Authors: James X Sotiropoulos (NHMRC Clinical Trials Centre, Faculty of Medicine and Health, University of Sydney, Sydney, Australia), Roger F Soll (H. Wallace Professor of Neonatology, Larner College of Medicine, University of Vermont; Director, Vermont Oxford Network Institute for Evidence Based Practice, Burlington, Vermont, USA), Michelle Fiander (Cochrane Neonatal Group, Vermont Oxford Network, Burlington, Vermont, USA), Matteo Bruschettini (Department of Clinical Sciences Lund, Paediatrics, Lund University, Skåne University Hospital, Lund, Sweden), Ju Lee Oei (NHMRC Clinical Trials Centre, Faculty of Medicine and Health, University of Sydney, Sydney, Australia; Faculty of Medicine and Health, University of New South Wales, Sydney, Australia; Department of Newborn Care, Royal Hospital for Women, Randwick, Sydney, Australia; Mater Research Institute, Mater Misericordiae Ltd, Brisbane, Australia; Faculty of Health, Medicine and Behavioral Sciences, University of Queensland, Brisbane, Australia), Vishal Kapadia (Department of Pediatrics, University of Texas Southwestern Medical Center, Dallas, Texas, USA), Anna Lene Seidler (NHMRC Clinical Trials Centre, Faculty of Medicine and Health, University of Sydney, Sydney, Australia; Department of Child and Adolescent Psychiatry, University Medical Centre Rostock, Rostock, Germany; German Center for Child and Adolescent Health (DZKJ), partner site Greifswald/Rostock, Rostock, Germany)
Source: The Cochrane Database of Systematic Reviews
Authors: James X Sotiropoulos, Roger F Soll, Michelle Fiander, Matteo Bruschettini, Ju Lee Oei, Vishal Kapadia, Anna Lene Seidler
This is a protocol for a Cochrane Review (intervention). The objectives are as
Research objective to assess the effects of different oxygen saturation targets for the delivery room resuscitation of preterm infants.
Research objective to assess the effects of different titration strategies for the delivery room resuscitation of preterm infants.
Preterm birth is a leading cause of childhood morbidity and mortality worldwide [1]. Many preterm infants require supplemental oxygen immediately after they are born to improve oxygenation. Historically, pure (100%) oxygen (i.e. fraction of inspired oxygen (FiO2) 1.0) was the gas of choice to resuscitate all infants [2]. However, research over the past several decades has revealed that using too much oxygen for even a few minutes in the delivery room can cause harm [3].
For term infants, it has now been shown with high confidence that commencing resuscitation with room air (FiO2 0.21) reduces deaths compared to 100% oxygen (FiO2 1.0) (risk ratio (RR) 0.71, 95% confidence interval (CI) 0.54 to 0.94) [4, 5]. Providing 100% oxygen in an unrestricted way contributes to the formation of harmful reactive oxygen species, which have downstream effects on the pathogenesis of morbidities of prematurity such as retinopathy of prematurity (ROP) and bronchopulmonary dysplasia [4, 5, 6].
For preterm infants (i.e. those born at less than 37 weeks' gestation), the evidence is less clear. The oxygen needs of preterm infants vary compared to term counterparts due to underdeveloped lungs, organ systems, and antioxidant defences [3]. Individual randomised controlled trials (RCTs) have demonstrated no differences in randomising infants to different starting oxygen concentrations for resuscitation, including concentrations such as 30%, 60%, or 100%. However, a recent individual participant data network meta‐analysis suggested a possible decrease in mortality when higher concentrations of oxygen (i.e. FiO2 0.9 to 1.0) were used for initial resuscitation of preterm infants at less than 32 weeks' gestation [7]. This meta‐analysis also highlighted current uncertainty about how to best adjust FiO2 after resuscitation has begun. The included studies each titrated FiO2 differently, and the methods were too heterogeneous to explore which strategy might be best.
Current treatment recommendations suggest starting the resuscitation process with lower oxygen concentrations [8, 9]. The exact recommended oxygen concentration to start resuscitation varies depending on gestational age. However, across all gestations, there is an emphasis on adjusting the delivered FiO2 according to the infant's response [9].
Pulse oximetry (a non‐invasive technology to measure the concentration of oxygenated haemoglobin) is the primary tool by which this is achieved [10, 11]. Pulse oximetry uses infrared light spectrometry to measure the relative proportion of oxygen to de‐oxygenated haemoglobin, expressed as oxygen saturation (SpO2) [12]. Reference standards have been developed for SpO2 over the first 10 minutes of life, where it is expected that infants' SpO2 increases gradually from around 70% at one to two minutes of life until plateauing at more than 90% by eight minutes. The reference standards are based mostly on term infants who did not require any form of delivery room resuscitation [13], and may also differ in infants who receive deferred umbilical cord clamping (DCC) [14]. Nevertheless, these data are the basis on which clinicians titrate delivery room oxygen therapy, whereby the goal is to mimic the gradual rise in SpO2 seen in healthy infants not requiring intervention. This approach balances the oxygen needs of infants in respiratory distress to avoid hypoxia; however, it also aims to prevent prolonged periods of hyperoxia.
Despite the widespread adoption of delivery room FiO2 titration, many uncertainties persist regarding how it should be conducted. The components of delivery room FiO2 titration of interest for this review 1. the SpO2 target against which the oxygen concentration is adjusted, and 2. the methods by which the chosen SpO2 target is achieved.
The current standard of care involves frequent clinician‐driven adjustments to FiO2 in response to SpO2 [9]. Achieving SpO2 of 80% to 85% by five minutes of life is a frequently quoted target and standard time point [15]. This is based on the approximate 50th centile from the Dawson centile curves [13]. In observational studies and pooled analyses from clinical trial data of preterm infants, failing to reach an SpO2 of 80% at five minutes has been associated with increased mortality (odds ratio 2.70, 95% CI 1.58 to 4.6). However, causality in this relationship is uncertain. Additionally, it is unknown whether this approach is valid in lower‐resource settings with limited access to the required technology [16, 17]. More recently, an effort has been made to examine the appropriateness of this reference standard for preterm infants, and for infants who receive DCC [18, 19]. One observational study found that moderate‐late preterm infants receiving DCC who did not require resuscitation took longer to reach a stable SpO2 than their term counterparts [19]. Uncertainty persists about whether the current reference standards (which have been developed mostly with data from spontaneously breathing term infants) are appropriate and confer the best outcomes for preterm infants.
Further, the best strategy to achieve the chosen SpO2 targets is unknown. Clinicians are challenged by the cognitive load of the busy resuscitation environment. When clinicians are tasked with frequently adjusting FiO2, there may be delays in adjusting the FiO2 or inappropriate adjustments [20]. These might both contribute to time spent outside the defined SpO2 range or other deleterious outcomes. Computerised algorithmic approaches, or indeed artificial intelligence‐informed software, offer possible solutions to reduce this burden, and to make more precise and timely adjustments. These have shown promise in the neonatal intensive care unit (NICU) environment, but their suitability for the delivery room is a subject of ongoing study [21].
This review will address the above uncertainties by summarising the available high‐quality evidence to inform ongoing practice.
Research objective to assess the effects of different oxygen saturation targets for the delivery room resuscitation of preterm infants.
Research objective to assess the effects of different titration strategies for the delivery room resuscitation of preterm infants.
For this protocol, we followed the methodological guidance in the Cochrane Handbook for Systematic Reviews of Interventions [22] and Methodological Expectations for Cochrane Intervention Reviews (MECIR) [23]; and reporting guidance per MECIR [23] and PRISMA‐P [24].
For the review, we will follow the methodological and reporting guidance outlined in MECIR and the Cochrane Handbook for Systematic Reviews of Interventions [22, 25], and will report the review in accordance with PRISMA [26].
If we identify a reference to a study, or studies, involving an author of this review, other authors will undertake selection, data extraction, risk of bias assessment, and associated GRADE assessment.
We will include published and unpublished randomised controlled trials (RCTs), quasi‐randomised, or cluster‐randomised trials. We define quasi‐RCTs as those where participants are allocated to different arms of the trial using a method of allocation that is not truly random, such as date of birth, medical record number, or date of recruitment. The nature of the study setting, being only a brief period (10 minutes or less) in the delivery room environment, means that cross‐over studies are not feasible.
Participants will be infants born preterm (defined as less than 37 weeks of completed gestation) who are treated with oxygen or respiratory support in the delivery room (by any means, including low‐flow nasal prongs, continuous positive airway pressure, intermittent positive pressure ventilation, or intubation and mechanical ventilation) and have their oxygen saturation (SpO2) measured with a pulse oximeter. Infants will be included regardless of being born as part of a multiple pregnancy, or delayed/deferred cord clamping status. We will note whether each study defined time zero as time of birth or time of cord clamping.
Studies including both term and preterm infants will be eligible as long as data are presented stratified by gestational age subgroups (i.e. preterm and term infant data presented separately). If data are not presented separately, we will attempt to contact the study authors for stratified data before excluding the study.
We will include studies conducted in delivery room settings and examining the interventions of interest. The review will examine two related objectives with separate interventions of 1. oxygen saturation (SpO2) targets for delivery room resuscitation, or 2. strategies to titrate the fraction of inspired oxygen (FiO2) during delivery room resuscitation.
For research objective 1, regarding SpO2 targets, the intervention will be the SpO2 target that is aimed to be achieved at five minutes of life in the delivery room. In these interventions, the FiO2 will be adjusted according to the infant's SpO2 to achieve the SpO2 target. There will be no restriction to the method of titration employed (i.e. both clinician and computer‐driven approaches, or a combination of both). We will exclude interventions that do not titrate oxygen (i.e. provide a static FiO2). We will not include studies solely comparing different initial FiO2 (i.e. starting oxygen concentration for resuscitation).
We will group targets as lower or higher oxygen saturation targets, according to their relationship to the Dawson centile curves [13]. For example, the Neonatal Resuscitation Program (USA) uses the 50th centile of the Dawson curves as the basis of their recommendation (infants should achieve 80% to 85% SpO2 at five minutes of life) [15]. We have defined lower and higher oxygen saturation targets based on similar principles, as follows.
Lower oxygen saturation a target of 80% to 85% SpO2 or less at five minutes of life (approximate 50th centile or lower of the Dawson curves).Higher oxygen saturation a target of over 85% SpO2 at five minutes of life (greater than the approximate 50th centile of the Dawson curves).
We will explore alternative definitions of these groups in sensitivity analyses.
For research objective 2, the intervention will be the method by which the FiO2 is adjusted. There will be no restriction to the SpO2 target that is used. We will exclude interventions that do not titrate oxygen (i.e. provide a static FiO2). We will not include studies solely comparing different initial FiO2 (i.e. starting oxygen concentration for resuscitation).
We will group titration methods as clinician‐driven, automated algorithm‐based, or artificial intelligence‐informed, as follows.
Clinician‐driven: clinicians are in charge of adjusting FiO2 based on the clinical situation (clinical judgement, oximetry data, heart rate data, observation of the infant). There may or may not be prespecified rules for the clinician to follow; however, the clinician makes the final decision on when and how to adjust the oxygen.Automated algorithm‐based: adjustments are made according to prespecified rules in a closed‐loop automated oxygen titration system. There is no artificial intelligence component.Artificial intelligence‐informed: an artificial intelligence model synthesises inputted data to decide when and how to adjust the oxygen concentration. The model may or may not 'learn' or 'be trained' by reviewing data, reviewing its own decision‐making in real‐time, or by other means. The adjustments may be made automatically by an automated oxygen titration system, or manually by clinicians following instructions from the artificial intelligence‐informed model.
If there are insufficient studies to compare automated algorithm‐based approaches and artificial intelligence‐informed approaches, we will collapse these into a single group called computer‐driven approaches. If there are sufficient studies within one intervention group (e.g. fast or slow clinician‐based approaches), we may consider splitting interventions into additional groups.
We selected outcomes by consulting the core outcome set for Neonatal Research [27] and multidisciplinary researchers (including clinicians, biostatisticians, and methods experts) with appropriate experience in neonatal research. All outcomes are defined in Table 1.
Table 1. Outcome definitionsBroader outcome groupingOutcome domainOutcome measuresSurvivalMortality^a^All‐cause hospital mortality at discharge home from hospital (including data from hospital transfers, where applicable), or the latest available mortality data prior to discharge if this is not available (yes/no)Delivery room SpO2^b^SpO2^a^SpO2 at 3 minutes, 5 minutes, and 10 minutes, and (if appropriate) the area under the curve from time 0 to 10 minutes.Time to achieve SpO2 targetTime (minutes and seconds) to first achieve SpO2 target range. Target range defined by individual study.Time spent in target rangeTime (minutes and seconds) spent inside SpO2 target range. Target range defined by individual study.Respiratory healthInvasive respiratory support^a^The need for invasive respiratory support (i.e. intubation and mechanical ventilation) at any point during admission (yes/no)Duration of invasive respiratory support^a^The total duration (days and hours) of invasive respiratory support (i.e. intubation and mechanical ventilation) during admissionDuration of any respiratory support or supplemental oxygen^a^The total duration (days and hours) of any supplemental oxygen or positive pressure respiratory support (invasive or non‐invasive) including mechanical ventilation, continuous positive airway pressure, and high‐flow nasal cannulaBPD^a^Bronchopulmonary dysplasia or chronic neonatal lung disease, as defined by the individual study at 36 weeks' postmenstrual age (yes/no)Discharge on home oxygen^a^Discharge from hospital with home oxygen (yes/no)Other morbidities of prematurityNECThe presence of NEC (any grade or severity) at any point during hospital admission (yes/no)ROPThe presence of ROP (any grade or severity) at any point during hospital admission (yes/no)IVHThe presence of any IVH (any grade or severity) at any point during hospital admission (yes/no)Brain injury on neuroimagingThe presence of any brain injury (i.e. IVH, periventricular leukomalacia) on any accepted form of neuroimaging (i.e. ultrasound, computer tomography, magnetic resonance imaging) at any point during hospital admission (yes/no)Neurodevelopment (18–24 months)Neuro‐motorAny general gross motor dysfunction/cerebral palsy. GMFCS ≥ 1 (yes/no)Severe developmental delayBSID Third or Fourth Edition [28, 29], or Griffiths Mental Development Scale [30], assessed as more than 2 SDs below the mean (yes/no)If more than 1 scale is available, we will preferentially use BSID Fourth Edition, BSID Third Edition, and Griffiths Mental Developmental Scale in decreasing order of preference.Severe intellectual impairmentIntelligence quotient > 2 SDs below the mean (yes/no) as determined by a validated tool administered by an appropriately trained paediatrician/developmental psychologist/other developmental health professional.BlindnessVision < 6/60 in both eyes (yes/no) as determined by an optometrist/ophthalmologist/other health professional appropriately trained in eye examination.Sensorineural deafnessHearing impairment requiring amplification (yes/no) as determined by an audiologist/paediatrician/other appropriately trained health professional.^a^Critical outcomes
^b^Delivery room oxygen saturation (SpO2) outcomes are only applicable to research objective 2 (titration‐based interventions), due to the nature of the intervention.Abbreviations: BPD: bronchopulmonary dysplasia; BSID: Bayley Scales of Infant Development; GMFCS: Gross Motor Function Classification System; IVH: intraventricular haemorrhage; NEC: necrotising enterocolitis; ROP: retinopathy of prematurity; SD: standard deviation; SpO2: oxygen saturation.
For research objective 1 (target‐based comparisons), critical outcomes will
all‐cause mortality to hospital discharge;need for and duration of invasive respiratory support;duration of any respiratory support;bronchopulmonary dysplasia;discharge on home oxygen.
For research objective 2 (titration‐based comparisons), critical outcomes will
all‐cause mortality to hospital discharge;oxygen saturation (SpO2) in the delivery room;need for and duration of invasive respiratory support;duration of any respiratory support;bronchopulmonary dysplasia;discharge on home oxygen.
Other outcomes will
necrotising enterocolitis (NEC);retinopathy of prematurity (ROP);intraventricular haemorrhage (IVH);brain injury on imaging;sepsis;time to achieve specified SpO2 target (research objective 2 only);time spent in SpO2 target range (research objective 2 only);neurodevelopmental outcomes.
Neurodevelopmental outcomes will be assessed at 18 to 24 months of corrected age. If multiple assessments are available, we will use the latest available assessment. Outcomes will be any cerebral palsy, severe developmental delay (more than two SDs below the mean) as defined by the Bayley Scales of Infant Development Third or Fourth Edition [28, 29] or Griffiths Mental Developmental Scale [30], severe intellectual impairment (intelligence quotient (IQ) more than two SDs below the mean), blindness (vision less than 6/60 in both eyes) and sensorineural hearing impairment requiring amplification.
An Information Specialist (MF) has written the draft search strategy, which an Information Specialist assigned by the Cochrane Central Editorial Service will peer‐review. We will conduct searches without language or publication type restrictions and use methodological filters to identify RCTs and systematic reviews; the source of filters will be noted in the search strategies. Searches for trials will not be limited by date; searches for systematic reviews will be limited to the past two years.
We will search the following databases.
Cochrane Central Register of Controlled Trials (CENTRAL) via Cochrane Register of Studies (CRS)Ovid MEDLINE, All, from inceptionOvid Embase, 1974 to search date
A draft search strategy, preceded by a search narrative [31], is available in Supplementary material 1.
We will search two trial registries.
US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (https://clinicaltrials.gov)World Health Organization International Clinical Trials Registry Platform (https://trialsearch.who.int)
We will conduct manual searches of the following conference abstracts for the past four years.
European Academy of Paediatric Societies (EAPS)Pediatric Academic Societies (PAS)Perinatal Society of Australia and New Zealand (PSANZ)
We will scan the reference lists of related systematic reviews and included studies to identify additional studies; and will search Retraction Watch and PubMed for errata or retractions for any studies included in the review.
References identified by literature searches will be managed in Endnote and screened in Covidence [32]. The selection process will be guided by the Criteria for considering studies for this review. Two review authors (MF, JS, MB, JLO, and VK) will independently screen titles and abstracts, resolving any disagreements by discussion or in consultation with a third review author (ALS or RS). Following title and abstract screening, two review authors (MF and JS) will independently assess the full‐texts of retained studies, resolving any disagreements by discussion or in consultation with a third review author (ALS or RS). We will document the reasons for the exclusion of studies after full‐text review in the review.
We will include studies reported as conference abstracts if they include sufficient data for extraction and analysis. In cases where there are insufficient data, we will attempt to contact study authors or identify the full report of the study. If we are unable to obtain sufficient information, we will cite the abstract in studies awaiting assessment. In cases of missing or incomplete data, we will attempt to contact study authors for clarification or additional data. We will report our contact, or attempted contact, with study authors in the review.
We will cite any ongoing studies in the review.
We will record the selection process in sufficient detail to report it both narratively and in a PRISMA flow diagram [26].
If we identify studies in languages not read by review authors, we will use an online translation service such as Google Translate. If the translation is sufficient, we will use it. If it is insufficient, we will attempt to identify an individual conversant in the language of the report to translate the study. If translation by one of these methods is insufficient, we will place the study in 'awaiting assessment'.
We will collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review.
As some members of the author team have direct involvement in the conduct, analysis, and publication of studies that may be eligible for inclusion in the review, these authors will not be involved in making eligibility decisions about, extracting data from, carrying out the risk of bias assessment for, or performing GRADE assessments for that study.
Two review authors (JS, ALS, MF, JLO, VK or MB) will independently extract data using a form based on the Cochrane Effective Practice and Organisation of Care Group data collection checklist [33]. We will pilot the form within the review team using a sample of included studies. Data extracted by each review author will be compared, and any disagreements resolved by discussion. We will extract the following information.
Administrative study author(s), published or unpublished, year of publication, year in which study was conducted, presence of vested interest, details of other relevant papers cited.Study number of study centres and location, resourcing of study centre (including acuity and whether equipment to deliver the intervention appropriately is available, i.e. pulse oximeters, oxygen blenders), informed consent, ethics approval, completeness of follow‐up (e.g. greater than 80%).Participants: number randomised, the number lost to follow‐up/withdrawn, number analysed, mean gestational age, gestational age range, inclusion criteria, place of residence, race/ethnicity/culture/language, occupation of parents, sex, religion, education, socioeconomic status, social capital, and exclusion criteria [34].Type of intervention, according to Types of interventions.Outcomes, as outlined in Outcome measures.
Should any queries arise, or where additional data are required, we will contact study investigators/authors for clarification. Two review authors (JS and MF) will enter data into RevMan [35].
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, together with anticipated dates of commencement and completion, if reported, in the 'Characteristics of ongoing studies' table.
We will resolve any disagreement amongst the review authors by discussion, with the input of a third review author (ALS or RS).
We will report characteristics of included, excluded, and studies awaiting assessment in characteristics tables. In addition to a detailed table summarising the characteristics of the included studies, we will provide an overview of synthesis and included studies (OSIS) table.
Two review authors (JS, MF, MB, JLO, VK and ALS) will independently assess risk of bias using the Cochrane RoB 2 tool, outlined in the Cochrane Handbook for Systematic Reviews of Interventions [36, 37]. Separate risk of bias assessments will be conducted for each outcome (or group of outcomes, where appropriate). We will resolve any disagreements by discussion or by consultation with another review author (RS). If we encounter a 'problematic' study, as defined in the Cochrane Policy for Managing Potentially Problematic Studies, we will follow guidance within the policy. The outcomes to be assessed for each study are those described in Certainty of the evidence assessment.
We will assess the risk of bias according to the following domains.
Bias arising from the randomisation processBias due to deviations from intended interventions (we will assess the effect of assignment to the intervention at baseline, i.e. the intention‐to‐treat effect)Bias due to missing outcome dataBias in measurement of the outcomeBias in selection of the reported result
We will use the RoB 2 Excel tool to assess individually randomised, parallel‐group trials [38]. For cluster‐randomised trials, we will use the appropriate RoB 2 Excel tool.
Using the signalling questions in RoB 2, we will rate each domain as having 'low risk', 'some concerns', or 'high risk' of bias. We will summarise risk of bias judgements across different studies for each of the domains listed for each outcome. A judgement of high risk of bias within any domain has the same implications for the overall result, irrespective of which domain is being assessed. Therefore, if the answers to the signalling questions yield a judgement of high risk of bias, we will consider whether any identified problems are of sufficient concern to warrant this judgement for that result overall. When we judge there to be some concerns in multiple domains, we will consider an overall judgement of high risk of bias for that result or group of results. We will consider the overall RoB 2 judgement for each outcome as part of the GRADE assessment presented in our summary of findings table, as described in the Certainty of the evidence assessment section.
We will assign high risk of bias overall when we judge one or more domains to have a high risk of bias. Conversely, we will assign low risk of bias when we judge low risk of bias for all domains. Assessments will be conducted at the outcome level.
When considering treatment effects, we will take into account the risk of bias for studies that contributed to that outcome.
Our primary analysis will include all studies, no matter their risk of bias rating. However, if there is substantial heterogeneity that can be explained in a high versus low risk of bias post‐hoc sensitivity analysis, our conclusions will be based on the low risk of bias studies to avoid downgrading our certainty of evidence. This is in accordance with GRADE recommendations [39].
We will conduct the review according to this published protocol and report any deviations from it in the Methods section.
If we include a study or studies conducted by the authors of this review, other authors will independently undertake risk of bias assessment.
We will use the checks outlined in Table 2 of the IPD Integrity Tool to examine the integrity of the eligible studies [40]. These checks will include checking for retractions or expressions of concerns from the author or author group, checking for evidence of ethics approval, checking for evidence of trial registration or a publicly available protocol, implausible randomisation, implausible results or follow‐up, implausible author group (e.g. only two authors for an international multicentre RCT). We will report the results of integrity checks narratively and in tables.
Two review authors (JS, MF, MB, or ALS) will independently perform integrity checks. Disagreements will be resolved by consensus or the introduction of a third review author (RS), if required. If we identify one or more concerns about a study, we will contact the study authors for further information. This may include requesting individual participant data to perform the more extensive checks outlined in the IPD Integrity Tool [40].
If we are unable to address minor concerns following investigation and contact with study authors, we will exclude the studies from the primary analysis and conduct sensitivity analysis to determine whether the results are robust to their exclusion (see Sensitivity analysis).
If we identify major/serious concerns that we are unable to address following investigation and contact with study authors, we will exclude the study and not include it in any sensitivity analyses.
Decisions surrounding the handling of integrity concerns will be made via consensus with at least three review authors, including at least one methods expert and one clinical expert.
We will present dichotomous data using risk ratios (RR) and risk differences (RD) with 95% confidence intervals (CIs). If there is a statistically significant reduction (or increase) in RD, 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.
For continuous data, we will use the mean difference (MD) when studies measure outcomes in the same way. We will use the standardised mean difference (SMD) to combine data from studies that measured the same outcome but used different methods. Where studies reported continuous data as median and interquartile range (IQR), and data passed the test of skewness, we will convert the median to mean, and estimate the SD as IQR/1.35 [41].
The unit of analysis will be the individual participant (i.e. the infant) included in individually randomised trials; a participant will only be considered once in the analysis. For any cluster‐randomised trials, the cluster (e.g. neonatal unit or part thereof) will be the unit of analysis. For cluster‐randomised 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 randomised observations (e.g. infants within clinics, but also clustering of multiple births, where applicable). 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 correlations (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 Cochrane guidance [42]. Where possible, we will derive the ICC for these adjustments from the study itself, or from a similar study. If an appropriate ICC is unavailable, we will conduct sensitivity analyses to investigate the potential effect of clustering, by imputing a range of values of ICC.
If any studies compare multiple arms against the same control condition, which will be included in the same meta‐analysis, we will either combine groups to create a single pairwise comparison, or select the pair of interventions that more closely match the definitions given in Types of interventions, and exclude the others. We will acknowledge this potential selective bias of data used for analysis in the Discussion section.
We intend to perform an intention‐to‐treat analysis for all included outcomes. Whenever possible, we will analyse all randomised participants in the group to which they were randomly allocated, regardless of the actual treatment received.
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 favouring 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 randomised participants in the denominator.Extreme‐case analysis favouring 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 randomised participants in the denominator.
For continuous outcomes, we will calculate missing SDs using reported P values or CIs [41]. If calculation is not possible, we will impute an 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.
To assess reporting bias, we will compare the stated primary and secondary outcomes in the included studies against the reported outcomes. If they are available (via published reports or through contact with study authors), we will refer to related study documents including published protocols, statistical analysis plans, or trial registrations. Two review authors (JS, MB, and MF) will conduct independent assessments of reporting bias. Disagreements will be resolved by consensus or the introduction of a third review author (ALS or RS) if consensus cannot be reached.
We will document, in the Characteristics of included studies table, any studies that use interventions in a potentially eligible infant population but do not report on any of the outcomes.
If study numbers are sufficient (more than 10), we will use funnel plots to explore funnel plot asymmetry as an indicator of possible publication bias [43]. This will be incorporated into our certainty of evidence assessments. If our review includes fewer than 10 studies eligible for meta‐analysis, the ability to detect publication bias with funnel plots will be largely diminished, and we will comment on this in the Discussion section. However, we also note that including a search for unpublished evidence with clinical trial registers (as described in Searching other resources) will reduce the potential for publication bias.
If we identify multiple studies that we consider to be sufficiently similar for appropriate meta‐synthesis, we will perform meta‐analysis using aggregate data using RevMan [35]. As described in Types of interventions, we will conduct separate meta‐analyses for the two research objectives of interest (i.e. oxygen saturation target‐based interventions and titration‐based interventions). For categorical outcomes, we will calculate estimates of RR and RD, each with their 95% CI. For continuous outcomes, we will calculate MD or SMD with their 95% CI.
As we expect a small number of studies, we will use a fixed‐effect model to combine data [44]. We will assume that studies were estimating the same underlying treatment effect. If we identify a larger number of studies, we will consider random‐effects models.
We will attempt to explain any clinical heterogeneity by exploring different study characteristics and appropriate subgroup analyses. We will use forest plots to graphically represent study data.
If we judge meta‐analysis to be inappropriate (e.g. study numbers are too few, or studies are too different to permit meaningful meta‐synthesis), we will refer to methodological guidance in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions [45], and the Synthesis Without Meta‐analysis (SWiM) reporting guidance [46]. We will create a table with studies ordered by risk of bias, and calculate standardised effect estimates for each study. This table will be modelled on the worked example, Table 12.4.b, in the Cochrane Handbook for Systematic Reviews of Interventions [45]. We will use a forest plot to graphically represent the study data.
We will describe the clinical diversity and methodological variability across the eligible studies narratively and in tables. Tables will include relevant information on study characteristics, such as design features, population characteristics, study centres and acuity, 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 measure the proportion of total variability due to between‐study heterogeneity [47, 48].
Our interpretation of the I^2^ statistic will take into account the understanding that measures of heterogeneity will be estimated with high uncertainty when the number of studies is small [47].
If we suspect substantial heterogeneity, we will report the finding and explore possible explanatory factors using prespecified subgroup analysis.
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 of Systematic Reviews for Interventions [47].
In particular, subgroups with very few studies per category (i.e. fewer than five) are unlikely to ascertain valid differences in effects. As such, we will only perform subgroup analyses if there are sufficient numbers of studies (i.e. at least five per subgroup). 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 the effect of heterogeneity (e.g. Cochran's Q test, meta‐regression [47]). If studies report interaction effect estimates, we will conduct a meta‐analysis of within‐study interactions (deft approach) to avoid aggregation bias.
We plan to conduct three subgroup analyses.
Gestational age. As we expect treatment effects might vary according to infant gestational age (see Background), we will group infants into categories based on gestational age at birth. Extremely preterm (less than 28 weeks' gestation); very preterm (28 to less than 32 weeks' gestation); moderate preterm (32 to less than 34 weeks' gestation); late preterm (34 to 36 weeks' gestation). Depending on the number of available studies, we may collapse these categories into two only (very and extremely preterm, moderate to late preterm).Income/setting. Given that access to critical equipment required for different aspects of the intervention (e.g. pulse oximeters) is variable in lower‐resourced settings, we will examine for possible effect differences across different settings [16, 18] (see Background). We will group studies into low or middle‐income countries (LMIC) or high‐income countries (HIC), classifying countries according to the World Bank classification. This is based on gross national income per capita in US dollars converted from local currency using the World Bank Atlas Method.DCC. The timing of umbilical cord clamping may influence the evolution of oxygen saturation in the delivery room [14]. Infants who receive DCC (30 seconds or greater) may respond differently to infants who receive immediate cord clamping (less than 30 seconds) [14]. As such, we will perform subgroup analysis according to the method of umbilical cord management, stratified into two DCC (umbilical cord clamped at 30 seconds or greater) and immediate cord clamping (umbilical cord clamped at less than 30 seconds). If we identify a sufficient number of studies/participants, we will consider adding additional groups to account for alternate methods of umbilical cord management (e.g. umbilical cord milking, longer deferrals of cord clamping).
We will limit our examination of subgroups to critical outcomes only.
Access to equipment required to deliver the interventions of interest, specifically pulse oximeters and oxygen blenders, is variable in settings with lower resourcing [16, 18]. We will extract relevant information related to health equity considerations as described in Data extraction and management in line with guidance from the PROGRESS‐Plus group [34] and Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions [49]. We will report this information narratively and in tables.
Our planned subgroup analysis according to country income classification aims to explore whether economic circumstances might impact the effectiveness of these interventions.
We will also comment on the implications of resourcing to deliver the interventions of interest in the Discussion section.
We will conduct a sensitivity analysis exploring the effect of the methodological quality of studies by excluding studies judged at high overall risk of bias and excluding studies for which we have integrity concerns. We will also explore the choice of using a fixed‐effect model for the primary analysis by conducting sensitivity analysis using a random‐effects model.
Differences in the design of studies included in this review might also affect our results. Therefore, we will perform a sensitivity analysis to compare the effects of RCTs as opposed to quasi‐randomised trials (if any are present).
For missing dichotomous outcomes, we will include participants with incomplete or missing data in the sensitivity analyses by imputing them according to the best‐worst case scenario and the worst‐best case scenario (see Dealing with missing data).
As the boundaries for higher and lower oxygen saturation targets for research objective 1 are somewhat arbitrary (see Types of interventions), we will explore alternative definitions in sensitivity analysis.
As we plan to use a fixed‐effect model for the primary analysis, we will explore random‐effects models in sensitivity analyses.
Sensitivity analyses will be conducted and reported for the critical outcomes only.
We will use the GRADE approach to assess the certainty of evidence for critical outcomes according to guidance from the GRADE Handbook [39].
We will prepare two summary of findings tables as follows [50].
Target‐based interventions. Lower oxygen saturation target compared to higher oxygen saturation target for delivery room FiO2 titration.Titration‐based interventions. Clinician‐driven approaches compared to automated algorithm‐based approaches or artificial intelligence‐informed approaches for delivery room FiO2 titration.
Two review authors (JS and ALS) will independently assess the certainty of evidence for each of the critical outcomes (see Table 1 in Outcome measures). Any disagreements between the two review authors will be resolved via consensus or the introduction of a third review author if required (RS). 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 design (risk of bias), consistency across studies, directness of the evidence, precision of estimates (up to three levels for extremely serious), and presence of publication bias. We will use GRADEpro GDT software to create the summary of findings tables and to report the certainty of the evidence [51].
Final GRADE ratings will be discussed amongst all review authors, except review authors who are involved in the design or conduct of the eligible studies. These authors will not input into the certainty of assessment ratings for the studies they are involved in, in line with Cochrane's editorial policy on conflicts of interest.
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 we have very little confidence in the effect estimate; the true effect is likely to be substantially different from the estimate of the effect.
We will not involve consumers in this review due to limited resources, although we will use core outcome sets which have been developed with consumer involvement [27].
Supplementary materials are available with the online version of this 10.1002/14651858.CD016293.
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