Infant pacifiers for reduction in risk of sudden infant death syndrome

  • Protocol
  • Intervention


  • Kim Psaila,

    Corresponding author
    1. University of Western Sydney, College of Health and Science, CHoRUS Project, Family and Community Health Research Group, School of Nursing and Midwifery, Penrith South DC, NSW, Australia
    • Kim Psaila, CHoRUS Project, Family and Community Health Research Group, School of Nursing and Midwifery, University of Western Sydney, College of Health and Science, Locked Bag 1797, Penrith South DC, NSW, 1797, Australia.

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  • Jann P Foster,

    1. University of Western Sydney, School of Nursing & Midwifery, Sydney, NSW, Australia
    2. University of Sydney, Central Clinical School, Discipline of Obstetrics, Gynaecology and Neonatology, Sydney Medical School/Sydney Nursing School, Sydney, NSW, Australia
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  • Neil Pulbrook,

    1. Liverpool Hospital, Newborn Care, Liverpool, Australia
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  • Heather E Jeffery

    1. University of Sydney, Sydney School of Public Health, Sydney, NSW, Australia
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This is the protocol for a review and there is no abstract. The objectives are as follows:

To determine whether the use of pacifiers during sleep versus no pacifier during sleep reduces the risk of SIDS.

We will undertake the following subgroup analyses:

1. postmenstrual age (infants less than 28 weeks; 28 to 32 weeks; 32 to 37 weeks of age);

2. exclusively breast-fed; not exclusively breast-fed infants.


Description of the condition

Sudden infant death syndrome (SIDS) has been most recently defined as the sudden unexpected death of an infant less than 1 year of age, with onset of the fatal episode apparently occurring during sleep, that remains unexplained after a thorough investigation, including the performance of a complete autopsy and a review of the circumstances of death and clinical history (Krous 2004). The incidence of SIDS has varied over time, and between nations. For example, the incidence of SIDS per 1000 live births in 2004 in the Netherlands was 0.09, in Japan 0.19, in Canada 0.24, in England and Wales 0.32, in the USA 0.55, in Argentina 0.47 and in Australia 0.22 (Hauck 2009). According to Australian Social Trends 2007 statistics, death from SIDS in Australia between 1985 and 2005 declined by 83%, from 523 deaths in 1985 to 87 in 2005 (Linacre 2007). Of the 297,900 births in Australia in 2010, 81 cases of SIDS were reported (SIDS 2012). This decline is strongly associated with a public health campaign launched by SIDS and Kids, formerly the National SIDS Council of Australia (Linacre 2007). However, there has been no similar reduction in the rate of SIDS among Aboriginal and Torres Strait Islander (ATSI) infants. Between 2002 and 2006, infants from an ATSI background were five times more likely to die from SIDS than non-indigenous infants (AHMAC 2008).

Despite the success of several prevention campaigns, SIDS remains a leading cause of infant mortality. Deaths classified as SIDS occur unexpectedly from birth to 1 year of age, but predominantly occur between one and four months of age (Page 2000). Reported risk factors for SIDS include male sex, preterm birth, low birth weight, poor prenatal medical care, low socioeconomic status of the family, young age of parents, parental low educational level, short periods between pregnancies, multiple pregnancy, drug intake by pregnant woman, winter months, prone sleeping, bed sharing, exposure to cigarette smoke during pregnancy and after birth, overheating, head covering and infection (Harper 2000). Despite the identification of major risk factors that increase an infant’s chance of dying of SIDS, the underlying mechanism by which infants die still remains unknown.

Read 1984 first suggested a model for SIDS, consisting of the vulnerable infant (prematurity, state of arousal), subtle neurological impairment (in pregnancy) and an external precipitating factor, to provide a research framework for use with the then key known risk factors. A variety of theories relating to the mechanisms by which SIDS occurs have been proposed, including: airway obstruction during sleep and the subsequent re-breathing of expired gases on arousal leading to hypoxic coma (Kahn 2003); undiagnosed infections and genetic abnormalities (Panigrahy 2000; Opdal 2004 ) that may affect brainstem-mediated control of respiratory and autonomic function (Hunt 2005; Weese-Mayer 2008); and cardiac arrhythmia and genetic disorders such as cardiac ion channel mutations (Klaver 2011). Other genetic factors such as immunologic polymorphisms, and autonomic and metabolic disorders have been identified (Klaver 2011). It has been hypothesised that pregnancy-related factors, such as low birth weight, preterm birth and maternal smoking, may alter cardiovascular function and control of autonomic, behavioural and homeostatic function in the infant (Schellscheidt 1998; Cohen 2009; Cohen 2010; Franco 2010). The effect of genetic or pregnancy-related factors causes the failure of normal ‘protective’ reflexes during normal stresses that may occur in sleep (Malloy 2004). More recently, Filiano 1994 proposed a ‘triple risk model', that describes SIDS as an event that results from the intersection of three factors: (1) a vulnerable infant; (2) a critical development period in homeostatic control (age related); and (3) an exogenous stressor.

Few theories have been tested. One that has is the role of gastro-oesophageal reflux, which can be a major cause of cardiorespiratory events in early postnatal life, especially via the triggering of the laryngeal chemoreflex (LCR). Response to LCR stimulation in mature infants and adults results in short apnoea, laryngeal closure, expiratory reflex, cough and swallowing, as well as arousal if it occurs during sleep. In contrast, an immature response to LCR results in life-threatening apnoeas, bradycardias and oxygen desaturation. These have been observed in many mammalian species, especially in preterm newborn infants, the reflex becoming rapidly attenuated with postnatal age. Studies in human infants and piglets have suggested that the coexistence of reflux to the level of the pharynx during sleep, together with impaired swallowing, depressed arousal or both, is one mechanism that may lead to an age-limited, sudden and fatal apnoea (Jeffery 1995). Hence, the occurrence of gastro-oesophageal reflux to the level of the pharynx during sleep, an infrequent event that is usually innocuous, could be converted to a fatal event if swallowing is impaired and arousal depressed by a variety of mediating factors such as prone sleeping, preterm birth, sedatives, seizures or upper respiratory tract infections (Jeffery 1999; Page 2000; McKevey 2001) The LCR is both sleep and age related (vulnerable infant), and apnoea may be worsened by hypoxia or infection (neurological impairment) and any external factor that decreases airway protection by reducing swallowing or arousal. Other researchers have suggested that the LCR does not cause SIDS as such, but acts as a trigger, perhaps as a component of the ‘triple risk model', ultimately leading to death if the multiple recovery mechanisms, such as arousal and anoxic gasping, fail (Marom 2012).

Description of the intervention

A pacifier or dummy is a device that is placed in the mouth to stimulate non-nutritive sucking behaviour. Non-nutritive sucking is considered a natural reflex to satisfy a child’s need for contact and may include unrestricted sucking on a breast, digit, pacifier or other object (Pinelli 2005). A pacifier is usually similar in material and shape to a feeding teat and is attached to a broad flat disc of plastic that covers the child's mouth to prevent ingestion (Schwartz 2008).

Worldwide pacifier use in early childhood is very common, especially in developing countries, where mothers believe pacifier use satisfies their infants' natural need to suck (Moimaz 2008). Use of pacifiers in developing countries is controversial due to conflicting evidence regarding the potential for increased infantile infection (Rossit 2007; Alrifai 2010). Historically, the pacifier has been used to soothe or calm a distressed infant or to prevent an infant sucking on hands. Pacifiers are used for other purposes, such as non-nutritive sucking for the management of painful procedures (Stevens 2009). A Cochrane review (Pillai Riddell 2011) found non-nutritive sucking to be effective for both pain re-activity and pain-related regulation in neonates and preterm infants.

More recently, pacifier use has been proposed as a protective intervention for SIDS (Schwartz 2008). However, the most recent American Academy of Pediatrics guidelines recommend that pacifiers should not be used until the child is approximately three to four weeks old when, presumably, breast-feeding would be well established (Moon 2012). This recommendation was made in light of the primary argument against the use of pacifiers, relating to the claim that pacifier use is linked to early weaning of breastfeeding (Jenik 2009). However, a recent Cochrane review concluded that pacifier use before or after breastfeeding was established did not significantly affect the prevalence or duration of exclusive and partial breastfeeding up to four months of age (Jaafar 2011).

Six case-control studies (Mitchell 1993; Arnestad 1997; L'Hoir 1998; Fleming 1999; Li 2006; Moon 2012) and a systematic review (Hauck 2006) have found a relationship between pacifier use and a reduction in SIDS. Epidemiological studies have shown that infants that died of SIDS used a pacifier for the last period of sleep significantly less often than control infants (Fleming 1999; Hauck 2006).

Adverse effects reported from prolonged pacifier use include recurrent acute otitis media, gastrointestinal infections (Hauck 2005; Marter 2007; Jenik 2009) and oral candidiasis (Darwazeh 1995).

How the intervention might work

Significant debate has been generated around the use of pacifiers by infants, particularly when pacifiers are given to the infant prior to sleeping, and the role that this plays in the prevention of SIDS. There have been a number of theories put forward to explain why pacifiers may reduce SIDS. The use of a pacifier may result in improved autonomic control of breathing and cardiovascular stability, may maintain airway patency in infants during sleep in the first year of life, or both (Franco 2004). An alternative hypothesis is the possibility that the infant’s sleeping environment is altered by the pacifiers’ external handle, which may in turn change the configuration of the airway passage around the area of the mouth and nose. The altered airway passage could help prevent accidental hypoxia resulting from, for example, smothering by a blanket or soft bedding (Li 2006). The pacifier may also prevent the infant from rolling into the prone position (Franco 2004). A case-control study showed that sucking a pacifier enhanced neural pathway development, which controls the patency around the upper airway (Li 2006). The sensory input from the pacifier is important for upper airway muscle tone in the infant, which helps maintain upper airway patency by keeping the tongue forward via its active protrusion (Mitchell 1993; Weiss 2001).

In infants, several arousal states are usually recognized: (a) active sleep (rapid eye-movement sleep, REM); (b) quiet sleep (non-REM, NREM, or slow-wave sleep); (c) indeterminate sleep; and (d) waking (sometimes separated into crying, active and quiet) (Read 1984). The rate, depth and regularity of breathing in infants is closely related to behavioural state (Read 1984). Read 1984 proposed that various breathing patterns may reflect altered central-nervous-system activity. Breathing is regular in quiet sleep and irregular in active sleep. The rate and depth cycles are of larger amplitude and are in-phase, leading to marked swings in minute ventilation in active sleep. Infants have small oxygen stores in their lungs in relation to their metabolic oxygen consumption, resulting in an instability in arterial oxygen tension. Further instability would be expected in active sleep, since lung volume is reduced and metabolic rate is increased (Read 1984). Jeffery 1991 found oesophageal pH readings to be stable, between pH 5 and 7, in preterm infants during quiet sleep, whereas in active sleep, reflux occurred, with a significant decrease in oesophageal pH. A study of term infants at 10 weeks of age showed these infants as having increased cardiac sympathovagal balance during sucking sleep periods, whereas lower sympathetic activity together with high parasympathetic tone were associated with non-sucking sleep periods (Franco 2004; Horne 2010).

Defects in normal arousal mechanisms have long been theorised to cause SIDS, and gene mutations affecting the development of the autonomic nervous system appear in as many as 15% of cases (Weese-Mayer 2004). Pacifier use possibly creates a lower arousal threshold in infants, which may result in increased sensitivity to critical situations such as cardiac arrhythmia, obstructive apnoea or external conditions leading to asphyxia or hypoxia (Franco 2000).

Even if the pacifier becomes dislodged from the mouth as the infant falls asleep, habitual use of the pacifier appears to still protect against SIDS. The reason for this remains unclear and more research is needed in this area (Franco 2001; Hanzer 2010).

However, several authors have reported a link between sleep states, movement, and the incidence and duration of gastro-oesophageal reflux episodes (Jeffery 1983; Kahn 1990). Infants reportedly experience increased incidence and longer duration of gastro-oesophageal reflux during states of wakefulness and active sleep as opposed to quiet sleep (Jeffery 1991). Reflexes that protect the airway against aspiration and provide respiratory defence against asphyxia are also depressed in active sleep compared with quiet sleep (Jeffery 1991). A theory that the decrease in SIDS among non-nutritive sucking infants is due to its effect in decreasing the rate of gastro-oesophageal reflux disease has been put forward (Mitchell 1993; Mitchell 2009); the mechanism being that use of pacifiers allows for non-nutritive sucking during sleep, which potentially helps acid neutralisation by increasing sucking and swallowing, and therefore assisting the clearance of refluxed gastric contents (Page 2000; Hanzer 2010; Jeffery 1991). This may contribute to a protective effect of pacifiers against SIDS. However, Page 2000 noted different responses to acid gastro-oesophageal reflux between term and preterm infants. Similar to the response to acid gastro-oesophageal reflux found in the adult, the term infant responded with increased swallowing that in turn led to increased primary peristalsis. However, preterm infants did not increase pharyngeal swallowing, but rather increased propagated peristalsis. Both responses, however, help clear acid reflux.

Why it is important to do this review

This review will examine the current evidence for the use of pacifiers to reduce SIDS. Outcomes of this review will provide guidance to professionals and parents as to whether to offer pacifiers to infants. Pacifier use is a non-invasive, cost-effective intervention that has the potential to reduce the risk of SIDS.


To determine whether the use of pacifiers during sleep versus no pacifier during sleep reduces the risk of SIDS.

We will undertake the following subgroup analyses:

1. postmenstrual age (infants less than 28 weeks; 28 to 32 weeks; 32 to 37 weeks of age);

2. exclusively breast-fed; not exclusively breast-fed infants.


Criteria for considering studies for this review

Types of studies

We will consider all published and unpublished randomised and quasirandomised controlled trials (RCTs). Cluster randomised trials will be included.

Types of participants

We will include infants born at term and at preterm (< 37 weeks gestation) and with low birth weight (< 2500 g). Infants must be randomised by 1 month postmenstrual age.

Types of interventions

Pacifier use (when infant placed down to sleep, for all sleep events) versus no pacifier use.

Types of outcome measures

Primary outcomes
  • Deaths attributed to SIDS during the course of the study

Secondary outcomes
  • Episodes of otitis media during the course of the study

  • Episodes of oral candidiasis during the course of the study

  • Episodes of gastrointestinal infection during the course of the study (laboratory confirmed)

  • Incidence of breast feeding at 6 months

  • Incidence of breast feeding at 12 months

  • All-cause mortality

Search methods for identification of studies

We will use the standard search strategy of the Cochrane Neonatal Review Group (CNRG), as documented in The Cochrane Library. See the CNRG search strategy (http://neonatal.cochrane

Electronic searches

Two review authors (KP, JF) will perform the electronic database searches independently. We will search MEDLINE (from 1966 to current), EMBASE (from 1988 to current) and CINAHL (from 1982 to current) and the Cochrane Central Register of Controlled Trials (current issue) for RCTs using the following medical subject headings (MeSH) and text words: [infant-newborn OR infan*, OR Neonat*, OR Preterm* OR low birth weight] AND [non-nutritive sucking OR nonnutritive sucking] AND [dummy OR  dummies OR pacifier(s) OR soother(s) OR comforter(s)] AND [SIDS OR sudden infant death OR cot death]. We will search clinical trial registries for ongoing or recently completed trials (, and We will attempt to identify all relevant studies regardless of language or publication status (published and completed unpublished studies).

Searching other resources

We will communicate with expert informants and search bibliographies of reviews and trials for references to other trials. We will also search previous reviews including cross-references, abstracts, and the conference and symposia proceedings of the Perinatal Society of Australia and New Zealand, and other Pediatric Academic Societies (American Pediatric Society/Society for Pediatric Research and European Society for Paediatric Research) from 1990 to the current date. If we identify an unpublished trial, we will contact the corresponding investigator for information. We will consider unpublished studies or studies reported only as abstracts as eligible for review if the methods and data can be confirmed by the author. We will also contact the corresponding authors of identified RCTs for additional information about their studies when further data are required.

Data collection and analysis

We will use the standard methods of The Cochrane Collaboration, as documented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) and proposed by the CNRG.

Selection of studies

Review authors will independently assess for inclusion all the potential studies identified as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a Cochrane review arbiter.

Specifically, we will:

  1. merge search results using reference management software and remove duplicate records of the same report;

  2. examine titles and abstracts to remove irrelevant reports;

  3. retrieve the full text of the potentially relevant reports;

  4. link together multiple reports of the same study;

  5. examine full text reports for compliance of studies with eligibility criteria;

  6. correspond with investigators, when appropriate, to clarify study eligibility;

  7. note, at all stages, reasons for inclusion and exclusion of articles; disagreements will be resolved through consensus, or referred for arbitration to the editorial base of the CNRG, if needed;

  8. make final decisions on study inclusion and proceed to data collection;

  9. resolve all discrepancies through a consensus process.

Data extraction and management

We will design a form for data extraction. For eligible studies, review authors will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a review arbiter. We will enter data using Review Manager 5.2 (RevMan 2012) and check them for accuracy. When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.

Assessment of risk of bias in included studies

Review authors will independently assess the risk of bias in each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a review arbiter.

(1) Random sequence generation (checking for possible selection bias)
We will describe 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 will assess the method 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); or
• unclear risk.

(2) Allocation concealment (checking for possible selection bias)
We will describe for each included study the method used to conceal the allocation sequence in sufficient detail and determine whether intervention allocation could have been foreseen in advance of, or during, recruitment, or changed after assignment. We will assess the methods 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); or
• unclear risk.

(3) Blinding (checking for possible performance bias)

We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will judge studies to be at low risk of bias if they were blinded or if we judge that the lack of blinding could not have affected the results. We will assess blinding separately for different outcomes or classes of outcomes. We will assess the risk of bias methods as:

  • adequate, inadequate or unclear for participants;

  • adequate, inadequate or unclear for personnel; and

  • adequate, inadequate or unclear for outcome assessors.

(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)
We will describe for each included study, and for each outcome or class of outcomes, the completeness of data, including attrition and exclusions from the analysis. We will state 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 can be supplied by the trial authors, we will re-include missing data in the analyses which we undertake. We will assess the risk of bias methods as: adequate (less than 20% missing data); inadequate; or unclear. 

(5) Selective reporting bias

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

  • low risk (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported);

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

  • unclear risk. 

(6) Other sources of bias

We will describe for each included study any important concerns we have about other possible sources of bias (e.g. early termination of a trial due to a data-dependent process, extreme baseline imbalance, etc.). We will assess whether each study was free of other problems that could put it at risk of bias. We will assess other sources of bias as: low risk; high risk; or unclear risk. 

We will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). With reference to the above, we will assess the likely magnitude and direction of the bias, and whether we consider it likely to impact the findings. We will explore the impact of the level of bias by undertaking sensitivity analyses (see 'Sensitivity analysis'). 

We will try to obtain the study protocols of all included studies.

Each criterion will be judged as being at 'low risk' of bias, 'high risk' of bias or 'unclear' risk of bias (based on either lack of information or uncertainty over the potential for bias).

Measures of treatment effect

The results of the studies will be analysed using Review Manager (RevMan 2012). Data will be summarised in a meta-analysis if they are sufficiently homogeneous, both clinically and statistically.

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

Continuous data
We will use the mean difference (MD) for continuous data, if outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) to combine trials that measure the same outcome, but use different methods.

Unit of analysis issues

The unit of analysis is the participating infant in individually randomised trials, and geographical area in cluster randomised trials.

Cluster randomised trials:

We will include cluster randomised trials in the analyses as well as individually randomised trials. We will analyse them using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible) or from other sources (Higgins 2011). If ICCs from other sources are used, 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 types of trial if there is little heterogeneity between the study designs and an 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 separate meta-analysis. 

Dealing with missing data

For all included studies, we will note levels of attrition. If data from the trial reports are insufficient, unclear or missing, we will attempt to contact the trial authors for additional information.

We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analyses. For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat (ITT) basis (i.e. we will attempt to include all participants randomised to each group in the analyses and we will analyse all participants in the group to which they were allocated, regardless of whether they received the allocated intervention). The denominator for each outcome in each trial will be the number randomised minus any participants whose outcome data are known to be missing.

Assessment of heterogeneity

We will use the I² statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity, we will explore it by prespecified subgroup analysis. We will grade the degree of heterogeneity as: less than or equal to 25%, no heterogeneity; 25% to 49%, low heterogeneity; 50% to 74%, moderate heterogeneity; and greater than or equal to 75%, high heterogeneity.

Assessment of reporting biases

We will try to obtain the study protocols of all included studies and we will compare outcomes specified in the protocol to those reported in each of the included studies. We will investigate reporting and publication bias by examining the degree of asymmetry of a funnel plot. Where we suspect reporting bias (see the section 'Selective reporting bias' in 'Assessment of risk of bias in included studies'), we will attempt to contact study authors asking them to provide missing outcome data. Where this is not possible and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results using a sensitivity analysis. 

Data synthesis

We will use the fixed-effect model in Review Manager 5.2 (RevMan 2012) for meta-analysis. 

Subgroup analysis and investigation of heterogeneity

We will explore potential sources of clinical heterogeneity through the following a priori subgroup analyses.

  1. postmenstrual age (less than 28 weeks; 28 to 32 weeks; 32 to 37 weeks);

  2. exclusively breast fed; not exclusively breast fed.

Sensitivity analysis

We will explore methodological heterogeneity through the use of sensitivity analyses. We will assess studies at low risk of bias as those with adequate sequence generation, allocation concealment and fewer than 10% losses on ITT analyses.


Protocol first published: Issue 7, 2014

13 March 2007New citation required and major changesSubstantive amendment

Declarations of interest


Sources of support

Internal sources

  • No sources of support supplied

External sources

  • Eunice Kennedy Shriver National Institute of Child Health and Human Development National Institutes of Health, Department of Health and Human Services, USA.

    Editorial support of the Cochrane Neonatal Review Group has been funded with Federal funds from the Eunice Kennedy Shriver National Institute of Child Health and Human Development National Institutes of Health, Department of Health and Human Services, USA, under Contract No. HHSN275201100016C.