Intratracheal instillation of corticosteroids combined with surfactant for preventing chronic lung disease in preterm infants

Objectives

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

Primary objective

To evaluate the benefits and harms of intratracheal instillation of corticosteroids combined with surfactant versus surfactant alone for the preventing chronic lung disease in preterm infants.

Secondary objective

To identify equity issues that may be associated with the implementation, uptake, or effectiveness of intratracheal instillation of corticosteroids.

Background

Description of the condition

Preterm infants often experience respiratory difficulty due to a deficiency of pulmonary surfactant, which is a complex of phospholipids and proteins formed by type II alveolar cells to reduce surface tension. This condition is known as respiratory distress syndrome (RDS). Surfactant replacement therapy has become the mainstay for treating RDS, and its use decreases lung injury and improves survival [1, 2, 3]. Although the risk of mortality for high‐risk preterm infants affected by RDS has decreased [4, 5, 6], many develop bronchopulmonary dysplasia (BPD), a form of chronic lung disease that has increased in prevalence since 2012 [7, 8].

With the survival of smaller preterm infants, our understanding of the pathogenesis of BPD has evolved. With advances in neonatal care that now routinely involve antenatal steroids, surfactant, and gentler ventilation strategies, larger preterm infants rarely develop BPD, while their extremely low birth weight (ELBW) counterparts continue to be greatly affected. No longer thought of as solely a consequence of barotrauma (physical damage to body tissues caused by a difference in pressure between a gas space inside, or in contact with, the body and the surrounding gas or liquid) and oxygen toxicity, the “new BPD” theorizes multiple causative agents resulting in dysmorphic, simplified and larger alveoli, with less fibrosis (development of fibrous connective tissue in response to an injury) and inflammation than in the pre‐surfactant era [9], with inflammation playing a key role in its pathogenesis [10, 11].

The definition of BPD has evolved [12, 13, 14, 15, 16]. In 2019, Jensen and colleagues provided the most recent, evidence‐based definition of BPD after comparing 18 different definitions found in the literature. They found the definition that best predicted death after 36 weeks' PMA (postmenstrual age), or adverse respiratory and neurodevelopmental outcomes at 18 to 26 months corrected age, categorizes disease severity based on mode of respiratory support at 36 weeks, regardless of supplemental oxygen use, using a grade I to III scale [17].

Description of the intervention and how it might work

Systemic (intravenous or enteral) postnatal corticosteroids can be beneficial for preventing and managing BPD, due to their anti‐inflammatory properties [18].

Although early use of systemic dexamethasone (0 to seven days of life) can reduce the duration of respiratory support and incidence of death or BPD, these benefits are outweighed by both immediate and longer‐term risks. These include the risk of gastrointestinal perforation, neurodevelopmental impairment, and cerebral palsy. For these reasons, the early use of dexamethasone for preventing BPD is not recommended [19, 20].

The late use of systemic dexamethasone (> seven days of life) can decrease rates of BPD and death, and reduce extubation failure rates (failure rates of the removal of a tube previously inserted into a patient's body) and the need for home oxygen therapy. Despite these potential benefits, data from early randomized controlled trials (RCTs) highlight the increased risk of adverse neurodevelopment, cerebral palsy in particular, with the use of higher doses and longer courses of dexamethasone [20, 21, 22, 23]. More data from RCTs studying the use of corticosteroids for preventing and treating BPD has emerged. Meta‐regression analysis of these data has concluded that if the pre‐treatment risk of BPD exceeds 60%, the neurodevelopmental benefits of corticosteroids appear to outweigh the risks [24, 25, 26, 27].

Alternatives to systemic corticosteroid administration have been tested, with the hope of avoiding the adverse systemic effects of steroid treatment. Inhaled steroids, predominately budesonide, have been used to both prevent and treat BPD. A 2017 Cochrane review investigated the use of early inhaled corticosteroids (< seven days of life) and found no significant reduction in the rate of BPD at 36 weeks' PMA, but a potential reduction of the combined outcome of death or BPD at 36 weeks' PMA [28]. A large RCT found no difference in the rate of neurodevelopmental disability for the early inhaled budesonide group, but a concerning increase in mortality at two years of age in infants receiving early administration of inhaled corticosteroids [29], thus deterring its use [30].

An additional limitation of inhaled corticosteroids in preterm infants is poor pulmonary deposition due to intrinsically low lung volumes and inspiratory pressures. To overcome this limitation and to potentially avoid negative systemic effects, the combination of surfactant and intratracheal corticosteroids has been the focus of recent investigations [31]. Thus, it is the focus of this Cochrane review.

Why it is important to do this review

BPD has long‐lasting effects, including poor neurodevelopmental outcomes and long‐term pulmonary dysfunction [32, 33, 34, 35, 36, 37, 38]. The use of systemic glucocorticoids for preventing BPD in the highest‐risk infants is common and effective, but is not without risk. Due to this risk, their use should come with thoughtful consideration. Notably, despite the use of systemic steroids and other advances in neonatal care, such as antenatal steroids and more gentle ventilation strategies, a recent report demonstrated an overall increase in BPD, with a steady rise since 2012 [7]. These data highlight the need for continued efforts in research looking at strategies to prevent BPD.

The use of exogenous surfactant is a proven therapy to reduce RDS severity [1, 2]. Researchers have looked at the feasibility of mixing a corticosteroid with a surfactant and administering it intratracheally (within or into the trachea, or windpipe) to mitigate the inflammation seen in this period, which is thought to be a key factor in the pathogenesis of BPD. The use of surfactant as a vehicle is theorized to help ensure more uniform distribution of the steroid, even to the more distal airways [39]. This approach offers a unique opportunity to combine two therapies with the goal of reducing BPD incidence, while potentially avoiding the harmful effects of systemic steroids. This review will investigate this potential therapy's impact on the combined and separate outcomes of death and BPD at 36 weeks' PMA.

Objectives

Primary objective

To evaluate the benefits and harms of intratracheal instillation of corticosteroids combined with surfactant versus surfactant alone for the preventing chronic lung disease in preterm infants.

Secondary objective

To identify equity issues that may be associated with the implementation, uptake, or effectiveness of intratracheal instillation of corticosteroids.

Methods

We have developed this protocol with reference to methodological guidance in the Cochrane Handbook for Systematic Reviews of Interventions [40], and the Methodological Expectations of Cochrane Intervention Reviews (MECIR) [41], and reporting guidance of PRISMA‐P [42]. We will follow the same methodological guidance for the review, and report it using guidance from PRISMA [43, 44].

Criteria for considering studies for this review

Types of studies

We will include RCTs, quasi‐RCTs (trials using strategies of allocation that are not truly random, e.g. allocation by patient identification number) with parallel groups, and cluster‐RCTs.

We will exclude cross‐over randomized trials, because they are not feasible given the timing of the intervention and do not allow assessment of long‐term outcomes. We will exclude non‐randomized cohort studies, because they are prone to bias due to confounding by indication, or by residual confounding: both of which may influence the results of the studies [45, 46].

Types of participants

We will include preterm infants (< 37 weeks' gestation) at risk of or having RDS and admitted to a hospital neonatal unit. For studies that include both preterm infants and term (born at 37 weeks' gestation or more) infants, we will contact the study authors to obtain outcome data regarding the preterm infants. If this is not possible, we will exclude the study if the mean age of the included participants is above 37 weeks' gestation.

Types of interventions

We will include studies comparing intratracheal administration of corticosteroids (including budesonide, fluticasone, or beclomethasone) in combination with exogenous surfactant preparations (animal‐derived or synthetic) versus surfactant alone.

Intratracheal administration may include administration via endotracheal tube (for purposes of respiratory support); intubation, surfactant administration followed by rapid extubation (INSURE); or thin catheter administration (less invasive surfactant administration (LISA) or minimally invasive surfactant administration (MIST)). We will exclude studies using laryngeal masks or similar devices, which do not pass through the vocal cords. In such cases, medication is delivered above the glottis and may reach the trachea only by gravity or during spontaneous inspiration, resulting in less precise delivery than with an endotracheal tube.

Outcome measures

The outcome measures are detailed below. We will include studies measuring one or more of the outcomes, even if the study reports no data for that outcome.

Critical outcomes

• Death or BPD (oxygen supplementation) at 36 weeks' PMA

• BPD (oxygen supplementation) at 36 weeks' PMA

• Death at 36 weeks' PMA

Important outcomes

• All‐cause mortality prior to hospital discharge

• Pneumothorax until hospital discharge

• Retinopathy of prematurity (any stage and ≥ severe stage 3) [47]

• Intraventricular hemorrhage (any grade and severe grades 3 and 4) [48], until hospital discharge

• Duration of respiratory support (days) until hospital discharge

• Duration of supplemental oxygen (days) until hospital discharge

• Duration of hospital stay (days) until hospital discharge

• Use of systemic postnatal corticosteroids

• Neurodevelopmental outcomes

  • Cerebral palsy. We plan to separately assess outcomes at 18 months to 24 months of corrected age, and at three to five years of corrected age.

  • Severe developmental delay per Bayley Mental Developmental Index [49, 50], or Griffiths Mental Development Scale [51], assessed as more than two standard deviations (SDs) below the mean. If severe developmental delay is measured by more than one scale (i.e. Bayley Mental Developmental Index and Griffiths Mental Development Scale), we will combine outcome data in the same analysis. We plan to separately assess outcomes at 18 months to 24 months of corrected age, and at three to five years of corrected age.

  • Developmental delay per Bayley Mental Developmental Index [49, 50], or Griffiths Mental Development Scale [51], reported as a continuous outcome. If developmental delay is measured by more than one scale (i.e. Bayley Mental Developmental Index and Griffiths Mental Development Scale), we will combine outcome data in the same analysis. We plan to separately assess outcomes at 18 months to 24 months of corrected age, and at three to five years of corrected age.

  • Severe intellectual impairment (intelligence quotient (IQ)) per Bayley Mental Developmental Index [49, 50] or Griffiths Mental Development Scale [51], more than two SDs below the mean. If severe intellectual impairment is measured by more than one scale (i.e. Bayley Mental Developmental Index and Griffiths Mental Development Scale), we will combine outcome data in the same analysis. We plan to separately assess outcomes at 18 months to 24 months of corrected age, and at three to five years of corrected age.

  • Intellectual impairment, IQ, per Bayley Mental Developmental Index [49, 50], or Griffiths Mental Development Scale [51], reported as a continuous outcome. If intellectual impairment is measured by more than one scale (i.e. Bayley Mental Developmental Index and Griffiths Mental Development Scale), we will combine outcome data in the same analysis. We plan to separately assess outcomes at 18 months to 24 months of corrected age, and at three to five years of corrected age.

  • Blindness (vision < 6/60 in both eyes). We will separately assess outcomes at the age of 18 months to 24 months of corrected age, and at three to five years of corrected age.

  • Sensorineural deafness requiring amplification. We will separately assess outcomes at the age of 18 months to 24 months of corrected age, and at three to five years of corrected age.

Search methods for identification of studies

Electronic searches

The Information Specialist (MF) drafted a search strategy. An Information Specialist assigned by the Cochrane Central Editorial Service will peer review the draft search strategy. Searches will be conducted without language or publication type restrictions. We will use methodological filters to identify RCTs and systematic reviews; we will note the source of filters in the search strategies. Searches for trials will not be limited by date, and we will limit searches for systematic reviews to the past two years.

We will search the following databases.

• Ovid MEDLINE, All, 1946‐

• Ovid Embase, 1974‐

• CENTRAL via Cochrane Central Register of studies (CRS)

A draft search strategy, preceded by a search narrative [52], is in Supplementary material 1.

Searching other resources

We will search the following two trial registries.

• US National Library of Medicine (clinicaltrials.gov)

• World Health Organization International Clinical Trial Registry Platform (https://trialsearch.who.int)

We will search the following conference abstracts.

• European Academy of Paediatric Societies (EAPS), 2020‐

• Pediatric Academic Societies (PAS), 2020‐

• Perinatal Society of Australia and New Zealand (PSANZ), 2020‐

We will scan the reference lists of related systematic reviews and included studies in an effort to identify additional studies. We will search for errata or retractions for included studies in PubMed (www.ncbi.nlm.nih.gov/pubmed) and Retraction Watch (retractiondatabase.org).

Data collection and analysis

We describe the methods for data collection below. In the event we identify and include studies by authors of this Cochrane review, two review authors will independently undertake the following: screening and selection, data extraction, risk of bias assessment, and assessment of the certainty of evidence. In the event multiple authors of this Cochrane review are involved in an included study, we will recruit independent colleagues to undertake these tasks and will acknowledge these individuals in the published review.

Selection of studies

We will manage the search results using reference management software. We will conduct screening using Covidence [53].

Two review authors (LB, AP) will independently screen titles/abstracts and independently review the full‐texts of references retained following title/abstract review. At any point during the screening process, we will resolve disagreements by discussion or by consulting a third review author (RS). We may use the RCT classifier in Covidence prior to author screening, and will report results of this process in the review.

We will collect information regarding the method of randomization, blinding, intervention, stratification, and whether the trial was single or multicenter for each included study. We will analyze the clinical outcomes noted above in the Outcome measures section. We will present this information in both a detailed ‘Characteristics of included studies’ table and in an ‘Overview of synthesis of studies’ table.

We will document the reasons for excluding studies during full‐text review in a ‘Characteristics of excluded studies table’. We will provide any information we can obtain about ongoing studies. Studies with insufficient information to allow data extraction will be presented in an ‘awaiting assessment’ reference list and will be incorporated into an update of the review should sufficient information become available. We will group multiple reports of the same study under a single study ID so that each study, rather than each report, will be the unit of interest in the review. The study selection process will be reported in a PRISMA flow diagram [43, 44].

In cases where there are questions about the data reported in a study, we will attempt to contact study authors for clarification or additional information. If we identify studies in languages not read by review authors, we will first use an online translation service (such as Google Translate) and, where possible, we will seek a native speaker.

Data extraction and management

Two review authors (LB, AP) will independently extract data using a data extraction form based on the Cochrane Effective Practice and Organisation of Care (EPOC) Group data collection checklist [54]. We will pilot the form within the review team using a sample of three included studies.

We will extract the following characteristics from each included study.

• Administrative details: study author(s); published or unpublished; year of publication; year in which study was conducted; presence of vested interest by the study authors

• Study characteristics: study registration, study design type, study setting, number of study centers and location; informed consent; ethics approval, details of any ‘run‐in’ period (if applicable), completeness of follow‐up (e.g. > 80%); country income classification

• Participants: number randomized, number lost to follow‐up/withdrawn, number analyzed, mean gestational age, gestational age range, mean chronological age, chronological age range, sex, severity of condition, diagnostic criteria, inclusion criteria and exclusion criteria), birth weight, comorbidities

• Interventions: initiation, dose, and duration of administration

• Outcomes: as mentioned above under Outcome measures

We will resolve any disagreements by discussion.

We will describe ongoing studies identified by our search and document available information, such as the primary author, research question(s), methods, and outcome measures, and an estimate of the anticipated reporting date in the ‘Characteristics of ongoing studies’ table.

Should any queries arise, or in cases for which additional data are required, we will contact study investigators/authors for clarification. Two review authors (LB, AP) will use Review Manager (RevMan) for data entry [55].

We will replace any standard error of the mean by the corresponding SD.

Risk of bias assessment in included studies

Two review authors (LB, AP) will independently assess the risk of bias using the Cochrane Risk of Bias 2 tool (RoB 2) outlined in the Cochrane Handbook for Systematic Reviews of Interventions [40, 56]. We will resolve any disagreements by discussion or by consulting another review author (MB). The outcomes to be assessed for each study are described in the Certainty of the evidence assessment section.

We will assess the risk of bias according to the following domains.

• Bias arising from the randomization process

• Bias due to deviations from intended interventions

• Bias due to missing outcome data

• Bias in measurement of the outcome

• Bias in selection of the reported result

To address these types of bias, we will use the signaling questions recommended in RoB 2 and will make a judgment using the following options.

• ‘Yes’: if there is firm evidence that the question was answered in the study (i.e. the study was at low or high risk of bias given the direction of the question)

• ‘Probably yes’: a judgment was made that the question was answered in the study (i.e. the study was at low or high risk of bias given the direction of the question)

• ‘No’: if there was firm evidence that the question was not answered in the study (i.e. the study was at low or high risk of bias given the direction of the question)

• ‘Probably no’: a judgment was made that the question was not answered in the study (i.e. the study was at low or high risk of bias given the direction of the question)

• ‘No information’: if the study report provided insufficient information to allow any judgment

We will then use the algorithms proposed by RoB 2 to assign each domain one of the following levels of bias.

• Low risk of bias

• Some concerns

• High risk of bias

This approach will allow the derivation of an overall risk of bias rating for each outcome in each study in accordance with the following suggestions.

• ‘Low risk of bias’: we judged the trial at low risk of bias for all domains for this result

• ‘Some concerns’: we judged the trial to raise some concerns in at least one domain for this result, but not at high risk of bias for any domain

• ‘High risk of bias’: we judged the trial at high risk of bias in at least one domain for the result, or we judged the trial to have some concerns for multiple domains in a way that substantially lowered confidence in the results

We will use the RoB 2 Excel tool to assess individually randomized, parallel‐group trials [57]. For cluster‐randomized trials, we plan to use the appropriate RoB 2 Excel tool.

Using the signaling questions in the RoB 2 Excel tool, we will rate each domain as having ‘low risk’, ‘some concerns’, or ‘high risk’ of bias. We will summarize the risk of bias judgments across different studies for each of the domains listed for each outcome. A judgment of high risk of bias within any domain has the same implications for the overall result, irrespective of which domain was being assessed. Therefore, if the answers to the signaling questions yield a judgment of high risk of bias, we will consider whether any identified problems are of sufficient concern to warrant this judgment for that result overall. When we judge there to be some concerns in multiple domains, we will consider an overall judgment of high risk of bias for that result or group of results. The overall RoB 2 judgment for each outcome will be considered as part of the GRADE assessment presented in our summary of findings table.

Overall risk of bias at study level

We will judge a study to have a high risk of bias overall when we judge one or more domains to have a high risk of bias. Conversely, we will judge a study to have a low risk of bias when we judge all domains to have a low risk of bias.

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

Analysis

Our primary analysis will include all studies, regardless of their risk of bias rating. However, if there is substantial heterogeneity that could be explained by a high versus low risk of bias subgroup analysis, we will base our conclusions on the low risk of bias studies to avoid downgrading our certainty in the evidence. In this case, excluding studies at high risk of bias may reduce the need to downgrade for study limitations. However, it can also reduce the number of studies and introduce the possibility of (further) downgrading for imprecision. This is in accordance with GRADE recommendations.

Assessment of bias in conducting the systematic review

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

Measures of treatment effect

Dichotomous data

For dichotomous data, we will present results using risk ratios (RRs) and risk differences (RDs) with 95% confidence intervals (CIs). We will calculate the number needed to treat for an additional beneficial outcome (NNTB), or the number needed to treat for an additional harmful outcome (NNTH) with 95% CIs if there is a statistically significant reduction (or increase) in RD.

Continuous data

For continuous data, we will use the mean difference (MD) when outcomes were measured in the same way between trials. We will use the standardized mean difference (SMD) to combine data from trials that measured the same outcome but used different methods. Where trials reported continuous data as median and interquartile range (IQR), and data passed the test of skewness, we will convert median to mean, and estimate the SD as IQR/1.35.

Count data

For counts and rates, we will calculate data as described by Rose and colleagues [58].

Unit of analysis issues

The unit of analysis will be the participating infant in individually randomized trials; we will consider an infant only once in the analysis. The participating neonatal unit or section of a neonatal unit or hospital will be the unit of analysis in cluster‐randomized trials. For cluster‐randomized trials, we will extract information on the study design and unit of analysis for each study, indicating whether clustering of observations is present due to allocation to the intervention at the group level, or clustering of individually randomized observations (e.g. infants within clinics). We will extract available statistical information needed to account for the implications of clustering on the estimation of outcome variances, such as design effects or intracluster correlation coefficients (ICCs), and whether the study adjusted results for the correlations in the data. In cases where the study does not account for clustering, we will ensure that appropriate adjustments are made to the effective sample size following guidance in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions [59]. Where possible, we will derive the ICC for these adjustments from the trial itself, or from a similar trial. If an appropriate ICC is unavailable, we will conduct sensitivity analysis to investigate the potential effect of clustering, by imputing a range of values of ICC.

If any trials have multiple arms compared against the same control condition that will be included in the same meta‐analysis, we will either combine groups to create a single pair‐wise comparison, or select the pair of interventions that more closely match the definitions given in the Types of interventions, and will exclude the others. We will acknowledge this potential selective bias of data used for analysis in the Discussion section.

Dealing with missing data

We intend to carry out analysis on an intention‐to‐treat basis for all included outcomes. Whenever possible, we will analyze all participants in the treatment group to which they were randomized, regardless of the actual treatment received. If we identify important missing data (in the outcomes) or unclear data, we will contact the original study authors and request the missing data. We will make explicit the assumptions of any methods used to deal with missing data.

For missing dichotomous outcomes, we will include participants with incomplete or missing data in the sensitivity analyses by imputing them according to the following scenarios.

• Extreme‐case analysis favoring the experimental intervention (best‐worst case scenario): none of the dropouts/participants lost from the experimental arm, but all the dropouts/participants lost from the control arm experienced the outcome, including all randomized participants in the denominator

• Extreme‐case analysis favoring the control (worst‐best case scenario): all dropouts/participants lost from the experimental arm, but none from the control arm experienced the outcome, including all randomized participants in the denominator

For continuous outcomes, we will calculate missing SDs using reported P values or CIs [40]. If calculation is not possible, we will impute a SD as the highest SD reported in the other trials for the corresponding treatment group and outcome.

We will address the potential impact of missing data on the findings of the review in the ‘Discussion’ section.

Reporting bias assessment

We will assess reporting bias by comparing the stated primary outcomes and secondary outcomes and the reported outcomes. When study protocols are available, we will compare these to the full publications to determine the likelihood of reporting bias. We will document studies using the interventions in a potentially eligible infant population, but not reporting on any of the primary and secondary outcomes, in the ‘Characteristics of included’ studies tables.

We will use funnel plots to screen for publication bias when there are a sufficient number of studies (> 10 studies) reporting the same outcome. If publication bias is suggested by a significant asymmetry of the funnel plot on visual assessment, we will incorporate this in our assessment of certainty of evidence. If our review includes fewer than 10 studies eligible for meta‐analysis, the ability to detect publication bias will be largely diminished, and we will simply note our inability to rule out possible publication bias or small study effects.

Synthesis methods

If we identify multiple studies that we consider to be sufficiently similar, we will perform meta‐analysis using RevMan [55]. For categorical outcomes, we will calculate the typical estimates of RR and RD, each with its 95% CI; for continuous outcomes, we will calculate the MD or the SMD, each with its 95% CI.

We will use a fixed‐effect model to combine data where it is reasonable to assume that studies were estimating the same underlying treatment effect. Cochrane Neonatal reviews have typically used a fixed‐effect model, as:

1. preterm infants are relatively similar in terms of their general condition as they are less likely to be influenced by confounding factors that take time to develop; and

2. the inclusion criteria reflect narrow research questions. Interventions administered to neonates are also considered to be relatively easily standardized due to a controlled environment in the neonatal intensive care unit (NICU) and standard basic care protocol.

Taking this into consideration, a fixed‐effect model is more sensitive in detecting small effect sizes. If we judge meta‐analysis to be inappropriate, we will analyze and interpret individual trials separately. If there is evidence of clinical heterogeneity, we will try to explain this based on the different study characteristics and subgroup analyses.

If we consider meta‐analysis to be inappropriate, we will refer to methodological guidance in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions [60], and Synthesis Without Meta‐analysis (SWiM) reporting guidance [61]. We will create a table with studies ordered by risk of bias, and calculate standardized effect estimates for each study. This table will be modeled on the worked example, Table 12.4.b, in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions [60]. We will use a forest plot to graphically represent the study data.

Investigation of heterogeneity and subgroup analysis

We will describe the clinical diversity and methodological variability of the evidence narratively and in tables. Tables will include data on study characteristics, such as design features, population characteristics, and intervention details.

To assess statistical heterogeneity, we will visually inspect forest plots and describe the direction and magnitude of effects and the degree of overlap between CIs. We will also consider the statistics generated in forest plots that measure statistical heterogeneity. We will use the I² statistic to quantify inconsistencies between the trials in each analysis. We will also consider the P value from the Chi² test to assess if this heterogeneity is significant (P < 0.1). If we identify substantial heterogeneity, we will report the finding and explore possible explanatory factors using prespecified subgroup analysis. We will grade the degree of heterogeneity as follows.

• 0% to 40%: might not represent important heterogeneity

• 30% to 60%: may represent moderate heterogeneity

• 50% to 90%: may represent substantial heterogeneity

• more than 75%: may represent considerable heterogeneity

A rough guideline will be used to interpret the I² value rather than a simple threshold, and our interpretation will take into account the understanding that measures of heterogeneity (I and Tau) will be estimated with high uncertainty when the number of studies is small.

We will interpret tests for subgroup differences in effects with caution, given the potential for confounding with other study characteristics and the observational nature of the comparisons; see section 10.11.2 of the Cochrane Handbook for Systematic Reviews of Interventions [40]. In particular, subgroup analyses with fewer than five studies per category are unlikely to be adequate to ascertain valid differences in effects, and we will not highlight them in our results. When subgroup comparisons are possible, we will conduct stratified meta‐analysis and a formal statistical test for interaction to examine subgroup differences that could account for effect heterogeneity (e.g. Cochran's Q test, meta‐regression) [62, 63].

We plan to perform the following subgroup analyses of factors that may contribute to heterogeneity in the effects of the intervention.

• Indication for administration: prevention or treatment of RDS

• Gestational age (≤ 30 weeks' gestation and > 30 weeks' gestation)

• Type of corticosteroid: including budesonide, fluticasone, or beclomethasone

• Type of surfactant: animal‐derived or synthetic

• Timing of corticosteroid dose: corticosteroids given with initial surfactant treatment or corticosteroids given with subsequent surfactant doses

For the equity‐related assessment, we plan to perform subgroup analysis based on the following.

• Setting, based on current World Bank country classifications [64]; specifically newborns born in low‐ and middle‐income countries versus high‐income countries, versus mixed or not reported.

Equity‐related assessment

In an effort to identify equity issues that may be associated with the implementation, uptake or effectiveness of clustered care, we will use signaling questions described in the PROGRESS‐Plus tool to characterize the patient populations receiving the intervention [65]. PROGRESS‐Plus suggests that documenting the following information can aid our understanding of potential equity issues: place of residence, race/ethnicity/culture/language, occupation, gender/sex, religion, education, socio‐economic status, and social capital [66, 67]. A second tool or framework, ‘Sex, comorbidities, race, age, and pathophysiology’ (SCRAP), aims to identify characteristics to reveal social determinants of health in a population by documenting sex, comorbidities, race, age, and pathophysiology [67, 68]. We hope our planned subanalysis by country income status will provide some indication of how geographic and economic circumstances affect the administration of corticosteroids and surfactant. We will consider the information we collect about the populations in the included studies and present it in our discussion.

Sensitivity analysis

We will conduct sensitivity analysis to explore the effect of the methodological quality of studies, and to ascertain whether studies with a high risk of bias (in at least two domains) overestimate the effect of treatment.

Differences in the study design of studies included in this review might also affect our results. We will therefore perform a sensitivity analysis to compare the effects of clustered nursing care in truly randomized trials as opposed to quasi‐randomized trials.

Certainty of the evidence assessment

We will use the GRADE approach, as outlined in the GRADE Handbook to assess the certainty of evidence [69]. We will consult Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions for guidance on completing the summary of findings tables for the following critical and important outcomes [70].

• Death or BPD (oxygen supplementation) at 36 weeks' PMA

• BPD (oxygen supplementation) at 36 weeks' PMA

• Death at 36 weeks' PMA

• Use of systemic postnatal corticosteroids

• Cerebral palsy at 18 months to 24 months corrected age

• Severe developmental delay per Bayley Mental Developmental Index [49, 50] or Griffiths Mental Development Scale [51], assessed as more than two SDs below the mean, at 18 months to 24 months of corrected age. If severe developmental delay is measured by more than one scale (i.e. Bayley Mental Developmental Index and Griffiths Mental Development Scale), we will combine outcome data in the same analysis.

• Severe intellectual impairment (IQ) per Bayley Mental Developmental Index [49, 50], or Griffiths Mental Development Scale [51], more than two SDs below the mean, at 18 months to 24 months corrected age. If severe intellectual impairment is measured by more than one scale (i.e. Bayley Mental Developmental Index and Griffiths Mental Development Scale), we will combine outcome data in the same analysis.

We will prepare only one summary of findings table, and we will describe the only comparison in the Types of interventions section.

Two review authors (LB, AP) will independently assess the certainty of the evidence for each of the outcomes above. We will consider evidence from RCTs as high certainty, downgrading the evidence one level for serious (or two levels for very serious) limitations based upon the following: design (risk of bias), consistency across studies, directness of the evidence, precision of estimates, and presence of publication bias. We will use GRADEpro to create a summary of findings table to report the certainty of the evidence [71].

The GRADE approach results in an assessment of the certainty of a body of evidence in one of the following four grades.

• High: we are very confident that the true effect lies close to that of the estimate of the effect

• Moderate: we are moderately confident in the effect estimate; the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different

• Low: our confidence in the effect estimate is limited; the true effect may be substantially different from the estimate of the effect

• Very low: we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of effect

We will justify all decisions to downgrade the certainty of the evidence using footnotes and make comments to aid the reader's understanding of the review where necessary. We will report results with reference to Cochrane's MECIR Standards [41], and recommended narrative statements as described in Chapter 15, Table 15.6.b of the Cochrane Handbook for Systematic Reviews of Interventions [72].

Consumer involvement

This Cochrane protocol has been developed with the involvement of consumers, and assistance from the parents of infants who have required NICU care. We expect that this assistance will make an important contribution to both the research question and the design of the review. It will be of additional importance when interpreting data and in the dissemination and translation of findings. We will request consumer peer review of the review before it is published to ensure it is relevant and accessible. More information is in Supplementary material 2.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016024.

Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.

Supplementary material 1 Search strategies

Supplementary material 2 Consumer involvement

New

Additional information

Contributions of authors

L Bolanos participated in writing the protocol.

F Borys participated in writing the protocol.

A Pahl participated in writing the protocol.

M Fiander reviewed the literature to inform the protocol, contributed to writing the draft, reviewed and approved the final version of the protocol, and wrote search strategies.

J Cracknell reviewed the literature to inform the protocol, contributed to writing the draft, and reviewed and approved the final version of the protocol.

KS Gautham reviewed the literature to inform the protocol, contributed to writing the draft, and reviewed and approved the final version of the protocol.

RF Soll identified the topic of the review, reviewed the literature to inform the protocol, and reviewed and approved the final version of the protocol.

M Bruschettini identified the topic of the review, reviewed the literature to inform the protocol, and reviewed and approved the final version of the protocol.

Declarations of interest

L Bolanos has no conflicts of interest to declare.

F Borys has no conflicts of interest to declare.

A Pahl has no conflicts of interest to declare.

M Fiander is the Managing Editor and Information Specialist for Cochrane Neonatal; however, she did not participate in the acceptance or editorial processes for this protocol.

J Cracknell is the Managing Editor for Cochrane Neonatal; she did not participate in the acceptance or editorial processes for this protocol.

KS Gautham is an Editor for Cochrane Neonatal; he did not participate in the acceptance or editorial processes for this protocol.

RF Soll is the Co‐ordinating Editor for Cochrane Neonatal; he did not participate in the acceptance or editorial processes for this protocol.

M Bruschettini is an Editor for Cochrane Neonatal; he did not participate in the acceptance or editorial processes for this protocol.

Sources of support

Internal sources

• Institute for Clinical Sciences, Lund University, Lund, Sweden

  MB is employed by this organization

External sources

• Vermont Oxford Network, USA

  Cochrane Neonatal reviews are produced with support from Vermont Oxford Network, a worldwide collaboration of health professionals dedicated to providing evidence‐based care of the highest quality for newborn infants and their families.

• Region Skåne, Skåne University Hospital and Lund University, Sweden

  Cochrane Sweden is supported from Region Skåne, Skåne University Hospital and Lund University

Registration and protocol

Cochrane approved the proposal for this review in August 2023.

Data, code and other materials

Data sharing is not applicable to this article as it is a protocol, so no datasets were generated or analyzed.