Types of studies

We will include studies with the following design characteristics:

• Randomised controlled trials.

We will include trials randomised both 'by patient' and 'by ear' providing, in the latter case, that the effects of treatment (both BET and the comparator) are measured using ear‐specific outcome measures (e.g. tympanometry).

The Unit of analysis issues section provides further details on how data will be analysed if both split‐person and between‐person studies are included.

Types of participants

Individuals aged 18 years or older with chronic (more than three months duration) obstructive Eustachian tube dysfunction, as defined by the diagnostic criteria used by the trial investigators.

We will not exclude patients who have had previous medical or surgical treatment of Eustachian tube dysfunction. If paediatric cases have been included in a study, we will extract the adult data if participants were stratified by age prior to randomisation. If not, we will accept a level of 'contamination' with paediatric cases, as long as the adults make up more than 75% of the population.

We will exclude studies that include patients with:

• nasopharyngeal malignancy or excised malignancy obstructing the Eustachian tube;

• past radiation therapy to the head and neck;

• cleft palate or repaired cleft palate;

• craniofacial syndrome including Down syndrome;

• ciliary dysmotility syndrome.

Types of interventions

Types of outcome measures

We will analyse the following outcomes in the review, but they will not be used as a basis for including or excluding studies.

We will extract data on outcomes according to the following time points: 0 to < 3 months, 3 to < 12 months, 12 to < 24 months, 2 to 5 years.

Electronic searches

Published, unpublished and ongoing studies will be identified by searching the following databases from their inception:

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

• the Cochrane Central Register of Controlled Trials (CENTRAL) (search via the Cochrane Register of Studies 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 date);

• Ovid Embase (1974 to date);

• LILACS (Latin American and Caribbean Health Science Information database; 1982 to date);

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

• CNKI (searched via Google Scholar 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).

The subject strategies for databases will be modelled on the search strategy designed for CENTRAL (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 Specialist will search Ovid MEDLINE, the Cochrane Library and Google 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.

We will not perform a separate search for adverse effects of balloon dilatation of the Eustachian tube for obstructive Eustachian tube dysfunction in adults. We will consider adverse effects described in the included studies only.

Selection of studies

Two authors (AP and MS) will independently screen the titles and abstracts of every record identified in the search and indicate which reports should be retrieved. If there is insufficient information in the title and abstract to make such decisions, we will retrieve the full text. Two review authors (AP and MS) will independently read the full reports and determine whether these studies meet the inclusion criteria. We will resolve disagreements via discussion, or with a third review author as necessary. If resolving the disagreement is not possible, we will contact the authors for clarification. We will include an adapted PRISMA (Preferred Reporting Items for Systematic reviews and Meta‐Analyses) flow chart of study selection (Liberati 2009).

Data extraction and management

For each included study, two review authors (AP and MS) will independently extract and record the following data using a piloted data collection form:

• Source: study, report and author ID, citation and contact details.

• Methods: study design, unit of randomisation, unit of analysis, total study duration, setting and follow‐up.

• Participants: total number, setting, diagnostic criteria, age, sex, country, prior treatment, co‐morbidity, socio‐demographics; data on different presentations of Eustachian tube dysfunction (including presence of OME, tympanic membrane retraction, tympanic membrane perforation and cholesteatoma). We will also extract symptoms of Eustachian tube dysfunction without any abnormal signs.

• Interventions: total number of intervention groups, details of specific intervention (i.e. balloon size, inflation pressure and device design), prior medical or surgical interventions, any co‐interventions. A recent systematic review found that no intervention has been demonstrated to be an effective treatment for Eustachian tube dysfunction (Llewellyn 2014), so we will group comparators in our analysis into medical and surgical treatments.

• Outcomes: outcome measures and time points (i) collected and (ii) reported, outcome definition, unit of measurement. We will categorise adverse events as early if occurring within 24 hours of the intervention or the start of medical treatment, or late if occurring more than 24 hours after. We will grade adverse events by severity according to the Clavien‐Dindo system (Dindo 2004).

• Results: sample size, missing participants, summary data for each intervention group and subgroup analyses.

• Miscellaneous: funding, study author conflicts of interest, comments, correspondence required.

We will resolve disagreements via discussion or with a third review author as necessary. Where necessary, we will contact study investigators for clarification. We will extract adjusted or unadjusted results as guided by the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011).

Assessment of risk of bias in included studies

Two review authors will undertake assessment of the risk of bias of the included trials independently, with the following taken into consideration, as guided by theCochrane Handbook (Handbook 2011):

• sequence generation;

• allocation concealment;

• blinding of participants and personnel;

• blinding of outcome assessment;

• incomplete outcome data;

• selective outcome reporting; and

• other sources of bias.

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. We will resolve disagreements via discussion, or with a third review author as necessary.

We will account for baseline imbalances between groups when assessing selection bias according to the framework proposed by Corbett 2014.

We will assess performance bias, detection bias and attrition bias for each of the review outcomes separately. We will report and group results as appropriate (for instance, by grouping self‐reported and objective outcomes separately). We will summarise an overall risk of bias per outcome (Higgins 2011; Appendix 2).

We will assess risk of bias associated with the reliability of outcome measurement tools separately ('other bias' in the 'Risk of bias' tool) and account for this in the interpretation of the results.

Measures of treatment effect

We will express dichotomous data as a risk ratio (RR) with 95% confidence interval (CI). We will express continuous data (final values will be preferred over change scores) as a standardised mean difference (SMD) with 95% CI. If studies perform an ANCOVA analysis to account for a significant imbalance in outcome at baseline, then we will use these results. Where possible we will express time‐to‐event data (e.g. disease recurrence and re‐treatment) as a hazard ratio. We will calculate unadjusted treatment effects using Cochrane's Review Manager (RevMan) software where possible (RevMan 2014).

Unit of analysis issues

We will take into account the level at which randomisation occurred. Unit of analysis issues may arise where the unit of randomisation differs from the unit of analysis. Trials may randomise participants to the interventions but report outcomes on a per‐ear basis. Where the number of ears appears to equal the number of participants we will treat the ear as the unit of analysis. When this is not the case we will contact the study authors and request additional information to enable us to carry out a per‐ear analysis, which takes into account the fact that some of the data may be non‐independent. Pairing of data (within‐patient) may arise where ears are both randomised and analysed. For such studies we will prefer adjusted results to account for within‐person correlation and we will request additional information to enable us to calculate adjusted results from the study authors.

Dealing with missing data

Where necessary, we will contact the corresponding authors of included studies to supply any unreported data (such as group means and standard deviations (SDs), details of dropouts and details of interventions received by the control group). If a study reports outcomes only for participants completing the study or only for participants who followed the protocol, we will contact the authors and ask them to provide additional information to allow analyses according to intention‐to‐treat principles. We will describe missing data and dropouts/attrition for each included study in the 'Risk of bias' tables, and discuss the extent to which the missing data may affect the results and conclusions of the review. If data are still unavailable after author contact, we will use an available case analysis method, where data are included on only those whose results are known, using as a denominator the total number of people who had data recorded for the particular outcome in question. We will assess variation in the degree of missing data across studies as a potential source of heterogeneity.

We will assess the sensitivity of any primary meta‐analyses to missing data using the method recommended by Higgins et al (Higgins 2008). We will report missing data per group.

Assessment of heterogeneity

We will assess clinical variation across studies by comparing the distribution of potentially important participant factors among trials (e.g. baseline severity, co‐morbidities), and trial factors (randomisation concealment, blinding of outcome assessment, losses to follow‐up, BET balloon size, inflation pressure, device type).

We will visually inspect the forest plots for heterogeneity by looking at the consistency of intervention effects across included studies. Where possible, we will describe statistical heterogeneity by computing the I² statistic and Chi² test. We will interpret the I² and Chi² values following the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011).

Assessment of reporting biases

If sufficient studies are found, we will assess reporting biases by visual inspection of funnel plots. Where possible, as a direct test for publication bias, we will compare results extracted from published journal reports with results obtained from other sources.

Data synthesis

Where appropriate, we will carry out all the analyses on an intention‐to‐treat basis. We will use RevMan 5.3 to carry out the meta‐analyses for comparable trials and outcomes (RevMan 2014). We will perform statistical analyses according to the statistical guidelines referenced in the most recent version of the Cochrane Handbook for Systematic Reviews of Interventions (Handbook 2011). In the event of substantial clinical heterogeneity (for instance, significantly different presentations of Eustachian tube dysfunction) or methodological or statistical heterogeneity, we will not pool studies in a meta‐analysis and we will present the results in a narrative summary. We will not pool split‐person and between‐person studies.

For some outcomes, such as Eustachian tube function test scores, symptoms scores and quality of life measures, different scales may be used, and some may be inverse to others. Where needed, we will standardise scales through multiplication or inversion, to allow comparison of results between methods.

We will look at all available data and, if data permit, combine and stratify studies according to intervention characteristics (for example, first‐ and second‐line interventions, device and inflation characteristics). For continuous outcomes, we will prefer change scores over final values.

Subgroup analysis and investigation of heterogeneity

We will perform subgroup analysis based on:

• the different presentations of Eustachian tube dysfunction;

• the use of a planned co‐intervention.

Presentation of Eustachian tube dysfunction can vary from symptoms of pressure to visible manifestations of chronic otitis media such as otitis media with effusion or cholesteatoma. We anticipate that study authors may select groups of patients with the same presentation in order to measure the effects of BET in an homogenous group.

If BET is used in combination with another intervention, for example, grommet insertion (and compared with grommet insertion alone) then that would also necessitate a subgroup analysis (measuring the effect of BET as an adjunct to grommet insertion). Large numbers of subgroup analyses may lead to misleading conclusions (Oxman 1992; Yusuf 1991), therefore these analyses will be exploratory and we will treat any conclusions with caution. Where possible we will investigate differences between two or more subgroups using the method described by Borenstein et al (Borenstein 2008).

Sensitivity analysis

We will perform sensitivity analysis to explore the influence of including only studies with an overall low risk of bias per outcome across all domains.