Medications for increasing milk supply in mothers expressing breastmilk for their preterm hospitalised infants

Abstract

Background

Breastmilk remains the optimal form of enteral nutrition for term and preterm infants until up to six months postnatal age. Mothers of preterm infants who have not established suck feeds must express their breastmilk and often have difficulty in maintaining sufficient volume for their infants' needs (Donath 2008). In preterm infants, donor breastmilk reduced the occurrence of necrotising enterocolitis, when compared with formula feeds (McGuire 2003). Also, case‐control studies have suggested that breastmilk is associated with an improvement in feeding tolerance, a reduction in significant gastrointestinal infective events (Beeby 1992) and a reduction in late‐onset sepsis (Schanler 1999) when compared with formula feeds in preterm hospitalised infants.

Objectives

To assess the effect of medication given for at least seven days to mothers of preterm infants whose breastmilk is insufficient for their infants' needs on the outcomes of expressed milk volume and duration of breastfeeding.

Search methods

We searched the Cochrane Pregnancy and Childbirth Group's Trials Register (31 December 2011).

Selection criteria

Randomised and quasi‐randomised controlled trials of breastmilk‐augmenting medications (compared with placebo or with other augmenting medications) in mothers with preterm hospitalised infants whose breastmilk volumes failed to meet their infants' requirements. We did not include trials with a cluster‐randomised or cross‐over design.

Data collection and analysis

Both review authors independently assessed studies for inclusion, assessed risk of bias, and extracted data. Any differences were resolved by consensus. Data were checked for accuracy.

Main results

Two trials (involving 59 mothers) that examined the use of domperidone in a total of 59 mother‐infant pairs met the inclusion criteria. Meta‐analysis of these trials showed a modest increase in expressed breastmilk (EBM) of 99.49 mL/day (95% confidence intervals ‐1.94 to 200.92; random‐effects, T² 3511.62, I² 63%) in mothers given domperidone. Both trials gave the same dose of domperidone (10 mg three times per day) with a duration of seven days in the smaller trial and 14 days in the larger.

Neither trial showed significant improvements in longer‐term outcomes of breastfeeding in a preterm population and no adverse effects were reported.

Authors' conclusions

Two studies with a total of 59 mothers suggest modest improvements in short‐term EBM volumes when a medication is used after insufficient EBM occurs in mothers following preterm delivery. In both studies, the medication was commenced ≧14 days post delivery and following insufficient EBM supply with other lactation supports.

Currently, no studies support prophylactic use of a galactagogue medication at any gestation. Use of any galactagogue medication has only been examined at more than 14 days post delivery and after full lactation support has been given. Further trials should examine larger groups of preterm mothers and consider breastfeeding outcomes over a longer period.

Plain language summary

Medications for increasing milk supply in mothers expressing breastmilk for their hospitalised infants

Breastmilk remains the optimal form of enteral nutrition for term and preterm infants until up to six months postnatal age. Mothers of premature and sick infants are separated from their infants while they are receiving hospital‐based care. These mothers often have difficulty supporting lactation, when milk production is solely maintained by breast expression.

In preterm infants, expressed breastmilk (EBM) given by a nasogastric tube, until sucking can be established, has been shown to reduce a bowel disease called necrotising enterocolitis where parts of the bowel become injured or dies. Further evidence suggests that EBM might improve feeding tolerance and may reduce infection.

Trials of medications used to improve the breastmilk supply in mothers who have insufficient milk for their hospitalised preterm infants' needs have been reported in two randomised controlled studies involving 59 mothers. These two studies gave the women domperidone 10 mg three times a day when mothers had insufficient EBM, two to three weeks after delivery. These studies showed a modest improvement in EBM volume over the following one to two weeks. No side effects to mothers or infants were noted in these studies.

These medications should only be considered in mothers who have received full lactation support and are more than 14 days post delivery but have insufficient EBM for their infants' needs.

Background

Breastmilk remains the optimal exclusive form of nutrition for term and preterm infants until up to six months postnatal age and extensive evidence from multiple sources including the World Health Organization have outlined short‐ and longer‐term benefits from breastmilk feeding (Dyson 2005; Kramer 2002; NHMRC 2003; WHO 2002). Amongst randomised controlled trials (RCTs) in preterm infants, donor breastmilk reduced the occurrence of necrotising enterocolitis, when compared with formula feeds (McGuire 2003). Also, data from case‐control studies have suggested that breastmilk is associated with a reduction in feed intolerance (in preterm infants defined as excess gastric residual milk or vomiting Ng 2008), a reduction in significant gastrointestinal infective events (Beeby 1992) and a reduction in late‐onset sepsis (Schanler 1999) when compared with formula feeds in hospitalised infants.

Infants who are born preterm, or are otherwise ill, are dependent on expressed breastmilk (EBM) for a substantial period of their hospitalisation. A high proportion of mothers have been reported to initiate lactation, and despite recommendations from health professionals and available support, a significant proportion of these mothers cease breastfeeding over the initial postnatal months (ABS 2003; Donath 2008). A variety of significant socio‐economic, medical, cultural and health service factors are reported to have an influence on observed breastfeeding rates (McCarter 2001; Scott 1999). In particular, mothers of premature and sick infants are separated from their infants while their infants are receiving hospital‐based care. These mothers often have difficulty supporting lactation, when milk production is solely maintained by breast expression (Lawrence 1999). Population cross‐sectional reports suggest that the exclusive and partial breastfeeding rates for preterm infants are lower than in term infants at discharge from their birth hospital (Donath 2008; QPDC 2000). The most common reason cited by mothers for their cessation of breastfeeding has been a perceived or apparent 'insufficient milk supply' (ABS 2003; Brodribb 1998; Simic 2004).

Multiple interventions have been assessed in attempts to improve breastmilk supply in mothers whose lactation has been insufficient to meet their infant's needs. Interventions reported to increase breastmilk supply have included hand and mechanical breast expression, enhanced maternal support, galactagogue medications and complementary medicines (Brodribb 1998; Jones 2007; Lawrence 1999; Riordan 1999). Galactogogue medications have included medications thought to improve breastmilk supply by increasing milk production or milk release from the breast during expression or suckling.

This review will focus on randomised and quasi randomised controlled trials that have assessed the use of medications for improving breastmilk supply in mothers of hospitalised preterm infants. These mothers have received advice on supportive measures (in a hospital setting) including maternal health, expression frequency and technique to assist their breastmilk expression. Only those mothers where these supportive measures did not result in expressed milk that was sufficient to meet their infant's enteral requirements were considered for a trial of medication.

It is not clear from the literature over what minimum period a preterm infant must receive exclusive breastmilk feeds to obtain the well documented improvements in their outcome. Non randomised observational studies in preterm infants that have reported improved outcomes for late onset sepsis and feeding tolerance have generally compared infants who were exclusively breastmilk fed for most of their hospital stay with those receiving infant formula (Beeby 1992; Hylander 1998). The shortest randomised trials of exclusive EBM versus formula feeding that showed improved preterm outcomes used donor breastmilk for four weeks (Lucas 1992). We have included all randomised trials of galactagogue interventions that were given to mothers of preterm infants for at least seven days as shorter periods are unlikely to provide clinically significant differences in preterm outcome. Trials of galactagogue medications that were initiated before one week post delivery were excluded as this was judged to be prophylactic rather than rescue treatment for established EBM supply failure and this use of galactagogues is to be the subject of a separate review.

Objectives

Primary objective

To assess the effect of medication taken by mothers to augment the breastfeeding of their preterm hospitalised infants on the outcome of breastmilk supply (breastmilk volume and duration of breastfeeding where breastmilk from a donor is not included).

Secondary objective

To assess maternal and infant adverse effects from medications taken to augment breastfeeding, when compared with placebo.

Methods

Criteria for considering studies for this review

Types of studies

We considered RCTs and quasi randomised trials of breastmilk‐augmenting medications that were compared with placebo or with other augmenting medications. It is unlikely that cross‐over designs will be a valid study design for Pregnancy and Childbirth reviews and so, have been excluded. Cluster‐randomised trials were not considered a valid method for assessment of a medication to alter EBM supply.

Types of participants

Breastfeeding mothers whose preterm (less than 37 weeks' gestation) infant/s required inpatient nursery care and who, despite support from health professionals, were not able to supply sufficient breastmilk for their infant's nutritional requirements. These breast fed preterm infants were predominantly fed using expressed milk via nasogastric tube until suck feeding could be established.

Types of interventions

Medications thought to increase breastmilk supply when administered to postpartum mothers. These medications include drugs to increase breastmilk production or breastmilk 'let down' where these satisfied study criteria.

Types of outcome measures

Primary outcomes

• Change in volume of EBM over at least seven days from commencement of trial medication or placebo. The inclusion of trials with EBM outcomes of at least seven days was used as we judged this to be the minimum assessable period for a clinically significant outcome on a preterm infant's feeding.

Secondary outcomes

• Proportion of total feeds within each mother‐infant pair as EBM.

• Maternal, exclusive and partial breastfeeding rates at hospital discharge. (Exclusive breastfeeding was defined as infants receiving only their mother's EBM or suckled breastmilk. Partial breastfeeding was defined as when part of a preterm infant's milk intake was not breastmilk.)

• Total duration of exclusive and partial breastfeeding.

• The rate of medication cessation for maternal/infant adverse reaction.

• Maternal satisfaction with medication.

• Maternal satisfaction with breastfeeding.

Search methods for identification of studies

Electronic searches

We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co‐ordinator (31 December 2011). 

The Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by the Trials Search Co‐ordinator and contains trials identified from: 

1. quarterly searches of the Cochrane Central Register of Controlled Trials (CENTRAL);

2. weekly searches of MEDLINE;

3. weekly searches of EMBASE;

4. handsearches of 30 journals and the proceedings of major conferences;

5. weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts. 

Details of the search strategies for CENTRAL, MEDLINE and EMBASE, the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service can be found in the ‘Specialized Register’ section within the editorial information about the Cochrane Pregnancy and Childbirth Group. 

Trials identified through the searching activities described above are each assigned to a review topic (or topics). The Trials Search Co‐ordinator searches the register for each review using the topic list rather than keywords.  

We did not apply any language restrictions.

Data collection and analysis

Selection of studies

Two review authors independently assessed for inclusion all the potential studies we identified as a result of the search strategy. We resolved any disagreement through discussion.

Data extraction and management

We designed a form to extract data. For eligible studies,at least two review authors extracted the data using the agreed form. We resolved discrepancies through discussion. We entered data into Review Manager software (RevMan 2011) and checked for accuracy.

When information regarding any of the above was unclear, we contacted authors of the original reports to provide further details.

Assessment of risk of bias in included studies

Two review authors independently assessed the risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We resolved any disagreement by discussion.

(1) Random sequence generation (checking for possible selection bias)

We describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.

We 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 described for each included study the method used to conceal allocation to interventions prior to assignment and assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.

We assessed the methods as:

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

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

• unclear risk of bias.   

(3) Blinding of participants and personnel (checking for possible performance bias) and outcome assessment (checking for possible detection bias)

We described for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We consider studies to be at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We assessed blinding separately for different outcomes or classes of outcomes.

We assessed the methods as:

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

• low, high or unclear risk of bias for personnel;

• low, high or unclear risk of bias for outcome assessment.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

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

We assessed methods as:

• low risk of bias (e.g. no missing outcome data; missing outcome data balanced across groups);

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomisation);

• unclear risk of bias.

(5) Selective reporting (checking for reporting bias)

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

We assessed the methods as:

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

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

• unclear risk of bias.

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

We describe for each included study any important concerns we have about other possible sources of bias.

We assessed whether each study was free of other problems that could put it at risk of bias:

• low risk of other bias;

• high risk of other bias;

• unclear whether there is risk of other bias.

(7) Overall risk of bias

We made explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we considered it was likely to impact on the findings.  We explored the impact of the level of bias through undertaking sensitivity analyses ‐ seeSensitivity analysis. 

Measures of treatment effect

Dichotomous data

For dichotomous data, we planned to present results as summary risk ratio (RR) with 95% confidence intervals (CIs). 

Continuous data

For continuous data, we used the mean difference (MD) as outcomes were measured in the same way between trials.

Dealing with missing data

For included studies, we noted levels of attrition. We explored the impact of including studies with high levels of missing data (more than 20%) in the overall assessment of treatment effect by using Sensitivity analysis.

For all outcomes, we carried out analyses, as far as possible, on an intention‐to‐treat basis, i.e. we attempted to include all participants randomised to each group in the analyses, and all participants were analysed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial was the number randomised minus any participants whose outcomes were known to be missing.

Assessment of heterogeneity

We assessed statistical heterogeneity in each meta‐analysis using the T², I² and Chi² statistics. We regarded heterogeneity as substantial if T² was greater than zero and either I² was greater than 30% or there was a low P value (less than 0.10) in the Chi² test for heterogeneity. 

Assessment of reporting biases

In future updates of this review, if there are 10 or more studies in the meta‐analysis, we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually, using formal tests for funnel plot asymmetry. For continuous outcomes, we will use the test proposed by Egger 1997, and for dichotomous outcomes, we will use the test proposed by Harbord 2006. If asymmetry is detected in any of these tests or is suggested by a visual assessment, we will perform exploratory analyses to investigate this.

As there were only two included studies, we were unable to use a funnel plot to assess reporting bias.

Data synthesis

We carried out statistical analysis using the Review Manager software (RevMan 2011). We planned to use fixed‐effect meta‐analysis for combining data where it was reasonable to assume that studies were estimating the same underlying treatment effect: i.e. where trials were examining the same intervention, and the trials’ populations and methods were judged sufficiently similar. If there was clinical heterogeneity sufficient to expect that the underlying treatment effects differed between trials, or if substantial statistical heterogeneity was detected, we planned to use random‐effects meta‐analysis to produce an overall summary when an average treatment effect across trials was considered clinically meaningful. The random‐effects summary was treated as the average range of possible treatment effects and we discussed the clinical implications of treatment effects differing between trials. If the average treatment effect was not clinically meaningful we would not have combined trials.

We used random‐effects analyses, the results are presented as the average treatment effect with its 95% CI, and the estimates of  T² and I².

Subgroup analysis and investigation of heterogeneity

In future updates, if we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random‐effects analysis to produce it.

We did not pre‐specify any additional subgroup analyses.

In future updates of this review, for fixed‐effect inverse variance meta‐analyses, we will assess differences between subgroups by interaction tests. For random‐effects and fixed‐effect meta‐analyses using methods other than inverse variance, we will assess differences between subgroups by inspection of the subgroups’ CIs; non‐overlapping CIs indicate a statistically significant difference in treatment effect between the subgroups.

Sensitivity analysis

We undertook sensitivity analysis examining the possible effects of the incomplete data post randomisation in the Silva 2001 trial. As there were six mothers in this study who were lost post randomisation out of 20 randomised (30% attrition), we performed two sensitivity analyses. In the first analysis, the overall result was considered with the Silva 2001 trial excluded. In the second analysis, mean EBM values were substituted for missing data on the two mothers with published incomplete data and we re‐assessed the outcome of the meta‐analysis.

Results

Description of studies

Results of the search

The search strategy identified 18 studies for initial consideration. We included two studies in the review (Campbell‐Yeo 2010; Silva 2001). We excluded 15 studies, mainly due to short intervention times or insufficient outcome data. One trial is awaiting classification (Powe 2010).

Included studies

We identified two RCTs which assessed the effect of medications on expressed breastmilk volumes. The trial by Silva included 14 mother‐infant pairs (Silva 2001). The infants were preterm with a mean gestational age of 29.1 weeks and the mothers had insufficient milk supply to meet their infants' daily enteral feeding requirements. This trial assessed the effect of oral domperidone 10 mg three times daily for seven days compared with placebo and commenced in the fifth week post delivery. A second trial by Campbell‐Yeo 2010 included results for 45 mothers who had delivered infants before 31 weeks' gestation and who had insufficient expressed breastmilk (EBM) at ≥ three weeks post delivery. In this trial, mothers received domperidone 10 mg three times daily or placebo for 14 days.

Both studies used expressed breastmilk volume at baseline compared with the final day of the intervention period as the primary outcome. Silva 2001 measured domperidone levels in expressed breastmilk and maternal serum and prolactin levels in maternal serum. In the trial by Campbell‐Yeo 2010, maternal prolactin levels and EBM nutrient levels were measured.

SeeCharacteristics of included studies for further information.

Excluded studies

Gunn 1996 included 20 mother‐infant pairs. The authors assessed the volume of expressed breastmilk but also allowed suckling from the breast which reduced the precision of the final outcome. These infants were preterm from 26 to 34 weeks' gestational age and the intervention was human growth hormone 0.2 IU/kg/day (max 16 IU/day) given subcutaneously for seven days or placebo. The trial by Ehrenkranz 1987a assessed the effect of oral metoclopramide 10 mg three times daily for seven days and placebo, included eight mother‐infant pairs and had a randomised cross‐over design. The infants were preterm with a gestational age of 28.1 ± 0.5 weeks and their mothers had an unspecified decrease in their total expressed daily breastmilk volume. We excluded this cross‐over trial because of the confounding associated with no "washout" period between interventions and concern with insufficient data. Ehrenkranz 1987b assessed serum prolactin levels and lactation in mothers of premature infants. There was no drug intervention in this study. Fewtrell 2006 assessed the effect of oxytocin nasal spray on expressed breastmilk volumes. However, this intervention was only for five days. Hansen 2005 assessed the effect of oral metoclopramide, however, the intervention occurred when the infant was less than 96 hours of age and did not assess the adequacy of the breastmilk supply prior to randomisation. Hofmeyr 1985 used domperidone 10 mg three times daily for two days only and the outcomes measured were serum prolactin levels and serum and milk domperidone levels. James 2004 investigated the effect of domperidone and metoclopramide on expressed breastmilk volumes but the interventions were only for five days as was a trial of the use of oxytocin nasal spray by Ruis 1981. Lewis 1980 used metoclopramide for seven days, however, mothers were randomised on day‐one post caesarean section without assessment of their breastmilk supply and the infants were not preterm. Their outcome measure was successful breastfeeding at 10 days and at three months and they noted no significant difference in these outcomes. Mersmann 1996 assessed the effect of therapeutic touch on milk 'let down' without any medication intervention. Kauppila 1981 assessed the use of metoclopramide in term infants of breastfeeding mothers only. In the study by Wan 2008, a dose effect comparison of two doses of domperidone was assessed in six preterm mothers but no placebo evaluation was performed. Powe 2011 examined breastmilk composition on human recombinant prolactin. Loh 2007 is a RCT of metoclopramide versus placebo but there were no published data and we did not receive a response from the trial authors. Chong 2006 was a RCT of metoclopramide but we excluded it because the intervention was used prophylactically before breastfeeding was established and the participants were mothers with diabetes.

SeeCharacteristics of excluded studies for further information.

Risk of bias in included studies

Allocation

Silva 2001 used a random numbers table for allocation. Despite this blind randomisation, mothers in the placebo arm had much lower baseline EBM volumes, with placebo 48.2 ± 63.3 mL and the domperidone arm 112.8 ± 128.7 mL. The authors in Silva 2001 also noted that randomisation resulted in three mothers of multiple pregnancies (two triplet and one twin pregnancy) receiving domperidone with only one mother of a multiple pregnancy receiving placebo. They were unable to ascertain whether this biased their findings but speculated that it may have contributed to the higher volume of EBM at baseline in the domperidone group than in the placebo group. In the other study of domperidone, Campbell‐Yeo 2010 allocated intervention using a computer‐based code in blocks of four known only by off‐site pharmacy staff. Allocation concealment was considered adequately described in Silva 2001 and Campbell‐Yeo 2010.

Blinding

In the studies by Silva 2001 and Campbell‐Yeo 2010, participants and observers were blinded to the intervention medication or to placebo.

Incomplete outcome data

There was some concern in the Silva 2001 study that five of the 11 mothers randomised to receive domperidone did not complete the trial with one infant death and four mothers with incomplete milk records. In the placebo arm of this trial, one mother of the nine randomised had incomplete milk records. This high attrition rate in the domperidone arm may have biased the outcome but as the remainder of the study appeared well conducted, we judged the available results to be appropriate for analysis. In the second domperidone study (Campbell‐Yeo 2010), outcome data were not available for one mother who withdrew after randomisation but before treatment in the domperidone arm.

Selective reporting

We did not find any definite evidence of selective reporting.

Other potential sources of bias

We did not identify any other potential sources of bias.

Effects of interventions

Primary outcomes

The meta‐analysis of the two included studies of domperidone suggest a moderate benefit in daily EBM volume (mean difference (MD): 99.49 mL/day, 95% confidence interval (CI), ‐1.94 to 200.92; random‐effects, T² 3511.62, I² 63%) when mothers with insufficient EBM were given domperidone (Analysis 1.1). This result was derived from only 59 mothers and there was high heterogeneity between the trials with wide variance in the standard deviation of the response suggesting large differences in individual responses. Because of this heterogeneity, we used a random‐effects analysis which yielded a P value for overall effect of 0.05. Limited subgroup analysis failed to further explain this effect. Both studies used a medication intervention and compared this with placebo with all mothers otherwise receiving full lactation support. Silva 2001 found a significant increase in the mean volume of expressed breastmilk per day in their report. However, when the two mothers with no EBM data from day five were excluded and the results were re‐analysed using change in EBM from baseline to day seven rather than from day two to day seven as reported, the results were not significant in this study for domperidone (MD: 57.12 mL 95% CI ‐3.66 to 117.90, seeAnalysis 1.1 ). In the second study examining domperidone by Campbell‐Yeo 2010, there was a significant improvement in the mean volume of EBM over the 14 days of the trial, in the domperidone arm compared with the placebo arm (MD: 162.7 mL, 95% CI 52.5 to 272.9, seeAnalysis 1.1). Sensitivity analysis because of the 30% post randomisation loss in the Silva 2001 trial suggested that the overall outcome of intervention with domperidone would not be substantially changed if mean EBM values were substituted for missing EBM values or if the trial was excluded.

1.1. Analysis.

Comparison 1 Domperidone versus placebo, Outcome 1 Difference in volume of EBM per day.

Secondary outcomes

The secondary outcomes of the duration of partial or exclusive breastfeeding were reported for the two domperidone studies. In Campbell‐Yeo 2010, the partial or exclusive breastfeeding rate at discharge was reported as 54.6% (12 of 22) in the domperidone group and 52.2% (12 of 23) in the placebo group. The authors acknowledged high rates of domperidone use after the 14‐day intervention trial with subsequent domperidone exposure for 63.6% of the intervention arm and 41.7% of the placebo arm. Because of this confounding, the breastfeeding rates at discharge have been presented in this review as text only. In the study by Silva 2001, it was reported that the proportion of infants discharged home "who were breastfeeding" did not differ between the intervention and placebo groups but no quantitative results were given.

The rate of medication cessation for maternal/infant adverse reaction, maternal satisfaction with medication and satisfaction with breastfeeding was not reported in either trial. Both trials also measured prolactin levels. These outcomes were not considered in the objectives of this review. No side effects to mothers or infants were reported by Silva 2001 or Campbell‐Yeo 2010.

Discussion

Despite strong evidence supporting the feeding of preterm infants with their mother's breastmilk, there remain a limited number of postnatal interventions currently proven to increase expressed milk supply in these mothers. For mothers where lactation support, relaxation techniques and advice on mechanical expression have not produced sufficient breastmilk to meet their preterm infant's requirements, only one medication has undergone short‐term trials of up to 14 days, domperidone (Campbell‐Yeo 2010; Silva 2001).

As many infants born at ≤ 32 weeks' gestation spend three weeks or longer feeding on predominantly expressed breastmilk, it remains important to measure outcomes over a longer period to best assess any of these interventions. When a medication is given to support breastfeeding, it is often used over a period of greater than seven days before weaning. None of the currently reported trials of medications to increase breastmilk supply have examined the effects on expressed milk volume for more than 14 days of treatment.

The timing of introduction of a medication to further support expressed breastmilk production remains controversial. The two included studies commenced at 31.9 ± 10.5 days (Silva 2001) and at more than 21 days (Campbell‐Yeo 2010) following preterm delivery. Although it is necessary to establish other lactation supports for these mothers before beginning any medication intervention, it is also important to establish as early as possible sufficient expressed breastmilk for the grading up of a preterm infant's enteral intake which is usually established well before 21 days post delivery.

Two excluded studies examined 'prophylactic' metoclopramide starting before 96 hours post delivery, both showed no significant improvement in outcome. In the excluded study by Hansen 2005, mothers delivering before 34 weeks were randomised to receive metoclopramide or placebo at less than four days after delivery. No significant change in expressed breastmilk volume or reported breastfeeding duration was found. The other excluded study of metoclopramide given on day one to term mothers post caesarean section, showed no difference in breastfeeding outcomes at 10 days, six weeks and three months after delivery (Lewis 1980). A further excluded study compared metoclopramide against domperidone or placebo in a preterm population (James 2004). This study of mothers delivering before 34 weeks commenced > 12 days post delivery but only measured expressed milk volume for five days. A significant improvement when compared with placebo between baseline expression and day five occurred only in the domperidone arm (119 ± 40 mL, P < 0.008) but not in the metoclopramide arm (84 ± 27 mL). Outcomes beyond five days were not reported and numbers in each arm of this trial were small, increasing the chance of missing a significant effect if one were present.

The side effects of promoting lactation with either metoclopramide or domperidone have been reported in non controlled studies. At recommended doses, metoclopramide may produce dystonic reactions in about 1% of adults (Pinder 1976) but this has yet to be reported in randomised studies. Domperidone is reported to less readily cross the blood‐brain barrier and thus to have less neurologic side effects on both infants and their mothers (Fischer 1998). Future studies should include careful ascertainment of any maternal and infant side effects of medications used to increase breastmilk supply.

Authors' conclusions

Implications for practice.

In conclusion, despite accumulating evidence of the significant advantages of breastmilk in a preterm population, relatively few controlled trials have examined the outcome of medications to increase breastmilk supply in those mothers whose expressed breastmilk (EBM) volume is insufficient. Two studies have examined rescue intervention when insufficient EBM is available more than 14 days post delivery. Two studies of domperidone together show a significant improvement on EBM expressed over a seven‐ to 14‐day period of observation in the short‐term (Campbell‐Yeo 2010; Silva 2001). In summary, there is evidence of a significant and clinically important improvement in EBM volume over the short‐term in mothers of preterm infants who have insufficient EBM for their infant's needs with the use of domperidone, although this is based on limited data (59 mother‐infant pairs).

Implications for research.

Further research is likely to be clinically relevant in the preterm population with the current evidence supporting breastmilk feeds in this group. Future trials of medications to support preterm mothers should include larger numbers to identify any maternal or infant side effects, and with outcomes measured at discharge, or later.

Data and analyses

Comparison 1. Domperidone versus placebo.

Outcome or subgroup title	No. of studies	No. of participants	Statistical method	Effect size
1 Difference in volume of EBM per day	2	59	Mean Difference (IV, Random, 95% CI)	99.49 [‐1.94, 200.92]

Characteristics of studies

Characteristics of included studies [ordered by year of study]

Silva 2001.

Methods	Random allocation by pharmacy to domperidone or placebo.
Participants	Mothers (n = 14) of preterm infants who were expressing and who had low milk production despite lactation counselling and pump expression advice.
Interventions	Domperidone 10 mg 3 times daily versus lactose powder 3 times daily, both in unmarked capsules for 7 days.
Outcomes	Expressed milk volume per day for 7 days published. Self‐reported side effects. Secondary outcomes not reported except for "the proportion of infants discharged home who were breastfeeding did not differ between groups". No side effects reported in mothers or infants.
Notes	4 withdrawn from domperidone arm: 3 of these for incomplete records and 1 for a neonatal death. Nil randomised but withdrawn from the placebo arm. Reported EBM volume change from day 2 not baseline but data provided to allow analysis of EBM volume change from baseline to day 7. Power calculation published suggested that 20 cases should be randomised and after excluding incomplete data and other attrition only 14 cases remained (i.e. 6/20 post randomisation loss).
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Unclear risk	Not specified.
Allocation concealment (selection bias)	Low risk	Random allocation by pharmacy.
Blinding (performance bias and detection bias) All outcomes	Low risk	Domperidone and lactose placebo in identical capsules.
Incomplete outcome data (attrition bias) All outcomes	Low risk	All randomised cases reported. Domperidone arm 4 post randomisation withdrawals (1 neonatal death, 3 incomplete milk records). In placebo arm no post randomisation withdrawals. Individual data published showing EBM volumes incomplete for a further 2 cases, 1 domperidone and 1 placebo mother.
Selective reporting (reporting bias)	Low risk	All randomised cases accounted for in published data.
Other bias	Low risk	Nil other bias evident.

Campbell‐Yeo 2010.

Methods	Randomised blinded controlled trial.
Participants	Mothers (n = 45) of infants delivered at < 31 weeks who had lactation failure at ≥ 3 weeks post delivery.
Interventions	Domperidone 10 mg tds versus lactose placebo for 14 days.
Outcomes	Nutrient levels (protein, energy, fat, carbohydrate, sodium, calcium and phosphate) in EBM post intervention and mean EBM volume change from baseline to day 14. Breastfeeding rate (undefined as partial or exclusive) at discharge in domperidone arm 54.6% vs 52.2% in placebo arm. High rate of domperidone use in the placebo arm post 14 day RCT (41.7%).
Notes
Risk of bias
Bias	Authors' judgement	Support for judgement
Random sequence generation (selection bias)	Low risk	Computer‐based randomisation in blocks of 4.
Allocation concealment (selection bias)	Low risk	Randomisation code only known to off‐site pharmacy staff.
Blinding (performance bias and detection bias) All outcomes	Low risk	Blinded to intervention but not to outcome.
Incomplete outcome data (attrition bias) All outcomes	Low risk	1 mother withdrew after randomisation in the domperidone arm.
Selective reporting (reporting bias)	Unclear risk	It is unclear whether 2 of 21 mothers in the domperidone arm and 5 of 24 mothers in the placebo arm who had "insufficient milk" were included in the EBM volume change assessment at 14 days.
Other bias	Low risk

EBM: expressed breastmilk 
 RCT: randomised controlled trial 
 tds: three times daily 
 vs: versus

Characteristics of excluded studies [ordered by study ID]

Study	Reason for exclusion
Chong 2006	RCT of metoclopramide to "hasten and improve" the establishment of breastfeeding. Excluded as intervention is used prophylactically before breastfeeding is established and is confined to mothers with diabetes.
Ehrenkranz 1987a	2 arm cross‐over trial of metoclopramide or placebo available in abstract form only. The study design allowed no washout period between interventions and had marked variations in the size of the 2 cross‐over arms as well as markedly different EBM outcomes between the 2 arms. These findings provide significant concern with interpreting the true effect of metoclopramide in this study. No contact could be established with the authors for further data.
Ehrenkranz 1987b	Observational study of prolactin basal and peak levels in mothers expressing for their preterm infants.
Fewtrell 2006	Randomised double blind placebo controlled trial of oxytocin nasal spray in mothers of < 35 week infants with insufficient expressed breastmilk. Excluded as intervention and outcome assessed only for 5 days.
Gunn 1996	RCT of Human Growth Hormone injections. Excluded as outcome measure included suckling infants with imprecise measure of breastmilk used.
Hansen 2005	RCT of metoclopramide and placebo but intervention was at < 96 hours post delivery and not confined to mothers with insufficient breastmilk for their infants needs.
Hofmeyr 1985	Observational study of prolactin levels in breastfeeding mothers and in their breastmilk.
James 2004	RCT of domperidone versus metoclopramide versus placebo but outcome of expressed breastmilk per day was measured only to 5 days post intervention.
Kauppila 1981	Randomised cross‐over trial of varying metoclopramide dosage and placebo. Trial confined to mothers of term infants only.
Lewis 1980	RCT of metoclopramide versus lactose placebo but not in mothers of preterm infants.
Loh 2007	Registered RCT of metoclopramide versus placebo with no published data or response to attempts to contact authors.
Mersmann 1996	Intervention was not a medication.
Powe 2011	Examines breastmilk composition on human recombinant prolactin.
Ruis 1981	Intervention with oxytocin nasal spray or placebo was in all mothers and not confined to those with insufficient breastmilk for their infant's needs. Outcome of expressed breastmilk volume was measured only till 5 days after instituting the intervention.
Wan 2008	Dose effect study of domperidone with no placebo comparison.

RCT: randomised controlled trial

Characteristics of studies awaiting assessment [ordered by study ID]

Powe 2010.

Methods	Blinded random allocation by research pharmacy.
Participants	Mothers of preterm infants with lactation insufficiency at 7 to 9 weeks postpartum who had received lactation support.
Interventions	3 intervention arms: 1. Recombinant human prolactin (r‐hPRL) 60 µg/kg subcutaneously every 12 hours for 7 days (n = 2) 2. r‐hPRL60 µg/kg subcutaneously alternating with normal saline placebo every 12 hours for 7 days (n = 3) or 3. Normal saline placebo subcutaneously every 12 hours for 7 days (n = 4).
Outcomes	Difference in volume of expressed breastmilk per day on day 1 to day 7.
Notes	Small pilot study of r‐hPRL use. Further data on placebo EBM outcome requested from authors.

EBM: expressed breastmilk

Differences between protocol and review

The methods have been updated to reflect the Cochrane Pregnancy and Childbrith Group's current standard methods text and the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). Herbal remedies were initially included in the protocol for this review. No studies were identified in the search strategies. If such studies are identified in future searches, consideration will be given as to whether or not the findings could be more clearly reported as the subject of a separate review.

Contributions of authors

Tim Donovan contributed to writing the first and subsequent drafts of protocol and the full review. K Buchanan contributed to the submission of protocol, examination of available studies and also contributed to the writing of drafts.

Declarations of interest

None known.

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