulting intraluminal thrombus in one or more of the coronary arteries, often caused by coronary artery disease.

• Type 2: myocardial infarction secondary to an ischaemic imbalance such as coronary artery spasm, coronary embolism, anaemia, arrhythmias, hypertension, or hypotension.

• Type 3: myocardial infarction with symptoms suggestive of myocardial ischaemia and resulting in sudden unexpected cardiac death when biomarker values are unavailable or could not be obtained before death.

• Type 4a: myocardial infarction associated with percutaneous coronary intervention (PCI).

• Type 4b: myocardial infarction associated with stent thrombosis as documented by angiography or at autopsy.

• Type 5: myocardial infarction associated with coronary artery bypass graft (CABG).

Major complications associated with myocardial infarction includes:

• Life‐threatening ventricular arrhythmias caused by changes in the electrophysiologic characteristics of the myocyte, electrolyte imbalance, continuous ischaemia, and variations in heart rate all due to obstruction and hence reduced flow to the myocardium and myocardial necrosis (Stevenson 1989; Brieger 2009).

• Mechanical complications caused by necrosis of the myocardium such as ventricular wall rupture, septum rupture, and papillary muscle rupture (Brieger 2009; Pohjola‐Sintonen 1989; Stevenson 1989).

• Cardiogenic shock caused by failure of the ventricle to pump an adequate amount of blood leading to a systemic hypotension (Stevenson 1989; Brieger 2009).

• Acute decompensated heart failure caused by impairment in systolic and diastolic function due to myocardial ischaemia (Brieger 2009).

• Depression (Thombs 2006).

Description of the intervention

The discovery of the difference between adrenergic receptors by Raymond Ahlquist in 1948 led Sir James Black to develop the first clinically useful beta‐receptor blocker (propranolol) in 1964 (Ahlquist 1948; Black 1964). This discovery was awarded the Nobel Prize in 1988 (Quirke 2006). Beta‐blockers are classified as non‐selective beta‐blockers or selective beta‐blockers according to their selectivity for one of the three subtypes of beta‐receptors.

• The beta₁‐receptor is mainly located in:

  • the heart, where it induces positive chronotropic effects (increases heart rate) and positive inotropic effects (increases contractility of the myocardium); and

  • in the kidneys where activation of the beta₁‐receptor results in a increased release of renin which in turn increases blood pressure, among other effects (Golan 2012; Marlin 1975; Singh 1975).

• The beta₂‐receptor is mainly located in smooth muscle cells, where it promotes relaxation; in skeletal muscle cells, where it promotes tremor and increased glycogenolysis; and in the liver, where it increases glycogenolysis (Golan 2012).

• The beta₃‐receptor is mainly located in adipose tissue where it primarily induces lipolysis (Golan 2012).

Beta‐blockers may be administered both intravenously and orally.

There are three different classes of beta‐blockers:

• The first generation non‐selective beta‐blockers (e.g. propranolol, oxprenolol, sotalol, timolol), affecting all beta receptors.

• The second generation selective beta₁‐blockers (e.g. metoprolol, bisoprolol, acebutolol, atenolol, esmolol), mainly affecting the heart.

• The third generation beta‐blockers, which have combined non‐selective beta‐blocking effects and alpha‐blocking effects (e.g. carvedilol), affecting all beta‐receptors plus alpha receptors in the vessels lowering the blood pressure.

Oral beta‐blockers may be used in the non‐acute phase of myocardial infarction as secondary prevention (Smith 2011).

How the intervention might work

The beta‐receptor is an adrenergic Gs heterotrimeric G‐protein‐coupled receptor located throughout the body. The beta‐receptors are stimulated by the sympathetic nervous system with catecholamines epinephrine (adrenaline) and norepinephrine (noradrenaline) as their primary endogenous agonists. The role of non‐acute treatment with beta‐blockers in people with myocardial infarction rests on their inhibition of the chronotropic and inotropic effects of the beta‐receptor. This may result in a reduction in heart rate, contractility, and blood pressure thereby decreasing the oxygen demand of the heart and consequently reducing ischaemic chest pain (Lopez‐Sendon 2004). Additionally, this inhibition of the beta‐receptor is thought to decrease recurrent ischaemia and might decrease the risk of life‐threatening ventricular arrhythmias and other complications associated with myocardial infarction (Roffi 2015; Steg 2012).

Why it is important to do this review

The prevalence of ischaemic heart disease is considerable and former meta‐analyses have shown conflicting results (see below). According to the WHO, 7.4 million people died from ischaemic heart disease in 2012 (Lloyd‐Jones 2010; Nichols 2014; Rosamond 2008; WHO 2015). The right treatment may therefore result in a considerable reduction in disease burden and health‐care cost.

The role of beta‐blockers in other settings is still debatable.

Beta‐blockers used to be contraindicated in people with congestive heart failure (Bristow 2000). Non‐selective combined alpha‐ and beta‐blockers are now a part of standard treatment of congestive heart failure (Chatterjee 2013; Yancy 2013). Beta‐blockers are also considered an option in the treatment of hypertension, but are rarely used as first‐line treatment (Mancia 2013). A recent Cochrane review found that beta‐blockers were inferior when compared with other anti‐hypertensive drugs (Wiysonge 2012). Non‐selective beta‐blockers are used in the treatment of anxiety due to their effect on decreasing tremor and tachycardia (Turner 1994).

Beta‐blockers may cause both cardiac adverse effects and non‐cardiac adverse effects. Among the most serious cardiac adverse effects is exacerbation of heart failure in people with acute decompensated heart failure, due to the need of sympathetic activity to maintain the cardiac output (Taylor 1982). In addition, beta‐blocker withdrawal has also been shown to cause exacerbation of ischaemic symptoms and precipitate acute myocardial infarction in people with ischaemic heart disease (Houston 1981).

Perioperative beta‐blockade for major non‐cardiac surgery in people with risk factors for ischaemic heart disease has been tested in several randomised clinical trials (Bangalore 2008; Devereaux 2008; Juul 2006) and seems to increase 30‐day all‐cause mortality as well as the occurrence of stroke, although non‐fatal myocardial infarctions are reduced (Bangalore 2008).

Case‐studies have suggested that depression, fatigue, and sexual dysfunction are among the beta‐blocker‐induced non‐cardiac adverse effects (Greenblatt 1974; Waal 1967; Warren 1977). However, a meta‐analysis comparing beta‐blockers versus placebo showed no difference on depressive symptoms and only a minor increase in sexual dysfunction and fatigue in participants randomised to beta‐blockers compared with placebo (Ko 2002).

While beta‐blockers are considered standard treatment in people with diagnosed heart failure (Chatterjee 2013; Yancy 2013), it remains unclear whether beta‐blockers have a beneficial effect in the non‐acute phase of myocardial infarction, in people without heart failure. This review will be the first to specifically assess the non‐acute treatment of beta‐blockers after myocardial infarction.

The evidence on the effects of beta‐blockers for myocardial infarction

Three meta‐analyses compared the effects of any type of beta‐blockers versus no beta‐blockers in participants with suspected or diagnosed myocardial infarction on long‐term outcomes (Bangalore 2014; Freemantle 1999; Yusuf 1985). While Freemantle 1999 and Yusuf 1985 showed a beneficial effect of beta‐blockers on mortality, Bangalore 2014 only found a beneficial effect on mortality in trials where the participants did not receive reperfusion in the form of revascularisation (percutaneous coronary intervention or coronary artery bypass graft) or thrombolytics (e.g. streptokinase). Bangalore 2014 found a beneficial effect of beta‐blockers on symptoms of angina and risk of recurrent myocardial infarction regardless of whether the participants received intervention for reperfusion or not. However, Bangalore 2014 also showed that beta‐blockers seemed to increase the severity of heart failure in participants receiving intervention for reperfusion (revascularisation or thrombolytics) (Bangalore 2014). It must be noted that Bangalore 2014 included a larger number of trials than Freemantle 1999 and Yusuf 1985, and only Bangalore 2014 included trials after the introduction of reperfusion strategies.

The American College of Cardiology Foundation/American Heart Association (ACCF/AHA) guideline recommends three years of beta‐blocker therapy as non‐acute secondary prevention in all people without heart failure (normal left ventricular function) who have had myocardial infarction (Smith 2011).

Former meta‐analyses have shown conflicting results and no former reviews have used Cochrane methodology to systematically assess the effects of beta‐blockers as an acute intervention in people with suspected or diagnosed myocardial infarction (Higgins 2011a). The present systematic review will be the first to take fully into account the risk of systematic errors ('bias'), design errors, and risks of random errors ('play of chance') (Higgins 2011a; Jakobsen 2014; Keus 2010; Thorlund 2011), and include trials irrespective of outcome, duration of follow‐up, number of participants, language, and publication status.

Objectives

To assess the benefits and harms of beta‐blockers compared with placebo, beta‐blockers and co‐intervention compared with similar co‐intervention, and beta‐blockers compared to no treatment in people after myocardial infarction.

Methods

Criteria for considering studies for this review

Types of studies

Randomised clinical trials irrespective of publication type, reported outcomes, publication status, publication date, and language. We will not specifically search for non‐randomised studies. However, if we identify non‐randomised studies (quasi‐randomised studies or observational studies), with adequate reports of harmful effects during the literature search, then we will narratively report these results. We are aware that this may bias our review, as we will put more emphasis on possible benefits than on possible harms (Higgins 2011a).

Types of participants

Participants irrespective of age, where the trialists have described the participants as being diagnosed with myocardial infarction. We will not include trials assessing the effects of beta‐blockers in non‐acute patients with heart failure.

Types of interventions

We will include three types of trials:

• beta‐blocker compared with placebo;

• beta‐blocker added to a co‐intervention compared with a similar co‐intervention; and

• beta‐blocker compared with no treatment.

We will accept any co‐intervention (any medical therapy or any revascularisation strategy) provided they are planned to be delivered similarly to the experimental group and the control group. We will assume that no interaction between the effects of the co‐interventions will ‘even out’ in both groups so the possible effects of beta‐blockers will be reflected in the results.

We will accept any type of beta‐blockers as experimental intervention (non‐selective beta‐blockers (e.g. propanolol, oxprenolol, sotalol, timolol), selective beta₁‐blockers (e.g. metoprolol, bisoprolol, acebutolol, atenolol, esmolol), and beta‐blockers which are combined alpha‐ and non‐selective beta‐blockers (e.g. carvedilol).

Our analysis will include trials assessing the effects of any type of secondary prevention beta‐blockers commenced in the non‐acute phase after myocardial infarction.

We will accept the trialists' definition of whether the beta‐blockers are commenced in an acute/ subacute phase or 'non‐acute phase'. However, as a rule of thumb we will consider beta‐blockers commenced more than 1 week after a myocardial infarction as 'commenced in a non‐acute phase'. The effects of beta‐blockers commenced in the acute/ subacute phase will be assessed in another review.

Types of outcome measures

Primary outcomes

• All‐cause mortality

• Major cardiovascular event defined as a composite outcome consisting of either cardiovascular mortality (as defined by trialists) or myocardial infarction (as 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 was life threatening, resulted in death, or was persistent or led to significant disability; prolonged hospitalisation or any medical event, which had jeopardised the participant or required intervention to prevent it (ICH‐GCP 1997).

Secondary outcomes

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

• Angina measured on any valid scale, such as 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‐up points:

• outcomes assessed at the time point closest to 12 months after randomisation (varying from 6 to 18 months) (this will be our outcome of primary interest);

• outcomes assessed at maximum follow‐up.

We chose 12 month follow‐up as our primary follow‐up time point because the possible effects of beta‐blockers need some time to show, and the follow‐up period is not so long that other factors, unrelated to the given trial but affecting the outcomes, might decrease the statistical power, that is, the results are 'diluted' by events (e.g. traffic accidents) unrelated to the trial.

Search methods for identification of studies

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL) (latest issue) in the Cochrane Library, MEDLINE (Ovid), Embase (Ovid), LILACS (Bireme), Science Citation Index Expanded, and BIOSIS (Web of Science, Thomson Reuters) in order to identify relevant trials (Royle 2003). Additionally, we will search the WHO International Clinical Trials Registry platform (ICTRP) (www.who.int/ictrp), ClinicalTrials.gov (clinicaltrials.gov), Turning Research Into Practice (TRIP) (www.tripdatabase.com), Google Scholar (scholar.google.dk) and Scisearch ipscience.thomsonreuters.com for finished trials as well as ongoing trials.

The preliminary search strategy for MEDLINE (Ovid) (Appendix 1) will be adapted for use in the other databases. We will apply the Cochrane sensitivity‐maximising RCT filter (Lefebvre 2011) to MEDLINE (Ovid) and adaptations of it to the other databases, except CENTRAL.

We will search all databases from their inception to the present and we will impose no restriction on language of publication. If we identify any papers in a language not known by the author group, we will seek help in our network and acknowledge it in 'Acknowledgements'.

Searching other resources

We will identify additional trials by searching the bibliographies of review articles and include them where relevant.

Data collection and analysis

We will use Review Manager 5 (RevMan 5) (RevMan 2014), STATA 14 (STATA 2015), and Trial Sequential Analysis (TSA) 0.9.5.5 Beta (CTU 2011; Thorlund 2011) to perform the analyses.

Selection of studies

Two authors (EEN and JF) will assess each identified trial independently. If a trial is identified as relevant by one author, but not by another, we will discuss the reasoning behind each decision. If no agreement can be reached, we will involve a third author (JCJ) to resolve the discussion.

Data extraction and management

We will use a data collection form for trial characteristics and outcome data, which has been piloted on at least one trial in the review. Four review authors (EEN, JF, SS, NJS) will independently extract trial characteristics and outcome data from included studies as follows.

• Methods: duration of the trial, details of any 'run‐in' period, and date of publication.

• Participants: number randomised, number analysed, mean age, sex, inclusion criteria, and exclusion criteria.

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

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

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

We will resolve disagreements by consensus or by involving another review author (JCJ). One review author (SS) will transfer data into the RevMan 5 file (RevMan 2014). We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the study reports. A second review author will spot‐check study characteristics for accuracy against the trial report.

Assessment of risk of bias in included studies

We will use the instructions given in the Cochrane Handbook for Systematic Reviews of Interventions in our evaluation of the methodology and the risk of bias of the included trials (Higgins 2011b). Two review authors will assess the included trials independently. We will evaluate the risks of bias in allocation sequence generation, allocation concealment, blinding of participants and treatment providers, blinding of outcome assessment, incomplete outcome data, selective outcome reporting, and other bias sources. These domains enable classification of randomised clinical trials with low risk of bias and of randomised clinical trials with unclear or high risk of bias. The latter trials overestimate benefits and underestimate harms (Gluud 2006; Kjaergard 2001; Lundh 2012; Moher 1998; Savovic 2012a; Savovic 2012b; Schulz 1995; Wood 2008). For additional details on how we will assess risk of bias see Appendix 2.

Overall risk of bias

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

• High risk of bias: we will classify the outcome result 'high risk of bias' if any of the bias risk domains described in the above are classified as '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.

Measures of treatment effect

Dichotomous outcomes

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

Continous outcomes

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

Dealing with missing data

We will contact all study authors for missing data.

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 is less than 5%. We will not impute missing values for any outcomes in our primary analysis. Additionally for continuous outcomes, if standard deviations (SD) are not reported, we will calculate the SDs 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:

'Best‐worst‐case' scenario

We will assume that all participants lost to follow‐up in the experimental group survived, had no serious adverse event, and had no major cardiovascular event, and all those with missing outcomes in the control group did not survive, had a serious adverse event, and had a major cardiovascular event.

'Worst‐best‐case' scenario

We will assume that all participants lost to follow‐up in the experimental group did not survive, had a serious adverse event, and had a major cardiovascular event, and all those with missing outcomes in the control group survived, had no serious adverse event, and had no major cardiovascular event.

We will present results from both scenarios in our publication.

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

• 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.

Assessment of heterogeneity

We will primarily investigate forest plots to visually assess any sign of heterogeneity. We will then assess the presence of statistical heterogeneity by Chi² test (threshold P < 0.10) and measure the quantities of heterogeneity by the I² statistic (Higgins 2002; Higgins 2003). We will follow the recommendations for threshold in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011):

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: considerable heterogeneity.

We will investigate possible heterogeneity through subgroup analyses and sensitivity analyses. Ultimately, we may decide that a meta‐analysis should be avoided (Deeks 2011).

Assessment of reporting biases

We will use a funnel plot to assess reporting bias if we include 10 or more trials. Using the asymmetry of the funnel plot we will assess the risk of bias. For dichotomous outcomes we will test asymmetry with the Harbord test (Harbord 2006) if Tau² is less than 0.1, and with the Rücker test (Rücker 2008) if Tau² is more than 0.1.

For continuous outcomes we will use the regression asymmetry test (Egger 1997).

Data synthesis

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‐from‐baseline scores are reported we will analyse the results together with end‐scores in the same meta‐analyses (Higgins 2011c).

We will undertake this systematic review according to the recommendations stated in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011) and according to Keus 2010 and Jakobsen 2014. We will use the statistical software RevMan 5 (RevMan 2014) provided by Cochrane to meta‐analyse data. We will use STATA (STATA 2015) in case of zero event trials, where RevMan 5 zero event handling (replacing zero with a constant of 0.5) is not sufficient, for example, in cases with skewed number of participants between groups, which we will handle according to Sweeting 2004, and in case meta‐regression (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, we will use the estimate with the widest confidence interval. We will examine 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 will examine 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 of studies at low risk of bias. If the results are similar we will base our primary conclusions at the time point closest to 12 months 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

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 2011c; Pogue 1997; Thorlund 2009; Wetterslev 2008); therefore Trial Sequential Analysis (TSA) (CTU 2011) can be applied to assess and control this risk (www.ctu.dk/tsa/) (Thorlund 2011). Similar to a sample size calculation in a randomised clinical 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 the risk of random errors (Wetterslev 2009). The required information size takes into account the event proportion in the control group, the assumption of a plausible RR 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 CI closest to 1.00 as the anticipated intervention effect (Jakobsen 2014). Additionally, we will calculate TSA‐adjusted CIs.

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% for secondary outcomes, 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.

Subgroup analysis and investigation of heterogeneity

We will perform the following subgroup analyses.

• Trials where the participants received intervention for reperfusion (coronary artery bypass graft, percutaneous coronary intervention or thrombolytics) to that in trials where the participants did not receive intervention for reperfusion. Additionally, we will assess if there seems to be a difference between the different reperfusion strategies.

• Trials where the experimental group received different types of beta‐blockers:

  • propanolol.

  • oxperenolol.

  • sotalol.

  • timolol.

  • metoprolol.

  • bisoprolol.

  • acebutolol.

  • atenolol.

  • esmolol.

  • carvedilol.

• Trials with different follow‐up:

  • six months or less;

  • between six months and 12 months;

  • between one year and three years;

  • three years or more.

• Trials with different age of participants:

  • aged 0 to 18 years;

  • aged 19 to 75 years;

  • aged 76 years or above.

• Trials that randomise men compared to trials that randomise women

• Trials with different clinical trial registration status:

  • pre‐registration;

  • post‐registration;

  • no registration.

• Comparison of the effect of beta‐blockers versus placebo or no intervention between trials including different types of acute myocardial infarction:

  • unstable angina pectoris

  • NSTEMI;

  • STEMI.

Sensitivity analysis

To assess the potential impact of bias, we will perform a sensitivity analysis where we exclude trials with overall 'high risk of bias'

To assess the potential impact of the missing data for dichotomous outcomes, we will perform best‐worst and worst‐best case scenarios (see 'Dealing with missing data').

All post‐hoc analysis will be regarded primarily as hypothesis generating.

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, serious adverse events), and two secondary outcomes (quality of life and angina) in our review. We will construct 'Summary of findings' (SoF) tables using the GRADEpro Guideline Development Tool (www.gradepro.org) 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 of 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

Appendices

Appendix 1. Preliminary MEDLINE (Ovid) search strategy

1. exp Adrenergic beta‐Antagonists/

2. betablock*.tw.

3. beta‐block*.tw.

4. b‐block*.tw.

5. (beta adj3 (antagonist* or receptor* or adrenergic* or block*)).tw.

6. (beta‐adrenoreceptor adj3 block*).tw.

7. beta‐adrenergic*.tw.

8. beta‐antagonist*.tw.

9. (beta‐receptor adj3 block*).tw.

10. acebutolol.tw.

11. alprenolol.tw.

12. atenolol.tw.

13. betaxolol.tw.

14. bisoprolol.tw.

15. brevibloc.tw.

16. bupranolol.tw.

17. butoxamine.tw.

18. carteolol.tw.

19. cartrol.tw.

20. carvedilol.tw.

21. celiprolol.tw.

22. coreg.tw.

23. corgard.tw.

24. dihydroalprenolol.tw.

25. esmolol.tw.

26. inderal.tw.

27. inderide.tw.

28. innopran.tw.

29. iodocyanopindolol.tw.

30. kerlone.tw.

31. labetalol.tw.

32. levatol.tw.

33. levobunolol.tw.

34. lopressor.tw.

35. metipranolol.tw.

36. metoprolol.tw.

37. nadolol.tw.

38. nebivolol.tw.

39. normodyne.tw.

40. oxprenolol.tw.

41. penbutolol.tw.

42. pindolol.tw.

43. practolol.tw.

44. propranolol.tw.

45. sectral.tw.

46. sotalol.tw.

47. tenoretic.tw.

48. tenormin.tw.

49. tertatolol.tw.

50. timolol.tw.

51. toprol.tw.

52. trandate.tw.

53. visken.tw.

54. zebeta.tw.

55. ziac.tw.

56. 1 or 2 or 3 or 4 or 5 or 6 or 7 or 8 or 9 or 10 or 11 or 12 or 13 or 14 or 15 or 16 or 17 or 18 or 19 or 20 or 21 or 22 or 23 or 24 or 25 or 26 or 27 or 28 or 29 or 30 or 31 or 32 or 33 or 34 or 35 or 36 or 37 or 38 or 39 or 40 or 41 or 42 or 43 or 44 or 45 or 46 or 47 or 48 or 49 or 50 or 51 or 52 or 53 or 54 or 55

57. exp Myocardial Infarction/

58. (myocardial adj2 infarct$).tw.

59. heart attack$.tw.

60. heart infarct*.tw.

61. 57 or 58 or 59 or 60

62. 56 and 61

63. randomized controlled trial.pt.

64. controlled clinical trial.pt.

65. randomized.ab.

66. placebo.ab.

67. drug therapy.fs.

68. randomly.ab.

69. trial.ab.

70. groups.ab.

71. 63 or 64 or 65 or 66 or 67 or 68 or 69 or 70

72. exp animals/ not humans.sh.

73. 71 not 72

74. 62 and 73

Appendix 2. Details on assessment of risk of bias

We will classify each trial according to the domains below for each outcome:

Random sequence generation

• Low risk: if sequence generation is achieved using computer random number generator or a random numbers table. Drawing lots, tossing a coin, shuffling cards and throwing dice are also be considered adequate if performed by an independent adjudicator.

• Unclear risk: if the method of randomisation is not specified.

• High risk: if the allocation sequence is not randomised or only quasi‐randomised.

Allocation sequence concealment

• Low risk: if the allocation of participants is performed by a central independent unit, on‐site locked computer, identical looking numbered sealed opaque envelopes, drug bottles or containers prepared by an independent investigator. There must be no risk of the investigator knowing the sequence.

• Unclear risk: if the trial is classified as randomised but the allocation concealment process is not described.

• High risk: if the allocation sequence is known to the investigators who assigned participants.

Blinding of participants and personnel

• Low risk: if the participants and the personnel are blinded to treatment allocation and this is described.

• Unclear risk: if the procedure of blinding is insufficiently described or not described at all.

• High risk: if blinding of participants and personnel is not performed.

Blinding of outcome assessment

• Low risk: if the trial investigators performing the outcome assessments, analyses and calculations are blinded to the intervention.

• Unclear risk: if the procedure of blinding is insufficiently described or not described at all.

• High risk: if blinding of outcome assessment is not performed.

Incomplete outcome data

• Low risk: (1) there are no dropouts or withdrawals for all outcomes, or (2) the numbers and reasons for the withdrawals and dropouts for all outcomes are clearly stated, can be described as being similar in both groups, and the trial handles missing data appropriately in intention‐to‐treat analysis using proper methodology, e.g. multiple imputations. As a general rule the trial is judged as at a low risk of bias due to incomplete outcome data if the number of dropouts is less than 5%. However, the 5% cut off is not definitive.

• Unclear risk: the numbers and reasons for withdrawals and dropouts are not clearly stated.

• High risk: the pattern of dropouts can be described as being different in the two intervention groups or the trial uses improper methodology in dealing with the missing data, e.g. last observation carried forward.

Selective outcome reporting

• Low risk: a protocol is published before or at the time the trial is begun and the outcomes called for in the protocol are reported on. If there is no protocol or the protocol is published after the trial has begun, reporting of the primary outcomes will grant the trial a grade of low risk of bias.

• Unclear risk: if there is no protocol and the primary outcomes are not reported on.

• High risk: if the outcomes which are called on in a protocol are not reported on.

Other bias risk

• Low risk of bias: the trial appears to be free of other components (for example, academic bias or for‐profit bias) that could put it at risk of bias.

• Unclear risk of bias: the trial may or may not be free of other components that could put it at risk of bias.

• High risk of bias: there are other factors in the trial that could put it at risk of bias (for example, authors have conducted trials on the same topic, for‐profit bias etc).

Contributions of authors

Emil E Nielsen (EEN): conceived, designed and drafted the protocol

Joshua Feinberg (JF): conceived, designed and drafted the protocol

Sanam Safi (SS): provided general advice and revised the protocol

Naqash J Sethi (NSJ): provided general advice and revised the protocol

Christian Gluud (CG): provided general advice and revised the protocol

Janus C Jakobsen (JCJ): provided general advice and revised the protocol

All authors agreed on the final protocol version

Sources of support

Internal sources

• No sources of support supplied

External sources

• National Institute for Health Research (NIHR), UK.

  This project was supported by the National Institute for Health Research via Cochrane Infrastructure, Cochrane Programme Grant or Cochrane Incentive funding to the Cochrane Heart Group. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS or the Department of Health

• Northwestern University, USA.

  The Cochrane Heart Group US Satellite is supported by intramural support from the Northwestern University Feinberg School of Medicine and the Northwestern University Clinical and Translational Science (NUCATS) Institute (UL1TR000150)

Declarations of interest

The performance of this review is free of any real or perceived bias introduced by receipt of any benefit in cash or kind, on any subsidy derived from any source that may have or be perceived to have an interest in the outcomes of the review.

Emil E Nielsen (EEN): no conflict of interest

Joshua Feinberg (JF): no conflict of interest

Sanam Safi (SS): no conflict of interest

Naqash J Sethi (NSJ): no conflict of interest

Christian Gluud (CG): member of The Copenhagen Trial Unit task force for developing Trial Sequential Analysis methods, manual, and software.

Januc C Jakobsen (JCJ): no conflict of interest

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