Types of studies

Randomised clinical trials irrespective of trial design, setting, blinding, publication status, publication year, and language. We will not include quasi‐randomised trials and observational studies for the assessment of harms. By focusing on randomised clinical trials, we are aware that the present review will be biased towards focusing on more benefits and less on harms.

Types of participants

Participants with any diagnosis of coronary heart disease, that is, acute myocardial infarction, previous myocardial infarction, stable angina, or unstable angina. We will accept the definitions used by the individual trialists. We will include participants irrespective of age, sex, and antibody status (e.g. for C pneumoniae, H pylori, P gingivalis, or E coli). We will exclude participants with any other cause of chronic inflammatory disease (e.g. lupus erythematosus, rheumatoid arthritis, ankylosing spondylitis, psoriatic arthritis, polymyositis/dermatomyositis, and inflammatory bowel disease). We will only include trials that include a subset of eligible participants if separate data for the eligible participants are available or if the majority of participants (i.e. more than 80%) are eligible. We will document difficult decisions in the review, and sensitivity analyses will assess the impact of these decisions on the review's findings.

Types of interventions

We will include three types of comparisons:

• antibiotic compared with placebo;

• antibiotic compared with no intervention (including no placebo tablet); and

• antibiotic added to a co‐intervention compared with a similar co‐intervention.

We will accept any type of antibiotic (e.g. azithromycin, clarithromycin, erythromycin, doxycycline, tetracycline hydrochloride, gatifloxacin, levofloxacin, moxifloxacin, telithromycin, penicillin, amoxicillin, or metronidazole) as the experimental intervention, irrespective of dose, route of administration, or duration. We will assess the effects of the individual types of antibiotics in subgroup analyses.

We will accept any type of co‐intervention when such co‐intervention is intended to be delivered similarly to the experimental and the control group. We will assume that the effects of the co‐interventions will 'even out' in both groups so that the possible effects of the antibiotic will be reflected in the results. We will do a check of co‐interventions after randomisation in both intervention groups and consider any major differences in our conclusions. As optimal medical therapy plays an important role for the secondary prevention of coronary heart disease, we will perform a sensitivity analysis excluding trials with sub‐optimal medical therapy. Optimal medical therapy indicates at least one drug for angina/ischaemic relief (e.g. short‐acting nitrates, beta blockers, and calcium channel blockers) plus drugs for event prevention (e.g. aspirin, clopidogrel, statins, ACE inhibitors, and angiotensin receptor blockers) (Montalescot 2013).

Types of outcome measures

For all outcomes we will use the trial results at maximal follow‐up. However, if the trialists report results at multiple time points, we will also assess the results reported at the time point closest to 24 months (plus and minus six months).

We chose 24 months' follow‐up based on the Kaplan‐Meier curve made by Winkel 2015. We believe that 24 months' follow‐up is long enough to show any possible secondary prevention effects of antibiotics. Furthermore, 24 months' follow‐up is not so long that other factors, unrelated to the given trial but affecting the outcomes, might decrease the statistical power, that is, that the results are 'diluted' by events unrelated to the trial.

Electronic searches

We will search the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, Embase, LILACS, Science Citation Index Expanded on Web of Science and BIOSIS in order to identify relevant trials. The preliminary search strategy for MEDLINE (Ovid) is given in Appendix 1 and will be adapted for use in the other databases. We will apply the Cochrane sensitivity‐maximising randomised clinical trial 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 or publication status. We will assess non‐English language papers by asking individuals that fluently speak the language for help. We will not perform a separate search for adverse effects of antibiotics used for the treatment of coronary heart disease. We will only consider adverse effects described in the included trials.

Searching other resources

The reference lists of included randomised clinical trials, previous systematic reviews, and other kinds of reviews will be checked for any unidentified randomised clinical trials. We will contact authors of included randomised clinical trials for further information and we will contact the following major pharmaceutical companies by email asking them for any unpublished randomised clinical trials:

• Merck & Co.;

• Roche Holding AG;

• Pfizer Inc.;

• Novartis AG;

• GlaxoSmithKline Plc;

• AstraZeneca Plc;

• Bristol‐Myers Squibb Co.;

• Sanofi‐Aventis;

• Abbott Laboratories;

• Taisho Pharmaceutical; and

• Pliva.

Furthermore, we will search for ongoing and unidentified randomised clinical trials on:

• Google Scholar;

• The Turning Research into Practive (TRIP) Database;

• ClinicalTrials.gov;

• EU Clinical Trial Register;

• Chinese Clinical Trial Registry (ChCTR);

• International Standard Randomised Controlled Trial Number (ISRCTN) registry;

• GSK Clinical Study Register;

• Pan African Clinical Trials Registry (PACTR);

• Australian New Zealand Clinical Trials Registry (ANZCTR);

• Clinical Trials Registry ‐ India (CTRI); and

• the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) search portal.

We will also examine relevant retraction statements and errata for included trials.

Selection of studies

Two authors (NJS, SS) will independently screen titles and abstracts. We will retrieve all relevant full‐text study reports/publications and two review authors (NJS, SS) will independently screen the full text and identify and record reasons for exclusion of the ineligible studies. We will resolve disagreements through discussion or, if required, by consulting with a third author (JCJ). We will display trial selection in a flow diagram as per the PRISMA statement (Moher 2009).

We will record the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table.

Data extraction and management

Three authors (NJS, SS, SKK) will extract data independently from included trials. We will resolve any disagreements by discussion with a fourth author (JCJ). We will assess duplicate publications and companion papers of a trial together in order to evaluate all available data simultaneously (maximise data extraction, correct bias assessment). We will contact the authors of the trials by email to specify any of the data, had they not been reported sufficiently in the publication.

Assessment of risk of bias in included studies

We will use the instructions given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017) in our evaluation of the methodology and hence the risk of bias of the included trials. We will evaluate the methodology in respect of:

• random sequence generation;

• allocation concealment;

• blinding of participants and personnel;

• blinding of outcome assessment;

• incomplete outcome data;

• selective outcome reporting;

• other risks of bias;

• overall risk of bias.

These domains enable classification of randomised trials with low risk of bias and high risk of bias. The latter trials tend to overestimate positive intervention effects (benefits) and underestimate negative effects (harms) (Schulz 1995; Moher 1998; Kjaergard 2001; Gluud 2006; Wood 2008; Savovic 2012; Lundh 2017).

We will classify the trials according to the criteria described in Table 1.

We will assess the domains 'blinding of outcome assessment', 'incomplete outcome data', and 'selective outcome reporting' for each outcome result. Thus, we will be able to assess the bias risk for each outcome assessed in addition to each trial.

Measures of treatment effect

Unit of analysis issues

We will only include randomised clinical trials. For trials using cross‐over design, we will only include data from the first period (Elbourne 2002; Deeks 2017). There will, therefore, not be any unit of analysis issues.

Dealing with missing data

We will, as a first option, contact all trial authors to obtain missing data (i.e. for data extraction and for assessment of risk of bias, as specified above).

Assessment of heterogeneity

We will primarily investigate forest plots to visually assess any sign of heterogeneity. We will secondly 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 thresholds in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017):

• 0% to 40%: might not be important;

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

• 50% to 90% may represent substantial heterogeneity;

• 75% to 100%: may represent considerable heterogeneity.

We will investigate possible heterogeneity through subgroup analyses. Ultimately, we may decide that a meta‐analysis should be avoided (Deeks 2017).

Assessment of reporting biases

We will use a funnel plot to assess reporting bias if we include 10 or more trials. We will visually inspect funnel plots to assess the risk of bias. We are aware of the limitations of a funnel plot (i.e. a funnel plot assesses bias due to small sample size. From this information, we will assess possible reporting bias). For dichotomous outcomes, we will test asymmetry with the Harbord test (Harbord 2006). For continuous outcomes, we will use the regression asymmetry test (Egger 1997) and the adjusted rank correlation (Begg 1994).

Data synthesis

Subgroup analysis and investigation of heterogeneity

We will perform the following subgroup analyses when assessing each outcome (all‐cause mortality, serious adverse event, quality of life, cardiovascular mortality, myocardial infarction, stroke, and sudden cardiac death) both at the time point closest to 24 months' follow‐up and at maximal follow‐up.

• Comparison of the effects between trials with different types of antibiotic (e.g. azithromycin, clarithromycin, erythromycin, doxycycline, tetracycline hydrochloride, gatifloxacin, levofloxacin, moxifloxacin, telithromycin, penicillin, amoxicillin, or metronidazole).

• Antibody status (i.e. people with identified C pneumoniae, H pylori, P gingivalis, orE coli antibodies compared to people without any identified C pneumoniae, H pylori, P gingivalis, orE coli antibodies).

• Comparison of participants on statins at entry compared to participants not on statins at entry (Jensen 2010).

• Comparison of the mean age of participants (0 to 59 years, 60 to 79 years, 80 years and over).

• Comparison of the effects between trials with different clinical trial registration status (pre‐registration, post‐registration or no registration).

Additionally, we will perform the following subgroup analysis when assessing each outcome (all‐cause mortality, serious adverse event, quality of life, cardiovascular mortality, myocardial infarction, stroke, and sudden cardiac death) at maximal follow‐up.

• Comparison of trials with less than 12 months' follow‐up with trials equal to or longer than 12 months' follow‐up.

We will use the formal test for subgroup differences in RevMan 5 (RevMan 2014).

Sensitivity analysis

To assess the potential impact of bias, we will perform a sensitivity analysis in which we exclude trials at overall high risk of bias.

To assess the potential impact of the missing data for dichotomous outcomes, we will perform the following four sensitivity analyses when assessing each dichotomous outcome (all‐cause mortality, serious adverse event, cardiovascular mortality, myocardial infarction, stroke, and sudden cardiac death).

• 'Best‐worst‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group have survived, had no serious adverse event, had no cardiovascular death, had no myocardial infarction, had no stroke, and had no sudden cardiac death; and all those participants lost to follow‐up in the control group have not survived, had a serious adverse event, had a cardiovascular death, had a myocardial infarction, had a stroke, and had a sudden cardiac death.

• 'Worst‐best‐case' scenario: we will assume that all participants lost to follow‐up in the experimental group have not survived, had a serious adverse event, had a cardiovascular death, had a myocardial infarction, had a stroke, and had a sudden cardiac death; and that all those participants lost to follow‐up in the control group have survived, had no serious adverse event, had no cardiovascular death, had no myocardial infarction, had no stroke, and had no sudden cardiac death.

• A modified 'best‐worst‐case' scenario: we will assume that half of the participants lost to follow‐up in the experimental group have survived, had no serious adverse event, had no cardiovascular death, had no myocardial infarction, had no stroke, and had no sudden cardiac death; and that half of the participants lost to follow‐up in the control group have not survived, had a serious adverse event, had a cardiovascular death, had a myocardial infarction, had a stroke, and had a sudden cardiac death.

• A modified 'worst‐best‐case' scenario: we will assume that half of the participants lost to follow‐up in the experimental group have not survived, had a serious adverse event, had a cardiovascular death, had a myocardial infarction, had a stroke, and had a sudden cardiac death; and that half of the participants lost to follow‐up in the control group have survived, had no serious adverse event, had no cardiovascular death, had no myocardial infarction, had no stroke, and had no sudden cardiac death.

We will present results of all four scenarios in our review.

When analysing quality of life, a ‘beneficial outcome’ will be the group mean plus two standard deviations (SDs) (we will then use one SD in another sensitivity analysis) of the group mean, and a ‘harmful outcome’ will be the group mean minus two SDs (we will then use one SD in another sensitivity analysis) of the group mean (Jakobsen 2014).

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

• Where SDs are missing and it is not possible to calculate them, we will impute SDs from trials with similar populations and low risk of bias. If we find no such trials, we will impute SDs from trials with a similar population. As the final option, we will impute SDs from all trials.

We will present results of this scenario in our review.

Other post‐hoc sensitivity analyses might be warranted if unexpected clinical or statistical heterogeneity is identified during the analysis of the review results (Jakobsen 2014).