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Cochrane Database of Systematic Reviews Protocol - Intervention

Post‐extubation use of non‐invasive respiratory support in preterm infants: a network meta‐analysis

Authors' declarations of interest

Version published: 25 October 2021 Version history

https://doi.org/10.1002/14651858.CD014509
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Abstract

Objectives

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

To evaluate the benefits and adverse effects of various NRS modes when used as post‐extubation support for preterm infants.

Background

Description of the condition

Extremely preterm infants experience respiratory insufficiency due to surfactant deficiency, immature respiratory drive, or both, resulting in inadequate gas exchange that necessitates respiratory support. Many preterm infants require invasive mechanical ventilation (Stoll 2010); however such prolonged invasive respiratory support is known to be associated with mortality, chronic lung disease (CLD), and neurodevelopmental impairment (NDI) (Choi 2018; Walsh 2005). This has driven clinicians to aim to extubate as early as possible. However, extubation is often challenging in preterm infants with inadequate respiratory drive and ongoing lung disease. In around 40% of preterm infants extubated to nasal continuous positive airway pressure (NCPAP), this support fails and endotracheal re‐intubation is required (Lemyre 2017). Furthermore, infants for whom extubation fails are at risk of increased mortality and morbidity (Chawla 2017). With a view toward reducing extubation failure, technological innovations in the field of non‐invasive respiratory support (NRS) have been introduced, with many NRS modes now available. Given the number of available options, it is imperative to understand the relative efficacy of various strategies, to improve extubation success rates.

Description of the intervention

Over the last three decades, NCPAP has become the prototypical NRS mode for preterm infants with respiratory distress syndrome (RDS), with apnea of prematurity, or post extubation. NCPAP has been shown to reduce the need for mechanical ventilation in preterm infants with RDS (Morley 2008); it is also effective in preventing extubation failure among preterm infants (Davis 2003). In recent years, nasal intermittent positive‐pressure ventilation (NIPPV) and biphasic positive airway pressure (BiPAP) have become popular. These modes may provide additional benefits over NCPAP for reducing dependence on mechanical ventilation as evaluated in Cochrane Reviews; meta‐analyses have revealed that NIPPV is more effective than NCPAP for reducing the need for intubation and invasive ventilation among preterm infants with RDS (Lemyre 2016), as well as among infants after extubation (Lemyre 2017).

High‐flow nasal cannula (HFNC) has also gained importance as a mode of NRS. This mode has been evaluated in a Cochrane Review, which revealed that HFNC has similar efficacy rates post extubation compared to other forms of NRS in preventing treatment failure, death, and CLD among preterm infants, to prevent extubation failure (Wilkinson 2016). Similarly, a recent non‐Cochrane review of 10 clinical trials revealed that HFNC has similar efficacy when compared to NCPAP as post‐extubation support. But limited data were available on preterm infants at gestational age less than 28 weeks (Fleeman 2019).

Further to this, additional NRS modes such as nasal high‐frequency oscillation ventilation (NHFOV) and non‐invasive neurally adjusted ventilatory assist (NIV‐NAVA) have been recently evaluated in systematic reviews (De Luca 2016; Goel 2020; Lee 2015). Additionally, clinicians are exploring higher than traditional levels of NCPAP. Typically, NCPAP levels in preterm infants have been reported up to 8 cmH₂O. Higher levels of NCPAP (> 8 cmH₂O), so‐called high NCPAP (H‐NCPAP), are being used to prevent extubation failure in preterm infants (ACTRN12618001638224p; Buzzella 2014; NCT03512158). Although many NRS modes have been compared against one another, head‐to‐head trials comparing some modes of NRS (e.g. NHFOV versus NIPPV or NCPAP) are lacking; this creates uncertainty regarding the choice of one mode of NRS over another, resulting in wide practice variability (Mukerji 2017). With so much ambiguity and ongoing addition of randomized controlled trials (RCTs), a systematic review with network meta‐analysis (NMA) is needed to determine whether there is a hierarchy of effectiveness of these modes of support.

How the intervention might work

NCPAP improves oxygenation and reduces the work of breathing by increasing functional residual capacity (Richardson 1978). It provides flow of gas resulting in a constant distending pressure at the nasal interface to maintain patency of the airway, thereby decreasing obstructive apnea (Miller 1986). The flow of gas can be variable (e.g. infant flow driver) or constant (e.g. ventilator continuous positive airway pressure [CPAP], bubble CPAP), depending on the device. NCPAP also reduces upper airway resistance (Miller 1990), stabilizes the chest wall, and enhances respiratory thoraco‐abdominal synchrony, thus improving diaphragmatic function. Although data are limited,it is plausible that NCPAP levels higher than those conventionally provided(> 8 cmH2O; H‐NCPAP) may reduce lung atelectasis and therefore improvedventilation.

HFNC is a relatively recent NRS mode used in the neonatal population. The precise mechanism underpinning its clinical benefits remains unknown. It is suggested that HFNC provides a constant distending pressure similar to CPAP (Locke 1993); however, pressure may be variable depending on the phase of the respiratory cycle and the interface‐patient seal. Gas flow washes out the anatomic dead space in the upper airway and reduces inspiratory resistance (Moller 2015). It also reduces metabolic demands on the airways by providing warm and humidified gases.

NIPPV, BiPAP, and NIV‐NAVA are non‐invasive respiratory strategies that encompass baseline CPAP, with an intermittent increase in applied pressure. All modes offer the benefits of NCPAP with presumed additional advantages by providing a fixed rate of intermittent pressure on top of baseline pressure. This increase in intermittent pressure (peak pressure) is purported to help preterm infants with poor respiratory drive after extubation (Lemyre 2017). Peak pressures can be synchronized (S‐NIPPV) or non‐synchronized (NS‐NIPPV). Peak pressures, ventilatory rates, and inflation times used in NIPPV are similar to those used in mechanical ventilation. BiPAP is a variant of NIPPV with small differences between high and low pressures (< 4 cmH₂O), lower cycle rates (10 to 30 per minute), and longer inflation times (0.5 to 1 second for higher pressures) compared to NIPPV (Cummings 2016). BiPAP is delivered by variable flow devices.

NIV‐NAVA is a form of synchronous NIPPV. The specialized catheter detects electrical activity of the diaphragm (Edi), which is converted to peak pressure, allowing the ventilator to assist the spontaneous breath of the infant in proportion to the effort generated. Synchrony in NAVA is not limited to initiation of the breath but affects the size and termination of the breath (Stein 2014). By improving patient‐ventilator synchrony, NIV‐NAVA may prevent lung injury and could affect neonatal outcomes (Lee 2015).

In NHFOV, the continuous distending pressure is generated by bias flow, with oscillations superimposed on neonatal tidal breathing. By providing distending pressure, NHFOV offers the advantages of NCPAP while improving gas exchange and preventing extubation failure. NHFOV appears effective and superior to NIPPV in carbon dioxide (CO₂) elimination (Mukerji 2013). Both the infant's breathing and superimposed oscillation may impact CO₂ removal independently, but a synergistic effect is also apparent (De Luca 2016). Oscillatory effects from NHFOV are minimal, as the oscillation is generally dampened by soft interfaces and leak. However, the effects of oscillation on apnea or on stimulation of breathing remain controversial (De Luca 2016).

Why it is important to do this review

Pair‐wise independent comparisons have focused on common NRS modes, that is, NCPAP, HFNC, and NIPPV post extubation, in preterm infants (Kotecha 2015; Lemyre 2016; Wilkinson 2016). Ongoing efforts to further reduce dependence on invasive mechanical ventilation have led to development and use of innovative NRS modes such as NHFOV and NIV‐NAVA. However, lack of head‐to‐head trials comparing some of these newer NRS modes with different modes of non‐invasive ventilation has created uncertainty for decision‐makers in choosing one mode of non‐invasive ventilation over another. Additionally, traditional pair‐wise meta‐analyses do not provide information about all comparisons or about the treatment hierarchy between available NRS modes. This NMA will allow indirect comparison of interventions that have not been evaluated in head‐to‐head RCTs. It will also inform a treatment hierarchy to aid clinicians in choosing between different modes of non‐invasive support.

In July 2020, an NMA on NRS modes used post extubation was published (Ramaswamy 2020); however following are key differences in our protocol.

  1. Extubation failure is included as an outcome (this is relevant, as in modern clinical practice rescue NRS modes are often used instead of intubation).

  2. We specified high CPAP (HCPAP) as a distinct intervention mode, as we believe this will gain importance in the years to come.

  3. We included key outcomes such as intestinal perforation and long‐term neurodevelopmental outcomes.

  4. Ours will be a “live” document that will be updated when new trials are published.

Objectives

To evaluate the benefits and adverse effects of various NRS modes when used as post‐extubation support for preterm infants.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomized, quasi‐randomized, and cluster‐randomized prospective controlled trials comparing any two or more NRS modes for preterm infants following extubation. Quasi‐randomized trials considered for inclusion will be those that closely mirror the structure of a randomized trial, but with allocation decided by an approximation to randomization (e.g. alternation, date of birth, case record number). We will exclude non‐randomized trials and cross‐over trials, as well as studies not evaluating the interventions or outcomes of interest. 

Types of participants

We will include preterm infants at less than 37 weeks’ gestational age (GA) who require NRS following extubation. Studies including preterm and term infants will be included if data relevant to preterm infants are available (or if > 80% of the population is preterm in cases when preterm‐specific data are unavailable). To ensure transitivity across the network, key patient characteristics and timing of randomization from individual studies will be evaluated to confirm that the exchangeability assumption is valid.

Types of interventions

Eligible NRS modes that will be evaluated include (1) NCPAP, (2) NIPPV, (3) BiPAP, (4) HFNC, (5) NHFOV, (6) NIV‐NAVA, and (7) H‐NCPAP.

  1. NCPAP includes continuous distending pressure provided by a ventilator or a bubble CPAP or a variable flow device, up to 8 cmH₂O, administered via the nasal route through any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

  2. NIPPV includes positive‐pressure inflation on top of CPAP provided by a ventilator in a synchronous or non‐synchronous manner, administered via the nasal route through any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

  3. BiPAP includes non‐invasive support that cycles between two pressure levels provided by a variable flow device in a synchronous or non‐synchronous way, administered via the nasal route through any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

  4. HFNC includes heated and humidified gas flows greater than 1 liter/min provided by a high‐flow device via the nasal route through any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

  5. NHFOV includes continuous positive pressure with superimposed oscillations provided by ventilator, administered via the nasal route through any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

  6. NIV‐NAVA includes positive‐pressure inflation on top of CPAP provided by a ventilator in a synchronous manner determined by electrical activity of the diaphragm (detected by a specialized catheter placed in the esophagus), administered via the nasal route by any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

  7. H‐NCPAP includes continuous distending pressure provided by a ventilator (or a bubble CPAP or variable flow device), greater than 8 cmH₂O, administered via the nasal route through any nasal interface including, but not limited to, bi‐nasal prongs, mask, nasopharyngeal tube, and RAM cannula.

We will exclude studies if they compared one of these NRS modes with any other mode (low flow, head box oxygen, or others), or if they compared entirely different modes not listed here. As required, we will revise and update this list of interventions in future iterations of the review, depending on the landscape of available modes.

Types of outcome measures

We will evaluate extubation failure and the need for intubation and ventilation, separately, as primary outcomes, because extubation failure is objective and is less susceptible to bias than intubation, which might be influenced by clinician preferences. Besides, in some trials, infants who have met failure criteria could be rescued by other non‐invasive support before intubation.

Primary outcomes

  1. Treatment failure within first seven days post extubation (failure criteria as defined by authors of included studies, such as respiratory acidosis, increased oxygen requirements, or clinically important apneas that may or may not result in escalation of respiratory support including use of an alternate NRS mode or intubation)*

  2. Need for endotracheal ventilation within first seven days post extubation

  3. CLD (defined as need for oxygen therapy or positive‐pressure support at 36 weeks’ postmenstrual age, or at discharge/transfer if earlier than 36 weeks' postmenstrual age)

*Note: Studies considering respiratory failure or need for endotracheal ventilation at any time within the first seven days post randomization (including, for example, studies that report these outcomes within 72 hours post randomization) will also be considered under the above‐mentioned outcomes.

Secondary outcomes

  1. Death (prior to discharge)

  2. Death or CLD (prior to discharge)

  3. Moderate to severe neurodevelopmental impairment: defined by study authors using Bayley Scales of Infant and Toddler Development ‐ Third Edition ‐ or other comparable validated scales, assessed at 18 to 24 months' corrected age among survivors

  4. Pulmonary air leak syndromes: pneumothorax, pneumomediastinum, or pulmonary interstitial emphysema (occurring while on NRS mode under investigation and prior to discharge)

  5. Intestinal perforation (occurring while on NRS mode under investigation and prior to discharge)

Search methods for identification of studies

An Information Specialist developed a draft search strategy for OVID MEDLINE in consultation with review authors (Appendix 1). This strategy will be peer‐reviewed using the PRESS Checklist (McGowan 2016a; McGowan 2016b). The MEDLINE strategy will be translated, using appropriate syntax, for other databases. Methodological filters will be used to limit retrieval to randomized controlled and quasi‐randomized trials and systematic reviews. Searches will be conducted without language, publication year, publication type, or publication status restrictions.

Electronic searches

The following databases will be searched without language, publication year, publication type, or publication status restrictions.

  1. Cochrane Central Register of Controlled Trials (CENTRAL), in the Cochrane Library.

  2. Ovid MEDLINE and Epub Ahead of Print, In‐Process, In‐Data‐Review & Other Non‐Indexed Citations and Daily (1946 to current).

  3. Embase (1974 to current) (Ovid).

  4. Cumulative Index to Nursing and Allied Health Literature (CINAHL) (EbscoHost).

  5. Web of Science.

Searching other resources

Trial registration records will be identified by using Cochrane CENTRAL and by conducting independent searches of the following registries.

  1. US National Library of Medicine (https://clinicaltrials.gov).

  2. World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) (https://www.who.int/clinical-trials-registry-platform/the-ictrp-search-portal).

  3. International Standard Randomized Controlled Trials Number (ISRCTN) Registry (https://www.isrctn.com).

Conference abstracts will be identified using CENTRAL and Embase without date or language limits. We will also conduct independent searches of the following conferences from 2017 forward: Pediatric Academic Societies (https://www.pas-meeting.or) and the European Society for Pediatric Research (www.espr.eu/).

We will check the reference lists of included studies and the reference lists of related systematic reviews to identify studies not captured in database searches.

We will search for errata and retractions for included studies published on PubMed (www.ncbi.nlm.nih.gov/pubmed).

Data collection and analysis

Selection of studies

We will use the described search strategy to obtain any titles and abstracts of studies that may be relevant to this review. One review author (AR) will screen titles and abstracts to discard studies that are not relevant, such as non‐randomized studies, cross‐over trials, cluster‐randomized trials, and studies not evaluating the populations and interventions of interest. Two review authors (AR, AM) will use a standardized form to assess the retained studies to determine which studies satisfy inclusion criteria. We will utilize Covidence (covidence.org) to perform the described screening and analysis of studies for inclusion. We will not employ any specific masking strategies. Any discrepancies will be resolved upon discussion with a third review author (PS).

Data extraction and management

Two review authors (AR, AM) will independently extract data using a standardized form (Appendix 2). Information extracted will include study characteristics, participants, interventions, outcomes, and risk of bias. Any potential effect modifiers will be encompassed in this data collection phase. Data will be cross‐checked between review authors and will be discussed, with discrepancies resolved upon discussion with a third review author (PS) if required. Before assessment, studies that report in non‐English language journals will be translated electronically. We will use studies with the most complete data if more than one publication is available for one study. Disagreements on data extraction will be discussed with a third review author (PS). We will contact trial authors by email to request missing data (with a maximum of two reminders, two weeks apart – allowing a total time of six weeks to obtain a response to consider for inclusion), including separate data for preterm infants if the trial has included term and preterm populations, and individual outcomes if the trial has reported only composite outcomes. Information extracted will include study characteristics, participants, interventions, outcomes, and risk of bias.

Assessment of risk of bias in included studies

We (AR, AM) will assess risk of bias by using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Intervention and will present this information in “Risk of bias" tables for the following domains (Higgins 2011). We will be using the Cochrane risk of bias tool to assess each included study in the following domains. 

  1. Was there adequate sequence generation (selection bias)?

  2. Was allocation adequately concealed (selection bias)?

  3. Was knowledge of allocated interventions adequately prevented during the study (detection bias)?

    1. Participants and personnel.

    2. Outcome assessors.

  4. Were incomplete outcome data adequately addressed (attrition bias)?

  5. Are reports of the study free of suggestion of selective outcome reporting (reporting bias)?

  6. Was there any other bias?

We will resolve disagreements by discussion, or by consultation with a third assessor (PS). See Appendix 3 for a more detailed description of risk of bias for each domain.

Note: if risk of bias for an included study has already been determined and published in a previous Cochrane Review, we will incorporate these assessments into our analysis, provided they follow the structure as described above. For new studies identified and included in this review, we will follow the process as described above. 

Measures of treatment effect

Relative treatment effects

For this Cochrane Review, we will use R 4.0.0 for all analyses with a Bayesian approach. As all outcomes are binary, we will use risk ratios (RRs) with 95% credible intervals (CrIs) as the measure of association between NRS treatments used for each outcome.

Relative treatment rankings

In addition, we will report the ranking probabilities of each intervention for each rank (for primary outcomes only). We will report the treatment hierarchy using the surface under the cumulative ranking (SUCRA) curve for all interventions for each primary outcome (Salanti 2011).

Unit of analysis issues

The unit of analysis will be the participating infant in individually randomized trials, and an infant will be considered only once in the analysis. For cluster‐randomized trials, the unit will be the center, but we will include studies in the NMA only when the intra‐cluster correlation coefficient has been taken into account, or when approximately correct analyses can be performed as per the Cochrane Handbook for Systematic Reviews of Interventions guidelines (Higgins 2020). We will include multi‐arm trials; in pair‐wise meta‐analysis, we will treat studies with multiple treatment arms as multiple independent two‐arm studies. However, for the NMA, we will use Woods, Hawkins, and Scott’s method to estimate standard errors (SEs) to account for the multiple arms in analyses before running the NMA (Woods 2010). 

Dealing with missing data

When feasible, we intend to carry out analysis on an intention‐to‐treat basis for all 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 request data by contacting the original investigators. We will consider more than 30% loss to follow‐up data for neurodevelopmental outcomes and more than 10% loss to follow‐up data for other outcomes as important, to alter the meaning or interpretation of results. Studies with loss to follow‐up higher than those thresholds will be excluded from analysis of that particular outcome.

Assessment of heterogeneity

Assessment of clinical heterogeneity

We will evaluate the presence of clinical heterogeneity among studies by comparing population characteristics, outcomes definitions, interventions, and study designs and methods.

Assessment of transitivity across treatment comparisons

To infer about the assumption of transitivity across the network, we will assess the following specific potential effect modifiers across various pair‐wise comparisons: (1) gestational age criteria; (2) birth weight criteria; (3) age at randomization; (4) respiratory support prior to extubation; (6) methylxanthine use; (6) antenatal steroid use; and finally, (7) assurance that intervention modes are utilized in a similar way (including interface employed). As an example, in a trial comparing NCPAP with NIPPV and a trial comparing CPAP with HFNC, we will assess for all of the aforementioned effect modifiers, according to the guiding principle that an individual patient should have been eligible for randomization into either trial. If a particular trial varies in a significant way in one or more of the aforementioned effect modifiers compared to other trials, that trial, although included in the systematic review, may not be included in quantitative analyses.

Assessment of statistical heterogeneity
Assumptions when heterogeneity is estimated

For standard pair‐wise meta‐analyses, we will estimate a different heterogeneity parameter for each pair‐wise comparison. For NMA, we will assume a single estimate for the heterogeneity parameter for all comparisons per outcome.

Measures and tests for heterogeneity

The I² statistic across trials will be used to test for statistical heterogeneity. We will consider I² thresholds to represent heterogeneity (low, moderate, and high I² threshold values for 25%, 50%, and 75%, respectively) (Higgins 2003). We will also evaluate P for the Chi² test and will consider a P value less than 0.10 as showing significant heterogeneity.

We will base assessment of statistical heterogeneity in the entire network on the magnitude of the heterogeneity variance parameter (τ 2) estimated from NMA models. We will compare the magnitude of a common heterogeneity variance for the specific network of interest with an empirical distribution of heterogeneity variances specific to types of outcomes and types of treatments compared (Turner 2012).

Assessment of statistical inconsistency
Local approaches for evaluating inconsistency

We will use the loop‐specific approach to evaluate the presence of inconsistency (incoherence) locally. A loop of evidence is formed by at least three treatment pairs that have been compared in studies, forming a closed path. Differences between direct and indirect evidence define their disagreement (inconsistency factor). We will look at the magnitude of the inconsistency factors and their 95% confidence intervals (CIs) to infer whether the inconsistency factor is incompatible with zero (Bucher 1997). We will extend the analysis to all closed triangular and quadratic loops while assuming single loop‐specific heterogeneity and will examine the estimates of inconsistency together with 95% CIs for each loop using a graphical representation (Salanti 2011). This approach can be easily applied and indicates loops with large inconsistency, but it cannot infer consistency of the entire network nor identify the particular comparison that is problematic. It should be noted that in a network of evidence, there may be many loops and estimates of inconsistency factors, and with multiple testing, the likelihood that we might find an inconsistent loop by chance is increased. Therefore, we will be cautious when deriving conclusions from this approach.

Global approaches for evaluating inconsistency

To check the assumption of consistency in the entire network, we will use the design‐by‐treatment interaction model, as fully explained in Higgins 2012. This method accounts for different sources of inconsistency that can occur when studies with different designs (two‐arm studies versus three‐arm studies) give different results, as well as when disagreement between direct and indirect evidence is apparent. By using this approach, we will infer whether any inconsistency from any source in the entire network is present based on a Chi² test. Inconsistency and heterogeneity are interwoven: to distinguish between these two sources of variability, we employed I² for inconsistency, which measures the percentage of variability that cannot be attributed to random error nor to heterogeneity (within‐comparison variability).

It should be noted in general that the power of statistical tests for inconsistency is low, which implies that absence of statistically significant inconsistency is not evidence of consistency.

Assessment of reporting biases

We intend to conduct a comprehensive search for eligible studies and will be alert for duplication of data. If we identify 10 or more trials for any pair of NRS modes, we will assess possible publication bias by inspecting the comparison‐adjusted funnel plot (Chaimani 2012). If we uncover reporting bias that could, in the opinion of the review authors, introduce serious bias, we will incorporate this into the GRADE assessment, as described further below.

Data synthesis

Geometry of the network

We will present a network diagram for each outcome to show graphically available evidence and the volume of evidence behind each comparison. Each node in the network diagram will represent one of the seven forms of NRS. An edge will connect two nodes if at least one trial compared the two corresponding NRS treatments. Node size will be made proportionate to the number of patients randomly assigned to the corresponding treatment, and the edge width to the number of trials between corresponding treatments.

Methods for direct treatment comparisons

We will conduct a standard pair‐wise meta‐analysis of each treatment pair of NRS modes. We will use a random‐effects model. We will assess heterogeneity by using I² statistics.

Methods for indirect and mixed treatment comparisons

We will perform NMA of different interventions for all listed outcomes, as long as assumptions of transitivity across studies are valid. We will use random‐effects NMA models with the Bayesian approach to estimate relative treatment effects: pooled risk ratio (RR) and 95% credible interval (95% CrI) for each outcome (van Valkenhoef 2012). We will use non‐informative priors for all parameters to be estimated. Common heterogeneity for all treatment comparisons will be assumed. We will assess inconsistency/incoherency by comparing direct and indirect estimates using the node‐splitting method (van Valkenhoef 2016). The convergence of Markov chain Monte Carlo (MCMC) approaches will be assessed by evaluating trace plots and by using the convergence criteria proposed by Gelman and Rubin (Gelman 1992). When we identify inconsistency (i.e. I² > 50%), we will conduct a sensitivity analysis while excluding treatments for which inconsistency is identified. We will also estimate the ranking of all treatments by using the posterior distribution of ranking probabilities and SUCRA (Hoaglin 2011; Salanti 2011). We will apply contrast‐level analysis; however, we will apply a mix of contrast‐level and arm‐level analyses when contrast‐level data are not available for some studies. We will account for the correlation induced by multi‐arm studies by using Woods, Hawkins, and Scott’s method (Woods 2010). Network meta‐regression will be conducted to examine the possible effects of some specific study characteristics (modifiers), if applicable, on the association between treatments and the primary outcome. We will assess publication bias by examining the comparison‐adjusted funnel plot using Egger’s test (Chaimani 2012).  We will perform all analyses described in a Bayesian framework using the "GeMtc" R package (version 1.0.‐1) in R 4.0.0 (https://www.r-project.org). 

Subgroup analysis and investigation of heterogeneity

We intend a priori to perform the following subgroup analyses: stratified by GA group: GA at birth: 28 weeks or less, and greater than 28 weeks. Subgroup analyses will be performed for primary outcomes only. Investigation of heterogeneity has been described in an earlier section of the protocol. 

Sensitivity analysis

We will perform sensitivity analyses for each of the three primary outcomes by excluding studies that score “high” or “unclear” for risk of bias on at least two of the domains outlined in Appendix 3.

Summary of findings and assessment of the certainty of the evidence

We will evaluate the certainty of evidence for each effect estimate (direct, indirect, and network) for all outcomes. We will use the Grading of Recommendations Assessment, and Development approach, which was specifically developed for NMA (Brignardello‐Petersen 2018; Puhan 2014). Two review authors (AR, AM) will independently evaluate and assess the certainty of evidence (Nikolakopoulou 2020). We will resolve discrepancies by consensus and discussion with the third review author (PS). We will present review results in a summary of findings table by using a model suggested for presenting NMA results (Yepes‐Nuñez 2019). The NMA summary of findings (NMA‐SoF) table will include the following components: clinical question details in population, intervention, control, outcome (PICO) format; network geometry plot; absolute and relative effect estimates; evidence certainty; interpretation of findings; and comments. The summary of findings table will be provided for primary outcomes only and will be presented using NCPAP as the reference intervention.