Types of studies

Randomised controlled trials (RCTs). This includes:

• parallel‐group study designs, where patients are randomised to unilateral or bilateral aids; or

• cross‐over study designs for the order of fitting of unilateral/bilateral aids for each patient; or

• cluster‐randomised trials, where randomisation is done by practice or setting (the number of randomised groups must be more than two);

• quasi‐randomised trials, because only a small number of trials is expected.

Types of participants

We will include studies if the participants meet the following criteria:

• adults (over 18 years);

• with a bilateral hearing impairment and both ears suitable for hearing aids.

We will exclude studies from the review if a majority of the participants have one or more of the following characteristics:

• although asymmetric hearing impairment will not be excluded, if a patient has one ear that is audiometrically normal or one ear that has a profound or total loss conventional hearing aids are not appropriate for them;

• active external or middle ear disease;

• previous experience of using a hearing aid.

Types of interventions

The comparison of interest is:

• fitting of two versus one ear‐level acoustic hearing aids.

We will exclude implants, body‐worn aids and bone‐conduction hearing aids.

We will apply no minimum duration of use or follow‐up as an inclusion criterion, but we will consider these as part of the GRADE evidence evaluation for indirectness of evidence.

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.

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Published, unpublished and ongoing studies will be identified by searching the following databases from their inception: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

• the Cochrane Central Register of Controlled Trials (CENTRAL, current issue);

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

• Ovid EMBASE (1974 to date);

• EBSCO CINAHL (1982 to date);

• LILACS (search to date);

• KoreaMed (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);

• Google Scholar (search to date).

The subject strategies for databases will be modelled on the search strategy designed for Ovid MEDLINE, Ovid Embase and CENTRAL in Appendix 1. 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 Specialists will search Ovid MEDLINE, Ovid Embase and theCochrane Library to retrieve existing systematic reviews relevant to this systematic review, so that we can scan their reference lists for additional trials.

Selection of studies

At least two authors will independently screen the titles and abstracts of the papers found by the searches against the criteria for inclusion. We will then retrieve and independently review the full text of the potentially eligible papers to determine if they meet the inclusion criteria for the review. We will resolve any differences by discussion and consensus, with the involvement of a third author for clinical or methodological input.

Data extraction and management

At least two authors will independently extract the data from each trial using a standardised data extraction form (Appendix 2). If any essential data are missing from a study then one author will contact the authors of the papers to request the additional information. We will try to identify multiple publications for included studies and, if a study has more than one publication, we will retrieve all publications to ensure complete extraction of data. 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.

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.

For each trial we will document the following information:

• Methods: study design (cross‐over, parallel etc.), randomisation method, unit of randomisation, blinding method, duration of follow‐up.

• Participants: setting, number of participants entered and analysed, age and sex, inclusion and exclusion criteria, levels of hearing impairment.

• Type of intervention: type of hearing aids fitted during the study, duration of each intervention, use of additional intervention, details of model, type of mould used and fitting strategy. We will record the rehabilitation strategy used (such as the ability to position the aid and mould in the ear and to use the controls).

• Outcomes: assessment method, time point of data collection.

• Funding sources and declarations of interest.

In addition, we will also extract baseline information on prognostic factors (often called 'predictors' in trials) or effect modifiers that may affect preferences and outcomes of the study. For this review, this includes:

• levels or severity of hearing impairment;

• presence of asymmetric hearing loss;

• whether participants had previous experience of hearing aid use;

• cognitive impairment;

• visual impairment;

• presence of tinnitus.

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. We will prioritise using change from baseline data whenever available. Where change data are not available, we will use the mean and standard deviation of each group at the end of the study. We will analyse data from measurement scales as continuous data.

• For binary data: the numbers 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 may convert into binary data.

Where studies report data at multiple time points, we will only extract the longest available data or end of the study data.

Assessment of risk of bias in included studies

GGB and PH will undertake assessment of the risk of bias of the included trials independently, with the following taken into consideration, as guided by theCochrane Handbook for Systematic Reviews of Interventions (Handbook 2011):

• sequence generation;

• allocation concealment;

• blinding;

• incomplete outcome data;

• selective outcome reporting; and

• other sources of bias (validity and sensitivity of questionnaires and measurement methods used to measure the outcomes).

We will use the Cochrane 'Risk of bias' tool in RevMan 5.3 (RevMan 2014), which involves describing each of these domains as reported in the trial and then assigning a judgement about the adequacy of each entry: 'low', 'high' or 'unclear' risk of bias. For other sources of bias, we will only consider the issue of validity and sensitivity of questionnaires as a high risk of bias if there is evidence or a strong rationale to believe that the lack of sensitivity will bias the results towards 'no difference', or the type of measure is unfairly favourable/unfavourable to either of the treatments. We will revisit and discuss disagreements with all authors until consensus is reached.

Measures of treatment effect

We will summarise dichotomous data as risk ratios (RR) with 95% confidence intervals (95% CI). 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 may also calculate the number needed to treat to benefit (NNTB) using the pooled results. The assumed baseline risk is typically 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 is used as the 'study population' (Handbook 2011). If a large number of studies are available, and where appropriate, we may also 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 summarise the treatment effect as the mean difference (MD) with 95% CI or as the standardised mean difference (SMD) with 95% CI if different scales have been used to measure the same outcome. We will provide a clinical interpretation of the SMD values.

We will dichotomise or analyse ordinal data as a continuous outcome, depending on the outcome and whether the scale can be expected to be normally distributed.

Unit of analysis issues

Dealing with missing data

To obtain any missing data we will make efforts to contact the corresponding author to request this. In the event of missing data we will perform an available case analysis.

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 theCochrane Handbook for Systematic Reviews of Interventions (Handbook 2011). If it is impossible to estimate these, we will contact the study authors.

Apart from imputations for missing standard deviations, we will conduct no other imputations. We will extract and analyse all data 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 between them in the types of participants recruited, interventions or controls used and outcomes measured.

We will assess statistical heterogeneity by visually inspecting the forest plots and considering the Chi² test (with the threshold for significant heterogeneity being an associated P value below 0.1). We will also express heterogeneity in terms of the I² statistic, which calculates the percentage of variability that is due to heterogeneity rather than chance with low, medium and high ranges of 20% to 40%, 41% to 60% and 61% to 100%, respectively (Handbook 2011).

Assessment of reporting biases

We will assess reporting bias as between‐study publication bias and within‐study outcome reporting 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 method. We will analyse time‐to‐event data using the generic inverse variance method.

For continuous outcomes, if all the data are from the same scale, we may 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

A number of factors could affect the relative benefit of binaural versus monaural hearing aids. If heterogeneity is detected, we will assess this using the following subgroup analyses, including:

• type of hearing aid;

• age;

• sex;

• severity of hearing loss ‐ degree of hearing loss will be based on the better ear hearing threshold average as classified earlier;

• asymmetry of loss;

• cognitive impairment;

• visual impairment;

• presence of tinnitus with hearing loss;

• first time users of hearing aid.

We will conduct some subgroup analyses regardless of whether statistical heterogeneity is observed, as these are widely suspected to be potential effect modifiers. For this review, this will be the type of hearing aid. We will present the main analyses of this review according to type of hearing aid. We will present all other subgroup analysis results in tables.

When studies have a mixed group of patients, we will analyse the study as one of the subgroups (rather than as a mixed group) if more than 80% of patients belong to one category.

Sensitivity analysis

We will 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 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);

• how outcomes were measured: we will investigate the impact of including data where the validity of the measurement is unclear.

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.