Vitamin A supplementation for preventing morbidity and mortality in children six months to five years of age

  • Protocol
  • Intervention

Authors


Abstract

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

To evaluate the effect of vitamin A supplementation (VAS) in children six months to five years of age with respect to the prevention of mortality and morbidity.

Background

Description of the condition

Vitamin A deficiency (VAD) is a major nutritional public health problem in the developing world. According to the latest report of the World Health Organization (WHO), globally about 190 million preschool-aged children and 19.1 million pregnant women are vitamin A deficient (i.e. serum retinol < 0.70 µmol/l) (WHO 2009). This corresponds to 33.3% of preschool-aged children and 15.3% of pregnant women in populations at risk of VAD. According to current estimates, 122 countries are classified as having a moderate to severe public health problem based on biochemical VAD in preschool-aged children, and 88 countries based on biochemical VAD in pregnant women (WHO 2009).

VAD impairs numerous body functions and can lead to many adverse health consequences including xerophthalmia (dry eyes), infectious morbidity, mortality, sub-optimal physical growth and anaemia (Sommer 1996; Rice 2004).  Xerophthalmia is the primary preventable cause of blindness; of the world’s children with xerophthalmia, nearly half reside in South or South-East Asia, of whom more than 85% live in India (West 2002a). About 5.2 million preschool-aged children and 9.8 million pregnant women suffer from night blindness, which represents 0.9% and 7.8% of the population at risk of VAD, respectively. The estimates show that Africa and South-East Asia contain the highest proportions of preschool-aged children and pregnant females with biochemical VAD and night blindness (WHO 2009).

The etiology of VAD is interconnected with a deprived ecological, social and economic environment, in which a chronically deficient dietary intake of vitamin A coexists with severe infections, such as measles, diarrhoea and respiratory diseases (Sommer 2002; Rice 2004). Intake of vitamin A is further lowered through depressed appetite and poor absorption, and body stores of vitamin A are depleted through excessive metabolism and excretion (Alvarez 1995; Mitra 1998). This combination of poor diet and increased frequency of infections in Vitamin A deficient populations leads to a vicious cycle of VAD and infection in vulnerable groups, notably young children and pregnant or lactating mothers (Sommer 2002; West KP 2003). These are the most compelling consequences of VAD, and underlie its significance as a public health problem around the world (West 2002a; WHO 2009).

Description of the intervention

Vitamin A is a term used for a subclass of a family of lipid-soluble compounds referred to as retinoic acids (Bates 1995). The molecule of retinoic acid consists of four isoprenoid units joined in a head to tail fashion. Vitamin A is found in two main forms: provitamin A carotenoids (beta-carotene and others), and preformed vitamin A. Provitamin A carotenoids, mainly found in plants, have many forms, but beta-carotene is the only one that is metabolised by mammals into vitamin A. Preformed vitamin A (retinol, retinal, retinoic acid, and retinyl esters), on the other hand, is the most active form of vitamin A and is found mainly in animal sources of food. It is also the form supplied in most supplements (Bates 1995; Shenai 1993). In humans, vitamin A is considered an essential nutrient which means that it cannot be synthesised by the body and therefore must be provided through diet (Bates 1995). Vitamin A is required for normal functioning of the visual system, and maintenance of cell function for growth, epithelial integrity, red blood cell production, immunity and reproduction (Sommer 1996).

In poor societies, especially in lower income countries, VAD among children is a major nutritional concern. In these areas, deficiency of dietary vitamin A can begin early in life, with colostrum being discarded or breastfeeding being inadequate, thereby denying infants their first, critical source of vitamin A (Haskell 1999). Later, in early childhood and adulthood, VAD continues to develop as a result of a diet deficient in vitamin A. It is a particular concern where consumption of animal source or fortified foods is minimal and diet relies heavily on vegetables and fruits (Ramakrishnan 2002). Modest amounts of vegetables and fruits as the sole source of vitamin A may not deliver adequate amounts, based on an intestinal carotenoid-to-retinol conversion ratio of 12:1, even though they are nutritious in many other ways (US Institute of Medicine, Food and Nutrition Board). This conversion efficiency reflects that VAD may even coexist in cultures that heavily depend on vegetables and fruits as their sole or main dietary source of vitamin A (West 2002). Due to the factors described above and the documented effect of synthetic vitamin A supplementation (VAS) in reducing infectious morbidity and mortality, the WHO recommends supplementation with vitamin A for preschool-aged children and pregnant mothers. It is recommended at a dose of 50,000 IU for infants under six months of age, 100,000 IU for infants six to 12 months of age and 200,000 IU for children over 12 months of age, every four to six months. Mothers should also be supplemented with 200,000 IU of vitamin A within eight weeks of giving birth (WHO 1997).

How the intervention might work

Vitamin A has been termed as an anti-infectious vitamin because of its role in regulating human immune function (Green 1928). Early studies in animals and humans revealed an association between VAD and increased susceptibility to infections (Semba 1999). Vitamin A also plays a major role in phototransduction in the eye. Vitamin A is required to produce rhodopsin, a photopigment in the retina that is responsible for sensing low light conditions. VAD causes degradation, beginning with night blindness and leading to xerophthalmia (Sommer 1996).

In addition to the documented preventive and therapeutic effect of VAS against xerophthalmia (Sommer 1996), prophylactic VAS in apparently healthy children (over six months of age) residing in developing countries has been shown to reduce childhood mortality by between 23% and 30% (Beaton 1993; Fawzi 1993; Glasziou 1993). Most of this reduction is due to the effect on diarrhoea and measles mortality. National and regional programmes of VAS are in place in over 70 countries worldwide and these programmes are not only highly effective in reducing mortality and morbidity, but also appear to be among the most cost-effective public health interventions available (Fawzi 2006). Side effects of VAS are rare in children aged six months or older with standard supplementation; however, vitamin A toxicity can develop if large amounts of vitamin A are used over a prolonged period of time. The symptoms of toxicity include liver damage, headaches, vomiting, skin desquamation, bone abnormalities, joint pain and alopecia (Smith 1976). A very high single dose can also cause transient acute toxic symptoms that may include a bulging fontanelle in infants; headaches in older children and adults; and vomiting, diarrhoea, loss of appetite, and irritability in all age groups. Toxicity from ingestion of food sources of preformed vitamin A is rare (Hathcock 1997). In addition to looking for specific effects, this review will examine all-cause mortality and morbidity to ensure that effects are not overestimated (for example, by discounting the possibility that the intervention reduces some causes of mortality whilst increasing others).

Why it is important to do this review

It is important to do this review given the huge burden of mortality and morbidity (infections) associated with VAD and to explore the role preventive VAS can play in reducing all-cause, cause-specific mortality and morbidities in children six months to five years of age. The role of prophylactic and therapeutic VAS has been the subject of several systematic and narrative reviews before; however, most of these are now out of date and the most recent includes fortification and maternal supplementation, which work differently for social (for example, delivery) and biological reasons.

The therapeutic role of vitamin A has been evaluated for measles and non-measles pneumonia in two separate Cochrane reviews (Ni 2005; Yang 2009). The prophylactic role of vitamin A has also been or is being evaluated in different Cochrane reviews in different subpopulations of children and mothers (Bello 2009; Chen 2008; Darlow 2007; Gogia 2008; Haider 2008; Oliveira 2006; van den Broek 2002; Wiysonge 2005). However, no Cochrane review has addressed VAS in children six months to five years of age. Four meta-analyses have been published that evaluate the role of VAS in reducing infant and childhood mortality in children under five years of age (Beaton 1993; Fawzi 1993; Glasziou 1993; Gogia 2008a). All reported a statistically significant reduction in all-cause child mortality in a range of 23% to 30%. However, these reviews had different inclusion and exclusion criteria and inadequate methodological evaluation of the included studies. For example, Gogia included studies of maternal VAS with childhood supplementation in the meta-analysis (Gogia 2008a). This makes it difficult to infer the impact of direct supplementation on the child with vitamin A alone compared to vitamin A reaching the child through breast milk with maternal VAS, or through both direct and breast milk pathways. In a review by Beaton, unpublished data were included whose methodological quality was not thoroughly evaluated (Beaton 1993).This review will include an up-to-date assessment of the best available evidence, including relevant subgroup analyses (described below), as a basis for recommendations to the WHO. VAS can be a very cost-effective intervention that can be easily administered to children and if evidence of benefit is found, then consideration could be given for its supplementation on a large-scale to save lives and avert morbidities like infections and blindness, especially among children in developing countries where routine VAS is not part of the national programme.

Objectives

To evaluate the effect of vitamin A supplementation (VAS) in children six months to five years of age with respect to the prevention of mortality and morbidity.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs) and cluster RCTs evaluating the effect of synthetic VAS in children aged six months to five years of age. We will include data from cross-over studies up to the time that the control group receives treatment. We will consider studies for inclusion irrespective of publication status or language of publication. We will exclude other intervention studies, such as quasi-experimental studies, before-after designs and observational studies.  

Types of participants

We will include children aged six months to five years living in the community. We will exclude children in hospital and children with disease or infection. We will contact trial authors if the study population includes some participants who are not eligible for this review (for example, children over five years), and we will request disaggregated data. If such data are not available, we will include studies if the majority of participants meet the inclusion criteria. If this cannot be determined and the participants meet the inclusion criteria on average, then we will include these trials.

Types of interventions

We will compare synthetic oral VAS with control (placebo or no intervention), including trials of various doses and frequencies. Co-interventions (for example, multiple vitamin or adjunct mineral supplementation), must be identical in both groups. We will exclude studies evaluating the effects of food fortification, consumption of vitamin A rich foods or beta-carotene supplementation.

If a trial includes more than one eligible intervention group (for example, differing in dose), we will combine the groups for the main analysis, although the groups may be treated separately for subgroup analyses. If a trial includes multiple control groups (for example, no intervention and placebo), we will select the control group that most closely replicates the non-specific treatment of the intervention group (that is, placebo).

Types of outcome measures

We will extract all outcome measures. In studies reporting more than one measure of an outcome, we will combine measures for meta-analysis using the methods described below (data synthesis).

Primary outcomes

All-cause mortality in children six months to five years of age.

Secondary outcomes

Cause-specific mortality (as defined by authors) due to:

  • diarrhoea;

  • pneumonia;

  • measles;

  • meningitis.

Cause-specific morbidity (i.e. incidence due to):

  • diarrhoea;

  • pneumonia;

  • measles;

  • malaria;

  • meningitis;

  • xerophthalmia;

  • night blindness;

  • Bitot's spots.

Adverse effects within 72 hours of supplementation:

  • vomiting;

  • diarrhoea;

  • other.

Vitamin A deficiency status (serum retinol < 0.70 µmol/l).

We will assign morbidities as defined by authors. In the case of diarrhoea, we will combine all subsets of presentation (for example, dysentery) for analysis. In the case of acute respiratory tract infection, we will only consider lower respiratory tract infection and pneumonia. We will exclude upper respiratory tract morbidities. We will present a Summary of Findings table in the review that will include the following outcomes: all-cause and cause-specific mortality; incidence of diarrhoea; pneumonia; measles; xerophthalmia; night blindness and adverse events.

Search methods for identification of studies

Electronic searches

We will search the Cochrane Developmental, Psychosocial and Learning Problems Review Group's trials register (current date); Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library, current issue); MEDLINE (current date); EMBASE (current date); Global Health (current date); Latin American Database (LILACS) (current date); metaRegister of Controlled Trials (current date) and African Index Medicus (current date).

We will limit the searches to clinical trials conducted on human subjects. We will impose no language restrictions. We will use the search terms set out in Appendix 1 to search MEDLINE and we will modify these search terms for other databases as necessary.

Searching other resources

We will search reference lists of relevant articles for additional citations. We will search related conference proceedings for relevant abstracts. We will contact organisations and researchers in the field for information on unpublished and ongoing trials. For further identification of ongoing trials, we will use the World Health Organization International Clinical Trials Registry (ICTRP), which searches multiple registers.

Data collection and analysis

Selection of studies

Two review authors will independently assess studies for inclusion in the review. Review authors will select studies as being potentially relevant by screening the titles and abstracts, if available. We will retrieve and review full texts when relevance cannot be ascertained from titles or abstracts. Two review authors will independently assess eligibility of all potentially relevant studies by reviewing their full texts and filling out eligibility forms designed in accordance with the specified inclusion criteria. We will resolve differences of opinion about suitability for inclusion by discussion. If a decision is not reached, we will consult a third review author. We will present excluded studies that appear to meet the inclusion criteria, but on further investigation do not, in the 'Characteristics of excluded studies' table, along with the reasons for exclusion. In the case of conference abstracts, if additional data are not forthcoming, we will use the information provided in the abstract for review purposes.

Data extraction and management

We will use a data extraction sheet to extract the following information from each study:

  • year;

  • location (country, urban/rural);

  • method of recruitment;

  • inclusion criteria;

  • unit of analysis;

  • allocation ratio; and

  • risk of bias (see below).

Participants:

  • sample size;

  • socio-demographics (age, sex); and

  • co-morbidities.

Intervention and comparison:

  • number of eligible intervention groups.

For each intervention and comparison group of interest:

  • dosage;

  • duration;

  • frequency;

  • co-intervention (if any); and

  • details of the comparison.

Outcomes:

  • outcomes and time points (a) collected and (b) reported.

 For each outcome of interest:

  • outcome definition and validity unit of measurement (if relevant); and

  • loss to follow up.

Miscellaneous:

  • key conclusions of trial authors;

  • references to other relevant trials; and

  • correspondence required.

Two review authors will independently extract data from the studies; we will resolve discrepancies through discussion.

We will group outcomes by time: 0-12 months; 13-60 months; and greater than 60 months. When trials report multiple time points, we will extract the longest outcome interval in a given period.

Assessment of risk of bias in included studies

Two authors will independently assess methodological quality using the Cochrane Collaboration’s tool for assessing risk of bias (Higgins 2008). We will assess eligible studies using the following key criteria: method of sequence generation; allocation concealment; blinding of participants, providers and outcomes assessors; addressing incomplete outcomes; and selective outcome reporting. We will assess, as needed, risk of other types of bias, including detection bias (for example, differential effort to locate death records for the intervention and control groups). We will present findings in a risk of bias table where, for each question-based entry, the judgement of the authors (‘Yes’ for low risk of bias; ‘No’ for high risk of bias; or ‘Unclear’ for unclear or unknown risk of bias) will be followed by a text box providing details on the available information that lead to each judgement. Further detail about the risk of bias tool is included in the Cochrane Handbook of Systematic Reviews of Interventions (Higgins 2008).

We will be attentive to sources of bias originating from differences between individual (RCTs) and cluster randomised trials. For example, the relationship between allocation concealment and recruitment bias may be greater in cluster randomised trials.

Measures of treatment effect

When data are presented in more than one format, we will extract raw values (for example, mean and standard deviation) rather than calculated effect sizes (e.g., Cohen’s d).  For mortality data, we will give preference to denominators in the following order: number with definite outcome known (or imputed as described below), number randomised, and child-years. For other dichotomous outcomes to which both survivors and non-survivors may contribute data (for example, incidence of measles), we will give preference to child-years, number with definite outcome known, and number randomised. 

In the case of cluster RCTs, we will make adjustments by inflating the standard error (SE) or by using adjusted estimates provided by the author (see below).

Unit of analysis issues

In studies randomising units other than the individual (i.e. clusters), results should be presented with controls for clustering (for example, robust SEs or hierarchical linear models). Where results do not control for clustering, we will contact authors to request an estimate of the intra-cluster correlation coefficient (ICC). If the authors are unable to provide an ICC, we will estimate an ICC from other published values. We will analyse clustered data using procedures outlined in Higgins 2008. That is, we will inflate SEs of effect sizes by multiplying by the square root of design effect. If it is impossible to adjust for clustering, we will analyse the outcomes from cluster-randomised trials using individuals as the unit of analysis, and we will describe the risk of overestimating treatment effect in the text. We will analyse the effect of clustering through sensitivity analyses that explore the effect of larger and smaller ICCs.

Dealing with missing data

We will describe missing data, including dropouts. Differential dropout can lead to biased estimates of effect size, and bias may arise if reasons for dropout differ across groups. We will report reasons for dropout. If data are missing for some cases, or if reasons for dropout are not reported, we will contact the authors. When analyses are reported for completers as well as controlling for dropout (for example, imputed using regression methods), we will extract the latter. When attrition between groups differs within studies, we will use sensitivity analysis to determine whether those studies bias the results of the meta-analysis.

Assessment of heterogeneity

We will assess included studies for clinical, methodological, and statistical heterogeneity. We will assess clinical heterogeneity by comparing the distribution of important factors, such as study participants, study setting, dose and duration of intervention and co-interventions. We will evaluate methodological heterogeneity on the basis of factors such as method of sequence generation, allocation concealment, blinding of outcome assessment, and losses to follow up. We will assess statistical heterogeneity amongst the trials by visual inspection of forest plots, by performing the Chi2 test (assessing the P value) and by calculating the I2 statistic (calculated as I2 = 100% x (Q-df )/Q; where Q is Cochrane’s heterogeneity statistic and df is the degree of freedom). If the P value is less than 0.10 and I2 exceeds 50% and visual inspection of forest plots is indicative, we will consider heterogeneity to be substantial and seek reasons for it.

Assessment of reporting biases

If we find sufficient studies, we will draw funnel plots to help assess the possibility of bias.

Data synthesis

We plan to perform the meta-analyses by using both fixed-effect and random-effects models. We will perform all the meta-analyses using Review Manager Software Version 5 (RevMan 2008). If we include a cluster randomised trial in meta-analysis, we will adjust the SE of effect size of that study as described above.

We will use risk ratio (RR) using original data to combine dichotomous outcomes and Hedges g for continuous outcomes; we will report both with 95% confidence intervals (CI). We will calculate overall effects using inverse variance methods.

We will use fixed-effect models for the main analysis; although there may be some differences across trials (for example, dose and population), the biological mechanism should be similar across trials and we will explore differences through analyses described elsewhere.  

Subgroup analysis and investigation of heterogeneity

Effectiveness may differ across members of populations (e.g. due to differences in baseline vitamin A status or due to prior supplementation) and may be affected by other interventions (e.g. immunisation). Unlike trial-level factors (e.g. dose), these factors generally vary with individual participants. Associations between individual-level moderators and outcomes should be analysed using individual patient data from RCTs and observational studies. We will not include subgroup analyses based on individual-level moderators in this review, as such analyses are at high risk of the ecological fallacy.

We plan to carry out the following prespecified subgroup analyses for all-cause mortality and cause-specific mortality and morbidity.

  1. To examine the possibility that there will be a variable response according to the 'dosages' of VAS as follows: standard dosages (up to 100,000 IU for children six to 11 months of age, and 200,000 IU for children 12 months to five years of age) versus high (greater than standard).

  2. Subgroup analysis according to the 'frequency' of VAS as follows: high (doses within six months) versus low (six-plus month interval and single doses).

  3. Subgroup analysis according to age of participants: six to 12 months versus one to five years.

  4. To examine the possibility that VAS will have a variable response in male and female children.

  5. Baseline HIV status of study population: HIV-positive vs HIV-negative versus mixed/unknown.

  6. Geographical status of the trial area to examine the possibility of a differential response in different regions (as is shown for neonatal VAS in Asia versus Africa) (Klemm 2009).

We will also explore the contribution of these variables to heterogeneity by meta-regression.

Sensitivity analysis

We will perform sensitivity analyses according to the following factors:

  • method and adequacy of allocation concealment;

  • blinding status of the participants;

  • percentage lost to follow up by excluding studies with attrition of greater than or equal to 20%; and 

  • random-effects model of the primary analysis.

Acknowledgements

We acknowledge generous contributions of the Cochrane Developmental Psychosocial and Learning Problems Group, particularly Geraldine Macdonald, Jo Abbott and Chris Champion.

Appendices

Appendix 1. MEDLINE search strategy

1. exp infant/ or exp child/ or exp child, preschool/

2. (child$ or infant$ or toddler$ or preschool$ or pre school$ or pre-school$ or young or youth or school age$ or kid or preteen or elementary or girl or boy).ab,ti

3. 1 or 2

4. exp Vitamin A/

5. (retinol$ or retinal or aquasol a or vitamin a or VAD).ab,ti.

6. 4 or 5

7. randomized controlled trial.pt.

8. controlled clinical trial.pt.

9. randomized.ab.

10. placebo.ab.

11. drug therapy.fs.

12. randomly.ab.

13. trial.ab.

14. groups.ab.

15. randomised.tw

16. humans.sh.

17. 7 or 8 or 9 or 10 or 11 or 12 or 13 or 14

18. 16 and 17

19. 3 and 6 and 18

What's new

DateEventDescription
11 May 2010AmendedSources of support for editorial base updated

History

Protocol first published: Issue 5, 2010

Contributions of authors

Dr Aamer Imdad wrote the protocol of the review under the guidance of Dr Mohammad Yawar Yakoob and Dr Zulfiqar A Bhutta. Mr Kurt Herzer and Evan Mayo-Wilson assisted in protocol writing especially in statistical methods.

Declarations of interest

None known.

Sources of support

Internal sources

  • Aamer Imdad, Mohammad Yawar Yakoob and Zulfiqar A Bhutta are supported by Aga Khan University, Karachi, Pakistan.

  • Mr Kurt Herzer and Evan Mayo-Wilson are supported by the Centre for Evidence-Based Intervention, University of Oxford, UK.

External sources

  • Micronutrients Unit, Department of Nutrition for Health and Development, World Health Organization, Switzerland.

    Financial support provided to the supporting Cochrane Review Group to expedite the editorial process, so that this review can be completed in line with its challenging timetable.

Ancillary