Types of studies

We will include studies with the following design characteristics:

• Randomised controlled trials (including cluster‐randomised trials where the unit of randomisation is the setting or operator) and quasi‐randomised trials.

• Patients were followed up for at least one week.

We will exclude studies with the following design characteristics:

• Cross‐over trials, because CSOM is not expected to be a stable chronic condition. Unless data from the first phase are available, we will exclude such studies.

• Studies that randomised participants by ear (within‐patient controlled) because, by definition, the effects of systemic treatments are not localised. This applies to studies that compared systemic antibiotics versus topical antiseptics. Note: We will not exclude studies comparing topical antibiotics with topical antiseptics that randomised participants by ear but we will analyse these using the methods outlined in Unit of analysis issues.

Types of participants

We will include studies with patients (adults and children) who had:

• chronic ear discharge of unknown cause; or

• chronic suppurative otitis media.

We will define patients with chronic ear discharge as patients with at least two weeks of ear discharge, where the cause of the discharge was unknown.

We will define patients with chronic suppurative otitis media (CSOM) as patients with:

• chronic or persistent ear discharge for at least two weeks; and

• a perforated tympanic membrane.

We will not exclude any populations based on age, risk factors (cleft palate, Down syndrome), ethnicity (e.g. Australian Aboriginal or Torres Strait Islanders) or the presence of ventilation tubes (grommets). Where available, we will record these factors in the patient characteristics section during data extraction from the studies. If any of the included studies mostly recruited these patients (80% or more), we will analyse them in a subgroup analysis (see Subgroup analysis and investigation of heterogeneity).

We will exclude studies where the majority (more than 50%) of participants:

• had an alternative diagnosis to CSOM (e.g. otitis externa);

• had underlying cholesteatoma;

• had ear surgery within the last six weeks.

We will not include studies designed to evaluate interventions in the immediate peri‐surgical period, which are focused on assessing the impact of the intervention on the surgical procedure or outcomes.

Types of interventions

Types of outcome measures

We will analyse the following outcomes in the review, but we will not use them as a basis for including or excluding studies.

We will extract and report data from the longest available follow‐up for all outcomes.

Electronic searches

Published, unpublished and ongoing studies will be identified by searching the following databases from their inception:

• the Cochrane Register of Studies ENT Trials Register (search via CRS Web to date);

• the Cochrane Central Register of Controlled Trials (CENTRAL) (search via CRS Web to date);

• Ovid MEDLINE(R) Epub Ahead of Print, In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE(R) Daily and Ovid MEDLINE(R) (1946 to present);

• Ovid EMBASE (1974 to date);

• EBSCO CINAHL (1982 to date);

• LILACS (search to date);

• KoreaMed (search to date);

• IndMed (search to date);

• PakMediNet (search to date);

• African Index Medicus (search to date);

• Web of Knowledge, Web of Science (1945 to date);

• ClinicalTrials.gov, www.clinicaltrials.gov (search via the Cochrane Register of Studies to date);

• World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (search to date);

• ISRCTN, www.isrctn.com (search to date).

The subject strategies for databases are detailed in Appendix 1. The strategy has been designed to identify all relevant studies for a suite of reviews on various interventions for chronic suppurative otitis media (Bhutta 2018; Brennan‐Jones 2018a; Brennan‐Jones 2018b; Chong 2018a; Chong 2018b; Head 2018a; Head 2018b). Where appropriate, these will be combined with subject strategy adaptations of the highly sensitive search strategy designed by Cochrane for identifying randomised controlled trials and controlled clinical trials (as described in the Cochrane Handbook for Systematic Reviews of Interventions Version 5.1.0, Box 6.4.b. (Handbook 2011)).

Searching other resources

We will scan the reference lists of identified publications for additional trials and contact trial authors if necessary. In addition, the Information Specialist will search Ovid MEDLINE to retrieve existing systematic reviews relevant to this systematic review, so that we can scan their reference lists for additional trials. The Information Specialist will also run non‐systematic searches of Google Scholar to retrieve grey literature and other sources of potential trials.

Selection of studies

At least two review authors (KH/LYC) will independently screen all titles and abstracts of the references obtained from the database searches to identify potentially relevant studies. At least two review authors (KH/LYC) will evaluate the full text of each potentially relevant study to determine whether it meets the inclusion and exclusion criteria for this review.

We will resolve any differences by discussion and consensus, with the involvement of a third author for clinical and methodological input where necessary.

Data extraction and management

At least two review authors (KH/LYC/CBJ/MB) will independently extract data from each study using a standardised data collection form (see Appendix 2). Whenever a study has more than one publication, we will retrieve all publications to ensure complete extraction of data. Where there are discrepancies in the data extracted by different review authors, we will check these against the original reports and resolve differences by discussion and consensus, with the involvement of a third author or a methodologist where appropriate. We will contact the original study authors for clarification or for missing data whenever possible. If differences are found between publications of a study, we will contact the original authors for clarification. We will use data from the main paper(s) if no further information is found.

We will include key characteristics of the included studies, such as study design, setting (including location), year of study, sample size, age and sex of participants, and how outcomes were defined or collected in the studies. In addition, we will also collect baseline information on prognostic factors or effect modifiers (see Appendix 2). For this review, this will include the following information whenever available:

• duration of ear discharge at entry to the study;

• diagnosis of ear discharge (where known);

• number people who may be at higher risk of CSOM, including those with cleft palate or Down syndrome;

• ethnicity of participants including the number who are from Indigenous populations;

• number who have previously had ventilation tubes (grommets) inserted (and, where known, the number who have tubes still in place);

• number who have had previous ear surgery;

• number who have had previous treatments for CSOM (non‐responders, recurrent versus new cases).

We will record concurrent treatments alongside the details of the interventions used. See the 'Data extraction form' in Appendix 2 for more details.

For the outcomes of interest to the review, we will extract the findings of the studies on an available case analysis basis, i.e. we will include data from all patients available at the time points based on the treatment randomised whenever possible, irrespective of compliance or whether patients had received the treatment as planned.

In addition to extracting pre‐specified information about study characteristics and aspects of methodology relevant to risk of bias, we will extract the following summary statistics for each trial and each outcome:

• For continuous data: the mean values, standard deviations and number of patients for each treatment group. Where endpoint data are not available, we will extract the values for change from baseline. We will analyse data from disease‐specific quality of life scales such as COMQ‐12, COMOT‐15 and CES as continuous data.

• For binary data: the number of participants experiencing an event and the number of patients assessed at the time point.

• For ordinal scale data: if the data appear to be approximately normally distributed or if the analysis that the investigators performed suggests parametric tests were appropriate, then we will treat the outcome measures as continuous data. Alternatively, if data are available, we plan to convert into binary data.

• Time‐to‐event outcomes: we are not expecting any outcomes to be measured as time‐to‐event data. However, if outcomes such as resolution of ear discharge are measured in this way, we will report the hazard ratios.

For resolution of ear discharge, we will extract the longest available data within the time frame of interest, defined as from one week up to (and including) two weeks (7 days to 14 days), from two weeks up to (and including) four weeks (15 to 28 days), and after four weeks (28 days or one month).

For other outcomes, we will report the results from the longest available follow‐up period.

Assessment of risk of bias in included studies

At least two review authors (KH/LYC/CBJ/MB) will independently assess the risk of bias of each included study. We will follow the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011), using the Cochrane 'Risk of bias' tool. With this tool we will assess the risk of bias as 'low', 'high' or 'unclear' for each of the following six domains:

• sequence generation;

• allocation concealment;

• blinding of participants, personnel and outcome assessment;

• incomplete outcome data;

• selective reporting;

• other sources of bias.

Measures of treatment effect

We will summarise the effects of dichotomous outcomes (e.g. proportion of patients with complete resolution of ear discharge) as risk ratios (RR) with confidence intervals (CIs). For the key outcomes that we will present in the 'Summary of findings' table, we will also express the results as absolute numbers based on the pooled results and compared to the assumed risk. We also plan to calculate the number needed to treat to benefit (NNTB) using the pooled results. The assumed baseline risk will typically be either (a) the median of the risks of the control groups in the included studies, this being used to represent a 'medium‐risk population' or, alternatively, (b) the average risk of the control groups in the included studies, which is used as the 'study population' (Handbook 2011). If a large number of studies are available, and where appropriate, we also plan to present additional data based on the assumed baseline risk in (c) a low‐risk population and (d) a high‐risk population.

For continuous outcomes, we will express treatment effects as a mean difference (MD) with standard deviation (SD). If different scales are used to measure the same outcome we will use the standardised mean difference (SMD) and we will provide a clinical interpretation of the SMD values.

Unit of analysis issues

Dealing with missing data

We will contact study authors via email whenever the outcome of interest is not reported, if the methods of the study suggest that the outcome had been measured. We will do the same if not all data required for meta‐analysis are reported, unless the missing data are standard deviations. If standard deviation data are not available, we will approximate these using the standard estimation methods from P values, standard errors or 95% CIs if these are reported, as detailed in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011). Where it is impossible to estimate these, we will contact the study authors.

Apart from imputations for missing standard deviations, we will not conduct any other imputations. We will extract and analyse data for all outcomes using the available case analysis method.

Assessment of heterogeneity

We will assess clinical heterogeneity (which may be present even in the absence of statistical heterogeneity) by examining the included studies for potential differences in the types of participants recruited, interventions or controls used, and the outcomes measured. We will not pool studies where the clinical heterogeneity makes it unreasonable to do so.

We will assess statistical heterogeneity by visually inspecting the forest plots and by considering the Chi² test (with a significance level set at P value < 0.10) and the I² statistic, which calculates the percentage of variability that is due to heterogeneity rather than chance, with I² values over 50% suggesting substantial heterogeneity (Handbook 2011).

Assessment of reporting biases

We will assess reporting bias as within‐study outcome reporting bias and between‐study publication bias.

Data synthesis

We will conduct all meta‐analyses using Review Manager 5.3 (RevMan 2014). For dichotomous data, we plan to analyse treatment differences as a risk ratio (RR) calculated using the Mantel‐Haenszel methods. We plan to analyse time‐to‐event data using the generic inverse variance method.

For continuous outcomes, if all the data are from the same scale, we plan to pool mean values obtained at follow‐up with change outcomes and report this as a MD. However, if the SMD has to be used as an effect measure, we will not pool change and endpoint data.

When statistical heterogeneity is low, random‐effects versus fixed‐effect methods yield trivial differences in treatment effects. However, when statistical heterogeneity is high, the random‐effects method provides a more conservative estimate of the difference.

Subgroup analysis and investigation of heterogeneity

We will subgroup studies where most participants (80% or more) meet the criteria stated below in order to determine whether the effect of the intervention is different compared to other patients. Due to the risks of reporting and publication bias with unplanned subgroup analyses of trials, we will only analyse subgroups reported in studies if these were prespecified and stratified at randomisation.

We plan to conduct subgroup analyses regardless of whether statistical heterogeneity is observed for studies that included patients identified as high risk (i.e. thought to be less responsive to treatment and more likely to develop CSOM, recurrence or complications) and patients with ventilation tubes (grommets). 'High risk' patients include Indigenous populations (e.g. Australian Aboriginal and Torres Strait Islanders, Native Americans and Inuit populations of Alaska, Canada and Greenland), people with craniofacial malformation (e.g. cleft palate), Down syndrome and people with known immunodeficiency.

We plan to present the main analyses of this review in the form of forest plots based on this main subgroup analysis.

• For the high‐risk group, this applies to the outcomes resolution of ear discharge (dry ear), quality of life, pain/discomfort, development of complications and hearing loss.

For patients with ventilation tubes, this applies to the outcome resolution of ear discharge (dry ear) for the time point of four weeks or more because this group is perceived to be at lower risk of treatment failure and recurrence than other patient groups. If statistical heterogeneity is observed, we will also conduct subgroup analysis for the effect modifiers below. If there are statistically significant subgroup effects, we will present these subgroup analysis results as forest plots.

For this review, effect modifiers include:

• Diagnosis of CSOM: it is likely that some studies will include patients with chronic ear discharge but who have not had a diagnosis of CSOM. Therefore, we will subgroup studies where most patients (80% or more) meet the criteria for CSOM diagnosis in order to determine whether the effect of the intervention is different compared to patients where the precise diagnosis is unknown and inclusion into the study is based purely on chronic ear discharge symptoms.

• Duration of ear discharge: there is uncertainty about whether the duration of ear discharge prior to treatment has an impact on the effectiveness of treatment and whether more established disease (i.e. discharge for more than six weeks) is more refractory to treatment compared with discharge of a shorter duration (i.e. less than six weeks).

• Patient age: patients who are younger than two years old versus patients up to six years old versus adults. Patients under two years are widely considered to be more difficult to treat.

We will present the results as subgroups regardless of the presence of statistical heterogeneity based on these three factors:

• Class of antibiotics. We will group by pharmacological class, e.g. quinolones, aminoglycosides, penicillins etc. The rationale for this is that different classes may have different effectiveness and side effect profiles.

• Spectrum of activity against Pseudomonas aeruginosa (groups with known activity against Pseudomonas aeruginosa versus groups without activity against Pseudomonas aeruginosa. This is the most commonly found bacteria in patients with CSOM and its presence is associated with tissue damage.

• Type of antiseptic used in the comparison arm (e.g. iodines, alcohols, acids). This is because different types of antiseptic have different mechanisms of action and therefore the treatment effects and adverse effect profiles are likely to be different.

When other antibiotics are also used as a common treatment in both the intervention and comparison group, we will investigate the class and antipseudomonal activity when statistical heterogeneity is present and cannot be explained by the other subgroup analyses.

No other subgroups based on the pharmacological properties of antibiotics are planned, but we will consider the method and frequency of aural toileting if there is remaining unexplained heterogeneity despite conducting the other subgroup analyses.

Sensitivity analysis

We plan to carry out sensitivity analyses to determine whether the findings are robust to the decisions made in the course of identifying, screening and analysing the trials. We plan to conduct sensitivity analysis for the following factors, whenever possible:

• Impact of model chosen: fixed‐effect versus random‐effects model.

• Risk of bias of included studies: excluding studies with high risk of bias (we will define these as studies that have a high risk of allocation concealment bias and a high risk of attrition bias (overall loss to follow‐up of 20%, differential follow‐up observed)).

• Where there is statistical heterogeneity, studies that only recruited patients who had previously not responded to one of the treatments under investigation in the RCT. Studies that specifically recruited patients who did not respond to a treatment could potentially have reduced the relative effectiveness of an agent.

If any of these investigations finds a difference in the size of the effect or heterogeneity, we will mention this in the 'Effects of interventions' section and/or present the findings in a table.