Introduction

The last three decades have witnessed a significant fall in infant mortality rates in developing countries, whereas neonatal mortality rates have decreased at a slower pace.1, 2 Estimates published in 2008 suggest that about 41% of all under-five mortality occurs in the neonatal period,3 contributing four million deaths worldwide each year.4 Nearly all (99%) global neonatal mortality occurs in developing countries.3 Lowering this mortality is vital for achieving further reductions in infant and child mortality.1, 5, 6, 7, 8

Among neonatal deaths, three quarters occur during the first week of life whereas 25 to 45% occur within the first 24 h. The majority of neonatal deaths happen at home against a backdrop of rural poverty, unskilled neonatal care and a suboptimal or absent referral system; a strategy that promotes universal access to antenatal care, skilled birth attendance and early postnatal care has the potential to contribute to a sustained reduction in neonatal mortality.1, 5 A complementary approach is community-based delivery of key newborn health interventions. Two related modalities have been attempted in programs and research trials in the last decade. The first approach involves home visits and other community activities for the promotion of optimal newborn-care practices. The second approach, in addition to the promotion of preventive interventions, includes home-based management of perinatal and neonatal morbidities such as birth asphyxia and neonatal sepsis.

Since utilization of health facilities for neonatal health is low, the potential complementary role for home-based newborn care in accelerating the decline in neonatal deaths to achieve Millennium Development Goal 4 needs to be assessed. Recent reviews have evaluated the efficacy of community-based interventions, including home-based neonatal care, in reducing neonatal mortality.9, 10 In these reviews, the relative paucity of eligible trials necessitated the inclusion of non-randomized or quasi-randomized trials, which partially compromised the quality of synthesized evidence. Following the recent publication of randomized controlled trials, updating the available systematic reviews to guide relevant policy is necessary.

The objective of this review is to assess the effect of home-based neonatal care provided by community health workers (CHWs) for preventing neonatal mortality in resource-limited settings with poor access to health facility-based care.

Methods

Criteria for considering trials for this review included the following:

Types of trials

Trials evaluating home-based neonatal care provided by CHWs with a concurrent control group and a random design, with individual or cluster allocation, were eligible for inclusion. Trials primarily evaluating home-based neonatal care following birth in a facility or hospital were excluded.

Types of participants

The trial population comprised neonates (first 28 days of life, or the first month of life where not specified in days) born in resource-limited settings with poor access to health facility-based care.

Types of interventions

Experimental interventions comprised promotion of optimal neonatal care practices at home, with or without home-based treatment of neonatal morbidities, delivered by CHWs during the neonatal period, with or without additional interventions during pregnancy and/or childbirth. The experimental intervention was compared with controls who did not receive any home-based intervention by CHWs during the neonatal period.

Interventions during pregnancy included: (i) promotion of antenatal care; (ii) health education and/or counseling of the mother regarding desirable practices during pregnancy; or (iii) promotion of delivery in a hospital or at home by a skilled birth attendant.

Interventions during childbirth included: (i) education about safe and/or clean delivery practices; or (ii) implementation of safe delivery practices in case of domiciliary deliveries.

Interventions during the neonatal period consisted of: (i) care of the newborn immediately after birth, including keeping the baby warm, neonatal resuscitation (if required) and early initiation of breastfeeding; (ii) health education and/or counseling of families regarding neonatal care practices such as exclusive breastfeeding, keeping the baby warm and hygienic cord care; (iii) education to improve caregiver recognition of life-threatening neonatal problems; (iv) education to improve health care-seeking behaviors; (v) identification of signs of severe neonatal morbidities and referral to a health facility; or (vi) home-based management of neonatal morbidities.

The term ‘community health worker’ included any of the following personnel: village or CHWs or volunteers (paid/unpaid), public health nurse or auxiliary nurse.

Types of outcome measures

Primary outcomes

All-cause mortality included: (i) neonatal deaths due to any cause during the period between initiation of the intervention and the last follow-up within the first month of life; and (ii) infant deaths due to any cause during the period between initiation of the intervention and the last follow-up within the first year of life.

Secondary outcomes

These secondary outcomes included: (i) perinatal mortality rate; and (ii) cause-specific mortality including deaths due to neonatal sepsis, tetanus, asphyxia and prematurity (as defined by the authors, irrespective of single- or multiple-cause assignment).

Search methods for identification of trials

We searched computerized bibliographic medical databases, including Medline, Cochrane Controlled Trials Register in the Cochrane Library, EMBASE, Health Services Technology, Administration, and Research (HealthSTAR) and clinical trials websites through 5 May 2012. For PubMed the following search strategy was used:

(newborn or neonat* OR peri-natal) AND (‘community’ OR community-based OR home OR home-based OR domiciliary OR rural OR traditional OR village OR village-based) AND (mortality OR death OR survival OR outcome) AND (Clinical Trial[ptyp] OR Randomized Controlled Trial[ptyp] OR Controlled Clinical Trial[ptyp] OR Evaluation Studies[ptyp] OR Journal Article[ptyp]) AND (infant [MeSH]) AND (Humans[Mesh]).

A lateral search using the link of related articles in PubMed was done for articles initially selected from the search strategy. We also reviewed the reference lists of identified articles and hand-searched reviews, bibliographies of books and abstracts and proceedings of international conferences and meetings. Experts in the field were contacted to identify any additional or ongoing trials. The title and abstract of the trials identified in the computerized search were scanned to exclude trials that were obviously irrelevant. Full texts of the identified trials that fulfilled the inclusion criteria were reviewed. To avoid publication bias, we attempted to include both published and unpublished trials.

Quality assessment

In order to enhance the validity of the meta-analysis, the quality of the identified trials was assessed by Cochrane Collaboration’s tool for assessing the risk of bias.11 This tool assesses the degree to which: (i) the allocation sequence was adequately generated (sequence generation); (ii) the allocation was adequately concealed (allocation concealment); (iii) knowledge of the allocated interventions was adequately prevented during the study (blinding); (iv) incomplete outcome data were adequately addressed; (v) reports of the study were free of suggestion of selective outcome reporting; and (vi) the study was apparently free of other problems that could put it at high risk of bias (for example, conflict of interest, premature trial termination). Each domain was allocated one of the three possible categories for each of the included studies: ‘Yes’ for low risk of bias, ‘No’ for high risk of bias and ‘Unclear’ where the risk of bias was uncertain or unknown.

Data abstraction

Data abstraction was done in duplicate using a standard questionnaire. The data included in the review were derived from the published manuscript or as provided by the authors for unpublished trials. Requests to the original investigators for additional data and information were made if required. Data entry and initial analysis were performed on SPSS (IBM, Armonk, NY, USA) (Version 14.0) software.12

Analysis

Meta-analysis was performed with a user-written program on STATA (version 9.2) software (StataCorp, College Station, TX, USA).13 The presence of bias in the extracted data was evaluated quasi-statistically using a funnel plot.14 The effect measure was plotted against the standard error of the effect size on a log scale. In the absence of bias, because of the sampling variability, the graph takes the form of an inverted funnel. In the presence of bias, the corner of the funnel is distorted or missing. Formal statistical tests for funnel plot asymmetry, namely the Begg’s and Egger’s methods, were also conducted with the user-written ‘metabias’ command in STATA (version 9.2) software.15, 16 Pooled estimates (relative risk (RR) with 95% confidence intervals (CIs)) of the evaluated outcome measures were calculated by the generic inverse variance method by the user-written ‘metan’ command15, 17 in STATA (version 9.2) software. The natural logarithm converted values of the individual trial RRs, and their standard errors were used for computing the pooled estimates as recommended.17 These pooled estimates were expressed in an exponential form. This program also computes formal tests of heterogeneity, namely, the statistic Cochran Q and I2 (variation in pooled estimate attributable to heterogeneity).

One option for analyzing the data was to calculate the change in mortality rates (from baseline to the end of the intervention or observation period) in the intervention and control groups separately, and then construct RRs and 95% CIs for the difference in the change between the two groups. The other option was to calculate the RR and 95% CIs on the basis of a comparison of mortality rates at the end of the intervention or observation period in the intervention and control groups. We utilized the second option because baseline and/or change data were not available for all included trials. For computing the summary RR, we required individual trial RR and 95% CI or standard error. In the case of cluster-randomized trials citing cluster-adjusted values, we used the reported values. For trials reporting only cluster-specific data, we used a random-effects version of the STATA procedure XTLOGIT to derive an odds ratio, allowing for the cluster design. Random effects were fitted for each village, and the odds ratio was used to give an estimate of RR in the rare outcomes we were modeling.

The outcome variables were pooled using both fixed-effects and random-effects model assumptions. No comprehensive rules exist on when to use these models; debate continues in the statistical community. The underlying assumption for the fixed-effects model is that each trial estimates the same true population value for the effect of interest, and thus the differences between observed results of trials can be accounted for fully by sampling variation. Random-effects models assume that a distribution of population effects exists and is generated by a distribution of possible trial effect situations. Thus, outcomes of trials may differ both because of sampling variation and true differences in effects. Both random- and fixed-effects models can be appropriately applied to pooling of data and also for evaluating the sensitivity of results to differing model assumptions. The random-effects model is generally preferred in the presence of significant heterogeneity.

Sensitivity and subgroup analyses

Sensitivity and sub-group analyses were performed only for the primary outcome, all-cause neonatal mortality, to explore heterogeneity and also as a hypothesis-generating exercise. The following pre-specified sensitivity and subgroup analyses were performed: (i) preventive interventions versus preventive and curative interventions (antibiotics for neonatal sepsis) to examine the potential effect of adding curative treatment; (ii) high (>50 neonatal deaths per 1000 live births) versus low (⩽50 neonatal deaths per 1000 live births) baseline neonatal mortality (derived from the control group) to examine the possibility of a greater benefit in populations with higher baseline mortality; (iii) proportion of neonates receiving a postnatal visit (<50% versus ⩾50%) to examine the effect of the extent of coverage on mortality; and (iv) various elements of risk of bias assessment (low risk versus unclear and high risk). The contribution of these variables to heterogeneity was also explored by meta-regression using the ‘metareg’ command in STATA (version 9.2) software with the restricted maximum likelihood option.18

Results

Trial flow

A total of 85 potentially eligible references were identified.19, 20, 21, 22, 23, 24, 25, 26, 27, 28, 29, 30, 31, 32, 33, 34, 35, 36, 37, 38, 39, 40, 41, 42, 43, 44, 45, 46, 47, 48, 49, 50, 51, 52, 53, 54, 55, 56, 57, 58, 59, 60, 61, 62, 63, 64, 65, 66, 67, 68, 69, 70, 71, 72, 73, 74, 75, 76, 77, 78, 79, 80, 81, 82, 83, 84, 85, 86, 87, 88, 89, 90, 91, 92, 93, 94, 95, 96, 97, 98, 99, 100, 101, 102, 103 Among these, 77 references were excluded19, 20, 21, 22, 23, 24, 25, 26, 27, 28, 29, 30, 31, 32, 33, 34, 35, 36, 37, 38, 39, 40, 41, 42, 43, 44, 45, 46, 47, 48, 49, 50, 51, 52, 53, 54, 55, 56, 57, 58, 59, 60, 61, 62, 63, 64, 65, 66, 67, 68, 69, 70, 71, 72, 73, 74, 75, 76, 77, 78, 79, 80, 81, 82, 83, 84, 85, 86, 87, 88, 89, 90, 91, 92, 93, 95, 97 (Figure 1). The reasons for excluding these references are detailed in Table 1. The remaining eight references, which pertained to five trials, were included in the review.94, 96, 98, 99, 100, 101, 102, 103

Figure 1
figure 1

Trial flow for selection of randomized controlled trials. KMC, kangaroo mother care; TBA, traditional birth attendant.

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Table 1 Reasons for exclusion of individual references
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Trial characteristics

Table 2 summarizes the characteristics of included trials. All five trials were conducted in South Asia, and all were cluster-randomized trials, which provided cluster-adjusted mortality data.

Table 2 Characteristics of included randomized controlled trials
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Intervention package

Table 3 summarizes the CHW characteristics and intervention package used in the included trials. Substantial heterogeneity was evident for these aspects.

Table 3 Details of CHW characteristics and interventions
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Training and supervision of health workers

Table 4 summarizes the duration and content of training provided to the CHWs delivering the intervention in the respective trials. Substantial heterogeneity was evident for these aspects.

Table 4 Training and supervision of CHWs
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Risk of bias assessment

The risk of bias assessment for these trials is detailed in Table 5 and depicted graphically in Figure 2. Except for an unclear risk of selection bias in one trial, all studies were assessed to be at low risk of bias for all elements.

Table 5 Details of risk of bias assessment for individual trials
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Figure 2
figure 2

Graphical summary of risk of bias assessment in included trials.

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Quantitative data synthesis

All five trials provided neonatal mortality data,94, 96, 98, 99, 100, 101, 102, 103 and three trials provided perinatal mortality data.96, 100, 101 One trial provided infant mortality data,100 and one trial provided cause-specific mortality data.102

The Shivgarh (India) trial96 had two very similar intervention groups, with home-based essential newborn care as the core intervention. One intervention group additionally used a technology called ‘Thermospot’ to help caregivers decide if their newborn’s temperature was low. We therefore excluded the intervention arm with ‘Thermospot’ and used the data provided by the authors comparing only the home-based neonatal care group with the control group.

The Sylhet (Bangladesh) trial99 also had two intervention arms, one called ‘home care’ and the other ‘community care’. We excluded the ‘community care’ arm from the analysis because the interventions in this arm did not meet the inclusion criteria for this review.

Neonatal mortality

All five trials provided neonatal mortality data.94, 96, 98, 99, 100, 101, 102, 103 The funnel plot (Figure 3) appeared symmetrical, and there was no evidence of significant (P=0.204) bias with the Egger’s (weighted regression) method. The intervention was associated with a reduced risk of mortality during the neonatal period; the pooled relative risk was 0.75 (95% CI 0.61 to 0.92, P=0.003; I2=82.2%, P<0.001) by random effects model (Figure 4) and 0.82 (95% CI 0.76 to 0.89, P<0.001) by fixed-effects model.

Figure 3
figure 3

Funnel plot for detection of publication bias. s.e., standard error.

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Figure 4
figure 4

Forest plot for relative risk of neonatal mortality.

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On performing pre-specified sensitivity and subgroup analyses (Table 6) significant heterogeneity was suggested only with higher baseline neonatal mortality. Trials with a baseline rate of more than 50/1000 live births had a significantly greater reduction in neonatal mortality (RR 0.46; 95% CI 0.35 to 0.60; P<0.001), compared with trials with a baseline rate <50/1000 live births (RR 0.86; 95% CI 0.79 to 0.94, P<0.001; heterogeneity P<0.001) (Figure 5). There was no evidence of significant heterogeneity in the other two pre-specified subgroups, namely, the coverage of home visits (Figure 6) and the type of care (Figure 7). The details of program coverage and curative treatment offered in various trials are depicted in Tables 7 and 8, respectively. The pre-specified sensitivity analyses for bias could not be performed because, except for an unclear risk of selection bias in one trial, all studies were assessed to be at low risk of bias for all elements.

Table 6 Sensitivity and subgroup analyses for the RR of neonatal mortalitya
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Figure 5
figure 5

Forest plot for relative risk of neonatal mortality stratified by baseline neonatal mortality rate (random effects model).

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Figure 6
figure 6

Forest plot for relative risk of neonatal mortality stratified by coverage of home visits (random effects model).

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Figure 7
figure 7

Forest plot for relative risk of neonatal mortality stratified by presence of curative intervention (antibiotics) for sepsis (random effects model).

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Table 7 Program coverage and RR of neonatal mortality in individual trials
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Table 8 Sepsis treatment in relation to RR of neonatal mortality in individual trialsa
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On performing univariate meta-regression (Table 9) analyses, none of the variables emerged as significant predictors of heterogeneity. However, baseline neonatal mortality approached conventional statistical significance (P=0.065).

Table 9 Meta-regression analysis for neonatal mortality (univariate)a
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We conducted a post hoc sensitivity analysis by combining evidence from three23, 24, 25, 95, 97 non-randomized or quasi-randomized trials with concurrent control groups (Figure 8). There was no evidence of significant heterogeneity (P=0.192) for the comparison between randomized and non-randomized trials. With the random effects model, the RR for randomized trials was 0.75 (95% CI 0.61 to 0.92; I2=82.2%) and for non-randomized trials was 0.67 (95% CI 0.40 to 1.13; I2=89.5%). The overall effect size with inclusion of all eight trials was 0.72 (95% CI 0.60 to 0.87; I2=83.8%).

Figure 8
figure 8

Forest plot for relative risk of neonatal mortality stratified by randomized and three additional non-randomized trials (random effects model).

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Infant mortality

Data were available from one trial that showed a significant decline in infant mortality with RR of 0.85 (95% CI 0.77 to 0.94).100

Perinatal mortality rate

Data were pooled from three trials.96, 100, 101 There was evidence of a reduced risk of perinatal mortality; the pooled RR was 0.78 (95% CI 0.64 to 0.94, P=0.009; I2=79.6%, P=0.007) by random-effects model (Figure 9). A similar result was obtained with the fixed-effects model.

Figure 9
figure 9

Forest plot for relative risk of perinatal mortality.

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Cause-specific mortality

Only one trial provided cause-specific mortality data in neonates in the form of rates in each comparison group without cluster-adjustment RRs.102

Summary of findings

The GRADE summary of findings is shown in Table 10. The quality of evidence was graded as high for neonatal and perinatal mortality, and moderate for infant mortality.

Table 10 GRADE summary of findings
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Discussion

This systematic review of five cluster-randomized trials indicates that home-based neonatal care provided by CHWs is associated with significant neonatal mortality reduction in resource-limited settings with poor access to health facility-based care (high-quality evidence). Data from three trials indicated a reduction in the perinatal mortality rate (high-quality evidence). There was evidence of a reduction in infant mortality in the only trial providing this information. The baseline neonatal mortality rate emerged as a potential predictor of the neonatal mortality effect.

Strengths and limitations of analyses

This updated systematic review incorporated relevant subgroup and meta-regression analyses, and there was no evidence of publication bias. All cluster-randomized trials were appropriately combined by design effect correction for mortality outcomes. This review represents the synthesis of the most contemporary evidence for translating into public health policy as all the included trials were published within the past 5 years.

Some limitations merit consideration. First, data on perinatal mortality was limited to three trials, whereas only one trial reported infant mortality and cause-specific mortality. Second, all trials were conducted in South Asia, which limits generalizing to similar settings in other continents, particularly sub-Saharan Africa. Trials evaluating community-based interventions without a specific element of home-based neonatal care delivered by a CHW were excluded because such data had different programmatic implications from the policy under consideration.

The findings of this systematic review are in conformity with two earlier reviews on this subject, which were not restricted to randomized trials. We included only randomized controlled trials to aim for the highest quality of evidence. However, the main findings remained stable in a post hoc sensitivity analysis combining the evidence from three additional non-randomized or quasi-randomized trials with concurrent controls (Figure 8).

As noted earlier, no comprehensive rules exist for when to use random effects or fixed effects models for meta-analysis. Fixed-effects analysis is appropriate if there is a reasonable assumption that the trials are estimating the same underlying treatment effect (that is, they are similar enough in their populations, interventions and methods to make this plausible). Random-effects analysis assumes a distribution of effect sizes, and it estimates the center of that distribution and the uncertainty around it. It is more appropriate for situations where there are differences in design, population or intervention between included trials that may be sufficient to affect their treatment effects. We preferred the random-effects model because of significant contextual differences in included trials and documentation of statistical heterogeneity (I2>50%) for neonatal mortality. However, the estimates from the random- and fixed-effects models were in broad conformity (Table 6).

Subgroup analyses and meta-regression suggested a greater survival benefit in settings with higher baseline neonatal mortality rates. Home-based neonatal care interventions are primarily effective in reducing neonatal sepsis and mild asphyxia. As the neonatal mortality rate decreases in an area, the cause-specific mortality due to sepsis decreases and asphyxia probably remains unchanged, whereas the proportion of mortality due to preterm births (as well as the absolute number) increases. In the Mirzapur trial102 (baseline neonatal mortality rate 27.9/1000 live births), nearly 60% of deaths were due to birth asphyxia or prematurity; the program had limitations in reaching households at critical times (that is, during labor, childbirth and immediately after delivery) to address these conditions, whereas the CHWs lacked the necessary tools and skills to effectively attend to them. Unfortunately, the other trials did not provide cause-specific mortality to explore this possibility. In settings with lower baseline neonatal mortality rates, there may be a greater role of community mobilization and effective referral to facility-based care to address these causes of death.

Program coverage did not emerge as a significant predictor of the decrease in the neonatal mortality effect. However, program coverage was defined by the number of live births receiving a postnatal home visit in the first 48 to 72 h. Hence, it does not encapsulate the whole construct of the intervention that the trials had employed; many trials had excellent community mobilization programs in spite of low coverage of postnatal visits.101 Furthermore, with a sample size of five trials, the analysis had limited power to detect a positive predictor.

The addition of a curative component (antibiotics for neonatal sepsis) to the intervention did not emerge as a significant predictor of neonatal mortality. No included trial provided for treatment of birth asphyxia by CHWs as part of the home-based package of neonatal care, and it is unclear whether providing training and equipment to CHWs reduces mortality due to asphyxia.68, 104 As CHWs are likely to encounter asphyxia only sporadically, continued training for maintenance of skills to manage it may be challenging.

In all the trials under review, the intervention was delivered as a package comprising three components, namely, home visits during pregnancy (four trials), home-based neonatal care (all trials) and community mobilization efforts (four trials). The reduction in neonatal and perinatal mortality cannot therefore be solely ascribed to the home-based neonatal care component. However, from a programmatic perspective this is not crucial; in practice antenatal visits would be required to establish contact with pregnant women for postnatal visits, and health workers can also perform some community mobilization services.

Implications for policy

Home-based neonatal care is associated with reductions in neonatal and perinatal mortality in settings with high neonatal mortality rates and poor access to health facility-based care. The high-quality evidence in this review thus provides support for adopting a policy of home-based neonatal care provided by CHWs in such settings. Concrete recommendations cannot be made regarding the optimal timing of home visits and specific responsibilities of CHWs. However, data suggest that antenatal visits and home-based neonatal care within the first week of life should be an integral part of this intervention. Incorporating a component of community mobilization in addition to home-based neonatal care would be desirable. All the evidence pertains to South Asia; however, there are no obvious reasons to suspect different results in other regions with similar neonatal mortality rates and access to health care.

Implications for future research

The following gaps in evidence should be addressed as a priority to provide further directions for policy: (i) efficacy of the intervention package in similar settings in other regions, particularly sub-Saharan Africa; (ii) evaluating the benefit of adding treatment of sepsis and birth asphyxia; (iii) the effect of the intervention package on infant and cause-specific mortality; and (vi) operational research in pilot programs to evaluate coverage levels and quality, reasons for poor performance and possible interventions for improvement.

Concluding comments

Home-based neonatal care is associated with reductions in neonatal and perinatal mortality (high-quality evidence) in South Asian settings with high neonatal-mortality rates and poor access to health facility-based care. Adopting a policy of home-based neonatal care provided by CHWs is justified in such settings.