Interventions for preventing unintended pregnancies among adolescents

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To assess the effects of primary prevention interventions (school‐based, community/home‐based, clinic‐based, and faith‐based) on unintended pregnancies among adolescents.

Background

Adolescents are individuals aged from 10 to 19 years [1]. Adolescence is regarded as a period of transition, growth, exploration, and opportunities. During this phase of life, adolescents experience physical and sexual maturation and tend to develop an increased interest in sex, with attendant risks of unintended pregnancies, abortion, and sexually transmitted infections (STIs), including HIV/AIDS, and health risks associated with early childbearing.

Adolescents who have an unintended pregnancy face several challenges, including stigma, abandonment by their partners, parents, and peers, inability to complete school education (which ultimately limits their future social and economic opportunities), and increased adverse pregnancy outcomes [2, 3, 4, 5, 6, 7].

Description of the condition

Unintended pregnancy among adolescents remains a significant public health concern worldwide, affecting countries across all income levels [8]. In 2019, a report by the Guttmacher Institute reported that low‐ and middle‐income countries (LMICs) recorded approximately 21 million pregnancies annually among adolescents aged 15 to 19, with nearly half of these being unintended, resulting in an estimated 12 million births [9].

Globally, the adolescent birth rate has declined from 64.5 births per 1000 women in 2000 to 41.3 births per 1000 in 2023, with notable regional variations. In 2022, rates were 13.3 per 1000 in Europe, 99.4 in sub‐Saharan Africa, and 52.1 in Latin America and the Caribbean [10]. The USA has experienced similar reductions, with a 10% decline in unintended pregnancies from 2012 to 2013 and a decrease of over 50% between 1991 and 2013 [11]. In 2022, the birth rate among females aged 15 to 19 years was 13.5 per 1000, down from 16.7 in 2019, although disparities persist, disproportionately affecting Native Hawaiian or other Pacific Islander, Black, and Hispanic adolescents [12, 13]. In the USA, these declines have been attributed to delayed sexual debut, increased contraceptive use, and greater uptake of highly effective methods such as intrauterine devices (IUDs) and implants.[14]. Similar factors are likely contributing to the global decline in the number of adolescents giving birth.

Nevertheless, repeat adolescent pregnancies are common and are linked with increased maternal and child health risks [15]. Unintended pregnancies also impose substantial financial burdens, including an estimated 12 billion USD annually in Medicaid‐subsidised care in high‐income countries [16]. This includes welfare support, educational and skills programmes, and lost tax revenues due to reduced employability and earnings [17, 18, 19, 20].

Adolescent mothers often face educational challenges, low socioeconomic status, and environments shaped by intergenerational patterns of limited maternal education and unintended teenage pregnancies. Their children are at higher risk of low birth weight, neglect, abuse, school dropout, and delinquent behaviour [21, 22].

Description of the intervention and how it might work

A wide range of interventions has been developed to prevent unintended adolescent pregnancy due to its substantial individual, familial, and societal consequences [23, 24]. These interventions have different mechanisms of action, and include increasing sexual health knowledge, shifting attitudes and norms, building behavioural skills, strengthening family communication, improving access to services, and addressing broader psychosocial determinants.

Curriculum‐based sex education programmes (e.g. Safer Choices [25], All for You [26]) aim to improve knowledge, attitudes, perceived norms, and self‐efficacy related to safer sexual behaviour. Abstinence‐alone programmes (e.g. Postponing Sexual Involvement [27], Sex can Wait [28]) focus on delaying sexual initiation. Comprehensive multicomponent models such as SHARE [29], RIPPLE ([30]), and the CAS‐Carrera program [31], integrate sexual health education with youth development and skill‐building activities.

Technology‐based interventions, including websites, apps, and text messages (It’s Your Game (IYG)‐Tech [32, 33], Pulse [34], and Girl2Girl for LGB+ youth [35]), deliver tailored sexual health content, increase privacy, and allow broad, low‐cost reach. Clinical and one‐to‐one interventions (e.g. emergency contraception provision [36], clinic‐based protocols [37], counselling programmes [38], and counselling for young men [39] improve access to services and individual risk management. Youth development and vocational programmes (e.g. Reach for health service‐learning program [40], Teen Outreach Program (TOP) [41]; and Summer Training and Education Program (STEP) [42] target non‐sexual antecedents, such as academic engagement, future aspirations, and positive social connections, to reduce risk‐taking behaviour.

Because adolescent pregnancy is influenced by multiple factors, interventions may be more effective when they combine sexual health education with broader developmental components and involve key stakeholders, including families, schools, health services, and community organisations. Cultural and religious influences may further shape the impact of interventions; for example, differences in pregnancy rates have been observed across religious groups [43, 44], suggesting potential roles for sustained faith‐based approaches. It has been argued that effective strategies address multiple sexual and non‐sexual factors and may be strengthened by mass media initiatives and expanded family‐planning services [45].

Why it is important to do this review

Existing reviews provide conflicting conclusions regarding which adolescent pregnancy prevention interventions are effective, and many of them have significant methodological limitations, including reliance on non‐randomised designs, exclusion of unpublished studies, and inadequate statistical analyses [46, 47, 48, 49]. Furthermore, most reviews focus on studies conducted in high‐income countries, limiting their applicability to other social and economic contexts [46]. These limitations hinder the ability of policymakers, programme implementers, and global health agencies to make decisions informed by reliable evidence. A rigorous, comprehensive synthesis of randomised controlled trials using Cochrane methods is therefore essential to generate reliable evidence about which interventions work, for whom, and in which contexts. By doing so, we hope this review will help address the gaps in the research and support more effective resource allocation, programme design, and public health policy.

Objectives

To assess the effects of primary prevention interventions (school‐based, community/home‐based, clinic‐based, and faith‐based) on unintended pregnancies among adolescents.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs) of individual or cluster design. We will include only trials with a minimum follow‐up of four weeks to ensure that there is sufficient time for the intervention to plausibly influence sexual behaviours and for early pregnancy outcomes to be detectable. Shorter follow‐up periods are unlikely to capture meaningful behavioural change or pregnancy‐related outcomes and may therefore underestimate intervention effects.

We will exclude cross‐over trials because educational and behavioural interventions aimed at preventing unintended pregnancy among adolescents are likely to have sustained effects, making cross‐over designs inappropriate due to the risk of carry‐over and contamination.

We will also exclude quasi‐RCTs, in which allocation is based on predictable, non‐random methods (e.g., date of birth, day of the week, or record number), as these approaches are associated with a higher risk of selection bias and limit causal inference.

In addition, we will exclude studies evaluating interventions focused solely on HIV/STI prevention or other sexual risk behaviours that do not explicitly address pregnancy prevention or unintended pregnancy outcomes.

Types of participants

We will include adolescents (individuals aged 10 to 19 years) [50], irrespective of gender. We will include only studies in which all participants fall within this age range or where data for adolescents can be extracted separately. Studies including broader age ranges without disaggregated data for adolescents will be excluded.

Types of interventions

We will include any intervention, whether health education, counselling, skills‐building, contraceptive education and/or distribution, or faith‐based group or individual counselling, that is designed to do one or more of the following.

• Increase adolescents’ knowledge and attitudes about the risk of unintended pregnancy

• Promote delay in the initiation of sexual intercourse

• Encourage consistent use of birth control methods

• Reduce unintended pregnancies

We will categorise the interventions as follows.

• Educational interventions: health education, community services, counselling only, health education plus skills‐building, faith‐based group or individual counselling

• Contraception‐promoting interventions: contraception education with or without distribution of contraception

• Combined interventions:

  • a combination of educational interventions and contraception‐promoting interventions, and/or

  • additional components such as structural or economic interventions (e.g. financial incentives, conditional cash transfers, school retention support, or community‐level interventions) designed to influence behaviour related to unintended pregnancy.

Participants in the comparator group may receive no intervention, usual practice (e.g. standard school‐ or community‐based programmes), or an alternative intervention aimed at reducing unintended pregnancy.

For eligible studies, we will not restrict inclusion based on the frequency, duration, or intensity of the interventions evaluated.

We will exclude studies of interventions that address HIV/STI outcomes only, without an explicit pregnancy or unintended pregnancy prevention objective.

We will also exclude studies where the evaluation of pregnancy‐related outcomes is not part of the stated aims of the intervention, but any report of these outcomes is incidental or post hoc.

Outcome measures

We will extract outcome data at the longest follow‐up reported in each study, to capture the sustainability of intervention effects.

Critical outcomes

• Unintended pregnancy (whether clinically recorded or self‐reported by either the pregnant adolescent or her male partner)

Important outcomes

• Reported changes in knowledge and attitudes regarding the risk of unintended pregnancy, defined as:

  • perceived likelihood of becoming pregnant or causing a pregnancy, or

  • the consequences of unintended pregnancy)

This outcome should be measured using validated or study‐specific questionnaires or scales, and reported as changes in scores over time.

• Initiation of sexual intercourse (e.g. self‐reported onset of sexual activity)

• Use of birth control methods (e.g. self‐reported use of contraception, including condom use and consistency of use, reported as proportions or changes over time)

• Pregnancy‐related outcomes, including:

  • abortion (e.g. self‐reported or clinically recorded, including rates or proportions of participants experiencing abortion);

  • childbirth (e.g. self‐reported or clinically recorded, including rates or proportions of participants experiencing childbirth);

  • morbidity related to pregnancy, abortion, or childbirth (as reported by study authors);

  • mortality related to pregnancy, abortion, or childbirth (as reported by study authors)

• Sexually transmitted infections (STIs) (whether laboratory‐confirmed or self‐reported diagnosis)

Search methods for identification of studies

The Fertility Regulation Group Information Specialist will conduct a search for all published, unpublished, and ongoing studies, without restrictions on language or publication status. The search strategies proposed for each database are available in Supplementary material 1.

Electronic searches

We will search the following databases from their inception to present.

• Cochrane Central Register of Controlled Trials (EBM Reviews), Ovid platform

• MEDLINE, Ovid platform

• Embase, Ovid platform

• PsycINFO, Ovid platform

• ERIC, Ebsco platform

• Global Index Medicus, Ovid platform

We will also search for ongoing trials on the following trial registries.

• ClinicalTrials.gov (https://www.clinicaltrials.gov)

• World Health Organization International Clinical Trials Registry Platform (ICTRP) (https://www.who.int/trialsearch)

We will combine the MEDLINE search with the Cochrane highly sensitive search strategy for identifying randomised trials, which appears in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions [51]. We will combine the Embase search strategy with an RCT filter developed by the Scottish Intercollegiate Guidelines Network (SIGN).

Searching other resources

We will search the reference lists of all included trial reports to identify additional eligible studies. In addition, we will screen for errata, retractions, and other post‐publication amendments associated with included or potentially eligible studies. This will be done by checking bibliographic databases (e.g. PubMed (https://pubmed.ncbi.nlm.nih.gov/) for linked corrections or retraction notices, searching the Retraction Watch database (https://retractionwatch.com/), and reviewing journal and publisher websites as needed. We will exclude retracted studies, and we will assess studies with errata to determine the extent to which the corrections affect the reported data, results, or conclusions.

Data collection and analysis

Selection of studies

At least two review authors will independently screen titles and abstracts identified through the search against the eligibility criteria, using Covidence [52]. We will retrieve full‐text copies of potentially relevant studies, and two review authors will independently assess them for inclusion, recording reasons for exclusion where applicable. We will resolve any disagreements at either stage through discussion, and, if necessary, consultation with a third review author. To minimise bias, the results sections of publications will be blinded during screening.

We will remove duplicates and collate multiple reports of the same study, as the unit of interest for this review is the study rather than individual reports. The study selection process will be presented in a PRISMA flow diagram [53].

For studies published in languages other than English, we will use translation software (e.g. Google Translate or similar). We may assess the accuracy of translations using artificial intelligence tools (e.g. ChatGPT, DeepSeek, or similar). Any inconsistencies or context issues will be resolved through review by an individual fluent in the target language.

Data extraction and management

For eligible studies, at least two review authors will independently extract the data using Covidence [52], following a pilot of the data extraction form. We will extract the following data from the included studies.

• Methods: type of trial (individual or cluster), method of allocation, type of allocation concealment (adequate, unclear, inadequate, or not done), provider and outcome assessor blinding, number lost to follow‐up, and potential confounders

• Participants: sample size, study setting (including country, state, region, community), and unit of randomisation (schools, households, communities, faith‐based institutions), age, sex/gender, race/ethnicity, and other sociodemographic characteristics of participants

• Interventions: nature of the intervention delivered to the study and control groups, and how it was delivered; timing and duration, and length of follow‐up

• Outcome measures and results: differences between intervention and control groups in terms of the outcomes listed in Outcome measures

• Additional notes: funding sources, declarations of interest, whether the trial was prospectively registered, and clinical trial registry number

We will resolve disagreements through discussion, and if consensus cannot be reached, we will consult a third review author.

Risk of bias assessment in included studies

At least two review authors will independently assess the risk of bias for each included study. We will resolve disagreements through discussion, and if consensus cannot be reached, we will consult a third review author. As recommended in the Cochrane Handbook for Systematic Reviews of Interventions [54], we will assess the risk of bias using the Cochrane RoB 2 tool [55]. For cluster‐randomised trials, we will use the RoB 2 tool for cluster‐randomised trials [56]. To implement RoB 2, we will use the Excel Tool available online (https://www.riskofbias.info/welcome).

We will assess the risk of bias for the effect of assignment to the intervention (intention‐to‐treat) at the outcome level, for key outcomes: unintended pregnancy, use of birth control methods at last sex, and initiation of sexual intercourse, assessed at the longest follow‐up time point reported.

We will evaluate the following domains for risk of bias.

• Bias arising from the randomisation process

• Bias due to deviations from intended interventions

• Bias due to missing outcome data

• Bias in measurement of the outcome

• Bias in selection of the reported result

In addition, for cluster‐randomised trials, we will assess additional components, namely, recruitment bias, baseline imbalance, loss of clusters, and incorrect analysis (i.e. whether results were adjusted for clustering).

For each of the above domains, we will make a judgement about which of the following categories the risk of bias should be described as: low risk, some concerns, or high risk. We will determine the overall risk of bias as follows.

• Low risk of bias: all domains are rated at low risk of bias.

• Some concerns: there are some concerns in at least one domain, but no domains are rated at high risk of bias.

• High risk of bias: at least one domain is rated at high risk of bias, or multiple domains are rated as some concerns.

Measures of treatment effect

We will express dichotomous outcome data as risk ratios (RRs), with 95% confidence intervals (95% CI), as the RR provides an interpretable measure of the relative likelihood of an event between groups. For continuous outcomes, we will use mean differences (MDs) and 95% CI when the studies use the same evaluation instrument or method. When studies assess the same outcome using different scales, we will use standardised mean differences (SMDs) with 95% Cl. We will conduct meta‐analyses by grouping studies with similar interventions and outcomes.

We anticipate that most outcomes will be reported as dichotomous or continuous data. However, if rate or time‐to‐event data are identified, we will extract them in the form reported by the study authors. For rate data (e.g. events per person‐time), we will use rate ratios with 95% confidence intervals. For time‐to‐event data, we will extract hazard ratios (HRs) with corresponding measures of uncertainty and analyse these using the generic inverse‐variance method [57].

Unit of analysis issues

Multiple articles

If one study is reported in multiple articles, we will treat these articles as a single study.

Cluster‐randomised trials

If we identify cluster‐randomised trials (e.g. schools, communities, or faith‐based institutions), we will assess whether the analyses adjusted for clustering. We will combine data from individually randomised RCTs and cluster‐RCTs in the same analysis, provided that clustering has been or can be appropriately accounted for in the cluster‐RCTs.

Where available, we will extract effect estimates from analyses that account for the cluster design (e.g. multilevel models or generalised estimating equations) and include these in meta‐analyses using the generic inverse‐variance method. If clustering has not been accounted for, we will apply approximate adjustments by calculating effective sample sizes using the number of clusters, average cluster size, and an intracluster correlation coefficient (ICC), in accordance with Cochrane Handbook guidance. When ICCs are not reported, we will use external estimates from similar studies. Where adjustment is not possible due to insufficient data, we will report the results narratively and not pool them quantitatively [58].

Multiple study arms

In studies with more than two intervention groups, we will include only arms relevant to the review question and limit comparisons to those that are clinically meaningful. Where intervention arms are sufficiently similar (e.g. variations of education interventions with comparable content or delivery), we will combine them into a single intervention group for comparison with the control. Where intervention arms differ substantially in content, intensity, or delivery (e.g. educational intervention versus multi‐component interventions), we will consider them to be conceptually distinct and analyse them in separate comparisons. To avoid unit‐of‐analysis errors and double‐counting, we will not include participants more than once in any single analysis [58]. Where quantitative synthesis is not appropriate, we will report results narratively.

Multiple time points

For studies reporting outcomes at multiple follow‐up time points, we will use data from the latest follow‐up.

Dealing with missing data

For missing data, we will follow Section 10.12 of the Cochrane Handbook [59]. Where possible, we will contact the original investigators to request missing data. We will avoid making assumptions about how missing outcome data were handled by study authors and will assess the risk of bias due to missing outcome data. Where necessary for meta‐analysis (e.g. missing standard deviations (SDs), cluster adjustments, or other statistical parameters), we will calculate or impute these values following Cochrane Handbook methods [57]. Where certain information is not reported in the article (e.g. numbers of participants per group, attrition rates, or percentage affected for each outcome), we will report the available results as stated in the article narratively. Where appropriate, we will consider performing sensitivity analyses to assess how robust the results are to the assumptions made.

Reporting bias assessment

We will assess the risk of publication bias using funnel plots if at least 10 studies are included in a meta‐analysis. We will assess funnel plot symmetry through visual inspection and, where appropriate, we will conduct formal statistical tests (e.g. Egger's test) [60]. To assess outcome reporting bias, we will compare trial protocols with published reports.

Synthesis methods

We will perform meta‐analyses when studies are sufficiently similar in terms of participants, interventions, and outcomes, and when effect estimates with corresponding measures of precision are available. We will conduct analyses using Review Manager (RevMan) [61]. Given the anticipated clinical and methodological heterogeneity across educational interventions and study populations, we will primarily use the random‐effects model to estimate average intervention effects. The Restricted Maximum Likelihood (REML) estimator will be used to estimate between‐study variance. The Hartung‐Knapp‐Sidik‐Jonkman (HKSJ) method will be used to calculate confidence intervals for the pooled effect when there are at least three studies, and heterogeneity is present; otherwise, a Wald‐type method will be used. We will use the fixed‐effect model in sensitivity analysis to assess the robustness of findings.

We will assess statistical heterogeneity through visual inspection of forest plots, the Chi² test (with a significance level of P < 0.10), and the I² statistic. We will interpret I² values in accordance with the Cochrane Handbook, where 30% to 60% may represent moderate heterogeneity and 50% to 90% may represent substantial heterogeneity [59]. Where we judge the extent and type of clinical and methodological heterogeneity to be acceptable, we will pool data using RRs with 95% CIs for dichotomous outcomes and MDs or SMDs, as appropriate for continuous outcomes. We will use forest plots to present individual study results and pooled estimates.

If studies are insufficiently homogeneous to justify quantitative synthesis, we will present study results in forest plots without a pooled effect estimate or summarise findings narratively, following the Synthesis Without Meta‐analysis (SWiM) guidelines [62]. For studies that cannot be included in our meta‐analyses due to substantial heterogeneity or limited data, we will provide a structured descriptive synthesis, including tabulated results and graphical displays where appropriate.

Where possible, we will stratify analyses by study design (individually randomised versus cluster‐randomised trials). We will conduct sensitivity analysis as detailed under Sensitivity analysis.

Investigation of heterogeneity and subgroup analysis

We will assess statistical heterogeneity through visual inspection of forest plots and by using the I² statistic. Where we identify moderate to substantial heterogeneity (I² > 50%) and sufficient data are available, we will first conduct sensitivity analyses to explore the influence of individual studies on the overall estimates (see Sensitivity analysis). If heterogeneity is reduced following the exclusion of specific studies, we will interpret these studies as potential sources of heterogeneity.

If substantial heterogeneity persists and sufficient data are available, we will undertake the following subgroup analyses:

• age group (early adolescents 10 to 14 years of age versus older adolescents 15 to 18 years of age);

• baseline sexual experience (sexually inexperienced versus sexually experienced at baseline); and

• duration of follow‐up (short‐term ≤ 6 months versus medium‐ to long‐term > 6 months).

We will not conduct equity‐related subgroup analyses due to anticipated limitations in reporting across the included studies.

We will formally assess differences between subgroups using the Chi² test for interaction in RevMan and will interpret both subgroup and sensitivity analyses cautiously, in accordance with Cochrane Handbook guidance [59].

Equity‐related assessment

We will not conduct a primary health equity–focused analysis in this review. However, we acknowledge that unintended pregnancy and access to pregnancy prevention interventions are socially patterned and may vary across PROGRESS‐Plus characteristics [65]. Therefore, we will consider relevant participant and study characteristics when interpreting the applicability and generalisability of the findings and their implications for health equity.

Sensitivity analysis

We will undertake sensitivity analyses to assess the robustness of the review findings to key methodological decisions. Specifically, we will repeat meta‐analyses excluding studies at high risk of bias. Where substantial heterogeneity is identified (I² > 50%), we will conduct sensitivity analyses by excluding studies with outlying effect estimates and by removing studies one at a time, to assess their influence on the pooled estimates. We will also compare results using the fixed‐effect model (Mantel‐Haenszel method for dichotomous outcomes and inverse‐variance model for continuous outcomes).

Certainty of the evidence assessment

We will assess the certainty of the evidence using the GRADE (Grading of Recommendations, Assessment, Development, and Evaluation) approach [63], following guidance in Chapter 14 of the Cochrane Handbook [64]. Two review authors will independently assess the certainty of the evidence, with disagreements resolved through discussion, and, where necessary, consultation with a third review author. In the assessment, we will consider five domains: risk of bias (limitations in study design or implementation), inconsistency (unexplained variability in results), indirectness (applicability of the evidence to the review question), imprecision (statistical uncertainty or small sample sizes), and publication bias (selective reporting).

We will classify the certainty of the evidence as high, moderate, low, or very low. Evidence from randomised controlled trials is initially rated as high certainty and may be downgraded by one or two levels depending on the seriousness of concerns identified across the GRADE domains. We will document and justify all decisions to downgrade the certainty of the evidence and consider these judgments when interpreting the findings.

We will present the main findings in summary of findings (SoF) tables for the following key comparisons.

• Educational interventions versus no intervention or routine population‐wide interventions

• Contraception‐promoting interventions versus no intervention or routine population‐wide interventions

• Multiple interventions versus no intervention or routine population‐wide interventions

Each SoF table will include the key outcomes (unintended pregnancy, use of birth control methods at last sex, and initiation of sexual intercourse), relative and/or absolute effect estimates, the number of participants and studies contributing to each outcome, the certainty of the evidence based on GRADE criteria, and explanatory footnotes where appropriate. We will use GRADEproGDT software to develop the SoF tables and to make our certainty assessments transparent [63].

Consumer involvement

We will not involve consumers in this review due to limited time and resources.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016356.

Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.

Supplementary material 1 Search strategies

New

Additional information

Contributions of authors

Conceptualisation: JEE

Co‐ordination of the protocol: MMM

Writing – original draft: JEE, MMM, CO, and AM

Writing – review and editing: JEE, MMM, CO, EBE, HGA

Search strategies: Cochrane Fertility Regulation review group

Chioma Oringanje (CO); Martin M Meremikwu (MMM); Heidi G Arth (HGA); ⁠⁠Ekpereonne B Esu (EBE); Anne Meremikwu (AM); John E Ehiri (JEE)

Declarations of interest

• Chioma Oringanje: none known

• Martin M Meremikwu: no relevant interests; Paediatrician, University of Calabar Teaching Hospital, Calabar 54001,Cross River State, Nigeria

• Heidi G Arth: none known

• ⁠⁠Ekpereonne B Esu: none known

• Anne Meremikwu: none known

• John E Ehiri: none known

Sources of support

Internal sources

• Cochrane Evidence Synthesis Unit (CESU), Nigeria

  Funding support for the review

External sources

• WHO Regional Office for Africa (WHO AFRO), Nigeria

  Support for updating the review

• Australian Cochrane Centre, Australia

  Provided the funding for the first version of the review

Registration and protocol

Protocol first published: Issue 2, 2005

Review first published: Issue 4, 2009

Data, code and other materials

Data sharing is not applicable to this article as it is a protocol. No datasets have been generated or analyzed.