Health system and community level interventions for improving antenatal care coverage and health outcomes

  • Protocol
  • Intervention

Authors


Abstract

This is the protocol for a review and there is no abstract. The objectives are as follows:

To assess the effects of health system and community interventions for improving coverage of antenatal care and other outcomes.

Background

In 2010, about 287,000 maternal deaths occurred worldwide (WHO 2012a). Despite considerable efforts to curb maternal mortality, close to 800 women continue to die every day due to complications of pregnancy and childbirth, and about 99% of these deaths occur in developing countries (WHO 2012c). In these settings, neonatal mortality rates are also high, despite the availability of evidence-based interventions that could avert up to 72% of neonatal deaths (Darmstadt 2005). Interventions such as maternal immunisation against tetanus and skilled care at delivery can reduce both maternal and neonatal deaths (Lassi 2010).

Interventions to reduce maternal mortality may focus on three periods. The first is during pregnancy (antenatal care (ANC)), the second is the intrapartum period,(i.e. during labour and delivery) and the third is in the post-partum period (after delivery). The intrapartum period is much shorter and less predictable than the longer more stable pregnancy period (Mbuagbaw 2011). It is also more challenging to provide adequate care in this period, especially in developing countries where human resource shortages and other health system weaknesses limit the availability of emergency obstetric care (Dogba 2009). ANC, on the other hand, is less resource-intensive and its provision can be spread throughout the pregnancy period.

ANC generally comprises the following interventions (Kinzie 2004).

  1. Health promotion: ANC is an opportunity to educate the woman about her health, pregnancy and child birth, recognising danger signs, the benefits of good nutrition, the harms of alcohol, tobacco and drugs, exclusive breast feeding and other relevant issues.

  2. Disease prevention: immunisation against tetanus, prophylactic treatment against malaria, protection against iron deficiency anaemia are some conditions that can de addressed during ANC visits.

  3. Early detection and treatment for complications and diseases: pregnant women would be screened for syphilis, human immunodeficiency virus (HIV) and other sexually transmitted infections (STI). Complications of pregnancy such as pre-eclampsia and eclampsia, infection and vaginal bleeding among others can be addressed.

  4. Birth preparedness: the pregnant woman is counselled on her decision about where to deliver, choice of a skilled birth attendant and a care-giver (for herself or her other children at home). The ANC visit may cover planning for transportation to the hospital, costs of care and supplies for delivery.

  5. Complication readiness: women are encouraged to have an emergency plan for complicated deliveries. This plan should include money for extra medical or surgical care and potential blood donors.

ANC may not address all the causes of maternal deaths; however, it is positively associated with receiving professional assistance at delivery (Bloom 1999; Mbuagbaw 2011; Mishra 2006; Oakley 2009) and improved pregnancy outcomes such as normal birthweight (Mbuagbaw 2011). In different regions, the effects of ANC on enhancing rates of delivery in a health facility are disparate (Mbuagbaw 2011; Raatikainen 2007).

Description of the condition

The World Health Organization (WHO) recommends at least four ANC visits for all pregnant women (WHO 2013).The first visit should take place during the first trimester (before the 12th week but no later than the 16th week), the second visit between the 24th and 28th week, and the third and fourth visits at 32 weeks and 36 weeks respectively. Reports indicate that only 53% of pregnant women worldwide receive this amount of care (WHO 2013). Coverage is lower in developing countries where the use of maternal health care in general is limited and varies widely within and between countries (Say 2007). Poor attendance of ANC is associated with delivery of low birthweight infants (Mbuagbaw 2011; Raatikainen 2007; Showstack 1984; Siza 2008) and more neonatal deaths (Raatikainen 2007). ANC models with reduced visits may also be linked to higher perinatal mortality (Dowswell 2010; Vogel 2013).

Measuring antenatal care

Even though the WHO recommends four ANC visits during pregnancy, this is not a very informative measure (WHO 2013), as it gives no indication of the quality or timing of the visits. Furthermore, there is no measure of access. A comprehensive measure of ANC should include a measure of personal health-seeking behaviour and also a measure of the availability of ANC services, as both are integral to effective ANC. More comprehensive measures have been proposed, which include the number and timing of visits, the provider of care and the adequacy of care provided (Delgado-Rodriguez 1996; Mbuagbaw 2011). Well-timed ANC visits are critical to the success of some interventions, as a systematic review has shown that adverse outcomes from syphilis can best be prevented by intervening in the first two trimesters (Hawkes 2013).The content of each ANC visit is also important, as some ANC interventions may not be beneficial, such as routine aspirin to prevent pre-eclampsia in low-risk women or external version for breech lie (Bergsjo 1997; Villar 1997). Irrespective of how it is measured, ANC is beneficial and represents an important point of contact with the health system for communication and pregnancy preparedness (Lassi 2010).

For the purposes of this review, coverage will be considered as the proportion of pregnant women who attend at least four ANC visits.

Description of the intervention

The fifth United Nations' Millenium Development Goal (MDG5) targets maternal health and explicitly calls for more ANC (United Nations 2013). The WHO now recommends a package of reduced visits with evidence-based interventions through goal-oriented clinic visits (WHO 2011). A variety of interventions can be used to increase the number of women who receive ANC. A systematic review on the effectiveness of interventions to improve early initiation of ANC in vulnerable populations identified two broad categories of interventions: outreach/community-based interventions and alternative models of clinic-based ANC. The former included the use of lay health workers and mobile health clinics, while the latter included adaptations of clinic-based ANC to be more collaborative and comprehensive, and also to accommodate teens (Oakley 2009).

Community-based interventions such as community support, mobilisation, education and home visits by trained community health workers can lead to significant reductions in maternal morbidity and neonatal mortality, and an increase in referrals to a health facility (Lassi 2010). In underserved areas, a community health van may improve access to adequate ANC (Edgerley 2007).

Other interventions, such as mass media campaigns, social mobilisation, information-education-communication (IEC) interventions, financial incentives, behaviour change interventions and policy interventions targeting health workers or pregnant women will also be investigated.

How the intervention might work

Interventions targeting the factors that reduce antenatal care coverage may be beneficial.

Health policy is a critical component of any health system and guides how resources (man power, money and material) are used. Policy can be applied at any level of the health system. Regional health managers are capable of making policy changes that influence the use of ANC services. Recent papers suggest that the effects of policy change in health outcomes should be explored in more detail (Dettrick 2013). Such policy changes may include capacity building in ANC to improve quality of care (Lassi 2010; Say 2007; van Eijk 2006), re-organisation of services to include more midwives providing ANC (Dowswell 2010; Khan-Neelofur 1998), and reduction of user fees to eliminate financial barriers (Lassi 2010; Mbuagbaw 2011; Say 2007; Titaley 2010; van Eijk 2006). Where coverage is better in the private sector (Cesar 2012), adopting their (private sector) model of care may be beneficial. Switching to individual counselling sessions may also improve the number of high-risk women delivering in hospitals (Ballard 2013).

Mass media campaigns can be used to improve the utilisation of health services (Grilli 2002), and may also help to improve the use of ANC services. Social mobilisation- engaging multiple stakeholders - is an important way of bringing change in communities. If pregnant women receive the same consistent message on the benefits of ANC from health workers, community health workers and in other social gatherings, they may be more likely to take heed. Lack of awareness (Lassi 2010; Titaley 2010) and misconceptions (Agus 2012; Say 2007) about ANC can be addressed using IEC sessions. Financial incentives can be used to encourage pregnant women to attend ANC and cover costs including user fees and transportation costs where these problems exist (Lassi 2010; Mbuagbaw 2011; Say 2007; Titaley 2010; van Eijk 2006). They are most effective in the short term, and in resource-limited settings (Marteau 2009). Behavior change interventions are interventions derived from a specific model or theory of behaviour change and can play a role in improving health outcomes (Marteau 2006). Such interventions could play an important role in encouraging women to attend ANC.

Why it is important to do this review

Regions of the world with low ANC coverage can benefit from a comprehensive synthesis of the evidence surrounding the ways in which ANC coverage can be improved. In these places, low ANC coverage comes with low rates of deliveries in health facilities and assistance by skilled birth attendants. The latter two factors are associated with high materno-fetal morbidity. This review will have important implications for reproductive health policy, the provision of services to women in reproductive ages and may highlight gaps in current evidence or openings for further research.

Objectives

To assess the effects of health system and community interventions for improving coverage of antenatal care and other outcomes.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs), quasi-randomised trials and cluster-randomised trials.

Types of participants

This review will include studies of stakeholders, providers of care and beneficiaries, including but not limited to:

  1. professional health workers;

  2. lay health workers;

  3. community members;

  4. pregnant women;

  5. women of reproductive age.

Types of interventions

All interventions susceptible to improve coverage of ANC are eligible for inclusion in this review. These interventions may be aimed at the health system, the population or both. Owing to the potentially wide variety of interventions, there will be no restrictions to duration or frequency of the intervention. For the purposes of this review, we are going to classify these interventions into the following two main categories.

Interventions aimed at the health system
  1. Policy changes

  2. Health worker education

  3. Re-organisation of health services

Interventions aimed at the community
  1. Mass media campaigns

  2. Social mobilisation

  3. Information-education-communication (IEC)

  4. Financial incentives

  5. Behaviour change interventions

Types of outcome measures

Primary outcomes
  1. Coverage of ANC: the proportion of pregnant women who attend at least four ANC visits during pregnancy.

  2. Pregnancy-related deaths: the proportion of women who die during pregnancy or 42 days after, irrespective of cause (WHO 2004).

Secondary outcomes
  1. Coverage of ANC: the proportion of pregnant women who attend at least one ANC visit during pregnancy.

  2. The proportion of pregnant women who initiate ANC in the first trimester.

  3. The proportion of pregnant women who receive ANC from professional health workers.

  4. The proportion of deliveries in health facilities.

  5. The proportion of pregnant women with a written birth and emergency plan by 37 weeks of pregnancy.

  6. The proportion of pregnant women who receive Intermittent Prophylactic Treatment (IPT) for malaria as per recommended guidelines (WHO 2012b).

  7. The proportion of women with tetanus protection at birth.

  8. The proportion of pregnant women who screen for syphilis.

  9. The proportion of women who screen for asymptomatic bacteriuria.

  10. The proportion of women who screen for HIV.

  11. The proportion of women with HIV who receive a complete antiretroviral course for prevention of mother-to-child transmission of HIV.

  12. Maternal near miss, defined as: "a woman who nearly died but survived a complication that occurred during pregnancy, childbirth or within 42 days of termination of pregnancy" (Pattinson 2009).

  13. The proportion of women with preterm labour or delivery.

  14. The proportion of low-birth-weight infants born.

  15. The incidence of perinatal mortality.

We will also consider combinations of the above outcomes if the data are not dissociable. For example, the proportion of women who have at least four well-spaced ANC visits attended by a professional health worker (Mbuagbaw 2011).

Search methods for identification of studies

Electronic searches

We will contact the Trials Search Co-ordinator to search the Cochrane Pregnancy and Childbirth Group’s Trials Register.

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

  1. monthly 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.

Searching other resources

We will search the reference lists of retrieved studies and contact authors and experts in the field. We will not apply any language restrictions.

Data collection and analysis

Selection of studies

Two review authors (L Mbuagbaw (LM) and H Garga (HG)) will independently assess for inclusion all the potential studies we identify as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third author (P Ongolo-Zogo (POZ)). Agreement on the inclusion of studies will be estimated using the Kappa statistic (Viera 2005).

We will create a Preferred Reporting Items for Systematic Reviews and Meta-analyses (PRISMA) study flow diagram to map out the number of records identified, included and excluded (Liberati 2009).

Data extraction and management

We will design and test a form to extract data. For eligible studies (abstract or full text), LM and HG will extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult the third review author (POZ). We will enter data into Review Manager software (RevMan 2012) and check for accuracy.

When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.

Assessment of risk of bias in included studies

LM and HG will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a third assessor (POZ).

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

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

We will assess 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.

(3.1) Blinding of participants and personnel (checking for possible performance bias)

We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are 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 will assess blinding separately for different outcomes or classes of outcomes.

We will assess the methods as:

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

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

(3.2) Blinding of outcome assessment (checking for possible detection bias)

We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.

We will assess methods used to blind outcome assessment as:

  • low, high or unclear risk of bias.

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

We will 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 will 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 can be supplied by the trial authors, we will re-include missing data in the analyses which we undertake.

We will assess 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.

Attrition of 20% or more will be considered as high risk of bias.

(5) Selective reporting (checking for reporting bias)

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

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

We will assess 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 will make explicit judgements about whether studies are at high risk of bias, according to the criteria given in the Handbook (Higgins 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.

For this review, it is likely that we will include cluster-randomised trials. If any cluster-randomised trials are included additional sources bias will be considered (Higgins 2011), such as:

  • recruitment bias: whether individuals are recruited into the trial after the clusters have been formed;

  • baseline imbalances: due to the small numbers of clusters;

  • attrition of entire clusters;

  • methods of analysis ignoring the correlation between members of the same cluster;

  • their comparability with individually-randomised trials.

Agreement on the authors' judgement on risk of bias with be estimated using the Kappa statistic (Viera 2005).

Measures of treatment effect

Dichotomous data

For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals.

Continuous data

For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised mean difference to combine trials that measure the same outcome, but use different methods.

Unit of analysis issues

Cluster-randomised trials

We will include cluster-randomised trials in the analyses along with individually-randomised trials. We will adjust their sample sizes using the methods described in the Handbook using an estimate of the intra cluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC.

If we identify both cluster-randomised trials and individually-randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both, if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomisation unit is considered to be unlikely.

We will also acknowledge heterogeneity in the randomisation unit and perform a sensitivity analysis to investigate the effects of the randomisation unit.

Other unit of analysis issues

Some of the included studies may have more than one intervention arm. In this event, both intervention arms will be combined, and pair-wise comparisons conducted.

Dealing with missing data

For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis.

For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat basis, i.e. we will attempt to include all participants randomised to each group in the analyses, and all participants will be 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 will be the number randomised minus any participants whose outcomes are known to be missing.

Assessment of heterogeneity

We will assess statistical heterogeneity in each meta-analysis using the I², T² and Chi² statistics. We will regard heterogeneity as substantial if an I² is greater than 30% and either a T² is greater than zero, or there is a low P value (less than 0.10) in the Chi² test for heterogeneity.

Assessment of reporting biases

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. If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis

We will carry out statistical analysis using the Review Manager software (RevMan 2012). We will use fixed-effect meta-analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect: i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random-effects meta-analysis to produce an overall summary, if an average treatment effect across trials is considered clinically meaningful. The random-effects summary will be treated as the average range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials.

If we use random-effects analyses, the results will be presented as the average treatment effect with 95% confidence intervals, and the estimates of T² and I².

We will consider the following comparisons.

  1. One intervention versus no intervention.

  2. Two interventions compared.

  3. One intervention versus a combination of interventions.

  4. Combination of interventions versus no intervention.

  5. Different combinations of interventions.

Subgroup analysis and investigation of heterogeneity

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 plan to carry out the following subgroup analyses.

  1. Urban versus rural settings.

  2. High-income versus lower-income settings.

  3. Interventions targeting the health system versus interventions targeting the population.

  4. Single versus combined interventions.

These subgroup analyses will be limited to the primary outcomes of the review.

We will assess subgroup differences by interaction tests available within RevMan (RevMan 2012). We will report the results of subgroup analyses quoting the χ2 statistic and P value, and the interaction test I² value.

Sensitivity analysis

Sensitivity analyses will be conducted to explore the effects of trial quality and trial design on the outcomes. In the first instance, we will compare the results from the studies with high risk of bias with those at low risk of bias, and secondly we will investigate the effect of the unit of randomisation (individual versus cluster) on the outcomes. Likewise, we will also explore the effects of fixed-effect or random-effects analyses for outcomes with statistical heterogeneity and the effects of any assumptions made such as the value of the ICC used for cluster-randomised trials.

Acknowledgements

We acknowledge the assistance of the Centre for the Development of Best Practices in Health (CDBPH) and the South African Cochrane Centre (SACC). This review is written within the scope of activities of the Effective Health Care Research Consortium (EHCRC).

As part of the pre-publication editorial process, this protocol has been commented on by three peers (an editor and two referees who are external to the editorial team), members of the Pregnancy and Childbirth Group's international panel of consumers and the Group's Statistical Adviser.

Contributions of authors

LM is the guarantor for this review. He contributed to the background and methods section of the protocol. LM, HG and POZ jointly conceived the idea for the review as a response to policy debates in Cameroon. All authors worked on the protocol and approved the final manuscript.

Declarations of interest

None known.

Sources of support

Internal sources

  • Centre for Development of Best Practices in Health, Cameroon.

  • South African Cochrane Centre, Medical Research Council, South Africa.

External sources

  • Effective Health Care Research Consortium, UK.

Ancillary