The comparative risks and benefits of early rather than later clamping of the umbilical cord for the preterm infant (fewer than 37 weeks' gestation) have been the subject of much debate, and the optimal timing to clamp the cord is unclear. Attempts to transfuse the baby from the placenta, by leaving the cord unclamped for longer at the time of birth, may conflict with a perceived need for immediate resuscitation, which usually takes place away from the mother.
The proportion of blood in the feto-placental circulation that resides in the placenta and cord varies with gestational age. In the second trimester of pregnancy the circulating blood volume can be 100 to 120 mL/kg of body weight. Upto two-thirds of this amount can be distributed in the placenta at the time of delivery of a preterm infant.
The third stage of labour is the time between birth of the infant and delivery of the placenta. Cord clamping is part of active management of the third stage of labour, a package of care aimed at reducing the risk of postpartum haemorrhage for the women. The cord is usually clamped by applying two clamps. The cord is cut between the clamps, without blood loss for either the infant or the mother. Before the clamps are applied the infant can either be placed on the mother's abdomen (above the level of the placenta), between the mother's thighs (at the level of the placenta) or held below the level of the placenta. Blood flow from the placenta to the infant will depend on which position is used. Some birth attendants also 'milk' the cord towards the infant before clamping, as it can contain up to 20 mL of placental blood (Brune 2002). Whether additional blood actually passes to the infant as a result of this practice is unclear. Also, this milking of the cord is not a physiological transition. It is done with the aim of shortening the time for blood to transfer to the baby at birth, but this ignores a potential role of a slower placental transfusion which may be to facilitate transition from the fetal to the neonatal circulation. For preterm births, an alternative strategy is to provide initial care for the newborn at the bedside and so allow time for delayed cord clamping. There is no consensus about the definition of early or delayed cord clamping regarding the time intervals. Some authors prefer to use the term 'defer' rather than 'delay'.
Common complications and conditions of preterm babies born before 33 weeks' gestation include low blood pressure during the first days of life, the need for respiratory support due to immature lungs and the need for blood transfusions. Intraventricular haemorrhage (bleeding into the brain) and necrotising enterocolitis (severe infection of the bowel) can be life threatening events. These conditions inevitably add to the distress of the parents of these babies.
Suggested advantages of delaying clamping of the umbilical cord and subsequent increased placental transfusion include larger blood volume for the preterm baby, better adaption to extrauterine life; higher haemoglobin for the baby; less anaemia for the baby and better iron stores, less need for blood transfusion, less respiratory distress (Linderkamp 1978), and less requirement for respiratory support (Holland 1991; Hudson 1990; Kinmond 1993). Potential disadvantages include delay in resuscitation, hypothermia, polycythaemia, hyperbilirubinaemia needing treatment (Saigal 1972) and a possible risk of intraventricular haemorrhage (Hofmeyr 1988). If there are benefits for preterm infants in the first few days and weeks of life, it would also be important to assess whether these short-term benefits are reflected in improved long-term outcome.
There are different potential comparative effects of early rather then delayed cord clamping for term and preterm infants. For example, in term infants increasing placental transfusion by delaying cord clamping may increase respiratory morbidity after birth (Yao 1974). As a consequence the issue of timing of cord clamping is reviewed separately for preterm and term infants. There is a separate Cochrane review of this topic for term infants (McDonald 2008).
For developing countries, with limited resources and a high risk of transmitting infection through blood transfusion, the potential value of a reduced need for blood transfusion would be of particular interest. In more developed countries, 60% to 80% of preterm infants less than 32 completed weeks' gestation (Brune 2002; Ringer 1998) require transfusion, and strategies that might reduce this without risk would be desirable.
This review will be of interest to obstetricians, midwives, neonatologists as well as pregnant women and their partners.
To assess the short- and long-term effects of early rather than delayed clamping of the umbilical cord for births before 37 completed weeks' gestation. A secondary objective is to assess the effect of positioning the baby above or below the introitus at birth, and the effect of milking the umbilical cord.
Criteria for considering studies for this review
Types of studies
Randomised controlled trials including cluster-randomised trials. Quasi-randomised trials were not included.
Types of participants
Preterm infants born before 37 completed weeks' gestation and their mothers.
Types of interventions
Immediate cord clamping versus delayed clamping (after 30 seconds or more). This could be with or without oxytocin, with or without the baby held above or below the level of the placenta, and with or without milking of the cord towards the infant. In this version of the review we have also considered studies examining cord milking with clamping earlier than 30 seconds.
Types of outcome measures
For the baby
- Death of the baby: before discharge from hospital, after discharge from hospital, total.
- Death or neurosensory disability at age two to three years.
- Intraventricular haemorrhage (IVH) - ultrasound diagnosis grade three and four.
- Periventricular leukomalacia.
For the mother
- Postpartum haemorrhage (blood loss greater than 500 mL).
For the baby
Condition at birth
- Requirement for resuscitation.
- Apgar score at one, five and 10 minutes.
- Hypothermia during first hour of life or on admission to labour ward.
- Respiratory distress syndrome (assessed by clinical signs, oxygen requirement, respiratory support, chest x-ray) during first 36 hours of life.
- Use of exogenous surfactant.
- Days of oxygen dependency.
- Oxygen dependency at 28 days after birth.
- Oxygen dependency at equivalent of 36 completed weeks' gestational age.
- Chronic lung disease (Northway Stage two, three or four).
- Volume (colloid, sodium chloride 0.9%, blood transfusion) administration for hypotension during the first 24 hours of life.
- Inotropic support for hypotension during the first 24 hours of life.
- Treatment for patent ductus arteriosus.
- Anaemia, number or volume of blood transfusions.
- Treatment for hyperbilirubinaemia with phototherapy.
- Treatment for hyperbilirubinaemia with blood exchange transfusion.
- Blood counts at six and 12 months of age (haemoglobin and ferritin).
Central nervous system
- IVH all grades.
- Necrotising enterocolitis.
- Length of hospital stay.
For the mother
- Manual removal of the placenta.
- Effects on Rhesus-isoimmunisation.
- Psychological well-being.
- Bonding to the infant.
- Mother's views.
For the father
- Psychological well-being.
- Bonding to the infant.
- Father's views.
Search methods for identification of studies
We contacted the Trials Search Co-ordinator to search the Cochrane Pregnancy and Childbirth Group's Trials Register (31 May 2011). We updated this search on 26 June 2012 and added the results to Studies awaiting classification.
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:
- monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
- weekly searches of MEDLINE;
- weekly searches of EMBASE;
- handsearches of 30 journals and the proceedings of major conferences;
- weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts.
Details of the search strategies for CENTRAL, MEDLINE and EMBASE, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group.
Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co-ordinator searches the register for each review using the topic list rather than keywords.
We did not apply any language restrictions.
For details of additional searching carried out in the previous version of the review, please see Appendix 1.
Data collection and analysis
For the methods used to assess the trials identified in the previous version of this review, see Appendix 2.
For this update we used the following methods when assessing the trials identified by the updated search.
Selection of studies
Two review authors independently assessed for inclusion all the potential studies we identified as a result of the search strategy. We resolved any disagreement through discussion or, if required, we consulted the third review author.
Data extraction and management
We designed a form to extract data. For eligible studies, two review authors extracted the data using the agreed form. We resolved discrepancies through discussion or, if required, we consulted the third review author. We entered data into Review Manager software (RevMan 2011) and checked for accuracy.
When information regarding any of the above was unclear, we attempted to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We resolved any disagreement by discussion, or by involving a third assessor.
(1) Random sequence generation (checking for possible selection bias)
We have described for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We assessed the method as:
- low risk of bias (any truly random process, e.g. random number table; computer random number generator);
- high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number);
- unclear risk of bias.
(2) Allocation concealment (checking for possible selection bias)
We have described for each included study the method used to conceal allocation to interventions prior to assignment and have assessed whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We assessed the methods as:
- low risk of bias (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes);
- high risk of bias (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);
- unclear risk of bias.
(3) Blinding of participants and personnel (checking for possible performance and detection bias)
Blinding participants and staff to the types of interventions considered in this review may not be feasible, but it may be possible to blind outcome assessors for at least some of the outcomes reported. We have described for each included study the methods used, if any, to achieve blinding. We considered studies to be at low risk of bias if they were blinded, or if we judged that the lack of blinding would be unlikely to affect results.
We assessed the methods as:
- low, high or unclear risk of bias for participants;
- low, high or unclear risk of bias for personnel;
- low, high or unclear risk of bias for outcome assessors.
(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)
We have described for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We have stated whether attrition and exclusions were reported and 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 was reported, or was supplied by the trial authors, we re-included missing data in the analyses which we undertook.
We assessed methods as:
- low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);
- high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);
- unclear risk of bias.
(5) Selective reporting (checking for reporting bias)
We have described for each included study how we investigated the possibility of selective outcome reporting bias and what we found.
We assessed the methods as:
- low risk of bias (where it is clear that all of the study’s pre-specified outcomes and all expected outcomes of interest to the review have been reported);
- high risk of bias (where not all the study’s pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest are reported incompletely and so could not be used; study fails to include results of a key outcome that would have been expected to have been reported);
- unclear risk of bias.
(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)
We have described for each included study any important concerns we have about other possible sources of bias.
We assessed whether each study was free of other problems that could put it at risk of bias:
- low risk of other bias;
- high risk of other bias;
- unclear whether there is risk of other bias.
(7) Overall risk of bias
We have made explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we considered it was likely to impact on the findings. We explored the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous data, we have presented results as summary risk ratio with 95% confidence intervals.
For continuous data, we used the mean difference if outcomes were measured in the same way between trials. We used the standardised mean difference to combine trials that measured the same outcome, but used different methods.
Unit of analysis issues
Had we found any, we would have included cluster-randomised trials in the analyses along with individually-randomised trials. If in future updates we do include cluster-randomised trials, we will adjust their sample sizes using the methods described in the Handbook (Higgins 2011) using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster-randomised trials and individually-randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there was little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely. We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.
Due to the nature of the studied interventions cross-over designs are not possible.
Other unit of analysis issues
Other unit of analysis issues could include, e.g. multiple pregnancies or more than two treatment groups, which need specialist statistical analysis. However, these type of trials have, so far, not been reported for cord clamping interventions.
Dealing with missing data
For included studies, we noted levels of attrition. We had planned to explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis but levels of attrition in the included studies were generally low.
For all outcomes, we carried out analyses, as far as possible, on an intention-to-treat basis, i.e. we attempted to include all participants randomised to each group in the analyses, and all participants were analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial was the number randomised minus any participants whose outcomes were known to be missing.
Assessment of heterogeneity
We assessed statistical heterogeneity in each meta-analysis using the T², I² and Chi² statistics. We regarded heterogeneity as substantial if T² was greater than zero and either I² was greater than 30% or there was a low P value (less than 0.10) in the Chi² test for heterogeneity.
Assessment of reporting biases
Where there were 10 or more studies in the meta-analysis, we investigated reporting biases (such as publication bias) using funnel plots. We assessed funnel plot asymmetry visually, and where there appeared to be asymmetry we planned to use formal tests for funnel plot asymmetry. For continuous outcomes we planned to use the test proposed by Egger 1997, and for dichotomous outcomes the test proposed by Harbord 2006. If asymmetry was detected in any of these tests or was suggested by a visual assessment, we planned to perform exploratory analyses to investigate it. For most outcomes in this review too few studies contributed data to carry out this planned analyses.
For all meta-analyses we ordered studies according to weight so that we would be able to identify any obvious differences in effect associated with smaller studies.
We carried out statistical analysis using the Review Manager software (RevMan 2011). We used fixed-effect meta-analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect: i.e. where trials examined the same intervention, and the trials’ populations and methods were judged sufficiently similar. If we suspected clinical heterogeneity sufficient to expect that the underlying treatment effects would differ between trials, or if substantial statistical heterogeneity was detected, we planned to use random-effects meta-analysis to produce an overall summary if an average treatment effect across trials was considered clinically meaningful. In this version of the review we identified little statistical heterogeneity between studies.
Subgroup analysis and investigation of heterogeneity
We planned to carry out the following subgroup analyses.
- By position of the baby relative to the level of the placenta before cord clamping: below the level of the placenta; at the level of the placenta; above the level of the placenta; or position not known or unclear.
- By whether the woman was given oxytocin as a uterotonic drug before cord clamping: with oxytocin; no oxytocin before clamping; unclear or not known whether oxytocin given.
- By milking of the cord: with milking; without milking; unclear or not known whether milking.
- By route for birth: vaginal, abdominal, or mixed or not known.
- By gestational age at birth: less than 32 completed weeks' gestation, 32 or more completed weeks, gestation mixed or not known.
We planned to restrict subgroup analyses to the primary outcomes.
In this version of the review there was insufficient information in the trial reports to allow us to carry out planned subgroup analysis other than for cord milking. We assessed differences between subgroups by inspection of the subgroups’ confidence intervals with non-overlapping confidence intervals suggesting a statistically significant difference in treatment effect between the subgroups. Where sufficient data were available, we carried out more formal statistical tests to assess differences between subgroups by applying the interaction tests available in RevMan 2011.
We planned sensitivity analysis by study quality based on allocation concealment, excluding studies with high risk of bias or unclear risk of bias. We carried out this analysis for primary outcomes only.
Description of studies
Results of the search
From the May 2011 search, fifteen trials qualified for inclusion into this review. We excluded 10 studies (see Characteristics of excluded studies). We updated the search on 26 June 2012 and added the new reports to Studies awaiting classification.
See Characteristics of included studies for more detail of participants and interventions, such as gestational age, mode of delivery, positioning of the infant and length of cord clamping time.
The trials enrolled preterm babies between 24 and 36 weeks' gestation. For some studies the unit of randomisation was the baby, but for most mother-infant pairs were randomised. There was some inconsistency in both the intervention and the control procedures between studies and wide variation in outcome measures.
The women recruited into the trials were all expecting to deliver their infants prematurely. The infants in the studies by Kinmond 1993 and Ultee 2008 were all delivered vaginally, while those in the trial carried out by Nelle 1998 were delivered by caesarean section only. All other trials included women undergoing both methods of delivery.
At birth, blood flow in the umbilical arteries and veins usually continues for a few minutes. The additional blood volume transferred to the infant during this time is known as placental transfusion. The interventions in the review are aimed at modifying placental transfusion. For the analysis graphs where we have combined data across studies comparing a range of interventions, we have therefore used the terms 'more placental transfusion' and 'less placental transfusion'.
Interventions in the included studies were as follows.
Early cord clamping: the definition of early umbilical cord clamping was not clear in most studies except for McDonnell 1997 where the exact time to cord clamping in the immediate group was five seconds and in Ultee 2008 where the mean recorded time was 13.4 seconds. It seems likely that there is a time lag between delivery and cord clamping and that variation may be up to 10 seconds or more. In Rabe 2000, early cord clamping was defined as clamping at 20 seconds and there was no immediate clamped group for comparison. We have included this study in this review because we believe that there is close proximity to the immediate clamped groups, and that in clinical practice such delays may occur. Furthermore, it allows the review to focus on at least 20 seconds interval between early and late cord clamping.
Delayed cord clamping: the definition of delayed umbilical cord clamping varied between studies. McDonnell 1997 had a mean timed delay of 31 seconds, Rabe 2000 45 seconds, Hofmeyr 1988 and Hofmeyr 1993 60 and 120 seconds, Aladagandy 2006 and Baezinger 2007 60 to 90 seconds, Kugelman 2007, Mercer 2003 and Mercer 2006 30 to 45 seconds, and Strauss 2008 60 seconds. Ultee 2008 had the longest timing with 180 seconds, but in a study group of more mature preterm infants of 34 to 36 weeks' gestation. The exact time to clamping was not given in other studies, nor was there an adequate description of how the timing was done and by whom. The number of babies allocated to delayed cord clamping but in whom resuscitation was considered necessary before the allocated time is described in several studies. In Hofmeyr 1988 for example, eight of 24 babies in the delayed clamping group required earlier intervention.
Cord milking: this is a technique, sometimes called stripping the cord, in which the cord is pinched between the fingers and the hand then moved towards the baby before releasing the cord. The aim is to move blood towards the baby, so that blood transfers from the placental bed to the baby more quickly than occurs from just waiting before clamping the cord. Hosono 2008 describes the technique used in this study as: infants are placed at or below the level of the placenta. Approximately 20 cm of the umbilical cord is vigorously milked towards the umbilicus two or three times before clamping the cord. The speed of milking is approximately 20 cm per two seconds. This means that the baby might receive a bolus of blood in a short time period.
Position of the baby in relation to the placenta: the position in relation to the placenta or uterus varied between studies. It is accepted that positioning the baby below the placenta during caesarean section is difficult, and that for most studies the baby lies on the mother's thighs above the level of the uterus whilst waiting to clamp the umbilical cord. Most studies have positioned the baby at the level of the introitus for vaginal deliveries. Only in one study (Rabe 2000) was the baby kept at or more than 20 cm below the placenta. Subgroup analysis based on position of the baby in relation to the placenta has not therefore been possible. In one study (Ultee 2008), the baby was placed on the mother's abdomen in vaginally delivered infants.
Uterotonic drugs (Syntocinon or ergometrine): the use of pharmacologic stimulants to the uterus after delivery is not consistent between studies or is ill defined. However, Hofmeyr 1988 had shown that there is no significant difference in the two groups allocated to delayed umbilical cord clamping with or without ergometrine. We have therefore not attempted a subgroup analysis on this variable.
No two studies had the same outcome objectives and there were wide and varied definitions in the type of outcome measured. Similarly, the manner of reporting the same outcome varied between studies. We requested raw data from all authors in order to clarify issues and to improve our reporting for those outcomes that, a priori, we considered important. The authors of several studies have stated that they performed a pilot or feasibility study and these were powered to answer short-term specific questions only. In general, the studies that we included are not powered individually to answer the range of clinical questions that we feel are important in day-to-day neonatal practice.
Umbilical cord blood analysis
No study described how and when the cord blood was obtained (whether from placenta, cord, isolated segment, etc).
Subgroup analysis by position or effects on mothers and fathers was not possible in this version of the review due to lack of data. While two studies included only women undergoing vaginal deliveries (Kinmond 1993; Ultee 2008), we have not included results for subgroup analysis by mode of delivery as, either no data, or no estimable data were available for our primary outcomes. We carried out subgroup analysis by delayed cord clamping versus cord milking for out primary outcomes (comparison 2).
Risk of bias in included studies
Individual assessments of risk of bias for included studies are set out in the Characteristics of included studies tables. Overall summaries of assessments of bias in included studies are set out in Figure 1 and Figure 2, and are briefly described below.
|Figure 1. 'Risk of bias' graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.|
|Figure 2. 'Risk of bias' summary: review authors' judgements about each risk of bias item for each included study.|
The method used to generate the randomisation sequence in the included studies was generally not well described. Only three studies clearly described the method used to determine the sequence for group allocation: Mercer 2006 used a computer-generated method, Strauss 2008 a table of random numbers and Oh 2002 used an external randomisation service. In the remaining 12 studies the method used to generate the randomisation sequence was either not mentioned, or was not described in sufficient detail to allow us to judge risk of bias. In some studies the sample was stratified by factors such as gestational age or estimated birth weight (see Characteristics of included studies).
The methods used to conceal allocation at the point of randomisation were not that well described although only one study (Ultee 2008) described using methods that we judged were at high risk of bias. In this study, one of the staff providing care carried out randomisation and there were post randomisation exclusions if the baby had a low Apgar score at one or five minutes. In 12 of the studies there was insufficient information to allow us to judge whether or not methods were at low risk of bias.
For this type of intervention blinding participants and the staff present at delivery to group allocation is not possible. For outcome assessment it may be possible to blind assessors collecting data. We assessed all included studies at either high risk of bias or unclear for this domain. For some outcomes lack of blinding may be an important source of bias while the impact of lack on blinding on outcomes such as laboratory tests is less clear. We have noted in the Characteristics of included studies tables where investigators have attempted blinding of outcome assessors. None of the studies reported on the success of blinding.
Incomplete outcome data
Most of outcome data in included studies were collected soon after the birth, and loss to follow-up was not generally a problem. In three studies post randomisation exclusions or loss to follow-up meant that results were difficult to interpret and we assessed these studies as high risk of bias (Baezinger 2007; Strauss 2008; Ultee 2008). In eight of the studies all of the women randomised were accounted for in the analysis or there was minimal loss which was explained. In four of the studies there was insufficient information (for example, denominators were not provided in tables) to allow us to make a clear judgement about whether loss to follow-up or exclusions were likely to introduce bias.
For most of the included studies only published data were available to us, and we did not have access to trial registration reports or study protocols. Under these circumstances we were not able to assess whether authors had omitted to report findings for all of their pre-specified outcomes. We were not able to detect any clear instances of outcome reporting bias.
Other potential sources of bias
In most of the included studies there were no obvious other sources of bias, and in most cases there were descriptions of the characteristics of participants so that it was clear that there were no obvious baseline differences between groups. In Baezinger 2007 and Strauss 2008, the size of the intervention and control groups were uneven; in the study by Hofmeyr 1988 there were baseline differences in the condition of infants and this made results more difficult to interpret; the Kinmond 1993 study was terminated early and there was a chance excess of boys in the intervention group (13/17) compared with controls (7/19); McDonnell 1997 also reported that there was imbalance for infant sex. The study by Nelle 1998 was reported in a brief abstract with little information on study methods and this meant that the overall risk of bias was unclear.
Effects of interventions
We included 15 studies involving 738 infants (data from several studies were reported in more than one publication).
(a) Delayed (more placental transfusion) versus immediate (less placental transfusion) cord clamping: 15 studies, 738 infants
For the baby
Death of the baby
Thirteen of the included studies with a total of 668 infants reported infant death (largely death before discharge from hospital), and overall there were 27 deaths. In the group allocated more placental transfusion 3.1% (10/319) babies died before hospital discharge compared with 4.9% (17/349) of those allocated less placental transfusion (unweighted percentages), there was no clear difference between groups in the risk of death (risk ratio (RR) 0.63, 95% confidence interval (CI) 0.31 to 1.28) ( Analysis 1.1) We did not identify statistical heterogeneity or find evidence of funnel plot asymmetry for this outcome (Figure 3).
|Figure 3. Funnel plot of comparison: 1 More placental transfusion (delayed clamping) versus less placental transfusion (early clamping), outcome: 1.1 Infant death (up to discharge/variable).|
Death or neurosensory disability at age two to three years
No trials reported these outcomes at age two to three years. One trial (Mercer 2006) reported outcomes after discharge from hospital: neurodevelopmental outcome at a median age of seven months. Of the 72 children recruited, five died before seven months. Of the 67 survivors, nine were lost to follow-up. Fifty-eight children were assessed at age seven months (corrected for gestation at birth). There were no significant differences between the groups in the Bayley II mean scores for Mental Development Index and Psychomotor Developmental Index (data not shown).
Intraventricular haemorrhage (IVH)- ultrasound diagnosis grade three and four
Severe IVH (grade three and four) was reported in six trials ( Analysis 1.2). There were 12 events in 305 babies (5/154 versus 7/151) with a RR of 0.68 (95% CI 0.23 to1.96) for babies allocated more placental transfusion rather than less placental transfusion.
Only two studies (71 infants) ( Analysis 1.3) reported periventricular leukomalacia; overall, there were three events which is insufficient evidence for any reliable conclusions (RR 1.02, 95% CI 0.19 to 5.56).
For the mother
Postpartum haemorrhage (blood loss greater than 500 mL)
None of the included studies reported results for this outcome.
For the baby
Apgar score at one, five and 10 minutes
Mean Apgar scores were reported at one minute (three trials, 184 infants, mean difference (MD) (random-effects) 0.30, 95% CI -0.52 to 1.12) ( Analysis 1.4); five minutes (three trials, 184 infants MD 0.12, 95% CI -0.20 to 0.43) ( Analysis 1.5); and 10 minutes (one trial, 39 infants, MD 0.00, 95% CI -1.05 to 1.05) ( Analysis 1.6). There were no clear differences between groups at any of these time points. There was no statistically significant difference between the groups in Apgar scores less than eight at five minutes (three trials, 161 infants, RR 0.86, 95% CI 0.45 to 1.62) ( Analysis 1.7).
Hypothermia during first hour of life, on admission to special care unit or in delivery room
None of the studies reported on hypothermia in the delivery room. Three studies (143 infants) ( Analysis 1.8) reported mean infant temperature on admission to special care unit; there was no clear difference between the groups (MD 0.14, 95% CI -0.03, to 0.31).
Respiratory distress syndrome
Respiratory distress syndrome was reported by three small studies (total 115 babies). There was no clear difference between the two groups (RR 1.16, 95% CI 0.89 to 1.50) ( Analysis 1.9). Only one trial (39 infants) reported results for severe respiratory distress and this study was too small for any reliable conclusions about the difference between the two groups (RR 0.79, 95% CI 0.20 to 3.07) ( Analysis 1.10).
Other respiratory outcomes
Use of surfactant was reported in two trials with 85 infants ( Analysis 1.11); there was no clear difference between the groups (RR 1.28, 95% CI 0.56 to 2.93). Despite difficulties with definitions, five trials involving 265 infants reported ventilation for some form of respiratory distress (RR 0.97, 95% CI 0.71 to 1.31) ( Analysis 1.12).
Need for oxygen at 28 days after birth was reported by two trials (76 infants) ( Analysis 1.13), and there was no clear difference between the groups (RR 0.48, 95% CI 0.15 to 1.59). Need for oxygen at 36 weeks' gestational age was reported by five trials (209 infants); there was also no clear difference between the groups (RR 0.69, 95% CI 0.42 to 1.13) ( Analysis 1.14).
The number of infants with chronic lung disease (Northway Stage two, three or four) was not reported in any of the included studies.
Infants allocated to more placental transfusion were less likely to need transfusion for low blood pressure after birth although the difference between groups did not reach statistical significance. There was moderate heterogeneity for this outcome (I² = 33%) so we used a random-effects model and results represent the average treatment effect (four trials, 130 infants, RR 0.52, 95% CI 0.24 to 1.11) ( Analysis 1.15). The mean arterial blood pressure was significantly higher in those allocated more placental transfusion, both at birth (two trials, 97 infants, MD 3.52, 95% CI 0.60 to 6.45) ( Analysis 1.16) and at age four hours (two trials, 111 infants, MD 2.49, 95% CI 0.26 to 4.72) ( Analysis 1.17), but at 24 hours of age the arterial blood pressure is reported by just one trial (38 infants) ( Analysis 1.18).
Need for inotropic support
Overall, infants in the delayed clamping group had significantly less need for inotropic support (RR 0.42, 95% CI 0.23 to 0.77) ( Analysis 1.19).
Treatment for patent ductus arteriosus
There was no clear difference between the groups in respect of treatment for patent ductus arteriosus (five trials, 223 infants, RR 1.04, 95% CI 0.60 to 1.81) ( Analysis 1.20).
Central nervous system
IVH all grades
IVH is a risk factor for adverse developmental outcome. However, this risk is largely associated with severe IVH (grade 3 or 4) which is a primary outcome for this review. Ten trials (539 infants) reported IVH (all grades). Allocation to more placental transfusion was associated with a lower risk ratio for IVH (all grades) (RR 0.59, 95% CI 0.41 to 0.85). There was no evidence of statistical heterogeneity or funnel plot asymmetry for this outcome ( Analysis 1.21; Figure 4).
|Figure 4. Funnel plot of comparison: 1 More placental transfusion (delayed clamping) versus less placental transfusion (early clamping), outcome: 1.21 Intraventricular haemorrhage (all grades).|
Necrotising enterocolitis was reported in five trials with a lower risk associated with more placental transfusion (241 infants, RR 0.62, 95% CI 0.43 to 0.90) ( Analysis 1.22).
Anaemia, number or volume of blood transfusions
Seven studies (392 infants) reported the number of infants requiring blood transfusion for anaemia. Overall 24% (44/186) of those allocated more placental transfusion had blood transfusion for anaemia compared with 36% (5/206) of those allocated less placental transfusion, giving a RR for this reduction of 0.61 (95% CI 0.46 to 0.81) ( Analysis 1.23). There was also a reduction in the overall number of blood transfusions given in the delayed clamping group (five trials, 210 infants, MD -1.26, 95% CI -1.87 to -0.64; Analysis 1.24).
The peak bilirubin concentration was higher for infants allocated more placental transfusion rather than less placental transfusion (seven trials, 320 infants, MD 15.01 mmol/L, 95% CI 5.62 to 24.40) ( Analysis 1.25). One small trial (35 infants) reported red cell mass after birth, which are insufficient data for reliable conclusions.
The bilirubin level above which treatment was started is likely to differ between centres, and the criteria for treating hyperbilirubinaemia in each study were not stated. However, treatment (phototherapy) was reported by three studies (180 infants, RR 1.21, 95% CI 0.94 to 1.55) ( Analysis 1.26) with no significant difference between the groups, although there was a non-significant trend towards more phototherapy for infants allocated more placental transfusion. Data on exchange transfusion were not reported by any of the studies.
Other pre-specified secondary outcomes including blood counts at six and 12 months of age (haemoglobin and ferritin) were not reported.
One study (Baezinger 2007) reported mean regional tissue oxygenation of the brain at four hours (39 infants, MD 6.44, 95% CI 5.47 to 7.41) ( Analysis 1.24) and 24 hours of age (39 infants, MD 4.29 95% CI 3.44 to 5.14) ( Analysis 1.28) with statistically significantly higher values for the delayed cord clamping group.
There was an increase in haematocrit MD at birth or one hour (seven trials, 318 infants, MD 3.26%, 95% CI 1.79 to 4.74) ( Analysis 1.29), haematocrit at four hours (five trials, 173 infants, MD 5.40%, 95% CI 3.62 to 7.17) ( Analysis 1.30) and haematocrit at 24 hours (three trials, 199 infants, MD 3.28%. 95% CI 1.34 to 5.22) ( Analysis 1.31). Two trials (81 infants) reported blood volume after birth (MD 8.41, 95% CI 2.14 to 14.67) ( Analysis 1.32). The results in these two trials varied and we used a random-effects model for this outcome. A further post-hoc analysis to include sepsis as an outcome was generated by Mercer 2006. This outcome was reported by two trials (137 infants, average RR 0.34, 95% CI 0.05 to 2.11) ( Analysis 1.34).
There was no evidence of a difference between groups for the number of babies with retinopathy of prematurity (reported in one study) ( Analysis 1.35). Mean cord pH was examined in three studies and there was no significant difference between groups ( Analysis 1.36). Mean length of stay in hospital was reported in only one of the included studies, and although it was reduced in the delayed cord clamping group the difference between groups was not statistically significant ( Analysis 1.37).
For the mother
None of the included studies reported results for any of our secondary outcomes for mothers (death; manual removal of the placenta; psychological well-being, anxiety, maternal views, bonding with the infant or effects of rhesus-iso-immunisation).
For the father
None of the included studies reported results for any of our secondary outcomes for fathers (psychological well-being, anxiety, fathers' views or bonding with the infant).
Subgroup analysis: delayed cord clamping versus cord milking
Only one trial (with 40 infants) evaluated cord milking, all the remaining trials evaluated delayed cord clamping. We found no clear evidence of differences between these subgroups in the effects on the primary outcomes ( Analysis 2.1; Analysis 2.2; Analysis 2.3).
For our primary outcomes we carried out sensitivity analysis separating studies where risk of bias associated with allocation concealment was low, or unclear/high. This did not alter the interpretation of results ( Analysis 3.1; Analysis 3.2; Analysis 3.3).
Summary of main results
This updated review now includes data from 15 trials involving more than 700 mother and baby pairs. Most trials compared alternative timings for cord clamping. For the three primary outcomes of infant death, severe intraventricular haemorrhage, and periventricular leukomalacia the confidence intervals for the risk ratio are wide and so there is insufficient evidence for reliable conclusions about the differential effects of these alternative policies for care at birth. No study has yet reported the fourth primary outcome of neurodevelopment at age two to three years.
More placental transfusion, rather than less placental transfusion, is associated with fewer blood transfusions for anaemia and for low blood pressure. More placental transfusion also appears to protect against intraventricular haemorrhage (all grades), although the clinical significance of this is unclear as there are too few data for any reliable conclusions about the comparative effect on severe intraventricular haemorrhage (grades three or four) and no trials have assessed neurodevelopment of the children at age two to three years. Necrotising enterocolitis and sepsis also appear to be reduced, but these outcomes are only reported for a limited number of studies in the review. There is no clear difference in the effect on Apgar scores, or temperature on admission to special care unit; although again, these outcomes were not reported for all trials.
Overall, even when taking all trial results together, most outcomes had wide confidence intervals and so results should be interpreted with caution. Nevertheless, later umbilical cord clamping to allow more placental transfusion at preterm birth appears to be associated with a reduction in the risk ratio of intraventricular haemorrhage (all grades) and the need for transfusion, either for anaemia or for low blood pressure and less risk for necrotising enterocolitis. These effects may be related to an improvement in the circulating neonatal blood volume, and better control of blood pressure, following greater placental transfusion.
Surprisingly, as one of the rationales for early clamping is to allow the infant to be transferred to a resuscitaire for respiratory support, there are few data on respiratory outcomes. No study reported on spontaneous onset of respiration. A clinical concern about delayed umbilical cord clamping is the potential for the baby to get cold and develop hypothermia. This did not occur in the three trials that report temperature and there is no clear evidence that Apgar scores are significantly different.
One small study has evaluated milking of the cord (Hosono 2008) which reports positive effects on haemoglobin after birth, better blood pressure and less need for donor blood transfusion. It is too early to say whether this method would be better compared with delaying cord clamping, even though some obstetricians and midwives might prefer it. Future large studies could compare the various methods of achieving placental transfusion such as delayed cord clamping and milking of the cord.
Overall completeness and applicability of evidence
There are several ways to potentially influence placental transfusion for preterm births. We have reflected this in our review by broadened the types of intervention to include any strategy that might influence placental transfusion.These strategies include early or delayed cord clamping, using gravity to assist placental transfusion by lowering the baby below the introitus or the level of the placenta, clamping the cord as close as possible to the placenta and then after cutting the cord allowing the residual blood in the cord to drain into the baby, and milking of the cord. Nevertheless, timing of cord clamping remains the most widely evaluated intervention, with all but one study comparing alternative timings for cord clamping. There were insufficient data for subgroup analysis - with no data on optimal positioning of the infant, oxytocics to the mother and combinations of these with a timing of cord clamping.
There are issues with interpreting death as an outcome in some of the trials. Variations in clinical practice over time have substantially influenced the risk of death following preterm birth. These background variations in clinical practice may influence the risk of death more than any change in placental transfusion. The five neonatal deaths in Hofmeyr's study (Hofmeyr 1988), for example, are quoted as being "< 1300 g birthweight". This study was performed in the late eighties in South Africa, where access to ventilatory support for very preterm infants would have been, and still is, limited. In more recent years, and in most intensive care units in high-income countries, ventilatory support for these babies would have been offered. In the Hofmeyr 1988 study it is not clear whether ventilation was possible for these babies, but a comment in the report suggests that survival at this low birthweight was more the exception than the rule. Similarly, there is a high incidence of intraventricular haemorrhage in Hofmeyr 1988 and Hofmeyr 1993), both studies conducted in South Africa. The other studies conducted in high-income countries have a lower incidence of intraventricular haemorrhage, and therefore less power to demonstrate any clinically important effects on this risk.
The ideal volume and duration of placental transfusion is not known. Most attention has focused on the volume of placental transfusion, but duration may also be important. This seems particularly important to assess for preterm births allowing longer for placental transfusion may facilitate the immature infant making the transition from fetal circulation to neonatal circulation.
Quality of the evidence
The trials included in this review were largely of unclear risk of bias. Only three studies were low risk for sequence generation, and two were low risk for concealment of allocation. No studies were low risk for all assessments of quality, and eight trials were at high risk of bias for at least one assessment.
No outcome in this review was reported by all included studies. The most complete reporting was for death of the baby (reported by 13 trials with 668 infants) and intraventricular haemorrhage (all grades) (reported by 10 trials with 559 infants). Of the remaining 35 outcomes, 23 were reported by a maximum of three trials. Although it was not possible to check the protocols for these trials, selective reporting is a concern.
Potential biases in the review process
We are aware of potential biases in the reviewing process; and we took some steps to minimise bias (such as data extraction which was carried out by two review authors independently).
Agreements and disagreements with other studies or reviews
We are not aware of other reviews.
Implications for practice
More, rather than less, placental transfusion will increase the neonatal blood volume at birth. This review suggests the increased circulating volume improves blood pressure, reduces the need for blood transfusion, risk of intraventricular haemorrhage and necrotising enterocolitis. The effects on the important primary outcomes for this review are unclear. Disability-free survival is a key concern for children born preterm, and long-term follow-up for children recruited to these trials is needed to provide a reliable basis for recommendations about clinical practice.
Based on the available data, the European consensus guidelines on resuscitation of the preterm infant have recommended a slight delay of 30 to 45 seconds before clamping the umbilical cord to facilitate placento-fetal transfusion (Sweet 2010).
Implications for research
The review suggests potential benefit for strategies to allow more placental transfusion, rather than less placental transfusion. However, studies to date are small, have some risk of bias, are often imprecise in defining outcomes, do not report data for all important outcomes, and lack long-term follow-up with neurodevelopmental assessments. To reliably compare strategies for influencing placental transfusion, we need large high-quality trials, with sufficient power to reliably assess clinically relevant differences in important outcomes.
Larger multicentre studies are essential and demand international collaboration to provide a scientific rationale for improving the delivery and resuscitation of the preterm infant. Future studies should include more data on respiratory outcomes, especially on onset of spontaneous breathing of the preterm baby and on long-term neurodevelopmental outcome at two years of age. They should also report treatment details and outcomes for the mother.
Graham Reynolds for his editorial and clinical contributions to this update.
W Oh, M McDonnell, M Nelle, S Kinmond, J Mercer, N Aladangady and H Rabe who kindly provided additional information regarding their studies. The information about randomisation for the trials by W Oh and M Nelle was directly obtained from the authors. The review authors thank the authors for supplying the information.
As part of the pre-publication editorial process, this review has been commented on by three peers (an editor and two referees who are external to the editorial team), a member of the Pregnancy and Childbirth Group's international panel of consumers and the Group's Statistical Adviser.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Differences between protocol and review
- Index terms
Appendix 1. Additional searching carried out in previous versions of the review
Authors searched the Cochrane Neonatal Group Trials Register (16 January 2008), the Cochrane Central Register of Controlled Trials (The Cochrane Library 2007, Issue 4), PubMed (1966 to 16 January 2008) and EMBASE (1974 to 16 January 2008) using the following terms:
umbilical-cord AND clamp* AND (preterm OR premature OR infant, premature).
Appendix 2. Methods used to assess trials included in previous versions of this review
We used the methods described in the Cochrane Reviewers' Handbook (Clarke 1999). In addition, we assessed the methodological quality of each study in terms of selection, performance, attrition and detection as described by the Neonatal Review Group. See Review Group's details for more information. This includes the independent evaluation of each trial by all reviewers.
Three reviewers extracted data independently using previously prepared data extraction forms. We resolved any discrepancies by discussion. Whenever the disagreement could not be resolved by consensus, the trial was referenced as one that is awaiting assessment until additional information is obtained. We extracted data presented in graphs and figures whenever possible, but were only included if three reviewers independently had the same results. We double-checked all data for discrepancies. We requested additional data from the authors of each trial. Authors provided additional data for seven trials (Aladagandy 2006; McDonnell 1997; Mercer 2003; Mercer 2006; Nelle 1998; Oh 2002; Rabe 2000). We entered data into the Review Manager software developed by The Cochrane Collaboration (RevMan 2003).
The statistical methods used were as follows:
(1) Analysis: We described adverse outcomes as adverse event rates (AER) and relative risk (RR), the ratio of adverse events in the treated and control groups. For measures of treatment effect we gave RR, relative risk reduction (1-RR), risk difference and number needed to treat (1/RD). For continuous data, we used mean and standard deviations with reference to the original data if necessary. We calculated weighted mean difference (WMD) where appropriate. For the WMD, the weight given to each study (i.e. how much influence each study has on the overall results of the meta-analysis) as determined by the precision of its estimate of effect which in the Review Manager statistical software is equal to the inverse of the variance. This method assumes that all of the trials have measured the outcome on the same scale.
(2) Heterogeneity: We tested clinically and statistically important heterogeneity at the P < 0.05 level and used subgroup analysis to explain heterogeneous data if possible.
(3) We specified subgroup analysis before review.
Last assessed as up-to-date: 1 November 2011.
Protocol first published: Issue 3, 2001
Review first published: Issue 4, 2004
Contributions of authors
Graham Reynolds (GR) prepared the first draft of the protocol and commented on the second draft. Heike Rabe (HR) commented on the first draft of the protocol and wrote the second draft.
All review authors assessed studies independently. HR did not assess her own study. HR and GR entered study data. GR wrote the 'Methodological quality of included studies' section. HR completed all other sections of the review. JL Diaz-Rossello (JDR) completed the corrections to the statistics. All three review authors commented on the review and agreed on the conclusion.
For the update of this review the process of assessing the eligible studies and extracting the data were followed in the same way as described as above. HR updated the data tables and updated the text of the review. JDR and Therese Dowswell (TD) corrected the statistics. TD and Lelia Duley introduced the risk of bias tables, and revised the text of the review. All review authors agreed on the updated version of the review.
Declarations of interest
Studies by the contact author, which may be relevant for inclusion in this review, were not assessed by herself but by the co-authors who, in agreement with the Cochrane Pregnancy and Childbirth group, have named other experts in the field for this purpose. Lelia Duley was previously editor for this review, and currently holds a research grant which includes conducting a pilot randomised trial comparing deferred cord clamping with immediate cord clamping for births before 32 weeks' gestation. Graham Reynolds holds a research grant for a large multicentre trial to study ways to promote placental transfusion in preterm infants.
Differences between protocol and review
Some intended subgroup analysis could not be performed due to lack of suitable data.
The title of the previously published protocol was 'Early versus delayed cord clamping in preterm infants'.
Medical Subject Headings (MeSH)
*Premature Birth; *Umbilical Cord; Blood Transfusion [utilization]; Cerebral Hemorrhage [prevention & control]; Hematocrit; Infant, Newborn; Infant, Premature [blood]; Ligation [standards]; Placental Circulation [*physiology]; Randomized Controlled Trials as Topic; Respiration Disorders; Time Factors
MeSH check words
Female; Humans; Pregnancy
* Indicates the major publication for the study