Types of studies

We will include randomised controlled trials (RCTs) and non‐randomised studies. We expect to retrieve few RCTs and will include non‐randomised study designs to ensure that findings from the review are based on the widest available evidence base. We will include non‐randomised studies in which allocation to groups is more directly related to interventions, that is quasi‐randomised studies. We will exclude non‐randomised studies in which allocation to groups is related to outcomes, that is case‐control studies. We will include studies published as full‐text reports or abstracts only; we will also include unpublished data.

Types of participants

We will include children aged up to two years who are diagnosed with acute bronchiolitis on clinical assessment irrespective of confirmation of viral aetiology presenting to emergency departments, outpatient departments, admitted to hospital or intensive care units. We will not exclude studies in children with comorbidities or who have high risk factors. Comorbidities and high risk factors for the population of interest for this review include aged less than 12 weeks, preterm birth 34 weeks or less gestation, histories of diagnosed chronic lung or congenital heart disease, or immunodeficiency.

Types of interventions

Magnesium sulphate (any dose, route of administration, or timing) alone or as an adjunct to conventional treatments including:

• nebulised epinephrine;

• nebulised bronchodilators; or

• nebulised hypertonic saline.

We plan to compare:

• magnesium sulphate versus placebo;

• magnesium sulphate versus hypertonic saline;

• magnesium sulphate versus epinephrine; and

• magnesium sulphate versus conventional bronchodilator.

We will also include studies with the following co‐interventions, provided they are not part of the randomised treatment and participants in both study arms received the same treatments, except for magnesium sulphate:

• magnesium sulphate + bronchodilator versus no treatment or normal saline + the same bronchodilator;

• magnesium sulphate + hypertonic saline versus no treatment or normal saline + hypertonic saline; and

• magnesium sulphate + epinephrine versus no treatment or normal saline + epinephrine.

Types of outcome measures

Electronic searches

We will search the following databases from inception to present:

• Cochrane Acute Respiratory Infections Group Specialized Register;

• CENTRAL (Cochrane Central Register of Controlled Trials);

• MEDLINE (PubMed); and

• Embase.

We will also search the following databases, if relevant.

• CINAHL (Cumulative Index to Nursing and Allied Health Literature); and

• LILACS (Latin American and Caribbean Center on Health Sciences Information).

We will use the search strategy described in Appendix 1 to search MEDLINE. Because we plan to include RCTs and non‐randomised studies, we will not restrict the search to any particular study design.

We will also search ClinicalTrials.gov (www.clinicaltrials.gov) and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (apps.who.int/trialsearch/).

We will not impose language or publication restrictions for searches.

Searching other resources

We will check reference lists of all primary studies and review articles for additional references. We will contact experts in the field to identify additional unpublished materials.

Selection of studies

Two review authors (SC, AKY) will independently screen titles and abstracts of studies identified as a result of the search for potential inclusion in the review.

We will retrieve full‐text study reports of those studies deemed potentially eligible, and two review authors (SC, AKY) will independently screen the full texts to identify studies for inclusion and record reasons for exclusion of ineligible studies. Any disagreements will be resolved through discussion or by consulting a third review author (DK) if necessary. We will identify and exclude duplicates and collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table (Moher 2009). We will not impose any language restrictions.

Data extraction and management

We will use a data collection form for study characteristics and outcome data that has been piloted on at least one study in the review. One review author (AKY) will extract study characteristics from the included studies. We will extract the following study characteristics.

1. Methods: study design, total duration of study, details of any 'run in' period, number of study centres and location, study setting, withdrawals, and date of study.

2. Participants: N, mean age, age range, gender, severity of condition, diagnostic criteria, baseline lung function, inclusion criteria, and exclusion criteria.

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

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

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

Two review authors (SC, AKY) will independently extract outcome data from the included studies. We will note in the 'Characteristics of included studies' table if outcome data are not reported in a usable way. Any disagreements will be resolved by consensus or by involving a third review author (DK) if necessary. One review author (AKY) will transfer data into the Review Manager 5 file (Review Manager 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 (SC) will spot‐check study characteristics for accuracy against the trial report.

Assessment of risk of bias in included studies

Two review authors (SC, AKY) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), and the guidance from Cochrane Effective Practice and Organisation of Care Group (EPOC 2017). Any disagreements will be resolved by discussion or by involving another review author (DK) if necessary. We will assess the risk of bias according to the following domains.

1. Random sequence generation.

2. Allocation concealment.

3. Blinding of participants and personnel.

4. Blinding of outcome assessment.

5. Incomplete outcome data.

6. Selective outcome reporting.

7. Baseline outcomes measurement.

8. Baseline characteristics.

9. Other bias.

We will grade each potential source of bias as high, low, or unclear and provide a quote from the study report together with a justification for our judgement in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgements across different studies for each of the domains listed. We will consider blinding separately for different key outcomes where necessary. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome.

Measures of treatment effect

We will enter outcome data for each study into the data tables in Review Manager 5 to calculate the treatment effects (Review Manager 2014). We will use risk ratio or Peto odds ratio (when the outcome is a rare event, approximately less than 10%) for dichotomous outcomes such as need for mechanical ventilation, adverse effects, mortality, and readmission rate.

For continuous outcomes, such as duration of mechanical ventilation, length of intensive care unit and hospital stays, and pulmonary function tests, we will calculate mean difference because it is likely that the same scale was used for measurement of these outcomes. We will calculate standardised mean differences for clinical severity scores because we anticipate that different scales will have been used in studies. We will confirm that higher scores for continuous outcomes have the same meaning for the particular outcome, explain the direction, and report if the directions were reversed where required. We will report all pooled effect sizes with 95% confidence intervals.

We will undertake meta‐analyses only where this is meaningful, that is if the treatments, participants, and the underlying clinical question are similar enough for pooling to make sense.

Unit of analysis issues

We will include both RCTs and non‐randomised study designs. The unit of analysis will be the participants. For studies with more than two arms, we will combine groups to make a single pair‐wise comparison. In a trial that compares the magnesium arm with two treatment groups, we will divide magnesium arm participant numbers between comparisons to avoid double‐counting magnesium sulphate participants.

Dealing with missing data

We will contact investigators or study sponsors to verify key study characteristics and to obtain missing numerical outcome data where possible (e.g. when a study is identified as abstract only). Where this is not possible, and the missing data are thought to introduce high risk bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis.

If numerical outcome data such as standard deviations or correlation coefficients are missing, and they cannot be obtained from the study authors, we will calculate them from other available statistics such as P values according to the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011).

Assessment of heterogeneity

We will use the I² statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis.

We will consider an I² statistic of more than 50% or a Chi² test for heterogeneity that gives a P value of less than 0.10 as substantial heterogeneity (Higgins 2011).

Assessment of reporting biases

If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible small‐study and publication biases.

Data synthesis

We will pool data from studies that we judge to be clinically homogeneous using Review Manager 5 software (Review Manager 2014). If more than one eligible study provides usable data in any single comparison, we will perform a meta‐analysis. If both RCTs and non‐randomised study designs are available, we will pool results for analysis by study type.

We expect the studies identified in the searches to differ in terms of intervention dose, route of delivery, and study location. As these factors could affect our results, we will use the random‐effects model to analysis the results.

Subgroup analysis and investigation of heterogeneity

If data permit, we plan to carry out the following subgroup analyses:

1. according to age (children aged up to 12 months versus children aged from 12 to 24 months);

2. according to the setting (outpatient, emergency department, intensive care unit and admitted children);

3. according to disease severity; and

4. according to the treatment regimen for magnesium sulphate (route of administration, concentration, volume, interval, and duration).

We will use the Chi² test to test for subgroup interactions in Review Manager 5 (Review Manager 2014).

Sensitivity analysis

We plan to carry out the following sensitivity analyses if sufficient numbers of studies are available.

1. We will examine the effect of excluding studies assessed as at high risk of bias for primary outcomes.

2. We will examine the effect of excluding participants with poor prognostic risk factors.

3. We plan to exclude comparisons presenting outlier effect sizes. Outlier effect sizes are studies that appear to be separated from other studies on visual inspection. We will check the effect of exclusion of such outlying studies on the analysis. If we find a substantial change, we will consider that study as an influential study.