Low birthweight, usually defined as weight less than 2500 grams, is a major health problem for a baby and the baby's family, and one which consumes significant healthcare resources. In high-income countries preterm birth is the major reason for low birthweight (Blanc 2005). In low- to middle-income countries, chronic maternal malnutrition leads to large numbers of babies who are small for gestational age (SGA) at birth (Blanc 2005; Walker 2007; WHO 2003; Yasmin 2001).
Thus 'low birthweight' is an outcome that includes both infants that are born early (less than 37 weeks) and/or who are SGA. Combining babies who are born preterm with those who are SGA is problematic from a research perspective, since the underlying causes of the two problems are believed to be quite different, and treatment is different (WHO 2003; Yasmin 2001).
Effective prevention of low birthweight may depend in part on its cause. Nevertheless, many countries have programs offering special assistance to women thought to be at risk of giving birth to an infant weighing less than 2500 grams. These programs may include advice and counseling (about nutrition, rest, stress management, use of alcohol/ recreational drugs), tangible assistance (e.g. transportation to clinic appointments, help with household responsibilities), and emotional support. The programs may be delivered by multidisciplinary teams of health professionals, by specially trained lay workers, or by a combination of lay and professional workers. This Review includes all acceptably controlled trials of such programs.
Studies consistently show a strong relationship between social disadvantage and low birthweight (WHO 2003; WHO 2010a; Wilkinson 2003). The underlying causal pathways are unclear, but several theoretical mechanisms have been proposed that link the physiological and psychological stress associated with social disadvantage to an increased likelihood of complications during pregnancy, fetal growth restriction, intrapartum complications, operative delivery, preterm birth, and poor maternal and neonatal health. Chronic poverty can lead to malnutrition, unhealthy living environments, increased risk of infection, and increased stress in daily life. The social stigma associated with being marginalized in society is also a source of chronic stress. Social support may have a mediating influence on the relationship between life stress (regardless of the causes of the stress) and the development of pregnancy complications. (McIntyre 2006; WHO 2008; WHO 2010b; Wilkinson 2003).
The current Review focuses on evaluations of programs for pregnant women believed to be at high risk for giving birth to a preterm or SGA baby, that have the provision of support as a major component. Readers are referred to Cochrane Reviews that have evaluated other forms of care to prevent preterm birth, SGA birth, and/or low birthweight. These Reviews have evaluated bedrest, nutritional supplements, nutritional advice, interventions to assist pregnant women to stop smoking, plasma volume expansion, oxygen therapy, and various medications (Kramer 2003; Lumley 2009; Mahomed 1999; McDonald 2007; Reveiz 2007; Say 1996a; Say 1996b; Say 1996c; Say 2001; Say 2003a; Say 2003b; Say 2003c; Smaill 2007).
Debates have arisen regarding the relative benefits of 'professional' versus 'peer' support. Social support from a woman in one's community, who has a similar socioeconomic background and is experiencing similar life stresses, may be qualitatively different from support from a healthcare professional, who has broad professional knowledge and experience, but may not share the same socioeconomic background or life concerns, and who often provides other professional services as well as support. This Review includes studies of support by providers with varying backgrounds and qualifications.
The primary objective was to assess the effects of programs offering additional social support compared with routine care for pregnant women who are believed to be at high risk for giving birth to babies that are either preterm or weigh less than 2500 gm, or both, at birth. Secondary objectives were to determine whether effectiveness of support was mediated by timing of onset (early versus later in pregnancy) or type of provider (a healthcare professional or a lay woman).
Criteria for considering studies for this review
Types of studies
Inclusion criteria were: randomized controlled trial (RCT) comparing a program of additional support during at-risk pregnancy by either a professional (social worker, midwife or nurse) or a specially trained lay person, or both, in an effort to reduce the likelihood of preterm birth or low birthweight; random allocation to treatment and control groups.
'Additional support' was defined as some form of emotional support (e.g. counseling, reassurance, sympathetic listening) with or without additional information or advice, or both, occurring during home visits, clinic appointments, and/or by telephone. The additional support could also include tangible assistance (e.g. transportation to clinic appointments, assistance with the care of other children at home). We included studies if the additional support was provided during pregnancy and continued until the birth of the baby, or into the postnatal period.
We excluded trials if the intervention was solely an educational intervention or if the intervention was of brief duration (e.g. two to three weeks) and not intended to continue until the birth of the baby. We also excluded trials of smoking cessation programs or mind-body interventions for pregnant women, as they are the foci of other Reviews (Lumley 2009; Marc 2009).
Types of participants
Pregnant women judged to be at risk of having preterm or growth-restricted babies, or both.
Types of interventions
Standardized or individualized programs of additional social support, provided in either home visits, during regular antenatal clinic visits, and/or by telephone on several occasions during pregnancy.
Types of outcome measures
- Caesarean birth
- Gestational age less than 37 weeks at birth
- Birthweight less than 2500 gm
- Stillbirth/neonatal death
- Antenatal hospital admission
- Postnatal re-hospitalization (for mother)
- Postnatal depression
- Less than highly satisfied with antenatal care
- Long-term morbidity (as defined by trial authors)
Search methods for identification of studies
We searched the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting the Trials Search Co-ordinator (January 2010).
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;
- 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 and MEDLINE, 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
We evaluated trials under consideration for methodological quality and appropriateness for inclusion, without consideration of their results.
Selection of studies
Two review authors (E Hodnett (EH), S Fredericks (SF)) independently assessed for inclusion all the potential studies we identified as a result of the search strategy. We resolved any disagreement through discussion or, if required, we consulted a third person.
Data extraction and management
We designed a form to extract data. For eligible studies, two review authors (EH, J Weston (JW)) extracted the data using the agreed form. We resolved discrepancies through discussion or, if required, we consulted a third person. We entered data into Review Manager software (RevMan 2008) and checked them for accuracy.
When information regarding any of the above was unclear, we attempted to contact authors of the original reports to provide further details.
Assessment of risk of bias in included studies
Two review authors (EH, JW) independently assessed risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). We resolved any disagreements by discussion or by involving a third assessor.
(1) Sequence generation (checking for possible selection bias)
We describe for each included study the methods used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups.
We assessed the methods as:
- adequate (any truly random process, e.g. random number table; computer random number generator);
- inadequate (any non-random process, e.g. odd or even date of birth; hospital or clinic record number); or
(2) Allocation concealment (checking for possible selection bias)
We described for each included study the method used to conceal the allocation sequence in sufficient detail and determined whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment.
We assessed the methods as:
- adequate (e.g. telephone or central randomization; consecutively numbered sealed opaque envelopes);
- inadequate (open random allocation; unsealed or non-opaque envelopes, alternation; date of birth);
(3) Blinding (checking for possible performance bias)
We described for each included study the methods used, if any, to blind personnel from knowledge of which intervention a participant received. Since women and care providers cannot be blinded to type of antenatal care given, blinding was considered adequate if outcomes were recorded by outcome assessors who had no knowledge of the woman's group assignment. We judged studies at low risk of bias if they were blinded, or if we judged that the lack of blinding could not have affected the results. We assessed blinding separately for different outcomes or classes of outcomes.
(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)
We described for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We state whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomized participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. To be included in the review, data on a given outcome had to be available for at least 80% of those who were originally randomized. Where sufficient information is reported, or was supplied by the trial authors, we planned to include missing data in the analyses. We assessed methods as:
(5) Selective reporting bias
We described for each included study how the possibility of selective outcome reporting bias was examined by us and what we found.
We assessed the methods as:
- adequate (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);
- inadequate (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);
(6) Other sources of bias
We described for each included study any important concerns we have about other possible sources of bias. Examples of such potential sources of bias include stopping early due to a data-dependent process, extreme baseline imbalance, or claims of fraud.
We assessed whether each study was free of other problems that could put it at risk of bias:
(7) Overall risk of bias
We made explicit judgements about whether studies are at high risk of bias, according to the criteria given in Table 8.5c of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008). With reference to (1) to (6) above, we assessed the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We planned to explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.
Measures of treatment effect
For dichotomous data, we present results as summary risk ratio (RR) with 95% confidence intervals (CI).
For continuous data, we have used the mean difference if outcomes are measured in the same way between trials. We have used the standardized mean difference to combine trials that measure the same outcome, but use different methods.
Unit of analysis issues
We planned to include cluster-randomized trials in the analyses along with individually randomized trials. Their sample sizes would have been adjusted using the methods described in Gates 2009 using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), or from another source. If we use ICCs from other sources are used, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we had identified both cluster-randomized trials and individually-randomized trials, we planned to synthesise the relevant information. We would have considered it reasonable to combine the results from both if there were little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomization unit was considered to be unlikely. We would also have acknowledged heterogeneity in the randomization unit and performed a separate meta-analysis.
Dealing with missing data
For included studies, we noted levels of attrition. We included data for a given outcome only if the data were available for at least 80% of those originally randomized.
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 randomized to each group in the analyses. The denominator for each outcome in each trial was the number randomized minus any participants whose outcomes are known to be missing.
Assessment of heterogeneity
We assessed statistical heterogeneity in each meta-analysis using the I² and Chi² statistics. We regarded heterogeneity as substantial if I² was at least 50% or there was a low P-value (less than 0.10) in the Chi² test for heterogeneity. None of the analyses met the criteria for heterogeneity.
Assessment of reporting biases
Had we suspected reporting bias (see 'Selective reporting bias' above), we would have attempted to contact study authors asking them to provide missing outcome data. Were this is not possible, and the missing data were thought to introduce serious bias, we would not have included the outcome data from that trial.
We carried out statistical analysis using the Review Manager software (RevMan 2008). We used fixed-effect inverse variance meta-analysis for combining data. Had we suspected clinical or methodological heterogeneity between studies sufficient to suggest that treatment effects may differ between trials, we would have used random-effects meta-analysis. .
We excluded from analyses data for any outcome in which data were missing for more than 20% of those originally randomized.
Subgroup analysis and investigation of heterogeneity
We planned to carry out the following subgroup analyses:
- timing of onset of support (early in pregnancy versus after the first trimester is completed);
- type of provider of support (healthcare professional versus lay person).
We chose the outcomes to be used in subgroup analyses on the basis of their importance from the perspective of parents, care providers, and policy makers. They were: gestational age less than 37 weeks, birthweight less than 2500 gm, perinatal mortality, and caesarean birth.
For fixed-effect meta-analyses we conducted planned subgroup analyses classifying whole trials by interaction tests as described by Deeks 2001. For random-effects meta-analyses we would have assessed differences between subgroups by inspection of the subgroups’ confidence intervals; non-overlapping confidence intervals indicate a statistically significant difference in treatment effect between the subgroups.
We had planned to conduct sensitivity analyses based on three conditions:
- results when studies with a high risk of bias were included versus excluded;
- fixed-effect versus random-effects analyses when evidence of statistical heterogeneity was present (defined as an I
2value greater than 50% and inconsistency between trials in the direction or magnitude of effects (judged visually));
- results when non-uptake of the support intervention was high versus low.
We did not have any trials meeting the first two conditions. We did undertake a sensitivity analysis based on the third condition.
Description of studies
Seventeen trials, involving 12,264 women, met the inclusion criteria; see table of Characteristics of included studies. While all participants were judged to be at risk for giving birth preterm or to a low birthweight baby, the inclusion criteria defining risk status was variable. Most trials used a combination of social and obstetrical factors. The trials were conducted in Australia, Great Britain, France, Latin America, South Africa, and the United States. No single outcome was reported in all 17 trials. For example, data were available from 11 trials (n = 8681participants) for birthweight lower than 2500 gm, from another set of 11 trials (n = 10,429 participants) for gestational age less than 37 weeks, but from only single trials (n = 1887 and n = 458) for satisfaction with antenatal care and postnatal depression, respectively.
The descriptions of the additional support were generally consistent across all trials. Five trials included specific mention of education or client teaching as a component of the support (Brooten 2001; Heins 1990; Klerman 2001; McLaughlin 1992; Moore 1998). In 14 trials (Blondel 1990; Brooten 2001; Bryce 1991; Dawson 1989; Dawson 1999; Heins 1990; Moore 1998; Norbeck 1996; Oakley 1990; Olds 1986; Rothberg 1991b; Spencer 1989; Spira 1986; Villar 1992) the intervention consisted of one-to-one support, while in three trials (Klerman 2001; McLaughlin 1992; Rothberg 1991a), the intervention consisted of both one-to-one and group sessions. Two trials (Dawson 1989; Spira 1986) compared care and support during home visits with inpatient hospital care.
In 11 of the 16 trials in which the support intervention was provided by a health professional (Blondel 1990; Brooten 2001; Bryce 1991; Dawson 1989; Dawson 1999; Heins 1990; Moore 1998; Norbeck 1996; Oakley 1990; Olds 1986; Spira 1986), the provider of support was a midwife or a nurse, and in four trials (Klerman 2001; Rothberg 1991a; Rothberg 1991b; Villar 1992) the providers were social workers. In one trial (McLaughlin 1992) the support was provided by a multi-disciplinary team consisting of nurses, psychologists, midwives, and specially trained lay women. In one trial (Spencer 1989) specially trained lay women provided all of the additional support.
We found no randomized trials in which the onset of support for all women was early in pregnancy (in the first trimester).
Eight trials provided compliance rates for the intervention group (Blondel 1990; Bryce 1991; Norbeck 1996; Oakley 1990; Rothberg 1991a; Spencer 1989; Spira 1986; Villar 1992). In seven of the trials 90% to 100% of the participants randomized to receive additional support did receive it. In Spencer 1989, women were randomized based on assessment of eligibility criteria in their medical records. Consent was then sought only for those randomized to the intervention group, and 58.6% refused the intervention but still consented to be part of the study.
Eight trials had women complete questionnaires during the postpartum period (Blondel 1990; Brooten 2001; Dawson 1989; Dawson 1999; Klerman 2001; Oakley 1990; Olds 1986; Villar 1992). The time of completion varied across the trials and ranged from three days to eight weeks postpartum. Response rates were at least 80% in only two trials (Oakley 1990; Villar 1992). One trial (Brooten 2001) also reported healthcare utilization information for the first year postpartum, but the data could not be used because of uncertainty about the follow-up rate for this information. This uncertainty stemmed from the following: 1) the one-year follow-up information was included in a table with delivery information and no separate denominators were reported; 2) the process for maintaining contact with the participants was not outlined; 3) some loss to follow up would be expected when tracking women for such a long period of time and none was noted; and 4) including the full sample for the one-year follow-up data meant that two participants with spontaneous miscarriages were included.
Risk of bias in included studies
Many of the trials were missing details about the sequence generation and allocation concealment, but none used methods that were of obviously poor quality (Figure 1; Figure 2). Incomplete outcome data and selective reporting were are a problem in one trial (Olds 1986). In this trial data were not provided for 46 non-white women and 20 cases with maternal or fetal conditions predisposing to preterm delivery and/or aberrations in fetal growth. The authors excluded these cases prior to data analyses. The resulting rate of completion for the majority of outcome data was 77.5%.
|Figure 1. Methodological quality summary: review authors' judgements about each methodological quality item for each included study.|
|Figure 2. Methodological quality graph: review authors' judgements about each methodological quality item presented as percentages across all included studies.|
Effects of interventions
Social support interventions for at-risk pregnant women have not been associated with reductions in the numbers of preterm babies (11 trials; n = 10,429; risk ratio (RR) 0.92, 95% confidence interval (CI) 0.83 to 1.01, low birthweight babies (11 trials; n = 8681; RR 0.92, 95% CI 0.83 to 1.03), or perinatal mortality (11 trials, n = 7522; RR 0.96, 95% CI 0.74 to 1.26). Social support interventions for at-risk pregnant women were associated with a decreased likelihood of caesarean birth (nine trials; n = 4522; RR 0.87, 95% CI 0.78 to 0.97) and antenatal hospital admission (three trials; n = 737; RR 0.79. 95% CI 0.68 to 0.92). Results of five trials indicate women who received additional social support were almost three times more likely to have their pregnancies terminated (n = 5587; RR 2.87, 95% CI 1.42 to 5.78). This outcome was not pre-specified.
When sensitivity analyses were conducted comparing the results with and without the Spencer trial (Spencer 1989) where 58.6% of those randomized to additional support did not accept it, the results did not change materially when the trial was excluded. For the termination of pregnancy comparison, the results were in the same direction but the 95% confidence interval did include 1.0 when the Spencer trial was removed (RR 1.94, 95% CI 0.85 to 4.43).
Because there was only one trial in which the support was provided by lay women (Spencer 1989), and in another trial the support was provided by a multidisciplinary team that included lay women (McLaughlin 1992), we did not perform the planned subgroup analysis. However, the results of these two trials were remarkably consistent with those of the other trials.
In general the social support intervention was comprehensive and intensive, although timing of onset varied from the first to third trimester, with the majority of women enrolled at about mid-pregnancy. Despite the comprehensiveness of the intervention, the diversity of outcomes, and despite the solid theoretical rationale for linking stress, social support, and pregnancy outcome, there was no significant reduction in the likelihood of low birthweight, preterm birth, or perinatal death . Depression (during and after pregnancy) and maternal satisfaction with antenatal care were also apparently unaffected. While the theoretical rationale for links between social support, stress, and health is strong, it may be that social support (regardless of the quality and quantity) is not sufficiently powerful to improve the outcomes of the pregnancy during which it is provided. An argument could be made that, given the immense social deprivation experienced by most of the women in these trials, it would be surprising if social support could have such an immediate and powerful effect.
An alternate, or complementary, explanation for the lack of effect of social support on preterm birth or low birthweight is that our abilities to identify women who are at high risk of preterm birth or low birthweight babies are seriously limited, and thus many women were included in these trials who were not actually at higher risk of these outcomes. Furthermore, the underlying causal mechanisms linking social disadvantage to adverse pregnancy outcomes have not been identified.
Two outcomes were significantly associated with enhanced social support during pregnancy: decreased likelihood of caesarean birth, and decreased likelihood of antenatal hospital admission. These meta-analyses involved multiple trials and over 4000 and 700 women respectively. On the assumption that the results did not occur by chance, we offer the following interpretations.
(1) Caesarean birth
It is noteworthy that the effect size is very similar to that in the Cochrane Review of support during labour (Hodnett 2007), and it is consistent with an observational study that linked social support to reduced likelihood of intrapartum complications and operative birth (Norbeck 1983). Both of the latter reports describe mechanisms whereby additional support, by lessening anxiety and fear, reduce the likelihood of obstetric complications and thereby increase the likelihood of normal vaginal birth.
(2) Antenatal hospital admission
It is possible that the enhanced support allowed for early detection of pregnancy complications either by the caregiver or the woman herself. Treatment could then be handled on an out-patient basis rather than requiring hospitalization.
We did find a significant association between enhanced social support during pregnancy and an increased likelihood of termination of pregnancy. But it must be noted that this was not a pre-specified outcome and the confidence interval did alter during the sensitivity analysis. However, we feel the following interpretation might be helpful. The additional support may have resulted in women's increased awareness of the added social risk to themselves or their families, and/or their increased awareness of an increased medical risk to the baby, and thus more women were likely to take action to avoid additional problems. Also, an important aspect of social support is the provision of information. Thus, it is possible that women in the additional support group sought or received additional information, or both, about the option of pregnancy termination.
Implications for practice
Pregnant women need and deserve to have the help and support of caring family members, friends, and health professionals. However, such support is unlikely to be powerful enough to overcome the effects of a lifetime of poverty and disadvantage, or a longstanding pregnancy complication, and thereby influence the remaining course of a pregnancy. Pregnant women and their caregivers should be informed that programs which offer additional support during pregnancy are unlikely to prevent the pregnancy from resulting in a low birthweight or preterm baby, but they may be helpful in reducing the likelihood of caesarean birth or antenatal hospital admission.
Implications for research
There appears to be no need for further trials evaluating the medical effects of social support during pregnancy on immediate pregnancy and maternal or neonatal outcomes, or both. The possibility of improved psychosocial outcomes requires confirmation by larger trials that ensure adequate follow up of participants. Qualitative studies conducted concurrently with such trials would provide valuable information about women's evaluations of the additional support. There is an urgent priority for studies which identify the cause(s) of preterm birth. Future studies of forms of care to prevent low birthweight should differentiate between the two distinct causes of low birthweight: being born preterm and being SGA.
We are grateful to Rita Iedema-Kuiper, RM, PhD, for providing us with a copy of her PhD thesis and English summary of the trial (Iedema-Kuiper 1996a), and to Winnie Chu, who assisted with double-data entry and with preparation of the included and excluded trials tables, for the previous version of this Review.
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
Last assessed as up-to-date: 3 May 2010.
Protocol first published: Issue 1, 1995
Review first published: Issue 1, 1995
Contributions of authors
Ellen Hodnett: all aspects of preparation of revised review. Suzanne Fredericks performed the second data entry for the new trials in the updated Review, wrote a draft of the revised Background, and participated in decisions regarding eligibility of trials, interpretations of the results and all other aspects of the Review. Julie Weston: prepared new data entry forms and re-did all data entry; editing of tables; assessment of methodological quality of the studies; edited all aspects of revised Review.
Declarations of interest
Sources of support
- University of Toronto, Canada.
- Ryerson University, Canada.
- No sources of support supplied
Differences between protocol and review
The revised Review adheres to current methodological guidelines, including a smaller list of primary and secondary outcomes.
Medical Subject Headings (MeSH)
MeSH check words
Female; Humans; Pregnancy
* Indicates the major publication for the study