Types of studies

We included randomised controlled trials (RCTs) and cluster‐RCTs evaluating the effect of synthetic VAS in children aged six months to five years. We included data from the first period of cross‐over studies only. We considered studies for inclusion irrespective of publication status or language of publication.

We excluded quasi‐RCTs with the exception of Herrera 1992 and Stansfield 1993; we made this decision post hoc (Differences between protocol and review). Given the design of the interventions and the placebos as well as steps to blind those administering the sequence, we do not think these studies are meaningfully different from RCTs. Herrera 1992 assigned participants alternately by household, while Stansfield 1993 used a random starting point and alternating distribution of red or green pills. Lack of a truly random sequence was not related to other sources of bias (for example, performance bias) because individuals delivering the capsules had no ongoing contact with participants, and the manufacturer (Roche) held the code until the study was completed. Though post hoc, we made the decision to include these studies before extracting data or conducting analyses; we conducted a sensitivity analysis to determine if the decision had any impact on the results, which it did not (see 'Sensitivity analysis' subheading, under 'Primary outcome: all‐cause mortality' in Effects of interventions section).

Types of participants

Children living in the community and aged six months to five years at the time of recruitment were eligible for inclusion. We excluded children in hospital and children with disease or infection.

We contacted trial authors to determine if the study population included some participants who were not eligible for this review (for example, children over five years of age) and requested disaggregated data. If such data were not available, we included studies if the majority of participants (51% or more) met the inclusion criteria. If this could not be determined and the participants met the inclusion criteria on average (for example, the mean age was within the eligible range), then we included these trials.

Types of interventions

Synthetic oral VAS compared to either placebo or treatment‐as‐usual control groups, including trials of various doses and frequencies. Co‐interventions (for example, multiple vitamin or mineral supplementation), must have been identical in both groups. We excluded studies evaluating the effects of food fortification, consumption of foods rich in vitamin A, and beta‐carotene supplementation.

If a trial included more than one eligible intervention group (for example, different doses), we combined the groups for the main analysis, although we treated the groups separately for subgroup analyses where appropriate. If a trial included multiple control groups (for example, both placebo and treatment as usual), we selected the control group that most closely replicated the non‐specific treatment of the intervention group (that is, placebo).

Types of outcome measures

We extracted data on the outcomes listed below. In studies reporting more than one measure of an outcome, we combined measures for meta‐analysis using the methods described in Data synthesis.

Electronic searches

For this update, we searched the databases and trials registers listed below on 1 March 2016, using the search strategies in Appendix 1. Further details about the searches are in Appendix 2. See Appendix 3 for the previous search strategies.

1. Cochrane Central Register of Controlled Trials (CENTRAL; 2016, Issue 2) in the Cochrane Library, which includes the Cochrane Developmental, Psychosoical and Learning Problems Specialised Register (searched 1 March 2016).

2. MEDLINE Ovid (1946 to February Week 3 2016).

3. Medline In‐Process & Other Non‐Indexed Citations Ovid (29 February 2016).

4. Embase Ovid (1980 to 2016 Week 9).

5. Science Citation Index Web of Science (SCI; 1970 to 27 February 2016).

6. Conference Proceedings Citation Index ‐ Science Web of Science (CPCI‐S; 1990 to 27 February 2016).

7. Cochrane Database of Systematic Reviews (CDSR; 2016, Issue 2) in the Cochrane Library.

8. Database of Abstracts of Reviews of Effects (DARE; 2015 Issue 2) in the Cochrane Library.

9. LILACS (Latin American and Caribbean Health Science Information database; bases.bireme.br/cgi‐bin/wxislind.exe/iah/online; searched 1 March 2016).

10. African Index Medicus (indexmedicus.afro.who.int/cgi‐bin/wxis.exe/iah/?IsisScript=iah/iah.xis⟨=I&base=AIM; searched 1 March 2016).

11. ClinicalTrials.gov (clinicaltrials.gov; searched 1 March 2016).

12. World Health Organization International Clinical Trials Registry Platform (WHO ICTRP; apps.who.int/trialsearch; searched 1 March 2016).

We applied no language limits.

Searching other resources

We checked the reference lists of reviews and included and excluded studies in order to identify additional citations. We also contacted organisations and researchers.

Selection of studies

For this update, two people (Aamer Imdad and Zunirah Ahmed) independently screened titles and abstracts for inclusion in the review. We resolved differences of opinion about suitability for inclusion by discussion and through consultation with a third review author (Evan Mayo Wilson). We recorded our decisions in a PRISMA diagram (Moher 2009).

Data extraction and management

For this update, two people (Aamer Imdad and Jai Das or Renee Sharma) used a data extraction sheet to independently extract the data below from each eligible study. Review authors resolved discrepancies through discussion.

1. General:

   1. year of study;

   2. location (country, urban/rural);

   3. method of recruitment;

   4. inclusion criteria;

   5. unit of analysis; and

   6. risk of bias (see Assessment of risk of bias in included studies).

2. Participants:

   1. sociodemographic characteristics (age, sex); and

   2. comorbidities.

3. For each intervention and comparison group of interest:

   1. dosage;

   2. duration;

   3. frequency; and

   4. co‐intervention (if any).

4. For each outcome of interest:

   1. time points collected and reported;

   2. definition;

   3. validity;

   4. unit of measurement (if relevant); and

   5. loss to follow‐up.

The main analyses included the longest reported follow‐up in each study. We grouped outcomes according to follow‐up period (0 to 12 months; 13 to 60 months, and greater than 60 months since randomisation); when trials reported multiple time points for a period, we extracted the longest outcome interval in a given period.

Assessment of risk of bias in included studies

Two people (Aamer Imdad and Jai Das or Renee Sharma) independently assessed the risk of bias within each included study using Cochrane's 'Risk of bias' tool (Higgins 2011a). For all studies, we assessed the following: sequence generation; allocation concealment; blinding of participants and providers; blinding of outcome assessors; incomplete outcome data; selective outcome reporting; and other sources of bias. We specifically looked for the possibility of performance bias (differential treatment of the intervention and control groups) and detection bias (for example, differential effort to locate death records for the intervention and control groups). Findings are discussed in the Risk of bias in included studies section and included in the 'Risk of bias' tables (beneath the Characteristics of included studies tables).

Measures of treatment effect

We measured morbidity in different ways, and we combined all available data whenever possible. For example, for diarrhoea, we included all types of diarrhoea (mild, moderate, and severe). In the case of pneumonia, we included lower (but not upper) respiratory tract infection.

To avoid reviewer bias, we predetermined the order of preference for extracting outcomes when data were available in several formats. For studies that randomised individuals, we gave preference to data that required the least manipulation by authors or inference by reviewers. We extracted raw values (for example, means and standard deviations) rather than calculated effect sizes (for example, Cohen's d). For mortality data, we gave 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 have contributed data (for example, incidence of measles), we gave preference to child years, number with definite outcome known, and number randomised. 

In the case of cluster‐RCTs, we used either adjusted estimates reported by the trial authors or raw data, and we inflated the standard error (SE) using the procedures described below in the Unit of analysis issues section.

Unit of analysis issues

Dealing with missing data

Differential dropout can lead to biased estimates of effect size, and bias may arise if reasons for dropout differ across groups. 

We described missing data, including dropouts and reasons for dropout, when given. If data were missing for some cases, or if reasons for dropout were not reported, we contacted the trial authors. When analyses considered completers and controlled for dropout (for example, imputed using regression methods), we extracted the latter.

Assessment of heterogeneity

We assessed included studies for clinical heterogeneity by comparing the distribution of important factors such as study participants, study setting, dose, and duration of intervention and co‐interventions. We assessed methodological heterogeneity by comparing data included in the 'Risk of bias' tables (beneath the Characteristics of included studies tables). We assessed statistical heterogeneity by visual inspection of forest plots, the Chi² test (and P value), and the I² statistic. If the P value was less than 0.10 and the I² exceeded 50%, we considered heterogeneity to be substantial. We also reported Tau² – an estimate of between‐study variance.

Assessment of reporting biases

To assess the possibility of small study bias, we drew funnel plots for outcomes with 10 or more studies and compared random‐effects estimates to the fixed‐effect estimate (see Sensitivity analysis).

Data synthesis

We performed meta‐analysis using Review Manager 5 (RevMan) software (RevMan 2014). When data were in several formats that we could not combine directly in RevMan, we used the generic inverse variance (GIV) option. This was meant to handle the scenario when only summary estimates (like the risk ratio, or RR) were available and no numbers for nominators and denominators were available to calculate the summary estimate. In this case, it would not be possible to pool that study with other studies using conventional methods. Hence, we used GIV, which does not require input of data in the form of nominators and denominators of intervention and control group, but the log of effect size (e.g. RR) and standard error (SE). For this update, we entered data into the built‐in calculator in RevMan to calculate the log of RR and their SE.  

We reported all outcomes with 95% confidence intervals (CIs) and weighted overall effects by the inverse of variance using a fixed‐effect model. Although there might be some differences across trials (for example, dose, and population), the biological mechanism should be similar. We explored differences through analyses described elsewhere (Mayo‐Wilson 2011).

For dichotomous outcomes, we calculated the overall RR. For incidence data, we combined RRs (events per child) and rate ratios (events per child‐year) because these ratios use the same scale and can be interpreted in the same way for these studies (the duration of studies was relatively short, i.e. median duration was one year or less).

In some cases, we estimated time at risk, as when trial authors reported incidence rate, duration of study, and number of children in each group.

We decided post hoc that we would pool incidence and prevalence data for morbidity separately. The primary difference between incidence and prevalence data is time at risk. Incidence data covers the time (prospectively) while prevalence data is a snapshot of a condition at one point in time. Therefore, we thought that combining incidence and prevalence data was not appropriate and so decided not to pool together these two types of data.

For continuous outcomes we calculated Hedges g. 

Subgroup analysis and investigation of heterogeneity

Effectiveness of the intervention may differ across members of populations (for example, due to differences in baseline vitamin A status) and may be affected by other interventions (for example, immunisation or deficiency of other micronutrients). For example, neonatal VAS is thought to have different effects in Asia versus Africa (Klemm 2009). Unlike trial‐level factors (such as dose), associations between individual‐level moderators (such as VAS) and outcomes should be analysed using individual patient data from RCTs and observational studies. With two exceptions, we did not include subgroup analyses based on individual‐level moderators in this review, as such analyses are at high risk of ecological fallacy (for example, lack of variation between studies would not indicate there was no variation within them). We included subgroups of age and sex; trials commonly report separate effects for these groups. We performed subgroup analyses when disaggregated data were available for groups within studies or between studies.

The following subgroup analyses were prespecified, and differences were tested using the Chi² test in RevMan 2014.

1. Dose: standard (up to 100,000 IU for children aged 6 to 11 months, and 200,000 IU for children aged 12 months to five years) versus high (greater than standard).

2. Frequency: high (doses more than once in six months) versus low (one dose every six months or six‐plus‐month interval).

3. Location: continent.

4. Age: six to 12 months versus one to five years.

5. Sex: boys versus girls.

Sensitivity analysis

We performed the following sensitivity analyses.

1. To test for bias, we repeated the primary analysis without studies at high risk of bias for sequence generation.

2. To test for small study bias, we repeated the analysis using a random‐effects model (as the assumption for this model is that effect is not identical across studies, and included studies are considered a 'random' sample of all the possible studies on the topic) and drew funnel plots for all outcomes with 10 or more studies.

3. To test the robustness of results when using imputed ICCs, we conducted sensitivity analyses using larger and smaller design effects (post hoc sensitivity analysis described under the 'Unit of randomisation' subheading in the Included studies section below).