Breastfeeding has a fundamental impact on the short-, medium- and long-term health of children and has an important impact on women’s health. Good quality evidence demonstrates that in both low- and high-income settings not breastfeeding contributes to infant mortality, hospitalisation for preventable disease such as gastroenteritis and respiratory disease, increased rates of childhood diabetes and obesity, and adult disease such as coeliac and cardiovascular disease, as well as increased risks of breast cancer and diabetes in the mother (Black 2008; Ip 2007; Horta 2007; Quigley 2007), and reduced birth spacing when other forms of contraception are not available (Thapa 1988). Not being breastfed has an impact on IQ, and educational and behavioural outcomes for the child (Heikkilä 2011; Quigley 2012). For many outcomes a dose-response relationship exists, with the greatest benefit resulting from breastfeeding exclusively, with no added food or fluids, for around six months, with breastfeeding continuing thereafter as an important component of the infant’s diet (Kramer 2002; Raisler 1999). The negative impact of not breastfeeding has been demonstrated in a range of settings and population groups, though the balance of risks and benefits varies from setting to setting; gastroenteritis will result in much higher mortality in low-income countries, for example (Black 2008; Victora 2008).
Few health behaviours have such a broad-spectrum and long-lasting impact on population health, with the potential to improve life chances, health and wellbeing. The cost burden of not breastfeeding is significant and includes the cost of caring for children and women with chronic disease as well as short-term illness (Bartick 2010; Smith 2010).
The established negative impact on a population of not breastfeeding has resulted in global and national support for encouraging the initiation and continuation of breastfeeding. The World Health Organization (WHO) recommends that, wherever possible, infants should be fed exclusively on breast milk until six months of age (WHO 2003), with breastfeeding continuing as an important part of the infant’s diet till at least two years of age. Other agencies and countries have endorsed the recommendation to breastfeed exclusively to around six months of age (e.g. CDC 2010; DoH 2003; EFSA Panel 2009).
Although some high-income countries such as Scandinavia, Germany, and Norway have high rates of both initiation and continuation of breastfeeding (Cattaneo 2003; Nicoll 2002), rates in many high-income countries are low. Initiation rates have risen in some high-income countries in recent years (e.g. NHS 2011; USDoHHS 2005), but there remains a marked decline in breastfeeding within the first few weeks after initiation, and exclusive breastfeeding is rare (Bolling 2007). In middle- and low-income countries, exclusive breastfeeding is far from universal, with urban areas often showing lower rates than rural areas (WHO 2011). This is particularly important as when breastfeeding continues for long periods of time, infant and young child mortality are reduced in the second year of life in low- and middle-income countries (WHO 2000).
The early discontinuation of breastfeeding is not a decision that is taken lightly by women; it is associated with a high prevalence of problems such as painful breasts and nipples, concern about adequacy of milk supply and about the baby’s behaviour, and embarrassment related to breastfeeding in public; and many mothers report distress related to the decision to discontinue breastfeeding (e.g. Bolling 2007), even in cultures where breastfeeding rates are high (Almqvist 2011). A key factor is the widespread lack of appropriate education for health professionals in the prevention and treatment of breastfeeding problems, which means that in a wide range of settings women commonly do not receive the care needed from the health services (EU 2008; Renfrew 2006).
Infant feeding is strongly related to inequalities in health and far from being an individual decision made by each woman, is influenced most strongly by structural determinants of health. The range of different rates of initiation and continuation of breastfeeding in different settings globally demonstrates that the key factors influencing infant feeding rates are likely to be socio-cultural and related to societal norms, public policy, and the availability of appropriate care and support, both professional and lay (EU 2008). In high-income countries, for example, young mothers and women in low-income groups, or women who ceased full-time education at an early age, are least likely either to start breastfeeding or to continue for a period of time sufficient to benefit from the greatest health gain (Bolling 2007). Enkin 2000 notes that industrial societies, on the whole, do not provide women with the opportunity to observe other breastfeeding women before they attempt breastfeeding themselves. In such societies, where breastfeeding is not normative behaviour and women may find it socially challenging to breastfeed, women are at particular risk of finding a serious lack of support to continue breastfeeding. Migrant women have been shown to adopt breastfeeding practices that are more similar to the country in which they live, than the country of their birth (e.g. McLachlan 2006). Rates in low-income countries also vary widely, especially rates of exclusive breastfeeding (WHO 2011).
In few settings is standard care offered by professionals with an in-depth understanding of the prevention and treatment of breastfeeding problems. To address this, UNICEF and the WHO established the global Baby Friendly Hospital Initiative (Baby Friendly Initiative in some countries) in 1991 to train health professionals and remove inappropriate routines such as supplementary feeding and restrictions on feeding times. Over 15,000 facilities in 134 countries have been accredited (UNICEF 2011), but most babies are still not born in a Baby Friendly environment.
It is therefore fundamentally important to examine the support that mothers receive when breastfeeding to determine what might be effective in helping women continue to breastfeed, whatever setting they live in. ‘Support’ can include several elements, including reassurance, praise, information, the opportunity to discuss and to respond to the mother’s questions. It can be offered in a range of ways, by health professionals or lay people, trained or untrained, in hospital and community settings. It can be offered to groups of women or one-to-one, it can involve mother-to-mother support, and it can be offered proactively by contacting women directly, or reactively, by waiting for women to get in touch. It can be provided face-to-face or over the phone, and it can involve only one contact or regular, ongoing contact over several months. Support is a complex intervention that tackles the multifaceted challenge of enabling women to breastfeed, and it should not be surprising that it varies from setting to setting and from study to study. However, it is likely that different forms of support in different contexts will be differentially effective. Whilst many support interventions include breastfeeding education for mothers, our review excludes interventions described as solely educational in nature and interventions with no postnatal component. A Cochrane review of antenatal breastfeeding education for increasing breastfeeding duration has recently been published (Lumbiganon 2011).
The purpose of this review is to examine interventions which provide extra support for mothers who are breastfeeding or considering breastfeeding; and to assess their impact on breastfeeding duration and exclusivity and, where recorded, on health outcomes and maternal satisfaction. The focus of this review is support for mothers and babies who are part of the general healthy population of their countries; mothers of premature and sick babies and mothers with some medical conditions have additional issues with breastfeeding, and interventions to support these mothers need to be reviewed separately. Specific objectives of this review were to describe forms of support which have been evaluated in controlled studies, and the settings in which they have been used. It was also of interest to examine the effectiveness of different modes of offering similar supportive interventions (for example, face-to-face or over the telephone), whether interventions containing both antenatal and postnatal elements were more effective than those taking place in the postnatal period alone, and whether the support was offered proactively to women, or whether they needed to seek it out. We also planned to examine the effectiveness of different care providers and the possible impact of background breastfeeding rates in the countries or areas where the trials took place on the effectiveness of supportive interventions. It is important to note that the support interventions offered were in addition to standard care, which varied from setting to setting, though in few settings is standard care offered by people with training and skill in enabling women to breastfeed.
- To describe forms of breastfeeding support which have been evaluated in controlled studies, the timing of the interventions and the settings in which they have been used.
- To examine the effectiveness of different modes of offering similar supportive interventions (for example, whether the support offered was proactive or reactive, face-to-face or over the telephone), and whether interventions containing both antenatal and postnatal elements were more effective than those taking place in the postnatal period alone.
- To examine the effectiveness of different care providers and (where information was available) training.
- To explore the interaction between background breastfeeding rates and effectiveness of support.
Criteria for considering studies for this review
Types of studies
All randomised or quasi-randomised controlled trials, with or without blinding.
Types of participants
Participants were women breastfeeding their babies. Studies that recruited pregnant women considering or intending to breastfeed were included if the intervention included breastfeeding support after the birth.
Types of interventions
Contact with an individual or individuals (either professional or volunteer) offering support which is supplementary to the standard care offered in that setting. ‘Support’ interventions eligible for this review could include elements such as reassurance, praise, information, and the opportunity to discuss and to respond to the mother’s questions, and it could also include staff training to improve the supportive care given to women. It could be offered by health professionals or lay people, trained or untrained, in hospital and community settings. It could be offered to groups of women or one-to-one, including mother-to-mother support, and it could be offered proactively by contacting women directly, or reactively, by waiting for women to get in touch. It could be provided face-to-face or over the phone, and it could involve only one contact or regular, ongoing contact over several months. Studies were included if the intervention occurred in the postnatal period alone or also included an antenatal component. Interventions taking place in the antenatal period alone were excluded from this review, as were interventions described as solely educational in nature.
Types of outcome measures
The main outcome measure was the effect of the interventions on stopping breastfeeding by specified points in time. Primary outcomes were recorded for stopping any or exclusive breastfeeding before four to six weeks and at the last study assessment (up to six months). Other outcomes of interest were stopping any or exclusive breastfeeding at other time points (two, three, four, nine and 12 months), measures of neonatal and infant morbidity (where available) and measures of maternal satisfaction with care or feeding method.
- Stopping breastfeeding before six months postpartum.
- Stopping exclusive breastfeeding before six months postpartum.
- Stopping any breastfeeding before four to six weeks postpartum.
- Stopping exclusive breastfeeding before four to six weeks postpartum.
- Stopping breastfeeding before two, three, nine and 12 months postpartum.
- Stopping exclusive breastfeeding before two, three, nine and 12 months postpartum.
- Maternal satisfaction with care.
- Maternal satisfaction with feeding method.
- All-cause infant or neonatal morbidity.
Search methods for identification of studies
We searched the Cochrane Pregnancy and Childbirth Group's Trials Register by contacting the Trials Search Co-ordinator (3 October 2011).
The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co-ordinator and contains trials identified from:
- quarterly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);
- weekly searches of MEDLINE;
- weekly searches 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.
Trials identified through the searching activities described above are given a code (or codes) depending on the topic. The codes are linked to review topics. The Trials Search Co-ordinator searches the register for each review using these codes rather than keywords.
In previous versions of the review, we carried out additional searches of MEDLINE (1966 to November 2005), EMBASE (1974 to November 2005) and handsearched Midwives Information and Resource Service (MIDIRS) quarterly Digest from 1991 to September 2005. We scanned secondary references and obtained relevant studies. Details of the search strategies can be obtained from the review authors. In this updated version of the review we did not carry out these additional searches.
We did not apply any language restrictions.
Data collection and analysis
For the methods used when assessing the trials identified in previous versions of this review, see Appendix 1.
Selection of studies
In this update, two review authors (B Quinn and T Dowswell) independently assessed all the studies identified as a result of the search strategy for possible inclusion in the review. We resolved any disagreement through discussion or, if required, we consulted a third review author (F McCormick or M Renfrew).
Data extraction and management
We designed and piloted a form to extract data. For eligible studies, two review authors extracted information using the agreed form. We resolved discrepancies through discussion. Data were entered into Review Manager software (RevMan 2011), and checked for accuracy.
When information regarding study methods and results were 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). Any disagreement was resolved by discussion or by involving a third assessor.
(1) Sequence generation (checking for possible selection bias)
We have described for each included study the method used to generate the allocation sequence and assessed whether it was likely to 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 the allocation sequence and assessed whether the treatment 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 (checking for possible performance or detection bias)
For this type of intervention, blinding women and clinical staff is generally not feasible, although it may be possible to blind outcome assessors. We have assessed blinding for outcome assessors as:
- low, high or unclear risk of bias.
(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)
In studies examining breastfeeding support women may be followed up over many months and loss to follow-up over time may mean that studies are at high risk of bias. We have described for each included study the completeness of data including attrition and exclusions from the analysis. We have 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. We assessed methods as:
- low, high or unclear risk of bias.
We have not included outcome data in the analyses if there was more than 25% missing data for that outcome. Several studies which were otherwise eligible for inclusion in the review have not contributed any outcome data due to post randomisation exclusions and loss to follow-up which resulted in more than 25% missing data for all outcomes reported.
(5) Selective reporting bias
We have described for each included study whether we suspected any selective outcome reporting bias.
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 cannot be used; study failed to include results of a key outcome that would have been expected to have been reported);
- unclear risk of bias.
(6) Other sources of bias
We have described for each included study any important concerns we had about other possible sources of bias.
We assessed whether each study was free of other problems that could put it at risk of bias:
- yes (low risk of other bias);
- no (high risk of other bias);
- unclear 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 possible bias through undertaking sensitivity analyses - see Sensitivity analysis.
|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.|
Measures of treatment effect
For dichotomous data, we have presented results as summary risk ratio with 95% confidence intervals (CI).
For continuous data, we planned to use the mean difference if outcomes were measured in the same way between trials or the standardised mean difference to combine trials that measured the same outcome, but used different methods.
Unit of analysis issues
We have included eight cluster-randomised trials in the analyses along with individually randomised trials. Their sample sizes have been adjusted using the methods described in the Handbook (Higgins 2011) and by Donner 2000 using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), or from another source. If ICCs from other sources were used, we have noted this and carried out sensitivity analyses to investigate the effect of variation in ICC. We have synthesised the findings from individually- and cluster-randomised trials provided that there was little heterogeneity between the study designs. and the interaction between the effect of intervention and the choice of randomisation unit was considered to be unlikely.
Dealing with missing data
For included studies, we have noted levels of attrition. We have not included any outcomes in the analyses if there was more than 25% missing data.
For all outcomes we have 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. For all primary outcomes the denominator for each outcome in each trial is the number of women randomised. We have assumed that all women who were lost to follow-up had stopped breastfeeding or stopped exclusive breastfeeding. This means that estimates of treatment effect may be diluted in studies where there has been moderate loss to follow-up.
Assessment of heterogeneity
We have use the I² and T² statistics to quantify heterogeneity along with the Chi² test for heterogeneity. If we identified substantial heterogeneity (I² greater than 30%), we have drawn attention to this in the text and have advised readers to interpret results with caution. For primary outcomes where moderate or high levels of heterogeneity were identified we have also given the 95% prediction interval which gives the range of effects expected across different settings (Riley 2011).
Assessment of reporting biases
Where we suspected reporting bias (see ‘Selective reporting bias’ above), we attempted to contact study authors asking them to provide missing outcome data.
For all outcomes we have ordered studies in terms of weight, and for primary outcomes, provided sufficient studies contributed data, we have generated funnel plots. We visually examined plots to see whether there was any evidence of asymmetry suggesting different treatment effects in smaller studies which may indicate publication bias (Harbord 2006).
We carried out statistical analysis using the Review Manager software (RevMan 2011). At the outset, we had anticipated that there would be some heterogeneity between studies in terms of the interventions and the populations studied, we therefore decided to use random-effects meta-analysis for combining data. Random-effects meta-analysis estimates the average treatment effect and this may not always be clinically meaningful. Further, where there is high heterogeneity the applicability of the overall effect estimate is likely to vary in different settings and we therefore advise caution in the interpretation of results.
Subgroup analysis and investigation of heterogeneity
We planned to carry out the following subgroup analyses.
- By type of supporter (professional versus lay person, or both).
- By type of support (face-to-face versus telephone support).
- By timing of support (antenatal and postnatal versus postnatal alone).
- By whether the support was proactive (scheduled contacts) or reactive (women needed to request support).
- By background breastfeeding initiation rates (low, medium or high background rates).
- By intensity of support (number of scheduled contacts).
We have used primary outcomes only in subgroup analysis.
We visually examined the forest plots of subgroup analyses to look at whether there was overlap between 95% CIs for the effects in different groups; with non-overlapping CIs suggesting a difference between subgroups. We also conducted formal statistical analyses to examine any possible differences between subgroups classifying whole trials by interaction tests as described in the Handbook (Higgins 2011) and available in RevMan 2011; we have reported results of interaction tests in the text.
We have carried out sensitivity analysis for primary outcomes by study quality; we did this by dividing the studies into subgroups according to whether they were at low risk of bias as opposed to unclear or high risk of bias for allocation concealment to see what impact this would have on the treatment effect.
Description of studies
The main purpose of this review was to analyse the impact of the intervention, extra breastfeeding support, compared with usual maternity care, with the purpose of facilitating continued breastfeeding. We included studies if the intervention occurred in the postnatal period alone or if it also included an antenatal component. We excluded interventions taking place in the antenatal period alone, as well as interventions described as solely educational in nature.
Primary outcomes were recorded for stopping any or exclusive breastfeeding before four to six weeks and at the last assessment up to six months Other outcomes of interest were stopping breastfeeding at other time points, measures of neonatal and infant morbidity (where available) and measures of maternal satisfaction with care or feeding method.
Results of the search
In the previous version of this review (Britton 2007), we included 34 trials. In this updated version, we assessed 218 reports; as several trials resulted in multiple publications this corresponded to 150 separate studies. We have included 67 studies and excluded 79. Three studies are still ongoing (Bonuck 2008; Eneroth 2007; Patel 2011) and one study is awaiting assessment (Nunes 2011) and we hope to include results from these in future updates (see Characteristics of studies awaiting classification, Characteristics of ongoing studies and Characteristics of studies awaiting classification tables for more information about these trials).
Of the 67 studies that we assessed as eligible for inclusion, 52 contributed outcome data to the review and have been included in the results. One of these trials reported results in three African countries, and in the data and analysis tables we have entered data for each country separately and have completed three Characteristics of included studies tables as there were some differences between the three countries in the characteristics of women recruited, and the way the intervention was delivered (Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c).
We have not included outcome data from 10 studies where loss to follow-up was greater than 25% because the results from trials with high levels of attrition are difficult to interpret, and are liable to be at high risk of bias (Aidam 2005; Anderson 2005; Ellis 1984; Gross 1998; Hall 1978; Khresheh 2011; McKeever 2002; Redman 1995; Wambach 2009; Wolfberg 2004). We have not included data from a further five trials as data were not reported in a way that allowed us to enter them into RevMan 2011 (e.g. results were not reported by randomisation group) (Bloom 1982; Caldeira 2008; Chen 1993; Kaojuri 2009; Ransjo-Arvidson 1998); where possible we have contacted authors for more information and may be able to include data from these studies in future updates.
In the results section below we will not discuss further those 15 studies not contributing data to the review, but additional information about these trials is provided in the Characteristics of included studies tables.
Description of included studies (n = 52)
Fifty-two included studies contribute data to this update of the review. The total number of mother-infant pairs in these studies is 56,451 (this total was 29,385 in the previous version of this review Britton 2007). The 52 studies were published/conducted between 1979 and 2011 and show increases over time both in number of studies (five studies are dated earlier than 1990, 10 are dated 1990 to 1999 and 37 are dated 2000 to 2011) and range of country settings (the seven studies with dates earlier than 1994 were all undertaken in high-income countries, and the four studies from low/low-middle income countries were published in 2000 or later). The data in this review come from participants living in 21 countries. Using the World Bank classification of countries by income (http://data.worldbank.org/about/country-classifications/country-and-lending-groups, accessed 25 Oct 2011):
- 12 studies with 21,649 participants (38%) were conducted in upper-middle-income countries (Belarus, Kramer 2001; Brazil, Albernaz 2003; Barros 1994; Coutinho 2005; de Oliveira 2006; Leite 2005; Santiago 2003; and Vitolo 2005; Iran, Froozani 1999; Mexico, Morrow 1999; Turkey, Aksu 2011 and South Africa, Tylleskar 2011c
- 37 studies with 30,800 participants (55%) were conducted in high-income countries (Australia, McDonald 2010 and Quinlivan 2003; Canada, Dennis 2002; Gagnon 2002; Lynch 1986; Mongeon 1995; Porteous 2000; and McQueen 2011; Denmark, Kronborg 2007; France, Labarere 2005; Italy, Di Napoli 2004; Netherlands, Kools 2005; Singapore, Su 2007; Sweden, Sjolin 1979 and Ekstrom 2006; UK, Graffy 2004; Hoddinott 2009; Jones 1985; Jenner 1988; Morrell 2000; Muirhead 2006; Sinclair 2007; and Winterburn 2003; US, Brent 1995; Bonuck 2005; Bunik 2007; Chapman 2004; Di Meglio 2010; Frank 1987; Grossman 1990; Hopkinson 2009; Petrova 2009; Pugh 1998; Pugh 2002; Pugh 2007; Serafino-Cross 1992; and Wrenn 1997).
Methods used in trials
The 52 studies include 44 individually-randomised trials and eight cluster-randomised trials.
Participants and setting
Socio-economic and health status
Participants were women from the general healthy population of their countries. However, 19 of the 52 studies were undertaken with women from low-income groups within their country. These 19 studies include 12 of the 14 US studies, with two other studies from high-income countries (Jones 1985; Quinlivan 2003), three of the studies from Brazil (Barros 1994; Coutinho 2005; Vitolo 2005), and the two studies from low-income countries. In one of these (Haider 2000, Bangladesh), participants were mainly of lower-middle and low socio-economic status. In the other (Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c), participants came from three countries in sub-Saharan Africa, with those in one country (Uganda) from low-income groups within that country. With regard to health of the general population of countries, this author notes local HIV prevalence rates of 10% to 34% in the South Africa study sites; during recruitment, women who had not been HIV tested were encouraged to visit the antenatal clinic, and those who disclosed HIV positive status were recruited into another study.
Background rates of breastfeeding initiation/“ever breastfed”
Among the 52 studies, World Bank country income group shows an inverse relationship with background rates of breastfeeding initiation ("ever breastfed"). All the studies with intermediate (60% to < 80%, n = 18) or low (< 60%, n = 11) background rates of breastfeeding initiation were undertaken in high-income countries. Nine of the 11 studies with low background rates recruited women from low-income groups in the US (Brent 1995; Bonuck 2005; Bunik 2007; Chapman 2004; Di Meglio 2010; Frank 1987; Grossman 1990; Pugh 2002; Serafino-Cross 1992); the remaining two (UK) studies were from areas of Scotland with lower breastfeeding initiation rates than the Scottish average (Hoddinott 2009; Muirhead 2006). All the country income groups are represented among the 24 studies with high (≥ 80%) rates, however the four studies from low-/low-middle-income countries all have very high rates (≥ 95% ever breastfed). Where background rates of “ever breastfed” were not reported, we have used rates published in The WHO Global Data Bank on Infant and Young Child Feeding http://www.who.int/nutrition/databases/infantfeeding/countries/en/index.html (and for the two studies from Scotland (Hoddinott 2009; Muirhead 2006), we used http://www.isdscotlandarchive.scot.nhs.uk/isd/1914.html, both accessed November 2011).
Hospital (Baby Friendly) and community settings
Twenty-two of the 52 studies were carried out both on hospital postnatal wards and in community settings (these include hospital and community clinics). Five of the 22 hospital-based studies were set in hospitals with Baby Friendly accreditation (Aksu 2011; Chapman 2004; Coutinho 2005; de Oliveira 2006; Sinclair 2007). Thirty studies were conducted in community settings only. In one of these (Kronborg 2007), the five hospitals serving the area from which the study participants were recruited had all adopted the standards of the Baby Friendly Hospital Initiative, and three of them were certified as Baby Friendly. In another (Hoddinott 2009) the clusters were seven intervention group localities paired with seven control group localities. In the intervention group, the number of localities in which the hospital where most women gave birth had the Baby Friendly award was three before the intervention and four after the intervention. In the control group, the corresponding numbers were four localities before and six after the intervention.
Level of the intervention
In 45/52 studies, women received the intervention. In six studies (three cluster-randomised trials; Bhandari 2003; Ekstrom 2006; and Kramer 2001, and three individually-randomised trials; Labarere 2005; Santiago 2003; Sinclair 2007), the intervention was additional training in breastfeeding support for staff. One cluster-randomised trial (Hoddinott 2009) evaluated a policy for providing breastfeeding groups.
Breastfeeding support: proactive/indirect
In 41/45 of the studies where women received the intervention and five of the six studies of staff training, breastfeeding support was delivered directly to women. In five other studies (Graffy 2004; Hoddinott 2009; Labarere 2005; Morrell 2000; Winterburn 2003), breastfeeding support was not proactively offered; women were encouraged to access it, but breastfeeding support was not delivered directly to women as part of these interventions. One study (Kools 2005) evaluated a multi-faceted intervention of which breastfeeding support delivered directly to women was one component.
In 48/52 studies there was individual, one-to-one contact between the breastfeeding supporter and the breastfeeding mother. One study (Hoddinott 2009), offered group support, one (Ekstrom 2006) offered both individual and group support, and in two studies this aspect of support was unclear (Kools 2005; Kramer 2001).
Breastfeeding support from professional/ lay supporters
In the previous edition of this review, the people providing breastfeeding support were categorised as 'professional', 'lay and professional' or 'lay'. Using those categories, the 52 studies in this update comprise 30 studies of professional support, nine of lay and professional support and 13 of lay support. In view of the growing body of work evaluating breastfeeding peer support, we have distinguished between this and other kinds of lay support, following the definition by Dennis 2002: “Peer support is provided by lay individuals who are not part of the client’s own embedded network, who possess experiential knowledge of the targeted behaviour (i.e. successful breastfeeding skills) and similar qualities (i.e. age, socioeconomic status, ethnicity, residency etc.,) in order to aid the client during a time of actual or potential stress (i.e. the initiation and continuation of breastfeeding”.
In 30/52 studies a variety of medical, nursing and allied professionals (for example, nutritionists, lactation consultants and researchers) provided the breastfeeding support (Albernaz 2003; Bunik 2007; Bashour 2008; Bonuck 2005; Brent 1995; de Oliveira 2006; Di Napoli 2004; Ekstrom 2006; Frank 1987; Froozani 1999; Gagnon 2002; Jones 1985; Kramer 2001; Kronborg 2007; Lynch 1986; McDonald 2010; McQueen 2011; Petrova 2009; Porteous 2000; Pugh 1998; Quinlivan 2003; Santiago 2003; Serafino-Cross 1992; Sinclair 2007; Sjolin 1979; Su 2007; Vitolo 2005; Wrenn 1997).
Professional and lay
Professionals provided breastfeeding support with other people in a further nine studies; para-professionals (Kools 2005; Morrell 2000), peer supporters (Bhandari 2003; Hopkinson 2009; Pugh 2002; Pugh 2007), and lay people (employees who had to be mothers in Barros 1994; someone chosen by the mother in Winterburn 2003; and a group of mothers in Hoddinott 2009).
Lay people provided breastfeeding support in 13 studies. In eight of these, the lay people were peer supporters (Chapman 2004; Dennis 2002; Di Meglio 2010; Haider 2000; Leite 2005; Morrow 1999; Muirhead 2006; Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c). The other five studies (Aksu 2011; Coutinho 2005; Graffy 2004; Jenner 1988; Mongeon 1995) did not report that the lay supporters met the criteria (Dennis 2002) for us to classify them as peer supporters.
Training in breastfeeding support
Overall, 36/52 studies report that the people providing breastfeeding support had additional training to provide breastfeeding support (21/30 professional, 3/9 professional and lay and 12/13 peer/lay). Sixteen of the 21 studies where professionals had additional training give details of the training. In eight studies, the training was specific to the study (Bashour 2008; de Oliveira 2006; Ekstrom 2006; Labarere 2005; McDonald 2010; Santiago 2003; Sinclair 2007; Vitolo 2005) and lasted, where reported, five to 16 hours. In five of the remaining eight studies professionals had WHO/Unicef training for 18 hours (Di Napoli 2004; Kramer 2001; Kronborg 2007) or 40 hours (Albernaz 2003; Froozani 1999) and in three studies the professionals were International Board Certified Lactation Consultants (IBCLC) (Brent 1995; Petrova 2009; Pugh 1998).
In one of the studies of support from professionals and paraprofessionals, the professionals were lactation consultants (Kools 2005) and in the other they were midwives not stated to have had extra training in breastfeeding support (Morrell 2000); in both these studies the para-professionals were trained to refer women with breastfeeding problems to the professionals. Two of the four studies of support from professionals and peers reported training; in Bhandari 2003 peer supporters received WHO-based training, and in Hopkinson 2009 the professionals were IBCLCs and the peer supporters had three days training in lactation management, 20 hours training in peer counselling and at least one year’s work experience. One of the three studies study of professional and lay support states lay supporters received breastfeeding support training (Barros 1994).
All eight studies of peer support (alone) reported peer supporters were trained. The training was WHO 20 hours (Leite 2005), 40 hours (Haider 2000) or one week (Tylleskar 2011); La Leche League (LLL) 30 hours (Chapman 2004), 20 hours (Di Meglio 2010) and length not specified (Morrow 1999). Two studies reported the length but not the type of training; 2.5 hours (Dennis 2002) and more than two days (Muirhead 2006). Three of the five studies of lay support (alone) reported breastfeeding training; WHO 18 hours plus five days (Coutinho 2005), WHO 18 hours (Aksu 2011) and National Childbirth Trust training (Graffy 2004).
Mode of support (face-to-face and/or by telephone)
Twenty-seven of the 52 studies offered telephone support and all but one of these (Albernaz 2003, Brazil) were undertaken in countries classified High Income by the World Bank. Three studies (Dennis 2002; Bunik 2007; Di Meglio 2010) offered breastfeeding support only by telephone. Twenty-four offered both face-to-face and telephone support, with telephone support either predominant (e.g. Muirhead 2006; Petrova 2009) or as backup (e.g. Chapman 2004). In some studies (e.g. Kools 2005; Pugh 1998), telephone contact with the breastfeeding support specialist came after the women had been visited by someone else. Across the 27 studies examining telephone support, details of whether or not the telephone support was proactively offered by the peer or professional supporter were not consistently reported. Twenty-four studies offered only face-to-face support. In the one remaining study (Winterburn 2003), the support was not proactive and the mode of support was not specified.
Support with an antenatal component and intention to breastfeed
The outcomes of interventions intended to promote longer duration of breastfeeding could be expected to differ according to whether women were recruited before or after they started to breastfeed. Two-thirds of the studies (34/52) included postnatal women at or after initiation of breastfeeding. In the one study of breastfeeding in groups (Hoddinott 2009), pregnant women and breastfeeding mothers could be invited to attend groups. The remaining 17 studies recruited women before the birth, not all of whom went on to initiate breastfeeding. Six of the 17 studies (Kramer 2001, Belarus; Jenner 1988 and Winterburn 2003, UK; Serafino-Cross 1992, US; Mongeon 1995, Canada; Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c, Burkina Faso, Uganda and South Africa) included only women who intended to breastfeed. In the study by Tylleskar 2011, this inclusion criterion was related to HIV/AIDS prevention and management in the country and study populations. Eleven studies that recruited before the birth did not specify that participants had to intend to breastfeed.
Intensity of the intervention
Forty-five of the 52 studies reported the intensity of the intervention in terms of the number of postnatal contacts the mother could have for breastfeeding support. Sixteen studies specified three or fewer contacts, 16 four to eight contacts, and the remaining 13 studies specified nine or more contacts. We have performed a subgroup analysis and results are described in the text.
Duration of the intervention and duration of data collection
The length of time between the end of an intervention and collection of outcome data could be a factor in effectiveness of the intervention. Among the 52 studies, duration of the intervention ranged from three days to one year and the last data collection point for breastfeeding outcomes ranged from two weeks to 18 months (note the analyses in this review only include data where follow-up was at least 75%). For 46/52 studies it was possible to calculate the length of time between the end of the intervention and the end of data collection. In 21 studies the intervention and data collection ended at the same time (at one year in three studies; six months in seven studies; five months in one study; four months in four studies; three months in five studies and at four weeks in one study, Porteous 2000). In the remaining 25 studies the time interval between the end of the intervention and the end of data collection ranged from 1.5 weeks (Gagnon 2002) to 17.9 months (Aksu 2011); in these two studies the intervention ended at four and three days respectively.
Control group care
Five of the 52 studies were undertaken in hospital settings with Baby Friendly accreditation (Aksu 2011; Chapman 2004; Coutinho 2005; de Oliveira 2006; Sinclair 2007). These study interventions were additional to care that met Baby Friendly standards and were received by everyone at the hospital including all the study participants in the intervention and control groups. In two community-based cluster-randomised trials (Hoddinott 2009; Kronborg 2007), most of the maternity hospitals in which the participants had given birth had Baby Friendly accreditation. In 20 studies control group care was not specified (n = 7) or stated to be standard care but not described (n = 13). In half the studies (27/52) there was some description of control group care (see Characteristics of included studies). Standard postnatal care varies both between and within countries. Care may have differed within the study period and may also have differed from that which is offered at the present time.
Level of data collection
In 45/52 studies data outcome data were collected from the women who had received the intervention. In the other seven studies, the relationship between the recipients of the intervention and the source of the outcome data varied. In the three individually-randomised trials of staff training (Labarere 2005; Santiago 2003; Sinclair 2007), outcome data came from all the women randomised to receive, or not to receive, a support intervention from trained staff. In one of the three cluster-randomised trials of staff training (Ekstrom 2006), data came from mothers of singleton term healthy infants at centres where staff had been randomised, or not randomised, to receive training. In another (Bhandari 2003) trained staff visited all families in the intervention villages and outcome data were collected from all infants in the intervention and control villages, and in the third (Kramer 2001), staff in all intervention sites were trained and data were collected from mothers who intended to breastfeed in the intervention and control sites. In the cluster-randomised trial that evaluated a policy for providing breastfeeding groups (Hoddinott 2009), the policy intervention was made at locality level. Pregnant or postnatal women could be invited to groups in intervention clusters; however, only 1310 pregnant or breastfeeding women out of more than 9000 births in the intervention localities attended any group.
Duration of any and/or exclusive breastfeeding
The breastfeeding outcomes reported reflect World Bank country income group of the countries where the 52 studies were undertaken. Most studies (29/52) report the effect of the intervention on rates of both any and exclusive breastfeeding. However, all 14 studies that only report any breastfeeding were undertaken in high-income countries, and the nine studies that only report exclusive breastfeeding include all four from low-/lower-middle-income countries. Some studies newly included in this review report details about data collection that make it clear duration of exclusive breastfeeding at specific time points was not necessarily measured from birth (Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c; Vitolo 2005); most studies do not report this level of detail.
A few studies reported various infant morbidity and maternal satisfaction with feeding and care outcomes by intervention group, as follows: infant morbidity in 11 studies (Bashour 2008; Bhandari 2003; Bunik 2007; Frank 1987; Froozani 1999; Kramer 2001; Morrow 1999; Petrova 2009; Pugh 2002; Quinlivan 2003; Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c); maternal satisfaction with feeding in 11 studies (Bashour 2008; de Oliveira 2006; Dennis 2002; Hoddinott 2009; Hopkinson 2009; Kronborg 2007; Labarere 2005; McDonald 2010; McQueen 2011; Petrova 2009; Pugh 1998) and maternal satisfaction with care in six studies (Bashour 2008; Ekstrom 2006; Graffy 2004; Jones 1985; Kools 2005; Morrow 1999).
We excluded 79 studies from the review. The main reason for exclusion was because studies were not randomised trials, or it was not clear that allocation to groups had been carried out randomly; we excluded 18 studies identified by the search for this reason (Caulfield 1998; Davies-Adetugbo 1996; Ebbeling 2007; Garcia-Montrone 1996; Hall 2007; Jang 2008; Kistin 1994; McInnes 2000; Moreno-Manzanares 1997; Neyzi 1991; Nor 2009; Pascali-Bonaro 2004; Perez-Escamilla 1992; Segura-Millan 1994; Sisk 2006; Susin 2008; Thussanasupap 2006; Valdes 2000). A further two papers were reviews rather than reports of a randomised controlled trials (Guise 2003; Lewin 2005).
We excluded 38 trials because the intervention was not relevant to this review. We excluded 17 trials on the grounds that studies examined educational interventions where the focus was on instruction rather than on support to women to encourage breastfeeding (Bolam 1998; Cattaneo 2001; Forster 2004; Hauck 1994; Henderson 2001; Isselmann 2006; Jakobsen 2008; Jones 2004; Labarere 2003; Lavender 2004; Mattar 2003; Rea 1999; Rossiter 1994; Sakha 2008; Schy 1996; Wallace 2006; Westphal 1995). We excluded a further 13 trials as the intervention was not designed to support continued breastfeeding; these studies examined more general interventions in the postnatal period (Ball 2011; Barlow 2006; Barnet 2002; Black 2001; Gagnon 1997; MacArthur 2002; Peterson 2002; Pollard 2011; Ratner 1999; Rush 1991;Serrano 2010; Thomson 2009; Wiggins 2005); a further trial by Baqui 2008 focused on breastfeeding initiation only, rather than on postnatal support to encourage continuation. Seven of the studies examined interventions carried out in the antenatal period only, and had no postnatal support component (Forster 2006; Johnston 2001; MacArthur 2009; Olenick 2011; Noel-Weiss 2006; Reeve 2004; Wockel 2009).
Fifteen of the studies that we assessed for inclusion were excluded as they did not focus on healthy mothers with healthy term infants. Four trials examined interventions for low birthweight babies (Agrasada 2005; Brown 2008; Junior 2007; Pinelli 2001), while the study by Ahmed 2008 recruited only mothers of premature babies. In the trials by Davies-Adetugbo 1997 and Haider 1996, mothers of babies with severe diarrhoea were recruited, and the studies by Merewood 2006 and Phillips 2010 recruited only mothers of babies admitted to neonatal intensive care unit. The trial by Ferrara 2008 focused on an intervention for mothers with diabetes and that by Gijsbers 2006 on families with a history of asthma, while Moore 1985 looked at infants with a parent with eczema or asthma. Three other trials recruited only women in high-risk groups (Chapman 2011; McLeod 2003; Rasmussen 2011).
The remaining trials were excluded for other reasons (Finch 2002; Lieu 2000; Mannan 2008; Rowe 1990; Sciacca 1995; Steel O'Connor 2003). Further details of these, and other excluded studies, can be found in the Characteristics of excluded studies tables.
Risk of bias in included studies
Each trial was assessed for methodological quality as outlined in the Methods section.
We considered that approximately half of the studies contributing data to the review used methods that were at low risk of bias to generate the randomisation sequence and to conceal allocation to experimental groups. We assessed that 30 of the 52 studies contributing data were at low risk of bias for sequence generation and 26 were at low risk of bias for methods to conceal group allocation. Methods were either not described or were not clear for 15 studies with regard to sequence generation, and for 19 for allocation concealment. We assessed that seven studies were at high risk of bias for both the methods used to generate the randomisation sequence and to conceal group allocation at the point of randomisation (de Oliveira 2006; Froozani 1999; Grossman 1990; Jenner 1988; Jones 1985; Sjolin 1979; Wrenn 1997). These studies used methods such as alternation, day of clinic attendance, or time of day of birth to generate the randomisation sequence; the use of such methods would mean that those carrying out randomisation would not be blind to group allocation.
With interventions of this type, assessing risk of bias associated with blinding is very difficult. Both mothers and the staff providing care would be likely to be aware that they were either receiving or delivering an intervention. In studies where there was randomisation at the clinic level all women may have been exposed to the same intervention, and contamination between groups would thereby be reduced, but there may still have been a risk of response bias if outcomes were reported to staff providing care.
In 19 of the 52 studies contributing data there was an attempt made to blind those staff assessing outcomes. However, it was not clear whether these attempts at blinding were successful. While interviewers collecting outcome data were frequently described as "blind" to group status, mothers may well have revealed whether or not they had received an intervention. For outcomes such as reported breastfeeding, lack of blinding, or unsuccessful blinding of outcome assessors, may represent a serious source of bias.
Incomplete outcome data
We had prespecified that we would not include data for any outcome where there were missing data for more than 25% of the randomised group. Loss to follow-up was a particular problem in studies where women were recruited in the antenatal period and, as we have described above, we have not included any outcome data from 10 studies that were otherwise eligible for inclusion in the review because of high levels of attrition for all outcomes.
For some of those studies contributing data there was still considerable loss to follow-up, and loss was not always balanced across randomisation groups. In the study by Albernaz 2003, almost a quarter of the sample was lost to follow-up, and more than 20% were lost in the Di Meglio 2010 and Vitolo 2005 trials. In three studies, we were only able to use limited outcome data as at later data collection points attrition exceeded 25% of the randomised sample (Hoddinott 2009; Petrova 2009; Serafino-Cross 1992), and in the study by Wrenn 1997, loss was not balanced across treatment groups; even moderate attrition may be a serious source of bias if loss is not balanced both in terms of the amount of loss and the reasons for loss to follow-up.
We assessed bias in most of the studies included in the review from published study reports. In most cases we did not have access to the trial registration or protocol. Under these circumstances assessing risk of bias due to selective reporting bias is very difficult. For this reason, we assessed all of the studies as being of unclear risk of bias for this domain.
Other potential sources of bias
We have noted any other concerns about bias (including any apparent baseline imbalance between randomised groups) in the Characteristics of included studies tables along with further information about the judgements we made about risk of bias for each included study. The quality of the studies was very mixed and most of the studies had some methodological weakness, or did not provide good information about methods. It is important that the mixed quality of the evidence is taken into account in the interpretation of results.
Effects of interventions
Interventions to support breastfeeding versus usual care: 52 studies
The focus of this review is on breastfeeding support rather than on interventions to promote breastfeeding initiation which is addressed in another related Cochrane review (Dyson 2005). In this review we wanted to examine whether support would reduce the number of women who stopped breastfeeding early. For those studies with an antenatal component we cannot be certain that all women randomised actually started breastfeeding and received a postnatal support intervention. We carried out analysis on an intention to treat basis and all women are accounted for in the analysis whether or not they started breastfeeding and whether or not they received the intended support intervention. For primary outcomes the denominators are the number of women randomised and the women who are described as having “stopped” breastfeeding may include some women who may not have initiated or established breastfeeding.
The main outcome measures in the review are the effects of the interventions on duration of any, or exclusive breastfeeding up to specified points in time. Some studies reported exclusive breastfeeding rates and provided a clear definition of what this meant, but others were ambiguous and it was difficult for us to ascertain whether the infant was fed breast milk alone. For outcomes relating to any breastfeeding it was not always clear in study reports whether this meant that babies were predominantly or only occasionally receiving breast milk, and readers should be aware that definitions varied in different trials, and at different time points in the same trial as weaning foods were gradually introduced.
For cluster-randomised trials, where sufficient information was provided, we adjusted the sample sizes and event rates to take account of the design effect. Therefore, where we have provided information about the number of women in each analysis this represents the effective (adjusted) sample size (Donner 2000). In the analyses the cluster-randomised trial by Tylleskar et al carried out in three African countries has been entered and reported as three separate studies with adjustment of the sample size for each outcome using different reported ICCs for each country (Tylleskar 2011a (Burkina Faso); Tylleskar 2011b (Uganda); Tylleskar 2011c (South Africa)).
The main summary outcome measure was cessation of any breastfeeding at the time of the last study assessment up to six months. In the meta-analysis for this outcome we have included 40 trials with 14227 women (effective sample size). On average, interventions to support breastfeeding appear to have a beneficial effect on the number of women continuing breastfeeding beyond six months, with fewer women in the groups receiving support stopping breastfeeding by this time (average risk ratio (RR) 0.91, 95% confidence interval (CI) 0.88 to 0.96; 95% prediction interval 0.74 to 1.12) ( Analysis 1.1). Overall, 50.9% of those receiving support interventions had stopped any breastfeeding by six months compared with 55.5% of controls (unweighted percentages). However, there was moderate heterogeneity for this outcome, and although the average treatment effect was positive, the wide prediction interval indicates that the effect may not be beneficial in all settings. Results should therefore be interpreted with caution (heterogeneity: tau² = 0.01, I² = 56%, Chi² test for heterogeneity P < 0.0001)). Visual inspection of the funnel plot generated for this outcome suggested that there was some asymmetry with results from smaller studies tending to show a greater positive treatment effect (Figure 3). The Harbord 2006 test for small-study effects was significant (P = 0.009) (data not shown). Sensitivity analysis using only studies assessed as low risk of bias for allocation concealment demonstrated a similar positive treatment effect on breastfeeding at up to six months ( Analysis 1.8).
|Figure 3. Funnel plot of comparison: 1 All forms of support versus usual care, outcome: 1.1 Stopping breastfeeding (any) before last study assessment up to 6 months.|
Thirty-three studies with 11961 women reported the number of women who had stopped exclusive breastfeeding at up to six months. Women in the intervention groups were less likely to have stopped exclusive breastfeeding before six months (average RR 0.86, 95% CI 0.82 to 0.91); while 73.9% of women in the intervention groups had stopped exclusive breastfeeding by this time, this applied to 83.1% of women in control groups (unweighted percentages) ( Analysis 1.2). There was considerable variation in the size of the treatment effect amongst these studies and the wide prediction interval suggests that in some studies support may not be beneficial (heterogeneity: Tau² = 0.02, I² = 97%, Chi² test for heterogeneity P < 0.00001; 95% prediction interval 0.64 to 1.15). Sensitivity analysis using only studies assessed as low risk of bias for allocation concealment revealed that results still significantly favoured the intervention groups, although the effect size was considerably reduced in the studies at low risk of bias (RR 0.94, 05% CI 0.90 to 0.98; 95% prediction interval 0.76 to 1.17) compared with those at unclear or high risk of bias (RR 0.63, 95% 0.45 to 0.89) which suggests that the treatment effect may be partly due to bias ( Analysis 1.9). Visual examination of a funnel plot for this outcome suggested that the treatment effect may have been more pronounced in smaller studies and Harbord's test for asymmetry was significant (P = 0.003) (Figure 4).
|Figure 4. Funnel plot of comparison: 1 All forms of support versus usual care, outcome: 1.2 Stopping exclusive breastfeeding before last study assessment.|
Stopping breastfeeding before four to six weeks was reported in 25 studies with 8513 women. Women receiving support interventions were less likely to stop breastfeeding before six weeks (average RR 0.88, 95% CI 0.81 to 0.96) although there was considerable variation in the results from individual studies (heterogeneity: Tau² = 0.02, I² = 50%, Chi² test for heterogeneity P = 0.002; 95% prediction interval 0.65 to 1.19) ( Analysis 1.3) (Figure 5). Women in the intervention groups were also less likely to abandon exclusive breastfeeding by six weeks compared with women in the control groups, although results should be interpreted with caution as the size of the treatment effect varied considerably in different studies and the wide prediction interval for this outcome suggests that in some settings the intervention may not be beneficial (average RR 0.74, 95% CI 0.61 to 0.89; 24 studies, 7693 women), (heterogeneity: Tau² = 0.20, I² = 98%, Chi² test for heterogeneity P < 0.00001; prediction interval 0.29 to 1.91) ( Analysis 1.4), Again, there was some evidence that the treatment effect may be partly due to bias; sensitivity analysis including only those studies assessed as being at low risk of bias for allocation concealment showed that results still favoured the intervention group although the treatment effect was less pronounced in the studies at lower risk of bias and for any breastfeeding the result was borderline for statistical significance ( Analysis 1.10; Analysis 1.11). Visual examination of the funnel plot for this outcome suggested that the treatment effect may have been more pronounced in smaller studies and the test for asymmetry was significant (Figure 6).
|Figure 5. Funnel plot of comparison: 1 All forms of support versus usual care, outcome: 1.3 Stopping breastfeeding (any) at up to 4-6 weeks.|
|Figure 6. Funnel plot of comparison: 1 All forms of support versus usual care, outcome: 1.4 Stopping exclusive breastfeeding at up to 4-6 weeks.|
Analysis of results at different periods of follow-up presented us with some challenges in interpreting the data. There was variability between the studies regarding the time points when data were collected, therefore, caution has to be exercised when interpreting the trends. However, analysis of results at different periods of follow-up suggest that the benefit of all forms of support was present at all time points up to nine months ( Analysis 1.5).
Health outcomes for mothers and babies
Few trials reported health outcomes and due to variation in outcomes reported, and the time at which different outcomes were measured, it was not possible to combine results in meta-analysis.
Few trials reported mothers’ satisfaction or babies’ health outcomes and due to variation in the outcomes reported, times at which different outcomes were measured and missing data, it was not possible to combine results in meta-analyses.
Health outcomes for babies
Neonatal or infant morbidity outcomes were reported by study group in 11 studies. The PROBIT study (Kramer 2001) found a significant reduction in the risk of one or more gastrointestinal infections and of atopic eczema in the clusters receiving care from health professionals who had received the WHO/UNICEF Baby Friendly Initiative training. No significant reduction in respiratory tract infection was found. The PROBIT team have published several follow-up studies reporting child health outcomes (see Kramer 2001 References to included studies). Froozani 1999 observed a significant reduction in the mean number of days of gastrointestinal illness in the group receiving support but no significant difference in respiratory illness. The number of babies reported to have suffered diarrhoea within the last fortnight at three months was reduced in the intervention groups in all three study areas in the large cluster trial in three African countries, and at six months fewer babies in the intervention group were reported to have had diarrhoea in Burkina Faso and Uganda, although not in South Africa (Tylleskar 2011a; Tylleskar 2011b; Tylleskar 2011c). Bhandari 2003 found prevalence of diarrhoea at seven days was lower in the intervention than in the control communities at three months (odds ratio (OR) 0.64, 95% CI 0.44 to 0.95) and six months (OR 0.85, 95% CI 0.72 to 0.99). Morrow 1999 reported that at three months postpartum, fewer intervention (12/96) than control (9/34) infants had had an episode of diarrhoea (P = 0.029).
Bunik 2007 reported that 40/161 babies in the intervention required health care in the first month of life while this applied to 65/180 in the control group. Pugh 2002 (n = 41) reported that infants in the intervention group had fewer visits to the healthcare provider for both checkups and sick visits and significantly fewer prescriptions (P < 0.05) than control group infants. Frank 1987 and Petrova 2009 found no difference in re-hospitalisation rates between infants in the intervention and control groups. In the study by Bashour 2008 a broad range of outcomes relating to infant morbidity was reported, however, results were difficult to interpret as the intervention also included advice relating to immunisations and baby care. Quinlivan 2003 reported a reduction in adverse neonatal outcomes (infant death, severe non-accidental injury and non-voluntary foster care) in the intervention group (2/65) compared with the control group (9/71) (RR 0.24, 95% CI 0.32 to 1.52).
Maternal satisfaction with care
Maternal satisfaction with care was reported by study group in six studies. Jones 1985 found that mothers in the intervention group were more satisfied with the help they received than were mothers in the control group. When interviewed at the end of the study by Morrow 1999, 66% of mothers in the intervention group said the most important source of infant feeding advice was a peer counsellor, followed by a physician (19%) and their mothers (7%); in the control group, 50% listed a physician as their most important source, followed by their mother (22%) and a peer counsellor (2%). Graffy 2004 found that more women in the intervention group than in the control group said their most helpful advice came from counsellors rather than from other sources. In Kools 2005, opinions of mothers about feeding advice from caregivers were no more positive in the intervention group than in the control group, except for slightly less contradictory feeding advice (P = 0.04). Ekstrom 2006 found mothers in intervention clusters were more satisfied with emotional and informative support during the first nine months postpartum than mothers in control clusters. Bashour 2008 reported over 80% of the women in each group were happy about their experiences during the postnatal period, with no significant differences between the groups.
Maternal satisfaction with feeding
Maternal satisfaction with feeding was reported in 11 studies. Dennis 2002 found that significantly more mothers in the peer support group than in the control group were satisfied with their infant feeding experience. In the study by Petrova 2009 over 90% of women in both groups reported they were satisfied with their breastfeeding experience, with no statistically significant differences between the groups. Hoddinott 2009 found no significant differences in maternal satisfaction with breastfeeding between intervention and control localities.
de Oliveira 2006 reported a range of breastfeeding problems at seven and 30 days and overall, the intervention group appeared to have fewer problems with nipple pain and breast engorgement at both time points. In the study by Hopkinson 2009 outcomes relating to breastfeeding problems were reported including low milk supply, breast engorgement, difficulty breastfeeding, breast pain and exhaustion. Results were not consistent however; women in the intervention group had more positive outcomes for some problems (e.g. engorgement and breast pain). Labarere 2005 reported that similar numbers of women in the intervention and control groups reported breast pain and mastitis although fewer women in the intervention group (26/112) reported having "not enough milk" compared with women in control groups (43/114). Bashour 2008 reported the number of women complaining of breast engorgement; there were no clear differences between groups. Pugh 1998 found no differences between groups in mean maternal fatigue scores at six months. McDonald 2010 found no statistically significant differences between the groups in breastfeeding problems, though the problems experienced changed over time; engorgement, unsettled baby, nipple soreness and attachment difficulty were reported more frequently at two months, and low milk supply and unsettled baby at six months.
McQueen 2011 found no significant difference between intervention and control group mothers in breastfeeding self-efficacy scores. Kronborg 2007 found mothers in the intervention group reported more confidence than those in the control group about not knowing the exact amount of milk their babies had received when being breast fed.
There was considerable variation between the trials in terms of the interventions examined, the standard care offered to women, and the background breastfeeding initiation rates in the various study settings. We wanted to explore whether different types of support and settings were associated with different or more pronounced treatment effects. Therefore, for the review's four primary outcomes we carried out subgroup analysis to explore the impact of interventions involving different types of supporter (professional versus lay person, or both); types of support (face-to-face versus telephone support or both); timing of support (antenatal and postnatal versus postnatal alone); whether the support was proactive (scheduled contacts) or reactive (women needed to request support); and whether support interventions had similar effects in settings with different background breastfeeding initiation rates (low, medium or high background rates).
Who delivered the support
For our four primary outcomes, we examined whether the treatment effect was similar where the support was delivered by professionals as opposed to non-professionals (lay support) or both. For cessation of any breastfeeding at up to six months it appeared that support from non-professionals was associated with an increased treatment effect (RR 0.85, 95% CI 0.77 to 0.93), compared with support from professionals or both (RR 0.94, 95% CI 0.88 to 0.99 and RR 0.97, 95% CI 0.91 to 1.03 respectively), ( Analysis 2.1), although the test for subgroup differences was borderline for statistical significance (P = 0.05, I² = 66.4). For cessation of any breastfeeding by four to six weeks) there were no clear differences between subgroups; for this outcome there was considerable within subgroup heterogeneity and there were no significant differences between subgroups ( Analysis 2.3). For cessation of exclusive breastfeeding at up to six months the treatment effect appeared to be greater where the intervention was delivered by non-professionals (lay support) (average RR 0.74, 95% CI 0.64 to 0.87) compared with professionals (average RR 0.93, 95% CI 0.88 to 0.98) or both (average RR 0.76, 95% CI 0.44 to 1.32 ( Analysis 2.2). The test for subgroup differences for this outcome was statistically significant (Chi² = 7.67, df 2, P = 0.02, I² = 73.9%). This difference was consistent with cessation of exclusive breastfeeding at four to six weeks; again, the effect size was more pronounced with lay support than with professional support, ( Analysis 2.4). The test for subgroup differences was significant (Chi² = 6.44, df 2, P = 0.04, I² = 68.9%). However, in view of considerable within-subgroup heterogeneity, these findings should be interpreted with caution. Further, as we discussed above, there was some evidence that more pronounced treatment effects were associated with studies at higher risk of bias; this could potentially confound any differences between subgroups.
Type of support
We compared different types of intervention (support provided predominantly by face-to-face contact, predominantly by telephone, or by both face-to-face and telephone contact) for our primary outcomes. For cessation of exclusive breastfeeding there was some evidence that face-to-face support was associated with a greater positive treatment effect compared with either telephone support or mixed telephone and face-to-face support. For cessation of exclusive breastfeeding at up to six months women who received support face-to-face were almost 20% less likely to have given up exclusive breastfeeding by the last study assessment up to six months compared with those in the control groups (average RR 0.81, 95% CI 0.75 to 0.88), ( Analysis 3.2). There was no significant treatment effect for support that was predominantly by telephone, or that involved both face-to-face and telephone contact (average RR respectively: 1.00, 95% CI 0.99 to 1.01; average RR 0.98, 0.94 to 1.02) ( Analysis 3.2). The test for subgroup differences suggested that the difference between subgroups was statistically significant (Chi² = 27.52, df 2, P = 0.00001, I² = 92.7%).
This difference between subgroups persisted for cessation of exclusive breastfeeding at up to four to six weeks. Again, while there was no significant difference between control and intervention groups for predominantly phone and mixed support (RR 0.96, 95% CI 0.68 to 1.35; RR 0.94, 95% CI 0.88 to 1.01), ( Analysis 3.4), there was a positive treatment effect for those women receiving face-to-face support although there was considerable heterogeneity within this subgroup (average RR 0.62, 95% CI 0.51 to 0.77). The test for between subgroup differences was significant (Chi²= 13.73, df = 2, P < 0.001, I² = 85.4%).
These differences between subgroups did not apply to cessation of any breastfeeding at last study assessment or at up to four to six weeks; for these outcomes there was high heterogeneity within subgroups, and the tests for subgroup differences were not significant ( Analysis 3.1; Analysis 3.3).
When the support was offered
We examined whether offering support with an antenatal component rather than postnatal support alone was associated with any difference in treatment effect. The results were similar in both subgroups for all of our four primary outcomes and there were no statistically significant subgroup differences, ( Analysis 4.1; Analysis 4.2; Analysis 4.3; Analysis 4.4).
Proactive versus reactive support
We had planned to carry out formal subgroup analysis by whether support was proactive or reactive but due to the fact that most interventions included at least one scheduled contact (proactive), we did not think that this way of categorising studies would shed light on types of interventions that were effective or ineffective. However, in five studies the way in which support was offered differed substantively from other studies in that women were expected to access the support and it was not delivered directly to them (Graffy 2004; Hoddinott 2009; Labarere 2005; Morrell 2000; Winterburn 2003). None of these studies found a difference in outcomes between control and intervention groups. We will return to this issue in the discussion.
Background breastfeeding initiation rates in study settings
We were interested in whether or not background rates of breastfeeding in different settings had any impact on the success of interventions. We divided the studies into three groups: those carried out in settings where 80% or more women initiated breastfeeding (high background initiation), where between 60% to 80% initiated breastfeeding (intermediate) or where breastfeeding initiation rates were less than 60% (low). These groups showed an inverse relationship with World Bank country income groups. The studies with high background rates of breastfeeding initiation were set in countries from all the World Bank country income groups, however, the four studies from low-/low-middle-income countries had the highest rates (more than 95%). All the studies with intermediate or low background rates of breastfeeding initiation were undertaken in high-income countries.
While there was no clear differences between subgroups for cessation of any breastfeeding at up to six months ( Analysis 5.1), it appeared that for cessation of exclusive breastfeeding there were some differences between subgroups. Interventions were associated with a more pronounced effect on exclusive breastfeeding at up to six months in settings where there were high background rates of breastfeeding initiation (average RR 0.83, 95% CI 0.78 to 0.89) compared with areas where there was intermediate or low background initiation rates (average RR respectively 0.89, 95% CI 0.79 to 1.01; and RR 1.00, 95% CI 0.99 to 1.01), ( Analysis 5.2). The test for subgroup differences was statistically significant despite considerable within group heterogeneity (Chi² = 27.5, df = 2, P < 0.0001, I² = 92.7%). Results were even more pronounced for cessation of exclusive breastfeeding at up to four to six weeks with interventions seeming to be most effective for women living in areas with high background initiation rates (average RR 0.61, 95% CI 0.47 to 0.80) compared with areas with intermediate or low rates (average RR respectively 0.81, 95% CI 0.68 to 0.96; and RR 0.97, 95% CI 0.86 to 1.08), ( Analysis 5.4), (test for subgroup differences: Chi² = 10.26, df = 2, P < 0.006, I² = 80.5%). The same pattern persisted for cessation of any breastfeeding at up to four to six weeks with areas where background breastfeeding rates were high having a more pronounced treatment effect, although the test for subgroup differences did not reach statistical significance ( Analysis 5.3).
Intensity of the intervention: the number of postnatal contacts
We examined whether different numbers of postnatal contacts were associated with any difference in treatment effect. We divided the studies into four subgroups: unspecified or no direct contacts (for example in studies that involved staff training rather than direct contacts with women); less than four postnatal contacts; between four and eight contacts; and more than eight contacts. For any breastfeeding there were no clear subgroup differences, ( Analysis 6.1; Analysis 6.3). For exclusive breastfeeding at the final study assessment there was evidence of subgroup differences, although there was no clear "dose-response" effect; the most pronounced treatment effect was associated with between four and eight postnatal contacts (average RR 0.71, 95% CI 0.60 to 0.84) (test for subgroup differences P = 0.02, I² = 71%), ( Analysis 6.2). However, as we discussed above, there was some evidence that more pronounced treatment effects were associated with studies at higher risk of bias; this could potentially confound any differences between subgroups. For exclusive breastfeeding at up to four to six weeks the test for subgroup differences did not reach statistical significance, although again women receiving between four and eight postnatal contacts were the most likely to be still exclusively breastfeeding at this time-point, ( Analysis 6.4).
Summary of main results
This substantively updated review provides evidence that breastfeeding support interventions increase the number of women continuing to breastfeed, and the number of women continuing to exclusively breastfeed, at up to six months and at up to four to six weeks. The size of the treatment effects varied considerably in different trials, and average treatment effects may not be applicable in different settings. The subgroup analysis suggested that face-to-face support was associated with a greater treatment effect than telephone support for exclusive breastfeeding, and that interventions had an increased effect on exclusive breastfeeding in areas where background breastfeeding initiation was high.
The 52 trials included span the years from 1979 to 2011, with 37 (71%) having been published since 2000. They were conducted in 21 countries, with 37 (55% of participants) being conducted in high-income countries, two in low-income countries (one in Bangladesh, one in Burkino Faso, Uganda and South Africa) and the remainder in low-to-middle income countries. These numbers indicate that the challenge of supporting women to breastfeed is both longstanding and international; this is also reflected in the continuing low rates of duration and exclusivity of breastfeeding in many countries, despite increasing availability of good quality evidence of the scale of its public health impact.
A striking aspect of this updated review is the heterogeneity of the support interventions, and the diversity of setting and of standard care. Interventions deemed by researchers to be ‘supportive’ included some where it was difficult to see how women might actually feel supported, especially when the support service provided was one they had to ask for, or travel a distance to get to (e.g. Graffy 2004; Hoddinott 2009), or where there was only one scheduled contact with the support person. Having said that, this updated review has shown that the effect of supportive interventions is robust across settings and population groups, and results from a wide range of interventions.
Overall completeness and applicability of evidence
This review adds 18 trials to its predecessors (Britton 2007; Sikorski 2002), and the number of mother-infant pairs in these studies has increased to 56,451 from 29,385 in Britton 2007. The reporting of the included studies was, however, often not comprehensive - lacking, for example, in terms of a description of the components of the support intervention, details of the training and qualifications of the supporters, the definitions used of the extent of breastfeeding and in the description of adherence to the support protocol. There was also a failure to present details of the interventions and of the standard care available to both intervention and comparison groups. Very few of the trials described a theoretical basis for the intervention tested, with the result that the findings are difficult to explain or to replicate. There has been no notable improvement in study reporting or quality, with 26 out of the 52 trials contributing data (50%) reporting an approach to allocation concealment considered at low risk of bias compared to 15 of the 34 trials (44%) in the previous review.
Interventions offered were very diverse, as was the provision of standard care. Interventions included, for example, one individual session in hospital, offering women the opportunity to attend a group session in community settings, telephone support, and multiple one-to-one visits at home over several months. Five studies offered the intervention in the context of Baby Friendly accreditation of the hospital, and are unlikely to be generalisable to settings where this standard of care is not available to all women.
Study end-points also varied widely, with some substantial gaps of many months between the completion of the intervention and the last study outcome assessed. Very few interventions continue for longer than six months, and many only offered support in the early days or weeks. These factors, together with the range of different settings and population subgroups studied, should urge some caution in the interpretation of the analysis of pooled data.
Despite this caution, the overall benefit found from all forms of support interventions has been explored with subgroup and sensitivity analyses and is moderately robust following exclusion of the methodologically weaker trials. In this review, the greatest effect of breastfeeding support interventions on reducing cessation of breastfeeding before six months occurred in communities with high (over 80%) levels of breastfeeding initiation. This suggests that work to promote breastfeeding at a population level should continue as one strategy to increase breastfeeding duration and exclusivity (Dyson 2009).
While the effect size of support interventions on reducing the cessation of any breastfeeding is modest, there is evidence of a greater effect on the prolongation of exclusive breastfeeding. There was a reduction in the cessation of exclusive breastfeeding within the first six months and at up to four to six weeks when lay support was used, although the test for statistical significance was borderline at the earlier time point. Professional support, lay support and combinations of lay and professional support did not differ significantly in their effect on the continuance of any breastfeeding at either time-point, although the results were consistent with those for exclusive breastfeeding.
Few conclusions can be drawn about the impact on the health and wellbeing of mothers and babies in these studies, as very few studies measured such outcomes. Those that did identified a positive impact. This represents a missed opportunity to measure such key outcomes within a randomised trial context.
We have explored a range of possible reasons to explain the significant heterogeneity in the findings. As noted above, included studies were very varied in setting, population group studied, content, timing and intensity of the intervention, whether it was proactively offered to women or available only if they asked for it, the standard care available, staff training programmes, and the type and timing of the outcomes measured. Strategies that depend mainly on face-to-face support appear more effective than those that rely primarily on telephone contact. The duration of the intervention also seems to be an important factor. Interventions that relied on one session in hospital are very different from interventions where women receive repeated home visits. We attempted to examine this by assessing the intensity of the intervention, and found that studies with four to eight visits seemed to be associated with a more pronounced treatment effect. Care is needed in the interpretation of this finding as there is inconsistent reporting due to variations in the timing of outcome assessments, and the settings of studies and the population groups included in studies with more face-to-face visits also varied. It is likely that support will be most effective when it reflects the local needs of the population. It was notable that none of the five studies where women were expected to access support without any proactive element found a difference in outcomes between control and intervention groups. Four of these five were UK-based studies, which may help to explain the lack of effect seen in recent UK trials (Hoddinott 2011).
Quality of the evidence
We considered that the overall methodological quality of trials included in the review was mixed, with approximately half of the included studies using methods that we assessed as being at low risk of bias for generating the randomisation sequence and concealing group allocation. When we carried out sensitivity analysis including only those studies at low risk of bias for allocation concealment, the results were not substantially different. A potentially important source of bias in these studies was the general lack of blinding. For support interventions trialists would face considerable difficulties in blinding staff, women and outcome assessors to treatment group. Even where there was an attempt made to blind outcome assessment there would still be a high risk of response bias for outcomes relying on self-report such as any or exclusive breastfeeding. A further possible source of bias was loss to follow-up and missing outcome data. Although we did not include outcome data where there was attrition of more than 25%, we are aware that even lower levels of attrition are problematic, particularly where loss was not balanced in different arms of trials. To avoid problems associated with attrition, we carried out intention-to-treat analysis for our primary outcomes; that is, we assumed that all women who were lost to follow-up had stopped breastfeeding by given time points. This is likely to have diluted overall treatment effects but these estimates may be more appropriate given the possibility of response bias and the increased likelihood of women who stopped breastfeeding dropping out before those who continued.
Potential biases in the review process
We are aware that there was a risk of introducing bias at all stages in the review process. In this updated version of the review two authors independently assessed eligibility for inclusion and carried out data extraction, and data checks were carried out by a third author. However, assessing risk of bias is not an exact science and involves judgement. We would encourage readers to consider the tables where the characteristics of included studies are summarised, to assist them in interpreting results.
Agreements and disagreements with other studies or reviews
These findings are similar to previous versions of this review, and the findings of other reviews (e.g. Dyson 2009; Guise 2003; Renfrew 1995), in that peer and professional support have been shown to be effective interventions. We concur with others (e.g. Hoddinott 2011; Renfrew 2007) that it is critically important to identify the characteristics of support that may make this important but heterogenous intervention more or less effective in different circumstances.
Implications for practice
All women should be offered support to breastfeed their babies to increase the duration and exclusivity of breastfeeding. Healthcare settings should provide such trained support as standard. Support is likely to be more effective in settings with high initiation rates, so efforts to increase the uptake of breastfeeding should be in place. Support may be offered either by professional or lay/peer supporters, or a combination of both. Strategies that rely mainly on face-to-face support are more likely to succeed. Support that is only offered when women seek help is unlikely to be effective; women should be offered ongoing visits on a scheduled basis so they can predict that support will be available. Support should be tailored to the setting and the needs of the population group.
Implications for research
There are several areas which require further study in the light of the results of this review.
The review authors wish to thank those study authors who were very helpful in responding to queries.
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.
Work on this review was supported in part by a grant from the National Institute for Health Research Health Technology Assessment programme, grant number 10/106/01.
Data and analyses
- Top of page
- Authors' conclusions
- Data and analyses
- What's new
- Contributions of authors
- Declarations of interest
- Sources of support
- Differences between protocol and review
- Index terms
Appendix 1. Methods used to assess trials included in previous versions of this review
Titles and abstracts of the electronic searches were assessed for inclusion by a review author and a research assistant (Felicia McCormick (FM), Natasha Danson). All the included trials offered an intervention to breastfeeding women with the purpose of encouraging continued breastfeeding. All articles identified were available in English. Two review authors independently read articles identified via the search strategy to determine inclusion or exclusion (Cathryn Britton (CB), FM). Any differences in opinion were resolved in consultation with a third author (Mary Renfrew). When information regarding the study was unclear, we attempted to contact authors of original reports to provide further details. Angie Wade and Sarah King provided statistical advice and review.
We designed a data extraction form. Two authors (CB, FM) used data extraction forms and quality appraisal forms independently. One author extracted and the second author checked the data. Disagreements were resolved through discussion between the authors. We identified 34 randomised or quasi-randomised controlled trials from 14 countries as eligible for inclusion in this review. We extracted the following study characteristics and entered them in the table of included studies: country, setting, demographic data on study group and controls, study design, randomisation procedure, intervention package, length and completeness of follow-up, description of withdrawals and drop-outs, blinding of assessors and outcome measures. We used Review Manager software (RevMan 2003) to double enter all the data.
We assessed the method of allocation concealment used in each study using criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2005). We categorised studies according to whether the method of allocation concealment reported was judged to have been adequate (A), unclear (B) inadequate (C), or if allocation was not concealed (D). We also checked study reports for clear descriptions of inclusion and exclusion criteria; randomisation methods; withdrawals and drop-outs; statistical analysis used; blinding of outcome assessment; and intention-to-treat analysis. Methods used for generation of the randomisation sequence are described in the 'Characteristics of included studies' table. Included trials had a minimum of 75% initial follow-up. When included trials reported data at more than one time point and follow-up rates fell, we included only data from time points where follow-up rates were at least 75% in the analysis.
We carried out statistical analysis using RevMan 2003. We analysed data on an intention-to-treat basis whenever possible, even if intention-to-treat analysis had not been used in the study report. When cluster-randomised trials were incorporated, we calculated effective sample sizes and entered these into the meta-analyses. We determined effective sample sizes via calculation of the intraclass correlation coefficient, where the data were available, or through consideration of the relative sizes of the confidence intervals obtained from analyses which did and did not correct for clustering of the outcomes.
We calculated relative risk as the preferred estimate of treatment effect. We preferred random-effects models to perform all meta-analyses since studies were clinically heterogeneous. We also undertook subgroup analyses of all studies offering support compared with those that had adequate allocation concealment; studies in settings with high, medium and low baseline breastfeeding initiation rates; support offered by professional, lay or a combination of professional and lay supporters; face-to-face, phone or balanced telephone and face-to-face contact; and postnatal support alone or support with an antenatal component.
Last assessed as up-to-date: 2 April 2012.
Protocol first published: Issue 3, 1998
Review first published: Issue 1, 1999
Contributions of authors
This update is based on the previous Cochrane review (Britton 2007).
Mary Renfrew was co-author of all the earlier versions of this review. In this update of the review she contributed to planning its restructure, assessment of study eligibility, analysis, drafting text for the Background, Discussion and Conclusions, and commented on review drafts.
Felicia McCormick was co-author of Britton 2007. In this version she contributed to planning its restructure, assessment of study eligibility, data extraction and analysis, drafting text for the Description of included studies, and commented on review drafts.
Angie Wade provided statistical advice for this and all the earlier versions of this review. She advised about including cluster-randomised trials in the analyses and commented on review drafts.
Beverly Quinn was involved in this update and contributed to assessment of study eligibility, data extraction, and commented on drafts.
Therese Dowswell was involved in this update and contributed to planning its restructure, assessment of study eligibility and data extraction. She set up the analyses, drafted text for the Methods and Results sections and commented on review drafts.
Declarations of interest
Sources of support
- University of York, UK.
- UK Medical Research Council, UK.
- NIHR, UK.TD is supported by the NIHR NHS Cochrane Collaboration Programme grant scheme award for NHS-prioritised centrally-managed, pregnancy and childbirth systematic reviews: CPGS 10/4001/02
Differences between protocol and review
The methods section has been updated and the review now focuses on healthy mothers with healthy term infants.
Medical Subject Headings (MeSH)
MeSH check words
Female; Humans; Infant
* Indicates the major publication for the study