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Cochrane Database of Systematic Reviews Protocol - Intervention

Magnesium sulphate for acute bronchiolitis in children under two years of age

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Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the effects of magnesium sulphate in acute bronchiolitis in children below two years of age.

Background

Description of the condition

Acute bronchiolitis represents a significant burden on healthcare facilities, which in recent years has increased. Increased rates of bronchiolitis‐related emergency department visits, Carroll 2008; Hasegawa 2014a, and hospitalisation have been documented (Green 2016). The incidence of bronchiolitis is estimated to range from 265 per 1000 infants to 16.4 per 100 children aged up to two years (Carroll 2008; Muñoz‐Quiles 2016). It has been further estimated that 17% of children with bronchiolitis who are admitted to hospital are treated in intensive care units; 42% of these children are treated using either invasive or non‐invasive mechanical ventilation (Mansbach 2012a). The percentage of children to die from bronchiolitis is 4.2% (Shay 2001), and a case fatality rate of 0.08% in hospitalised children has been observed (Muñoz‐Quiles 2016). The numbers of children with advanced disease have increased, and consequently, healthcare costs (Hasegawa 2013).

Acute bronchiolitis is a lower respiratory tract disease affecting mostly infants aged up to two years. Many viral infections can result in bronchiolitis; respiratory syncytial virus is the most common aetiological agent, and affects more than 60% of children with bronchiolitis (Calvo 2010; Hasegawa 2014b; Mansbach 2012b). Infection induces inflammation of the lower airways, causing bronchiolar wall oedema, resulting in narrowing of the distal airways. Further tapering of the lumen of these airways occurs due to increased secretions and cellular debris. Bronchiolitis may cause significant airway obstruction via the bronchioles, leading to the need for mechanical ventilation in some circumstances. Irrespective of the causative virus, clinical presentation is typical; pathological investigation is not required for diagnosis. The diagnosis and management of bronchiolitis vary in different regions of the world. The American Academy of Pediatrics together with the European Respiratory Society defined bronchiolitis as the first episode of wheezing preceded by "a constellation of clinical symptoms and signs suggestive of a viral upper respiratory prodrome followed by increased respiratory effort in children less than 2 years of age" (AAP Subcommittee 2006). In the UK, a Delphi consensus defined bronchiolitis as "a seasonal viral illness characterised by fever, nasal discharge, and dry, wheezy cough. On examination there are fine inspiratory crackles and/or high‐pitched expiratory wheeze" (Lakhanpaul 2002). In the UK, the presence of wheeze is not mandatory for diagnosis. Most European countries restrict the diagnosis of bronchiolitis to children aged up to 12 months. For this review we will follow the AAP Subcommittee 2006 definition. Some of the risk factors associated with bronchiolitis severity are low socioeconomic status, male gender, prematurity, prenatal exposure to steroids, and maternal smoking (Lanari 2015; Murray 2014).

No specific treatment is currently available and remains supportive care including adequate hydration and humidified oxygen supplementation. Various treatment options have been proposed, of which only nebulised epinephrine and hypertonic saline have been shown to be useful (Hartling 2011; Zhang 2013).

Description of the intervention

Magnesium is the active component of its sulphate salt of magnesium, sulphur, and oxygen with many different pharmacological actions. Magnesium is an important cofactor of many enzymes involved in biological reactions and is present in tissues including brain, smooth muscles of uterus, bronchioles, and the gastrointestinal tract. It has many therapeutic uses such as controlling convulsions, preventing preterm labour, treatment of constipation, control of tachyarrhythmias, and reversing bronchoconstriction in status asthmatics. The action of magnesium on bronchioles results in dilation of the airways by several mechanisms. Use of magnesium sulphate for children with bronchiolitis is based on its treatment effectiveness for adults, Kew 2014, and children with asthma (Griffiths 2016). The clinical presentation of asthma is similar to bronchiolitis: both involve narrowing of distal airways.

Treatment with magnesium sulphate may reduce hospital admissions of children with acute asthma presenting to the emergency department; evidence on the efficacy of magnesium sulphate is required for children with bronchiolitis. Magnesium sulphate can be administered intravenously or nebulised. The dose of intravenous magnesium sulphate for bronchodilation effect used in trials ranges from 25 to 100 mg/kg/dose (maximum 2 g) (Alansari 2017; Ciarallo 1996; Scarfone 2000). Nebulisation dose ranges from 40 mg/kg, Modaresi 2015, to 150 mg per dose (Kose 2014). Common adverse effects of magnesium sulphate therapy include hypotension (Ciarallo 1996; Goodacre 2013; Scarfone 2000), cardiac arrhythmias (Goodacre 2013; Lu 2000), and respiratory depression (Lu 2000; Mahajan 2004). Respiratory depression can be monitored by examining deep tendon reflex; loss of this reflex is the first sign of impending toxicity (Lu 2000).

How the intervention might work

Acute bronchiolitis results in the narrowing of small distal airways causing airflow obstruction. Treatment to dilate airways may prove useful for treatment of children with acute bronchiolitis. Magnesium sulphate has been shown to dilate bronchial muscle in animal studies (Hirota 1999; Kumasaka 1996; Spivey 1990), and may result in bronchial smooth muscle relaxation by blocking the voltage‐dependent calcium channels, preventing calcium influx (Gourgoulianis 2004). Magnesium sulphate decreases acetylcholine accumulation at nerve endings, further preventing bronchoconstriction (Castillo 1954). Several ways that magnesium sulphate may act on bronchiolar wall oedema resulting in bronchodilation have been proposed. Magnesium sulphate may offer a safe, widely available, and low‐cost therapy to relieve airway obstruction in children with bronchiolitis.

Why it is important to do this review

Several Cochrane Reviews have investigated treatment options for children with acute bronchiolitis including nebulised deoxyribonuclease (Enriquez 2012), heliox inhalation (Liet 2015), bronchodilators other than magnesium sulphate (Gadomski 2014), nebulised epinephrine (Hartling 2011), nebulised hypertonic saline (Zhang 2013), and steroids (Fernandes 2013). However, none of these has been adopted as treatment. The role of magnesium sulphate therapy for bronchiolitis has not been reviewed previously. This review will complement other Cochrane Reviews to achieve consensus on treatment for children with acute bronchiolitis. Bronchiolitis leads to significant healthcare resource utilisation, so it is important to explore magnesium sulphate treatment.

Objectives

To assess the effects of magnesium sulphate in acute bronchiolitis in children below two years of age.

Methods

Criteria for considering studies for this review

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

Primary outcomes

  1. Mortality.

  2. Clinical severity score calculated measured using any validated scoring system or duration of mechanical ventilation, hospital or intensive care unit stay.

  3. Adverse effects of magnesium sulphate treatment.

Secondary outcomes

  1. Pulmonary function test.

  2. Hospital readmission rate within 30 days of discharge.

Search methods for identification of studies

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.

Data collection and analysis

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.

Assessment of bias in conducting the systematic review

We will conduct the review according to this published protocol and report any deviations from it in the 'Differences between protocol and review' section of the systematic review.

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.

GRADE and 'Summary of findings' table

We will create a 'Summary of findings' table using the following outcomes: mortality, clinical severity scores, adverse events such as hypotension and respiratory depression, need for mechanical ventilation, duration of mechanical ventilation, length of intensive care unit and hospital stay, and hospital readmission rate. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness, and publication bias) to assess the quality of a body of evidence as it relates to the studies that contribute data to the meta‐analyses for the prespecified outcomes (Atkins 2004). We will use methods and recommendations described in Section 8.5 and Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), employing GRADEpro GDT software (GRADEpro GDT 2015). We will justify all decisions to downgrade or upgrade the quality of studies using footnotes, and we will make comments to aid readers' understanding of the review where necessary.

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.