Newborn resuscitation with intact cord for non‐vigorous term or late preterm infants

Objectives

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

To assess the safety and efficacy of resuscitation with an intact cord compared to resuscitative care with immediate cord clamping or umbilical cord milking for non‐vigorous term or late preterm neonates (≥ 35 weeks' gestation).

Background

Description of the condition

Cord management at birth affects the health of the world's 140 million neonates annually (UN 2022). Over the last two decades, evidence has emerged that supports the health benefits of delayed cord clamping (DCC) by one to five minutes, thereby promoting placental transfusion (Andersson 2021; McDonald 2013). Most international governing bodies endorse DCC of more than 30 seconds for vigorous term and preterm neonates, and immediate cord clamping (ICC) for non‐vigorous term neonates (Aziz 2020; Perlman 2015). ICC is recommended for non‐vigorous (pale, limp, and have minimal or no breathing at birth) term neonates to help with immediate resuscitation.

Placental transfusion, defined as a transfer of blood volume from the placenta to the baby, differs significantly between neonates who receive ICC versus DCC. Throughout pregnancy, the foetal‐placental unit carries approximately 90 mL/kg to 115 mL/kg of blood volume, of which 50% in preterm, and 30% in term neonate, is in the placenta (Katheria 2017a; Linderkamp 1982). Various direct and indirect methods have been used to estimate the volume of placental transfusion after DCC, including changes in birth weight, haemoglobin and haematocrit, measurement of neonatal blood volume, and residual placental blood volume (RPBV). Studies have shown that compared to ICC, DCC results in a higher birth weight, by approximately 101 g; haemoglobin, by 1.5 g; and haematocrit, by 10% at 24 to 48 hours (Chen 2018; McDonald 2013; Oh 1966). Studies using iodine‐131 tagged albumin reported a neonatal blood volume of 78 mL/kg for ICC versus 98.6 mL/kg for a DCC of five minutes (Usher 1963); and blood volume distribution of 67% for neonatal and 33% for placental at birth; 80% for neonatal and 20% for placental at one minute; and 87% for neonatal and 13% for placental at three minutes (Yao 1969). The last 150 years of placental transfusion research showed conclusively that ICC results in a residual placental blood volume (RPBV) of 25 mL/kg to 35 mL/kg at term, which will deprive term neonates of approximately 15 mL/kg to 30 mL/kg of placental transfusion (Andersson 2023).

Linderkamp and colleagues reported higher blood volume with intrauterine asphyxia (90 mL) compared to non‐asphyxiated neonates (78 mL), due to loss of foetal vasomotor tone, which increased placenta‐to‐foetal blood flow. Intrauterine asphyxia, also known as foetal asphyxia, is defined as a lack of oxygen supply to the foetus while still in the uterus, due to issues associated with the placenta, umbilical cord, or maternal health. On the other hand, newborns with intrapartum asphyxia (tight nuchal cord or shoulder dystocia) had reduced blood volumes (67 mL/kg versus 78 mL/kg for non‐asphyxiated neonates) because the firm‐walled arteries were able to transfer blood back to the placenta, while preventing the infant from receiving blood from the placenta via the soft‐walled umbilical vein (Linderkamp 1978).Intrapartum asphyxia is defined as an inadequate supply of oxygen to the foetus during the process of labour and delivery (Low 1997).

At birth, neonates with intrapartum asphyxia are relatively hypovolaemic, and performing ICC will deprive them of placental transfusion (Katheria 2019; Menticoglou 2016; Mercer 2009). Depending on the degree of hypovolaemia, the body tries to shunt blood to vital organs, like the brain, heart, and adrenals from the skin, intestines, and kidneys (Lind 1965). Severe hypovolaemia can result in cardiac asystole, initiate an inflammatory cascade, hypoxic ischaemic encephalopathy (HIE), seizures, and death (Makley 2012; Mercer 2022; Rajnik 2002). Furthermore, neonates exposed to perinatal distress are at risk of persistent pulmonary hypertension (PPHN) and oxidative stress (Wedgwood 2019).

A commonly held paradigm during resuscitation for non‐vigorous neonates is that ventilation and lung opening are the first priority; this has recently been questioned (Mercer 2022). Data suggest that DCC allows the recruitment of the dense alveolar capillary bed (1 alveolus to around 900 capillary segments), facilitating the opening of lungs and preventing collapse during expiration, and assisting in the removal of lung fluid (Juykku 1958; Mercer 2022; Mercer 2023).

Description of the intervention

At birth, approximately 10% of neonates need some form of resuscitation for extrauterine adaptation (Aziz 2020); most of these neonates are deprived of placental transfusion because of the presumed need for immediate resuscitation. Resuscitation with an intact cord (RIC) and umbilical cord milking (UCM) have been studied as procedures to provide placental transfusion in non‐vigorous neonates (Katheria 2019).

Delayed cord clamping (DCC) and resuscitation with an intact cord (RIC)

Identifying term neonates who require RIC is challenging, as most asphyxiated neonates are born without warning signs. In a pilot study on RIC in term neonates, less than a third required resuscitation (Katheria 2017b). RIC requires a significant shift in workplace ergonomics, equipment design, and more importantly, a change in the mindset of obstetricians and resuscitation teams. To satisfy all the standards of a neonatal resuscitation programme, RIC requires a warm environment close to the mother, with a firm surface; equipment for suctioning, oxygenation, positive pressure ventilation, and intubation; access to the umbilicus; and a comfortable position for the resuscitation team and obstetrician (Aziz 2020). For RIC following a caesarean section, maintaining sterility of the operating field is an additional requirement. Resuscitation with an intact cord is the standard of care in some birth centres and home birth settings (Erickson‐Owens 2023; Mercer 2000). However, in hospital practice, RIC is performed mainly in research settings. There are no standard international RIC guidelines for providers.

Umbilical cord milking (UCM)

UCM is an alternative to DCC with an intact cord that allows rapid placental transfusion for non‐vigorous neonates, without a delay in initiating resuscitation (Katheria 2019; Perlman 2015). UCM can be performed on an intact cord (I‐UCM) or after cutting the cord (C‐UCM (Katheria 2019)). In I‐UCM, an intact umbilical cord of 20 cm to 30 cm is stripped several times towards the baby (usually two to five times) over 15 seconds to 20 seconds. In C‐UCM, the cord is cut immediately, leaving a cord length of 20 cm to 25 cm. The cord is then held perpendicular to the newborn, and the cord is stripped towards the baby. A small study comparing I‐UCM versus C‐UCM in term neonates showed better placental transfusion with I‐UCM (McAdams 2018). UCM may be a promising intervention when non‐vigorous neonates are born unexpectedly, because of the ease of application in any setting, without expensive equipment or training. However, limited data are available on the safety and feasibility of UCM for non‐vigorous neonates. A recent randomised controlled trial demonstrated that UCM in non‐vigorous infants was safe, resulted in fewer moderate to severe hypoxic‐ischaemic encephalopathy occurrences, fewer infants who required therapeutic hypothermia, and higher haemoglobin levels (Girish 2018). UCM appears to be a more attractive option compared to DCC for stem cell transfusion; it has greater mesenchymal stromal cell and haematopoietic stem cell populations, a composition more favourable for haematopoiesis (Katheria 2020).

How the intervention might work

It is envisaged that RIC will facilitate asphyxiated neonates in post‐natal adaptation. It prevents hypovolaemia by providing 20% to 30% of the blood volume that belongs to the newborn baby. In studies performed on infants at risk of requiring resuscitation, RIC showed higher cerebral oxygenation and blood pressure at 12 hours of life (Katheria 2017b), higher Apgar scores at 5 and 10 minutes, and better neurodevelopmental outcomes at two years of age compared to ICC (Andersson 2019; Isacson 2021). Two feasibility studies examined the effect of intact cord resuscitation on neonates with diaphragmatic hernia. They found higher haemoglobin levels, higher pH, lower plasma lactate, and higher blood pressure at 6 and 12 hours of life compared to the control group (Foglia 2020; Lefebvre 2017).

Placental transfusion associated with DCC results in higher haemoglobin and haematocrit at birth, higher iron stores at 3 to 12 months, less anaemia in infancy (Andersson 2011; Andersson 2021; Chaparro 2011), and greater myelin content in the region of the brain associated with motor, visual, and sensory processing and function (Mercer 2018). Non‐vigorous neonates are at risk of neuronal brain injuries, and optimising iron stores by placental transfusion in these neonates would be neuroprotective. In neonates suffering from intrauterine asphyxia, where blood volume is already elevated, RIC may have an adverse effect on postnatal homeostasis and be counterproductive, which needs further evaluation (Linderkamp 1978).

DCC decreases mortality in preterm infants by 30% (Tarnow‐Mordi 2017). For healthy term infants, the risk of mortality and admission to intensive care decreased by 20% for every 10 seconds of DCC after the onset of spontaneous respiration (Ersdal 2014).

Placental transfusion is rich in haematopoietic and non‐haematopoietic stem cells. It can protect and repair various organ injuries, which may be crucial in non‐vigorous neonates at risk of brain injuries (Chen 2005; Lawton 2015).

Reported adverse effects of placental transfusions include hyperbilirubinaemia, symptomatic polycythaemia, hypothermia, and delayed resuscitation (McDonald 2013). However, they have not been conclusively supported in recent randomised control and observational trials (Andersson 2021; Rana 2019; Yaşartekin 2020). Intact cord resuscitation is also safe for mothers. A study involving 9000 Swedish women reported less postpartum haemorrhage with an average DCC of six minutes (Winkler 2022).

RIC safety in neonates with intrauterine asphyxia and increased blood volume needs further evaluation. RIC may worsen polycythaemia, and may interfere with postnatal adaptation. (Linderkamp 1978).

The long‐term data of neonates who underwent RIC are limited. At two‐year follow‐up, the CORD pilot study found a trend toward decreased mortality, death, or neurodevelopmental impairment (NDI); however, the study's adherence to its protocol was low (Andersson 2019).

Why it is important to do this review

Cord management decisions at birth affect short‐ and long‐term outcomes of both vigorous and non‐vigorous neonates. Robust evidence unequivocally supports the short‐ and long‐term health benefits of placental transfusion by DCC in vigorous neonates (Andersson 2011; Andersson 2021). ICC is the standard of practice for non‐vigorous neonates (Aziz 2020); but ICC and moving neonates away from their mothers may be unwise and harmful. Resuscitation with an intact cord is considered natural, and is practised in home births and birthing centres in many countries. Evidence for the safety, efficacy, and applicability of RIC in non‐vigorous neonates in the hospital setting is growing rapidly (Katheria 2016; Katheria 2018; Koo 2023). Whether RIC is safe and superior to UCM or ICC in non‐vigorous neonates has yet to be fully discovered. There are no systemic reviews comparing the available options (RIC, UCM, and ICC) for providing placental transfusion.

This Cochrane review will compare outcomes of term and near‐term newborns resuscitated with an intact umbilical cord to the current practice of immediate cord clamping, resuscitation, or umbilical cord milking.

Objectives

To assess the safety and efficacy of resuscitation with an intact cord compared to resuscitative care with immediate cord clamping or umbilical cord milking for non‐vigorous term or late preterm neonates (≥ 35 weeks' gestation).

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised (RCT), quasi‐randomised (quasi‐RCT), or cluster‐randomised controlled studies (cluster‐RCT). We will include studies reported as full text, as abstract only, and unpublished data when the data can be sourced.

We will exclude any study that is not randomised or quasi‐randomised, e.g. cohort and case‐controlled studies.

Types of participants

We will include studies with neonates of ≥ 35 weeks' gestation who were randomised to resuscitation groups. According to the standard Neonatal Resuscitation Program (NRP) American Heart Association (AHA) guidelines, resuscitation is required for a newborn who is not crying or breathing, is limp, or has poor muscle tone (Aziz 2020; Kattwinkel 2011). We will include all studies that used standard NRP/AHA guidelines or algorithms, or World Health Organization (WHO) contextual, or local NRP‐HBB (Helping Baby Breathe) guidelines for low‐ and middle‐income countries (LMIC). We will include studies that include a subset of eligible participants if results are reported separately for the eligible subset. If separate data are not available, we will only include studies with a mixed population if ≥ 80% of participants adhere to the inclusion criteria. We will exclude studies that use guidelines that are different from ours, but mention them in their appropriate context in the discussion.

Types of interventions

We will include studies that use the following interventions and comparisons.

• Resuscitation with an intact cord (RIC) versus immediate cord clamping (ICC)

• RIC versus resuscitative care (umbilical cord milking) with an intact cord (I‐UCM)

• RIC versus resuscitative care (umbilical cord milking) after cutting the cord (C‐UCM)

Definitions

Immediate cord clamping (ICC) is defined as clamping the cord within 30 seconds (Perlman 2015).

Resuscitation with an intact cord (RIC) is defined as performing any or all steps of resuscitation outlined in the Neonatal Resuscitation Program Guidelines with an intact umbilical cord (Kattwinkel 2011).

Intact umbilical cord milking (I‐UCM) is defined as grasping the unclamped umbilical cord and pushing (stripping) the blood toward the infant two to five times before it is clamped. The procedure is usually completed in about 20 seconds, allowing resuscitation to take place quickly (Katheria 2017a).

Cut umbilical cord milking (C‐UCM) is defined as clamping and cutting a long segment of the umbilical cord immediately after birth, then milking (stripping) the cord toward the infant two to five times. After clamping and cutting the cord, the baby and the long cord are passed to the paediatrics provider for milking. The procedure is usually completed in about 20 seconds, allowing resuscitation to occur quickly (Katheria 2017a).

The duration of resuscitation with an intact cord (RIC) will be defined as both time‐based (one, two, or three minutes, or until cord pulsation stops) and physiology‐based (before or after onset of breathing or crying).

Types of outcome measures

Primary and secondary outcomes are outlined below.

Primary outcomes

• Death before discharge

• Neuro‐developmental outcomes at 12 months, 18 months, 24 months, and > 24 months, as available (assessed by a standardised and validated assessment tool, or a child developmental specialist)

Evidence of placental transfusion

• Haemoglobin and haematocrit (first measurement within 6 hours)

• Number of red blood cell transfusions during the hospital stay

• Polycythaemia (haematocrit greater than 65%) requiring any treatment

• Jaundice requiring treatment with phototherapy, or exchange transfusion, or both

Resuscitation‐related outcomes

• Hypoxic ischaemic encephalopathy (HIE) of any stage (defined by modified Sarnat staging or Thompson score); Sarnat HIE stage 2, and Thompson score 11 to 14 as moderate HIE; and Sarnat HIE stage 3 and Thompson score 15 to 22 as severe HIE (Jacobs 2013; Sarnat 1976; Thompson 1997)

• Admission to neonatal intensive care unit (NICU)

• APGAR scores at 5 and 10 minutes

• Receipt of positive pressure ventilation during resuscitation

• Receipt of chest compressions during resuscitation

• Receipt of adrenaline during resuscitation

• Severe acidosis (pH < 7.0) at first gas analysis

• Plasma lactate level (highest lactate measurement within 6 hours)

Hypoxaemic‐hypovolemic injury to any organ system

• Receipt of therapeutic hypothermia

Other neonatal outcomes

• Persistent pulmonary hypertension, confirmed by echocardiogram and treated

• Length of stay in hospital (days)

Maternal outcomes

• Maternal mortality (within 42 days after delivery (WHO 2023))

• Postpartum haemorrhage (PPH; > 500 mL blood loss for PPH; > 1000 mL for severe PPH, within 24 hours after birth (WHO 2012))

Search methods for identification of studies

Electronic searches

The MEDLINE strategy was drafted by an Information Specialist (MF) and will be peer‐reviewed by another Information Specialist, following PRESS guidelines (McGowan 2016). The MEDLINE strategy will be translated for other databases using appropriate syntax and subject headings. The draft strategy is provided in Appendix 1.

We will use a methodological filter to restrict retrieval to randomised and quasi‐randomised controlled studies; and a population filter to limit retrieval to the neonatal population. Searches will not be limited by language or publication type. Searches for trials will not be limited by date; searches for systematic reviews will be restricted to the past two years.

We will search the following databases:

• Cochrane Central Register of Controlled Trials (CENTRAL; current issue) in the Cochrane Library;

• MEDLINE OVID (1947 forward);

• Embase OVID (1974 forward);

• Epistemonikos (https://www.epistemonikos.org).

We will search these clinical trial registries for ongoing or recently completed trials:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov);

• World Health Organization International Clinical Trials Registry Platform (ICTRP; trialsearch.who.int/Default.aspx).

Searching other resources

We will identify conference abstracts indexed in CENTRAL and Embase, and by independent searches of the following for the past five years, if available:

• European Academy of Paediatric Societies (EAPS);

• Pediatric Academic Societies (PAS; www.pas-meeting.org/past-abstracts/).

We will search the reference lists of studies selected for inclusion, and systematic reviews on topics related to the objectives of this protocol in an effort to identify studies not found by other search methods. We will search for errata or retractions from included studies published in full‐text on PubMed and the Retraction Watch database, and report the date this was done in the review.

Data collection and analysis

We will use the standard methods of Cochrane Neonatal for data collection and analysis. We will design data extraction forms specifically for this review, test them on two studies, further refine them, and then use them to collect and collate data. For each included study, we will record the details of the method of randomisation, allocation concealment, blinding, drug intervention, stratification, and whether the study was single or multi‐centre. We will extract data for the participants, resuscitation details, and reported outcomes.

Selection of studies

We will download all titles and abstracts retrieved by electronic searching into reference management software. We will remove duplicates using reference management software and Covidence. We will use Covidence to screen results.

Two of three review authors (MM, RT, VK) will independently screen the titles and abstracts. After title/abstract review, they will independently review the full text of the remaining references. At any point in the screening process, we will resolve disagreements between review authors by discussion or consultation with other review authors (PS, MF). We will document reasons for reports excluded during full‐text screening in the characteristics of excluded studies table. We will exclude studies if one or more of the following do not meet our inclusion criteria: population, intervention, or study design. We will collate multiple reports of the same study so that each study, rather than each report or reference, is the unit of interest in the review; related reports will be grouped under a single study ID. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009; Moher 2009; Page 2021).

We will contact the authors of the unpublished studies or conference abstracts for more data or information as required. We will downgrade the evidence according to GRADE recommendations if we are unable to use the data for quantitative synthesis. If data are insufficient, we will classify the studies as studies awaiting assessment.

Data extraction and management

Two of three review authors (MM, RT, VK) will independently extract, assess, and code all data for each study, using a form designed specifically for this review. We will replace any standard error of the mean with the corresponding standard deviation. We will resolve any disagreements by discussion, or by consulting a third review author (PS, MF). Two review authors (RT MM) will independently enter final data for each study, which the other review author (VK) will check.

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; details of other relevant papers cited

• Study: study design; type, duration, and completeness of follow‐up (e.g. > 80%); country and location of study; informed consent; ethics approval

• Participants: sex, birth weight, gestational age, number of participants

• Interventions: initiation, dose, and duration of administration

• Outcomes, as listed under Types of outcome measures

We will resolve any disagreements by discussion. We will describe ongoing studies by detailing the primary author, research question(s), methods, and outcome measures, together with an estimate of the reporting date, and report them in the characteristics of ongoing studies table. Should any queries arise, or if additional data are required, we will contact study investigators/authors for clarification. Three review authors (MM, RT, VK) will enter the data into Review Manager (RevMan (RevMan 2024)).

Assessment of risk of bias in included studies

Two review authors (MM, RT) will independently assess the risk of bias (low, high, or unclear) in all included trials using the Cochrane RoB 1 tool, for the following domains (Higgins 2017).

• Sequence generation (selection bias)

• Allocation concealment (selection bias)

• Blinding of participants and personnel (performance bias)

• Blinding of outcome assessment (detection bias)

• Incomplete outcome data (attrition bias)

• Selective reporting (reporting bias)

• Any other bias

We will also assess the risk of bias in any cluster‐randomised studies, under the following domains (Higgins 2017).

• Baseline imbalance (in the clusters)

• Recruitment bias

• Loss of clusters

• Problems in analysis of cluster trials (not taking the intra‐cluster correlation into account in analysis)

We will resolve any disagreements by discussion. See Appendix 2 for a more detailed description of the risk of bias for each domain.

Measures of treatment effect

We will use RevMan for the statistical analysis (RevMan 2024). We will summarise the data in a meta‐analysis if they are sufficiently homogeneous, both clinically and statistically. If data are not reported in a format that we can enter directly into a meta‐analysis, we willconvert them to the required format using the information in Chapter 6of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2023).

Dichotomous data

For dichotomous data, we will present results using risk ratios (RR) and risk differences (RD), 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 for primary outcomes, or if there is a reduction (or increase) of at least 10% in the 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 report the 95% CI on all estimates. We will use the standardised mean difference (SMD) to combine 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 mean to median and estimate the standard deviation as IQR/1.35.

Unit of analysis issues

The unit of analysis will be the participating infant in individually randomised trials; an infant will be considered 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‐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. infant within clinics). Available statistical information needed to account for the implications of clustering on the estimation of outcome variances will be extracted, such as design effects or intracluster correlation, 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 (Higgins 2023). Where possible, we will derive the intracluster correlation for these adjustments from the trial itself, or from a similar trial.

If any trials have multiple arms that are compared against the same control condition, which will be included in the same meta‐analysis, we will combine groups if the interventions are similar (e.g. DCC for different times can be combined) to create a single group.

Dealing with missing data

Where feasible, we intend to carry out analysis on an intention‐to‐treat (ITT) basis for all outcomes. Whenever possible, we will analyse all participants in the treatment group to which they were randomised, regardless of the actual treatment received. If we identify important missing data (in the outcomes) or unclear data, we will request the missing data by contacting the trial investigators. We will make explicit the assumptions of any methods used to deal with missing data. We will address the potential impact of missing data on the findings of the review in the discussion.

Assessment of heterogeneity

We will describe the clinical diversity and methodological variability of the evidence in text 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 confidence intervals. 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:

• 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.

We will use a rough guideline to interpret the I² value rather than a simple threshold. Our interpretation will take into account an understanding that measures of heterogeneity (I²) will be estimated with high uncertainty when the number of studies is small(Deeks 2022).

Assessment of reporting biases

We will use funnel plots to assess reporting bias when more than 10 studies report the same outcome. If publication bias is suggested by a significant asymmetry of the funnel plot on visual assessment, we will incorporate this into our assessment of certainty of evidence.

We will assess reporting bias by comparing the stated primary and secondary outcomes and 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 that use interventions in a potentially eligible infant population but do not report on any of the primary and secondary outcomes in the characteristics of included studies tables.

We will identify and evaluate multiple reports of a single study (multiple publication bias) by comparing the reported baseline characteristics and the author details with clarifications requested from authors if required, to avoid double counting.

Data synthesis

We will undertake meta‐analyses in RevMan (RevMan 2024). For estimates of typical RR and typical RD, we will use the Mantel‐Haenszel method. We will use the inverse variance method for measured quantities. We will use the fixed‐effect model for all primary meta‐analyses, as recommended by Cochrane Neonatal.

We will replace any standard error of mean with the corresponding standard deviation. If the data are described in medians and IQ ranges, we will substitute medians for the means, and impute the corresponding SD by dividing the IQ ranges by 1.35. If the data are described in medians and ranges, we will use the formulae proposed by Hozo and colleagues to impute the SD (Hozo 2005).

If a cluster‐RCT used appropriate statistical methods to account for intracluster correlation (e.g. generalised estimating equations), we will use the appropriate effect sizes with the reported SD for analysis. However, if the appropriate statistical methods were not used or reported, we will use an approximate standard error (SE) by multiplying the SE by the square root of design effect (DE). DE will be calculated as DE = 1 + (mean cluster size ‐ 1) x intracluster correlation (Higgins 2023).

If we judge meta‐analysis to be inappropriate, we will analyse 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.

Subgroup analysis and investigation of heterogeneity

We will explore substantial or considerable heterogeneity (> 50%) in the outcomes by visually inspecting the forest plots and by removing the outlying studies in the sensitivity analysis (Higgins 2023). We will downgrade the certainty of evidence in the summary of findings tables, according to the GRADE recommendations for inconsistency (heterogeneity).

We will undertake subgroup analysis based on the following subgroups, if subgroup data are available, and as applicable to specific interventions:

• type of delivery: vaginal versus caesarean (for all comparisons);

• resources of setting (e.g. high‐income versus low‐ or middle‐income country)

• resuscitation with intact cord (RIC) for different time durations (e.g. one minute versus two minutes)

Tests for subgroup differences in effects will be interpreted with caution, given the potential for confounding with other study characteristics and the observational nature of the comparisons (Deeks 2023). 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, stratified meta‐analysis and a formal statistical test for interaction will be conducted as feasible, to examine subgroup differences that could account for effect heterogeneity (e.g. Cochran’s Q test, meta‐regression (Borenstein 2013; Deeks 2023)).

Sensitivity analysis

We will present the results of the sensitivity analyses only if they are significantly different from the results of the initial analysis. We will undertake a sensitivity analysis in the following situations:

• characteristics of bias: high risk of bias compared to those at low risk of bias;

• RCT type: cluster‐randomised trials compared to individually randomised trials;

• range of intracluster correlation coefficient values in cluster randomised trials if an appropriate intracluster correlation coefficient is not available;

• characteristics of publication status: e.g. RCTs published as abstract only compared to RCTs published in full.

Since there is no formal statistical test that can be used for sensitivity analysis, we will make informal comparisons between the different ways of estimating the effect under different assumptions. We will not use changes in the P values to judge whether there is a difference between the main analysis and sensitivity analysis, since statistical significance may be lost with fewer studies included.

Summary of findings and assessment of the certainty of the evidence

We will use the GRADE approach, outlined in the Handbook for Grading the Quality of Evidence and The Strength of Recommendations Using The GRADE Approach, to assess the certainty of evidence for the following, clinically relevant outcomes (Schünemann 2013). We will report results following recommended language, found in Chapter 15 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2023a); and we will create summary of findings tables for the following outcomes, following guidance in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions(Schünemann 2023b).

• Death before discharge

• Neuro‐developmental outcomes at 12 months and 24 months

• Maternal outcome: postpartum haemorrhage

Three review authors (MM, RT, VK) will independently assess the certainty of the evidence for each of these outcomes. 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: study limitations (risk of bias), consistency across studies, directness of the evidence, precision of estimates, and presence of publication bias. We will use GRADEpro GDT to create summary of findings tables for the following comparisons (GRADEpro GDT).

• Resuscitation with an intact cord (RIC) versus immediate cord clamping and cutting (ICC)

• RIC versus resuscitative care (umbilical cord milking) with an intact cord (I‐UCM)

• RIC versus resuscitative care after cutting the cord (C‐UCM)

The GRADE approach classifies the certainty of a body of evidence as one of four grades.

• High certainty: further research is very unlikely to change our confidence in the estimate of effect

• Moderate certainty: further research is likely to have an important impact on our confidence in the estimate of effect and may change the estimate

• Low certainty: further research is very likely to have an important impact on our confidence in the estimate of effect and is likely to change the estimate

• Very low certainty: we are very uncertain about the estimate

Notes

None

Appendices

Appendix 1. MEDLINE strategy

Database(s): Ovid MEDLINE(R) All

#	Searches	Results	Annotations
1	((intact or "in tact") adj3 (cord? or naval string? or umbilic*)).ti,ab,kw,kf.	858
2	((cord or cords or naval string? or umbilic*) adj4 (bind* or clamp* or cut or cuts or cutting? or ligation? or ligature?)).ti,ab,kw,kf.	3446
3	(cord? adj3 (circulat* or manag* or (respirat* adj2 fail*) or resuscit* or ventilat*)).ti,ab,kw,kf.	1433
4	(umbilical* adj3 (circulat* or manag* or (respirat* adj2 fail*) or resuscitat* or ventilat*)).ti,ab,kw,kf.	780
5	Umbilical Cord/ and Resuscitation/	82
6	PBCC.ti,ab,kw,kf.	73	Tested acronyms ECC, V‐DCC, DCC but not useful; too general.
7	or/1‐6 [Cord clamping; intact cord]	6152
8	exp Infant, Newborn/ or Intensive Care, Neonatal/ or Intensive Care Units, Neonatal/ or Gestational Age/	732813
9	(babe or babes or baby* or babies or gestational age? or infant? or infantile or infancy or low birth weight or low birthweight or neonat* or neo‐nat* or newborn* or new born? or newly born or premature or pre‐mature or pre‐matures or prematures or prematurity or pre‐maturity or preterm or preterms or pre term? or preemie or preemies or premies or premie or VLBW or VLBWI or VLBW‐I or VLBWs or LBW or LBWI or LBWs or ELBW or ELBWI or ELBWs or NICU or NICUs).ti,ab,kw,kf.	1069974
10	Asphyxia Neonatorum/ [Specific to population in this review]	8092
11	or/8‐10 [Filter: Neonatal Population 04‐2022‐MEDLINE]	1382530
12	randomized controlled trial.pt.	608549
13	controlled clinical trial.pt.	95553
14	randomized.ab.	634373
15	placebo.ab.	245632
16	clinical trials as topic.sh.	201753
17	randomly.ab.	426742
18	trial.ti.	302672
19	or/12‐18 [Cochrane HSSS‐SP Maximizing RCT Filter]	1578939
20	(quasirandom* or quasi‐random* or random*).ti,ab,kw,kf.	1493814
21	(control* adj2 (group? or trial? or study)).ti,ab,kw,kf.	1136939
22	or/20‐21 [Additional terms to increase sensitivity]	2110996
23	exp animals/ not humans/	5195276
24	(or/19,22) not 23 [RCT Filter]	2257213
25	meta‐analysis/ or "systematic review"/ or network meta‐analysis/ [/ finds same as.pt. syntax]	339076
26	((systematic* adj3 (review* or overview*)) or (methodologic* adj3 (review* or overview*))).ti,ab,kf,kw.	349658
27	((integrative adj3 (review* or overview*)) or (collaborative adj3 (review* or overview*)) or (pool* adj3 analy*)).ti,ab,kf,kw.	41344
28	(data synthes* or data extraction* or data abstraction*).ti,ab,kf,kw.	43694
29	(hand search* or handsearch*).ti,ab,kf,kw.	11471
30	(mantel haenszel or peto or der simonian or dersimonian or fixed effect* or latin square*).ti,ab,kf,kw.	37502
31	meta‐analysis as topic/ or network meta‐analysis/	29148
32	(meta analy* or metanaly* or meta regression* or metaregression*).ti,ab,kf,kw.	297687
33	(medline or cochrane or pubmed or medlars or embase or cinahl).ab.	362388
34	(cochrane or systematic review?).jw.	20928
35	or/25‐34 [SR filter‐Medline; based on CADTH https://searchfilters.cadth.ca]	671998
36	7 and 11 and 24 [Intact cord and Neonate and RCT]	579
37	7 and 11 and 35 and ("2022" or "2023" or "2024").yr,ed. [Intact cord and Neonate and SR]	41
38	or/36‐37 [All results]	600

Appendix 2. Risk of bias (RoB 1)

We will use the standard methods of Cochrane and Cochrane Neonatal to assess the methodological quality (to meet the validity criteria) of the trials. For each trial, we will seek information regarding the method of randomisation, and the blinding and reporting of all outcomes of all the infants enrolled in the trial. We will assess each criterion as low, high, or unclear risk. Two review authors will separately assess each study. We will resolve any disagreement by discussion. We will add this information to the characteristics of included studies table. We will evaluate the following issues and enter the findings into the risk of bias table:

Sequence generation (checking for possible selection bias). Was the allocation sequence adequately generated?

For each included study, we will categorise the method used to generate the allocation sequence as:

• low risk (any truly random process e.g. random number table; computer random number generator);

• high risk (any non‐random process e.g. odd or even date of birth; hospital or clinic record number);

• unclear risk.

Allocation concealment (checking for possible selection bias). Was allocation adequately concealed?

For each included study, we will categorise the method used to conceal the allocation sequence as:

• low risk (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);

• high risk (open random allocation; unsealed or non‐opaque envelopes; alternation; date of birth);

• unclear risk.

Blinding of participants and personnel (checking for possible performance bias). Was knowledge of the allocated intervention adequately prevented during the study?

For each included study, we will categorise the methods used to blind study participants and personnel from knowledge of which intervention a participant received. Blinding will be assessed separately for different outcomes or class of outcomes. We will categorise the methods as:

• low risk, high risk, or unclear risk for participants;

• low risk, high risk, or unclear risk for personnel.

Blinding of outcome assessment (checking for possible detection bias). Was knowledge of the allocated intervention adequately prevented at the time of outcome assessment?

For each included study, we will categorise the methods used to blind outcome assessment. Blinding will be assessed separately for different outcomes or class of outcomes. We will categorise the methods as:

• low risk, high risk, or unclear risk for outcome assessors.

Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations). Were incomplete outcome data adequately addressed?

For each included study and for each outcome, we will describe the completeness of data, including attrition and exclusions from the analysis. We will note whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported or supplied by the trial authors, we will re‐include missing data in the analyses. We will categorise the methods as:

• low risk (< 20% missing data);

• high risk (≥ 20% missing data);

• unclear risk.

Selective reporting bias. Are reports of the study free of suggestion of selective outcome reporting?

For each included study, we will describe how we investigated the possibility of selective outcome reporting bias and what we found. We will assess the methods as:

1. low risk (where it is clear that all of the study's prespecified outcomes and all expected outcomes of interest to the review were reported);

2. high risk (where not all the study's prespecified outcomes were reported; one or more reported primary outcomes were not prespecified outcomes of interest and are reported incompletely, so cannot be used; the study fails to include results of a key outcome that would have been expected to have been reported);

3. unclear risk.

Other sources of bias. Was the study apparently free of other problems that could put it at a high risk of bias?

For each included study, we will describe any important concerns we had about other possible sources of bias (for example, whether there was a potential source of bias related to the specific study design or whether the trial was stopped early due to some data‐dependent process). We will assess whether each study was free of other problems that could put it at risk of bias as:

• low risk; high risk; or unclear risk.

If needed, we plan to explore the impact of the level of bias by undertaking sensitivity analyses.

Contributions of authors

MNM: conceived, designed and wrote the protocol; will perform study selection and data extraction; check data entered into RevMan 2024; and write the manuscript

VK: conceived and designed the protocol; will check all calculations for imputed values and review the manuscript

RT: helped in protocol writing; will perform study selection and data extraction; will enter data into RevMan 2024; will review the manuscript

MF: wrote search strategy, search methods, results of search, and PRISMA; provided feedback on expression/writing

PSS: provided critical feedback for all aspects of protocol; will provide critical feedback for review analysis and final manuscript

All authors reviewed the manuscript.

Sources of support

Internal sources

• none to report, Other

  none to report

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.

Declarations of interest

MNM does not have any interests to disclose at this time.

VK does not have any interests to disclose at this time.

RT does not have any interests to disclose at this time.

MF is an Information Specialist and Managing Editor with Cochrane Neonatal. She did not participate in editorial processes or publication decisions for this protocol.

PSS is a Senior Editor for Cochrane Neonatal. She did not participate in editorial processes or publication decisions for this protocol.

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