Criteria for considering studies for this review
Types of studies
Fortification of staple foods is an intervention that aims at reaching the entire population of a country, or large sections of the population, and is frequently delivered through the market system. We anticipate, therefore, that we will not be able to assess the benefits and risks of this intervention if we only include randomised trials; thus in addition, we plan to examine data from other study designs.
In summary, we will include:
randomised controlled trials (RCTs), with randomisation at either individual or cluster level;
quasi-RCTs (where allocation of treatment has been made, for example, by alternate allocation, date of birth, alphabetical order, etc);
observational studies that are prospective and have a control group, including:
controlled before-and-after studies, and
interrupted time series (ITS) with a clearly defined point-in-time when the intervention occurred and at least three measure points both before and after intervention.
Although we plan to include both randomised and non-randomised studies, we will not pool results from randomised trials together with those from non-randomised studies in meta-analysis; we will present these in separate meta-analysis estimates based on the different study designs. We will consider quasi-RCTs together with the non-RCTs.
In addition to the above mentioned study designs, we will consider before-and-after studies without control groups for inclusion in this review. We will present the results for the primary outcomes from these studies in a table but we will not include them in any meta-analysis nor will they contribute to the conclusions of the review. Such studies may provide information on the implementation and feasibility of the intervention, along with other contextual factors related to the intervention under review.
Types of participants
General population of all age groups (including pregnant women), from any country. We will exclude studies of interventions targeted toward participants with a critical illness or severe comorbidities.
Types of interventions
We will include interventions in the review in which staple foods have been fortified with any combination of vitamin A and other vitamins and minerals, irrespective of the fortification technology used.
We will include the following staple foods in this review.
We will make the following comparisons.
Staple foods fortified with vitamin A versus same unfortified staple foods.
Staple foods fortified with vitamin A versus no intervention.
Staple foods fortified with vitamin A plus other micronutrients versus same unfortified staple foods.
Staple foods fortified with vitamin A plus other micronutrients versus no intervention.
We will include studies with co-interventions only if the comparison group also receives the co-intervention. For example, fortified food plus education versus unfortified foods plus education.
We will exclude studies examining rice fortification with vitamin A as this comparison is assessed by another Cochrane review (Ashong 2012). We will also exclude other types of interventions such as biofortification, point-of-use fortification with multiple micronutrient powders, or supplementation. We will not compare the effects of vitamin A fortification with other forms of micronutrient interventions either.
Types of outcome measures
We will include studies if they assess any of the following primary and secondary outcomes. (Timepoint for measurements of the outcomes will be at the end of the intervention or the closest time period to the end of the intervention).
Serum/plasma retinol (mmol/L)
Subclinical vitamin A deficiency (serum/plasma retinol 70mmol/L or less)
Clinical vitamin A deficiency (night blindness, xerophtalamia (as defined by the trialists))
Any adverse effects (e.g. hypervitaminosis, as defined by the trialists)
Liver vitamin A stores (determined with a relative dose-response test)
Food intake (g/day)
Congenital anomalies (for pregnant women)
Breast milk vitamin A content of lactating women (milk retinol in mmol/L)
Search methods for identification of studies
We will search the following international and regional sources. We will use the search strategy shown in Appendix 1 and adapt it to the included databases.
CENTRAL (The Cochrane Library)
Ovid MEDLINE In-Process and Other Non-Index Citations
Web of Science (both the social science citation index and the science citation index)
Food Science and Technology Abstracts (FSTA)
EPPI centre databases BibiolMap and TRoPHI (public health databases)
ASSIA (social science database)
Global Index Medicus - AFRO (includes African Index Medicus); EMRO (includes Index Medicus for the Eastern Mediterranean Region)
PAHO (Pan American Health library)
WHOLIS (WHO Library)
WPRO (includes Western Pacific Region Index Medicus)
IMSEAR; Index Medicus for the South-East Asian Region
IndMED, Indian medical journals (http://indmed.nic.in/)
Native Health Research Database (http://hsc.unm.edu/library/nhd)
For thesis we will search WorldCat, Networked Digital Library of Theses and Dissertations, DART-Europe E-theses Portal, Australasian Digital Theses Program, Theses Canada Portal and ProQuest-Desertations and Theses. We will search OpenGrey for additional grey literature (http://www.opengrey.eu/).
We will also contact the Trials Search Co-ordinator of the Cochrane Public Health Group to search the Cochrane Public Health Group's Specialised Register. The search will use keyword and controlled vocabulary (when available), using the search terms set out in the Appendices and adapted as appropriate for each database. We will not apply any language restrictions.
We will search the International Clinical Trials Registry Platform (ICTRP) for any ongoing or planned trials, and contact authors of such studies to obtain further information or eligible data if available.
We will not apply any language or date restrictions.
If we identify articles written in a language other than English, Spanish or French we will commission their translations into English. If this is not possible, we will seek advice from the Cochrane Public Health Group. We will store such articles in the 'Awaiting classification' section of the review until a translation is available.
Searching other resources
For assistance in identifying ongoing or unpublished studies, we will contact the Department of Nutrition for Health and Development and the regional offices from the World Health Organization (WHO), the International Micronutrient Malnutrition Prevention and Control Programme (IMMPACT) of the US Centers for Disease Control and Prevention (CDC), the nutrition sections of the United Nations International Children's Emergency Fund (UNICEF), the World Food Programme (WFP), the Micronutrient Initiative (MI), Global Alliance for Improved Nutrition (GAIN), Hellen Keller International, the US Agency for International Development (USAID, and the Flour Fortification Initiative (FFI)).
We will search the reference list of all included papers and search the ISI Web of Science (both the social science citation index and the science citation index) for papers that cited the studies included in the review.
Data collection and analysis
Selection of studies
Managing references identified by the search strategy
We will store all the references identified by the search in Reference Manager software to prepare for importing them into Review Manager software (RevMan 2011).
Two review authors will independently screen the titles and abstracts of articles retrieved by each search to assess eligibility, as determined by the inclusion and exclusion criteria listed above; Luz Maria De-Regil (LMD) will screen all titles and abstracts and the rest of the authors one-half each. For those studies that are selected as potentially eligible for inclusion, we will retrieve full copies, and all review authors will be involved in assessing whether studies meet the review's inclusion criteria; each full-text report will be assessed independently and in duplicate. We will keep records of all eligibility decisions and will store the eligibility assessment form (with brief details of study design, participants and interventions, along with the final eligibility decision) with each study report.
We will resolve disagreements at any stage of the eligibility assessment process through discussion.
Data extraction and management
We will use the Reference Manager software version 12 to manage the records retrieved from the search.
Two review authors will extract data independently using data extraction forms, based on those from the Cochrane Public Health Group (Cochrane PHG 2010) and the Cochrane Effective Practice and Organisation of Care (EPOC) Group (EPOC 2010). LMD will extract the information from all papers and JM and IS from half of the papers each. We will use a data extraction form which will include questions to capture data on identification details of the study, study characteristics, details of participants, types and length of intervention and the primary and secondary outcomes with results. One of the authors (LMD) will enter the data into the Review Manager software (RevMan 2011) and the data will be checked by the author who extracted the information in duplicate. We will resolve any discrepancies through discussion. For studies published only as abstracts, or study reports containing little information about methods, we will attempt to contact the authors to obtain further details on results and study design. If there is insufficient information for us to be able to extract appropriate data, we will mark studies as 'awaiting classification' until further information is published, or made available to us.
All review authors will be involved in piloting the form using a subset of articles to enhance consistency amongst reviewers, and based on this, we will modify the form if necessary. We will collect information on study design, study setting, participants (number and characteristics), and provide a full description of the interventions examined. We will extract details of outcomes measured (including a description of how and when outcomes were measured) and results.
We will design the form so that we are able to record results for our prespecified outcomes and for other (non-prespecified) outcomes (although such outcomes will not underpin any of our conclusions). We will extract additional items relating to study recruitment and the implementation of the intervention; these will include number of sites for an intervention, whether recruitment was similar in different places, resource use or costs of intervention, whether there were protocol deviations, levels of compliance/use of foods in different sites within studies and whether a process evaluation of the intervention was conducted.
We will use the PROGRESS (place, race, occupation, gender, religion, education, socioeconomic status, social capital) checklist to record whether or not outcome data have been reported by sociodemographic characteristics known to be important from an equity perspective (Evans 2003). We will also record whether or not studies included specific strategies to address diversity or disadvantage.
Assessment of risk of bias in included studies
We will use the EPOC 'Risk of bias' tool for studies with a separate control group to assess the risk of bias of all studies. This includes five domains of bias: selection, performance, attrition, detection, and reporting, as well as an 'other' bias category to capture other potential threats to validity.
Two review authors will independently assess risk of bias for each study and we will resolve any disagreement by discussion or by involving an additional review team member. If there is insufficient information to be able to address risk of bias, we will assess it as “unclear”. By insufficient we mean that more than half of the domains were judged as unclear and that the authors did not respond when we contacted them.
Assessing risk of bias in randomised trials
(1) Sequence generation (checking for possible selection bias)
We will assess studies as:
low risk of bias if there is a random component in the sequence generation process (any truly random process, e.g. random number table; computer random number generator);
high risk of bias if a non-random approach has been used (any non-random process, e.g. odd or even date of birth; hospital or clinic record number); or
(2) Allocation concealment (checking for possible selection bias)
We will assess studies as:
low risk of bias if participants and investigators enrolling participants could not foresee assignment because an appropriate method was used to conceal allocation (e.g. telephone or central randomisation; consecutively numbered sealed opaque envelopes). This rating will be given to studies where the unit of allocation was by institution and allocation was performed on all units at the start of the study;
high risk of bias if participants of investigators enrolling participants could possibly foresee assignments and potentially introduce selection bias (e.g. open random allocation; unsealed or non-opaque envelopes); or
(3) Similarity of baseline outcome measurements (checking for confounding, a potential consequence of selection bias)
We will assess studies as:
low risk of bias if outcomes were measured prior to the intervention, and no important differences were present across intervention groups;
high risk of bias if important differences in outcomes between groups were present prior to intervention and were not adjusted for in analysis; or
unclear risk of bias if there was no baseline measure of outcome (note: if 'high' or 'unclear' but there is sufficient information to do an adjusted analysis, the assessment should be 'low').
(4) Similarity of baseline characteristics (checking for confounding, a potential consequence of selection bias)
We will assess studies as:
low risk of bias if baseline characteristics are reported and similar across intervention groups;
high risk of bias if baseline characteristics are not reported or if there are differences across groups; or
unclear risk of bias if it is not clear (e.g. characteristics mentioned in text but no data presented).
5) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts and protocol deviations)
We will assess outcomes in each included study as:
low risk of bias due to incomplete outcome data (this could be either that there were no missing outcome data, or that the missing outcome data were unlikely to bias the results based on the following considerations: study authors provided transparent documentation of participant flow throughout the study; the proportion of missing data was similar in the intervention and control groups; the reasons for missing data were provided and balanced across intervention and control groups; the reasons for missing data were not likely to bias the results (e.g. moving house));
high risk of bias if missing outcome data were likely to bias the results. Studies will also receive this rating if an 'as-treated (per protocol)' analysis is performed with substantial differences between the intervention received and that assigned at randomisation, or if potentially inappropriate methods for imputation have been used; or
unclear risk of bias.
(6) Blinding (checking for possible performance and detection bias)
We will assess the risk of performance bias associated with blinding as:
low, high or unclear risk of bias for participants; and
low, high or unclear risk of bias for personnel.
We will assess the risk of detection bias associated with blinding as:
Whilst assessed separately, we will combine the results into a single evaluation of risk of bias associated with blinding as:
low risk of bias if there was blinding of participants and key study personnel and it was unlikely to have been broken, or the outcomes are objective. We will also give this rating to studies where either participants and key study personnel were not blinded, but outcome assessment was blinded and the non-blinding of others was unlikely to introduce bias;
high risk of bias if there was no blinding or incomplete blinding, or if there was blinding that was likely to have been broken, and the outcome or outcome assessment was likely to be influenced by a lack of blinding; or
unclear risk of bias.
(7) Contamination (checking for possible performance bias)
We will assess studies as:
low risk of bias if allocation was by community, institution or practice and it is unlikely that the control group received the intervention;
high risk of bias if it is likely that the control group received the intervention; or
unclear risk of bias if it is possible that contamination occurred but the risk of this happening is not clear.
(8) Selective 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 studies for this domain as:
low risk of bias (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported);
high risk of bias (where not all the study’s prespecified outcomes have been reported; one or more reported primary outcome(s) were not prespecified; outcomes of interest were reported incompletely and so cannot be used; or study fails to include results of a key outcome that would have been expected to have been reported); or
unclear risk of bias.
(9) Other sources of bias
We will describe other possible sources of bias for each included study and give a rating of low, high or unclear risk of bias for this item.
We will assess the risk of bias for interrupted time series (ITS) studies using the EPOC 'Risk of bias' tool for ITS study designs which includes items (5), (6), (8) and (9) from the EPOC 'Risk of bias' tool above, as well as the following additional items.
Was the intervention independent of other changes?
low risk of bias if there are compelling arguments that the intervention occurred independently of other changes over time, and the outcome was not influenced by other confounding variables/historic events during the study period;
high risk of bias if it is reported or if there are grounds to suspect that the intervention was not independent of other changes over the time period of the study; or
unclear risk of bias.
Was the shape of the intervention effect prespecified?
low risk of bias if the point of analysis is the point of intervention or a rational explanation for the shape of the intervention effect was provided;
high risk of bias if it clear that these conditions were not met; or
unclear risk of bias.
Was the intervention unlikely to affect data collection?
low risk of bias if it is reported that the intervention itself was unlikely to affect data collection (e.g. sources and methods of data collection were the same before and after the intervention);
high risk of bias if the intervention itself was likely to affect data collection; or
unclear risk of bias.
Overall risk of bias
We will summarise the risk of bias at two levels: within studies (across domains) and across studies (for each primary outcome).
Judgement on the overall risk of bias will take into account the likely magnitude and direction of the bias in each of the above mentioned domains and whether we consider they will likely impact on the findings. Studies at high risk of bias will be those with high or unclear risk of bias in all of the following domains: allocation concealment, similarity of baseline outcome measurements, and completeness of outcome data. Judgements will also take into account the likely magnitude and direction of bias and whether it is likely to impact on the findings of the study.
For the assessment across studies, the main findings of the review will be set out in 'Summary of findings' (SoF) tables prepared using GRADE profiler software (GRADEpro 2008). We will list the primary review outcomes for each comparison with estimates of relative effects along with the number of participants and studies contributing data for those outcomes. For each individual outcome, we will assess the quality of the evidence using the GRADE approach (Balshem 2010), which involves consideration of within-study risk of bias (limitations in design, inconsistency, indirectness, imprecision, publication bias, magnitude of the effect, dose-response effect and other plausible confounders. We will express the results as one of four levels of quality (high, moderate, low or very low).
Measures of treatment effect
For dichotomous data, we will present proportions and, for two-group comparisons, results as average risk ratio (RR) or odds ratio (OR) with 95% confidence intervals (CIs).
We will report results for continuous outcomes as the mean difference (MD) with 95% CIs if outcomes are measured in the same way between trials. Where some studies have reported endpoint data and others have reported change from baseline data (with errors) we will combine these in the meta-analysis if the outcomes have been reported using the same scale.
We will use standardised mean difference (SMD) with 95% CIs to combine trials that measure the same outcome (e.g. haemoglobin) but use different methods.
If we do not find enough studies, or the studies cannot be pooled, we will summarise the results in a narrative form.
Unit of analysis issues
We will combine results from both cluster and individually randomised studies if there is little heterogeneity between the studies. If the authors of cluster-randomised trials have conducted their analyses at a different level to that of allocation and they have not appropriately accounted for the cluster design in their analyses, we will calculate trials' effective sample size to account for the effect of clustering in data. We will utilise the intra-cluster correlation coefficient (ICC) derived from the trial (if available), or from another source (e.g. using the ICCs derived from other, similar trials) and then calculate the design effect with the formula provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). If this approach is used, we will report this and undertake sensitivity analysis to investigate the effect of variations in ICC.
Studies with more than two treatment groups
If we identify studies with more than two intervention groups (multi-arm studies) where possible, we will combine groups to create a single pair-wise comparison or use the methods set out in the Cochrane Handbook to avoid double-counting study participants (Higgins 2011). For the subgroup analyses, when the control group is shared by two or more study arms, we will divide the control group (events and total population) over the number of relevant subgroups to avoid double-counting the participants.
From cross-over trials, we will consider the first period of measurement only and will analyse the results together with the parallel group studies.
Interrupted time series
We will analyse interrupted time series (ITS) studies separately using the method described in Ramsay 2003.
Dealing with missing data
We will try to contact the authors if missing outcome data are unclear or have not been fully reported. We will capture the missing data in the data extraction form and report it in the 'Risk of bias' tables.
For all outcomes, we will carry out analysis, as far as possible, on an intention-to-treat basis, i.e. for randomised trials, we will attempt to include all participants randomised to each group in the analyses. The denominator for each outcome in each trial will be the number randomised, minus any participants whose outcomes are known to be missing. For non-randomised studies, where possible, we will analyse data according to initial group allocation, irrespective of whether or not participants received, or complied with the planned intervention.
When assessing adverse events, adhering to the principle of "Intention-to-treat" may be misleading, thus we will relate the results to the treatment received ('per protocol' or 'as observed'). This means that for side effects, we will base the analyses on the participants who actually received treatment and the number of adverse events that are reported in the studies.
Assessment of heterogeneity
We will examine the forest plots from meta-analysis to visually assess the level of heterogeneity (in terms of the size or direction of treatment effect) among studies. We will use the I² statistic, Tau2, and the Chi2 statistic to quantify the level of heterogeneity among the trials in each analysis. If we identify substantial heterogeneity, we will explore it by prespecified subgroup effects analysis.
Heterogeneity may be a particular concern in non-randomised studies, and where there is evidence of unexplained heterogeneity, we will summarise findings using a forest plot but will not present the pooled estimate.
We will exercise caution in the interpretation of those results with high levels of unexplained heterogeneity.
Assessment of reporting biases
Where we suspect reporting bias (see 'Selective reporting bias' above), we will attempt to contact study authors asking them to provide missing outcome data. Where this is not possible, and the missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis.
We do not anticipate that there will be sufficient studies contributing data for any particular outcome for us to examine possible publication bias; if more than 10 studies reporting the same outcome of interest are available, we will generate funnel plots in RevMan 2011 and visually examine them for asymmetry. Where we pool studies in meta-analysis, we will order studies in terms of weight, so that a visual examination of forest plots may allow us to assess whether the results from smaller and larger studies are similar, or if there are any apparent differences (i.e. we will check that the effect size is similar in smaller and larger studies).
We will carry out meta-analysis to provide an overall estimate of treatment effect when more that one study examines the same intervention, provided that studies use similar methods, and measure the same outcome in similar ways in similar populations. We will not combine results from randomised and non-randomised trials together in meta-analysis, nor will we present pooled estimates for non-randomised studies with different types of study designs. Evidence on different outcomes may be available from different types of studies (for example, it is likely that data on less common adverse events will be reported in larger non-randomised studies). Where there is evidence on a particular outcome from both randomised trials and non-randomised studies, we will use the evidence from trials which are at lower risk of bias to estimate treatment effect.
Where there is evidence from several randomised trials, or non-randomised studies at low risk of bias, we will carry out statistical analysis using the Review Manager 5 software (RevMan 2011). We will use a random-effects meta-analysis for combining data, as we anticipate that there may be natural heterogeneity between studies attributable to the different doses, durations, populations and implementation/delivery strategies. For continuous variables we will use the inverse variance method, while for dichotomous variables we will use the method proposed by Mantel-Haenzen.
For non-randomised studies, where results have been adjusted to take account of possible confounding factors, we will use the generic inverse variance method in RevMan 2011 to carry out any meta-analysis (if both adjusted and non-adjusted figures are provided we will carry out a sensitivity analysis using the unadjusted figures to examine any possible impact on the estimate of treatment effect).
We will also use narrative synthesis, guided by the data extraction form in terms of the ways in which studies may be grouped and summarised in this review to describe the outcomes, explore intervention processes, and describe the impact of interventions by sociodemographic characteristics, known to be important from an equity perspective based on the PROGRESS framework, where this information is available (Evans 2003).
Subgroup analysis and investigation of heterogeneity
Where data are available we will carry out the following subgroup analyses:
by age and physiological condition population: children (2 to 11.9 years), adolescents (12 to 19 years), adults (20 years and older), pregnant women, lactating women (6 months postpartum), and mixed populations;
by food intake: high versus low consumers of vitamin A-fortified edible oils, fats, sugar, and wheat or maize flours (defined as people consuming more or less than the median of their population);
by public health significance: countries where vitamin A deficiency is a public health problem versus countries without vitamin A deficiency as a public health problem (according to WHO 2009a);
by sex: males, females, and mixed/unknown; and
by length of the intervention: less than six months, six months to one year, and more than one year;
We will only use the primary outcomes in subgroup analysis. We will limit this analysis to those outcomes for which three or more trials contributed data.
We will examine differences between subgroups by visual inspection of the subgroups’ CIs; non-overlapping CIs suggesting a statistically significant difference in treatment effect between the subgroups. We will test for subgroup differences as described by Borenstein 2008 and implemented in RevMan 2011.
We will carry out sensitivity analysis to examine the effects of removing studies at high risk of bias (those with high or unclear risk of bias for allocation concealment, lack of similarity of baseline outcome measurements, or incomplete outcome data) from the meta-analysis. If cluster trials are included, we will carry out sensitivity analysis using a range of ICC values.