Study settings

Among the 14 included studies, seven were from Africa (three KwaZulu-Natal, South Africa,39–41 two Mali,42 43 one Ethiopia44 and one Senegal.45 The two reports from Mali42 43 and the two from rural South Africa,40 41 respectively, studied the same interventions delivered to the same populations, differing only with regard to when—and in South Africa, how—impact was assessed. Six studies were from Southeast Asia (three India,46–48 one Bangladesh,49 one Nepal50 and one Pakistan.51 Two reports from Haryana, India47 48 evaluated the same intervention delivered to the same population but assessed different outcomes. One study was from the Americas, in Dominican Republic.52 Four studies took place in urban or periurban settings,39 42 43 52 and eight in rural settings;40 41 44–46 49–51 the studies in Haryana47 48 did not indicate whether the setting was rural or urban.

Study designs and outcomes

The KwaZulu-Natal, South Africa39–41 and Haryana, India47 48 studies were cluster RCTs that evaluated a range of access to care, morbidity and mortality outcomes; the rural South Africa study did not report outcomes separately for children under 5 years.40 41 Two studies were NRCTs that measured morbidity outcomes;49 52 the Bangladesh study did not report outcomes separately for children under 5 years.49 The Nepal study50 that used a non-randomised, stepped-wedge design to assess risk of death among infants and children did not compare results between early and late treatment groups. Instead, it compared annual risks to baseline and used a test for trend to assess programme maturity. This study was therefore considered in this review to be an uncontrolled before–after study from baseline to end-line.

Four studies used a CBA design44–46 51 and reported percent differences or difference-in-differences for mortality, morbidity or access to care outcomes. However, some did not use the baseline or control group appropriately. The Pakistan study51 reported different baseline years for intervention and control areas; therefore, this study was deemed a NRCT and only the postintervention comparison between groups was presented in this review. The Ethiopia study44 presented a number of before–after access to care indicators for the intervention group, but only present before–after data for the comparison group for one outcome, the tuberculosis case notification rate; outcomes were not reported separately for children under 5 years. Finally, the Mali studies42 43 were included as ITS designs; yet, with only one baseline, they lacked a comparative preintervention trend and thus were treated in the review as uncontrolled before–after studies from baseline to end-line.

Participants

Half of the studies extended CHW services to the entire population,42–45 49 53 54 among which only the Mali studies42 43 reported outcomes specifically for children under 5 years. Five studies recruited pregnant women and delivered a mother–child intervention during the neonatal period, and in some cases, into infancy and childhood.39 46–48 52 The remaining two studies tested interventions that targeted children under 5 years of age during a period of 3 years.50 51

Characteristics of CHW programmes

The Bangladesh,49 Ethiopia,44 Senegal,45 rural South Africa40 41 and more recent India47 48 studies provided supplemental training in the context of the study (two-half days in Bangladesh, 1 day in Senegal, 8 days in India, 60 days in South Africa and unreported in Ethiopia) to CHWs from an already established CHW cadre. The remaining studies evaluated CHW programmes initiated by a research institute, all of which recruited local, literate community members and trained them for a duration of 60 hours52 to 6 months.46 In half of all programmes, CHWs were exclusively or predominantly female. Reporting of recipient and CHW sample sizes, and therefore CHW to population ratios, was poor.

Eleven studies reported enhanced CHW supervision as an adjunct to the intervention. However, the supervision strategy and frequency were not adequately described. Supervisors included physicians,46 nurses,51 accredited social health activists47 48 or senior project staff42 50 who monitored CHW activities periodically. Other studies employed a dedicated cadre of CHW supervisors, either based at the facility40 41 or in the community.43 44 Eleven studies paid CHWs for their work, with a salary in-line with government standards,39 43 44 50 a performance-linked46 or task-based47 48 remuneration scheme, or some other form of payment.40 41 45

CHWs provided services for the range of conditions eligible for inclusion in the review. CHWs in Mali,42 43 India46–48 and periurban South Africa39 provided integrated management of common neonatal and childhood illnesses. CHWs provided care exclusively for diarrhoea in Bangladesh;49 for pneumonia in Pakistan and Nepal;50 51 for malaria in Senegal;45 for malnutrition and at risk of being overweight in Dominican Republic;52 for tuberculosis in Ethiopia;44 and for HIV, tuberculosis, and sexually transmitted infections in rural South Africa.40 41 In addition to proactive case detection, most studies included doorstep treatment by CHWs and referral to a facility if necessary, with the exception of the studies in Dominican Republic, Ethiopia and periurban South Africa,39 44 52 which limited postdetection activities to referral for treatment and home-based follow-up.

Most studies compared proactive case detection by CHWs to the standard of care—passive case detection at public or private health facilities; six studies also included passive case detection by CHWs in the control arm. The South African studies included control CHWs who conducted home visits for purposes other than proactive case detection. Control arm CHWs conducted one pregnancy and two postnatal home visits to assist with securing identity documents and social grants in the urban study,39 and home visits to promote and refer clients to HIV counselling and testing in the rural studies.40 41

Selection bias

All studies, with the exception of those in Mali,42 43 allocated the study area into intervention and control groups. Five studies used cluster randomisation to assign groups.39–41 47 48 Among seven studies that did not use random allocation, sufficient evidence was provided in only two45 46 that outcome measurements were similar between groups at baseline, and in only three46 50 52 that population-level and/or cluster-level characteristics were similar between groups at baseline.

Performance bias and detection bias

Due to the nature of the intervention, blinding of participants and study personnel to allocation assignment was not possible and was scored high risk for all included studies. All six Southeast Asian studies46–51 and the periurban South Africa study39 blinded outcome assessors to allocation assignment, earning a low detection bias score.

Attrition bias

Reporting of incomplete outcome data varied considerably between studies. Studies involving pregnant women for a neonatal intervention discussed attrition bias with the use of a trial profile.39 47 48 52 A Data Safety and Monitoring Board stopped the Haryana, India trials early after the required sample size had been met, but prior to about half of children completing the 12-month assessment.47 48 Risk of attrition bias was high in the Dominican Republic study where roughly a quarter of mother–child dyads were lost, and there were statistically significant differences in some baseline characteristics that could be associated with the outcome between those who completed follow-up and those who did not.52 Missing survey data for date of birth and death were imputed in the Mali studies, but the extent and patterns of missing data were explicitly reported.42 43 Studies from India46 and Nepal50 did not comment on completeness of outcome data, but data were collected by an independent set of workers and analysed on an intention to treat basis. CBA studies in Pakistan51 and Senegal45 relied on CHWs to collect outcome data in intervention clusters and employed periodic surveys in control clusters. These studies did not discuss incomplete outcome data and were scored high risk due to the differences in data source and methods between the two groups.

Reporting bias

A published protocol was found for only one study.39 No studies reported outcomes in the methods that were then subsequently omitted from the results and, therefore, no studies were scored as being at high risk of reporting bias. Some studies subsequently added outcomes from posthoc analyses, but provided justifiable reasons for inclusion of the additional outcomes that were not prespecified.39 47 48

Protection against contamination

Risk of bias due to contamination was scored as low when large units of allocation were chosen and efforts to minimise contamination were discussed and/or a map was provided showing geographic separation of groups.44 46–50

Mortality

Seven studies measured mortality outcomes (table 2; Figure 1). Proactive case detection may reduce neonatal mortality (low certainty evidence). However, the effects vary and it is possible that it makes little or no difference to neonatal mortality (calculated RRs: 0.43 to 1.07; I²=79.1%). Proactive case detection may reduce infant mortality (calculated RRs: 0.52 to 0.94; I²=61.9%) (low certainty evidence). It is uncertain whether proactive case detection reduces mortality among children under 5 years (calculated RRs: 0.04 to 0.80; I²=94.4%) because the certainty of this evidence is very low.

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Figure 1

Forest plots for neonatal (top), infant (middle) and under 5 (bottom) mortality. CBA, controlled before–after; RR, risk ratio.

Three studies assessed impact on neonatal mortality over a 2–3 year timeframe (table 2; Figure 1). It was the primary outcome in the Maharashtra46 and Haryana47 studies of proactive case detection of newborn and infant danger signs, infections and illnesses. In rural Maharashtra, there was a 62% reduction in intervention areas compared with control areas (p<0.001).46 In Haryana, the neonatal mortality rate beyond the first 24 hours of life was lower in intervention clusters than in control clusters (adjusted HR=0.86; 95% CIs: 0.79 to 0.95), but not the case for the neonatal mortality rate overall—an effect, they explained, due to the higher than expected proportion of neonatal deaths occurring in the first 24 hours on which the intervention was unlikely to have had an effect.47 In both Maharashtra and Haryana, intervention groups included a mother’s education component and system strengthening in terms of user fee removal for CHW care46 or training of other provider cadres in Integrated Management of Newborn and Childhood Illnesses.47 An exploratory analysis of the effect of a home visit programme in periurban South Africa to improve appropriate infant feeding and HIV-free infant survival39 on neonatal mortality showed an increased risk of death in intervention compared with control clusters, although the effect was not statistically significant (RR=1.07; 95% CIs: 0.69 to 1.63).

Four Southeast Asia studies assessed infant mortality. The Maharashtra46 and Haryana47 studies found significant reductions (respectively, 45.7%; p<0.001 and AHR=0.89; 95% CIs: 0.78 to 1.00) in infant mortality between intervention and controls. Proactive case detection of childhood respiratory infection and doorstep treatment of suspected pneumonia compared with facility-based care led to reductions in infant mortality in rural Nepal,50 where cotrimoxazole was provided at home free of charge, and in rural Pakistan,51 where CHWs treated at home or referred to facilities where treatment protocols had been standardised. In Nepal, the greatest reduction in mortality after 3 years of intervention activities was seen in infants aged 6–11 months (RR=0.36; 95% CIs: 0.24 to 0.56). In Pakistan,51 the infant mortality rate was 74/1000 in the intervention area during the first 2 years of the study compared with 93/1000 in the control area.

A reduction in mortality was seen for all children under 5 years of age in Nepal, with a relative risk reduction of 0.72 from baseline to year 3,50 and in Pakistan, with a 26% reduction between intervention (29/1000) and control (39/1000) areas during the first 2 years of the study.51 In periurban Mali, the under-5 mortality rate declined from 154/1000 at baseline to 25/1000 after 3 years of proactive case detection of common childhood conditions in addition to primary health centre reinforcements and removal of user fees, and to 7/1000 after 7 years.43

Morbidity

Six studies assessed prevalence of disease, and four assessed hospitalisation (table 3; Figure 2). Proactive case detection may improve nutritional outcomes (low certainty evidence), although the effects vary, and it is possible that it makes little or no difference to nutritional outcomes (calculated RRs range from 0.61 to 1.16; I²=61.4%). It is uncertain whether proactive case detection reduces the prevalence of infectious diseases (calculated RRs: 0.06 to 1.02; I²=90.6%) or hospitalisation (calculated RRs: 0.38 to 1.26; I²=94.5%) because the certainty of this evidence is very low.

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Figure 2

Forest plots for prevalence of common childhood infections (top) and nutritional conditions (middle), and hospitalisation (bottom). BA, before–after; CBA, controlled before–after; RR, risk ratio.

In Mali42 43 and rural Senegal,45 proactive case detection of malaria led to significant reductions in the odds of febrile illness among children under five (adjusted OR (AOR) after 7 years=0.45; 95% CIs: 0.32 to 0.62), and symptomatic malaria among the general population in intervention villages compared with control villages (AOR=0.03; 95% CIs: 0.02 to 0.07), respectively. The Haryana48 study found significant reductions in danger signs (adjusted RR (ARR)=0.82; 95% CIs: 0.67 to 0.99) and local infection (ARR=0.91; 95% CIs: 0.71 to 1.17) among neonates, as well as diarrhoea (ARR=0.63; 95% CIs: 0.49 to 0.80) and pneumonia (ARR=0.60; 95% CIs: 0.46 to 0.78) among infants. The urban South Africa39 and Dominican Republic52 studies found no effects on childhood diarrhoea, a secondary intervention outcome.

The Dominican Republic52 study found that monthly home visits and mother’s groups to promote healthy babies and monitor physical growth during the first 2 years of life led to reductions in stunting (AOR=0.50; 95% CIs: 0.22 to 1.10) and risk of overweight (AOR=0.43; 95% CIs: 0.23 to 0.77), compared with standard facility-based controls. The Haryana48 study found no effect on wasting (ARR=0.99; 95% CIs: 0.94 to 1.04) or stunting (ARR=1.10; 95% CIs: 0.90 to 1.36) at 12 months of age in exploratory analyses. The South Africa39 study found an increase in infant weight-for-age (mean difference (MD)=0.09; SD: 0.00, 0.18) and length-for-age (MD=0.11; SD: 0.03, 0.19) z-scores, but not weight-for-length (MD=0.01; SD: -0.07, 0.09).

In Bangladesh,49 CHW home visits to inquire about diarrhoea and offer oral rehydration therapy packets free of charge were associated with a 29% reduction (p<0.01) in hospitalisation for diarrhoea compared with control villages with CHWs doing ‘surveillance and health work’. In the Haryana48 study, in which CHWs assessed newborns for signs of illness at each visit and treated or referred them, caregivers in the intervention clusters reported fewer hospital admissions during infancy (ARR=0.67; 95% CIs: 0.51 to 0.88). In the South Africa39 and Dominican Republic52 studies, where proactive CHWs did not offer doorstep treatment but referred all cases detected, caregivers reported more hospital admissions for their children, although results were not statistically significant.

Access to treatment

Four studies assessed access to effective and/or prompt treatment (table 3; Figure 3). Proactive case detection may increase access to effective treatment (calculated RRs range from 1.59 to 4.64; I²=97.0%) (low certainty evidence). It is uncertain whether proactive case detection increases access to prompt treatment (calculated RRs range from 1.00 to 2.39; I²=84.9%) because the certainty of this evidence is very low. Three studies assessed the effects of proactive case detection of HIV and/or tuberculosis on access to diagnostic services and/or treatment adherence support; these were excluded from the main analysis and summarised in online supplementary file 4.

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Figure 3

Forest plots for access to effective treatment (top) and prompt access to treatment (bottom). RR, risk ratio.

In Dominican Republic,52 proactive home visits increased the proportion of diarrhoeal children who received oral rehydration solution (AOR=3.86; 95% CIs: 1.14 to 13.02). In Haryana,48 caregivers in intervention clusters were more likely to seek any treatment within 24 hours and treatment from an appropriate provider for newborns with danger signs (respectively, ARR=1.14; 95% CIs: 1.10 to 1.18 and ARR=1.76; 95% CIs: 1.36 to 2.24) and local infections (respectively, ARR=1.97; 95% CIs: 1.71 to 2.27 and ARR=4.86; 95% CIs: 3.80 to 6.21). Caregivers were no more likely to seek any treatment within 24 hours for infants with diarrhoea (ARR=0.99; 95% CIs: 0.89 to 1.10) or pneumonia (ARR=1.10; 95% CIs: 0.96 to 1.25), but more likely to seek treatment from an appropriate provider for diarrhoea (ARR=1.22; 95% CIs: 1.06 to 1.42) or pneumonia (ARR=1.44; 95% CIs: 1.00 to 2.08). In Mali,42 43 a higher proportion of children with fever received antimalarial treatment within 24 hours of symptom onset compared with baseline (AOR=3.20; 95% CIs: 1.75 to 5.85).