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Cochrane Database of Systematic Reviews Protocol - Intervention

Food fortification with multiple micronutrients: impact on health outcomes

Authors' declarations of interest

Version published: 24 November 2014 Version history

https://doi.org/10.1002/14651858.CD011400

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view the current version 18 December 2019
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Abstract

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

To assess the impact of food fortification with MMNs on health outcomes.

Background

Description of the condition

Vitamins and minerals are essential elements for growth, metabolism and maintaining a healthy body. These micronutrients play a part in normal functioning of almost every organ with deficiencies accounting for numerous diseases and conditions. The World Health Organization (WHO) has estimated that more than two billion people are deficient in various vitamins and minerals, particularly vitamin A, iodine, iron and zinc (WHO 2000). It is believed that various micronutrient deficiencies co‐exist and are most prevalent in developing countries (Ramakrishnan 2002). One cross‐sectional survey conducted in six villages of a rural area in India showed that 73% of pregnant women were deficient in zinc and iron, while 26% had folate deficiency (Pathak 2004). Another survey from Nepal showed that 40% of pregnant women in a rural population had vitamin B6 deficiency (Jiang 2005). One review on micronutrient intakes during pregnancy showed that pregnant women in developed countries were at risk of suboptimal micronutrient intakes including folate, iron and vitamin D (Blumfield 2013). Iron deficiency is particularly widespread and globally about 1.62 billion people are anaemic, the majority with iron‐deficiency anaemia, with the highest prevalence among preschool‐aged children and the next highest among pregnant women (Benoist 2008). According to WHO approximations, worldwide about 190 million preschool children and 19.1 million pregnant women may be vitamin A deficient (WHO 2009). It is also projected that globally, about two thousand million people are affected by iodine deficiency (Li 2012). Reduced body stores of vitamin B6 and vitamin B12 have also been reported in various parts of the world (McLean 2008).

Micronutrient deficiencies can lead to major adverse health consequences, such as impairments in growth, immune competence, mental and physical development, and poor reproductive outcomes (Gibson 2002; Viteri 2002). It has been suggested that micronutrient deficiencies are also related to increased incidence and severity of infectious diseases and mortality from measles, malaria, diarrhoea and pneumonia (Bhutta 2008; Black 2013). Intervention studies have shown that vitamin A deficiency in children is associated with increased risk of mortality due to diarrhoea (risk ratio (RR) 1.47, 95% confidence interval (CI) 1.25 to 1.75) (Black 2008). Zinc deficiency for children under five years of age may also be associated with increased risk for diarrhoea (RR 1.27, 95% CI 0.96 to 1.63), pneumonia (RR 1.18, 95% CI 0.90 to 1.54) and malaria (RR 1.11, 95% CI 0.94 to 1.30) (Black 2008). Iron‐deficiency anaemia during pregnancy is an important risk factor for maternal mortality (Allen 2008).

Micronutrient deficiencies can have numerous adverse outcomes on potentially all population and age groups, with children and women of reproductive age being more susceptible. Micronutrient deficiencies are present worldwide among children, affecting normal physical and mental development (Haimi 2014; Ramakrishnan 2002; Tulchinsky 2010). Frequently, multiple micronutrients (MMNs) are deficient at the same time (Best 2011; Dijkhuizen 2001; Jiang 2005). One of the hypothesised reasons could be the poor dietary habits and prevalence of parasitic and infectious diseases particularly in the developing countries. These parasitic and recurrent infections can lead to malabsorption even if the diet is adequate (Jalal 1998). It is also believed that people living in developing countries have inadequate financial capabilities to provide their families with a healthy diet; in contrast, eating habits in the developed world are not generally healthy: as the consumption of junk food and soft drinks is higher compared with healthy homemade food (Schimdt 2005).

Description of the intervention

Multiple interventions have been designed to improve micronutrient deficiency, including exclusive breastfeeding during the first six months of life, dietary plans to include foods with highly absorbable vitamins and minerals, fortification of staple and complementary foods with vitamins and micronutrients, control of parasitic infections and provision of nutritional supplementation (Black 2008; DeMaeyer 1989; WHO 2000). Food fortification is one of the strategies that has been applied at various levels and directed to different age groups (de Lourdes Samaniego‐Vaesken 2012; WHO, FAO 2006). It is a striking public health strategy that may be cost‐effective (Hurrell 1997; Lotfi 1996), and has the advantage of being instated in the usual dietary patterns without a major change in dietary or health‐seeking practices (Serdula 2010a; Serdula 2010b). A range of micronutrient combinations has been used to fortify foods. There have been studies with various single micronutrients, dual micronutrients such as zinc combined with iron and others that have fortified more than two and up to 20 micronutrients, including zinc, iron, selenium, vitamin A, vitamin B complexes, vitamin C and vitamin E.

How the intervention might work

Proteins and energy from macronutrients are the primary requirements for normal growth and development, particularly in children and pregnant women. Low energy and protein intakes have been identified as a major cause for poor growth in children (Fleischer 2008). It is also suggested that under‐nutrition as a result of protein energy deficiency and low calorie intake is associated with increased susceptibility to numerous infectious diseases (Brown 2003; Calder 2000). People with macronutrient deficiencies are most likely to be deficient in vitamin and minerals as well. Hence, fortification of food can be a practical way to supply the body with carbohydrates, fats, proteins and MMNs to optimise health outcomes.

One cluster‐randomised trial from Nepal showed maternal mortality up to 12 weeks' postpartum was reduced by weekly vitamin A (RR 0.60, 95% CI 0.37 to 0.97) and β‐carotene (RR 0.51, 95% CI 0.30 to 0.86) supplementation compared with placebo (West 1999). One Cochrane review showed that peri‐conceptional folic acid supplementation significantly reduced the incidence of neural tube defects (RR 0.28, 95% CI 0.15 to 0.52) (De‐Regil 2010). Although these studies showed results of supplementation trials, they nevertheless highlighted how important it is to replace deficient micronutrients in pregnant women. Theoretically, similar results should be obtained through fortification of food with micronutrients; however, there are no reviews to provide such evidence for pregnant women.

Several trials have reported significant outcomes with micronutrient fortification. One study by Sazawal 2007 showed that milk fortified with MMNs reduced the odds for days with severe illnesses by 15% (95% CI 5% to 24%), the incidence of diarrhoea by 18% (95% CI 7% to 27%) and the incidence of acute lower respiratory illness by 26% (95% CI 3% to 43%) in children. Faber 2005 concluded that the motor development (assessed by a standardised 25‐item motor development scale) in children improved after food fortification. One study by Osei 2010 showed that micronutrient fortification of school meals by trained school personnel in a village in India was effective in improving vitamin A, vitamin B12, folate and total body iron status.

However, there are concerns that food fortification may lead to unacceptably high micronutrient intakes, especially for nutrients with relatively low tolerable upper intake levels among people who consume higher amounts of fortified foods (Fletcher 2004). One review of data from national surveys in European countries showed that there was a small proportion of the population, particularly children, who may exceed the upper intake level for some micronutrients, but it did not contribute appreciably to risk of adverse effects (Hennessy 2013).

Why it is important to do this review

While fortification is a recognised and effective strategy, questions arise as to whether these should be given individually or in combination. There are existing reviews that focus on food fortification with MMNs. The review by Best 2011 focused on MMN food fortification in school‐aged children and suggested consistently improved micronutrient status and reduced anaemia prevalence. The review by Eichler 2012 focused on MMN‐fortified milk and cereal products in children below three years of age and showed it to be effective in reducing anaemia in developing countries and Das 2013 focused on MMN fortification and its impact on women and children only. There is no clear evidence or guideline as to which combination might work better and if certain micronutrients work better with certain food products and provide maximum bioavailability. Moreover, there is a lack of evidence in terms of which age groups can get the maximum benefit and under what conditions. Our review will be a comprehensive review of all the available evidence irrespective of the developing or developed world and we aim to assess the effect of MMN food fortification on the population as a whole. Furthermore, we will perform various subgroup analyses to extrapolate the effects of fortification in terms of the food vehicle used, various combinations of micronutrients, age groups and duration of intervention, among others. This review will also provide information on implementation factors and guide decisions regarding scaling‐up of programmes. There are presently reviews on home fortification or point‐of‐use fortification of food in children through micronutrient powders (De‐Regil 2011; Salam 2013), and ready to use therapeutic food (RUTF) (Schoonees 2013), but we will not focus on these areas in our review.

Objectives

To assess the impact of food fortification with MMNs on health outcomes.

Methods

Criteria for considering studies for this review

Types of studies

We will include:

  1. randomised controlled trials (RCTs);

  2. quasi‐randomised trials;

  3. cluster RCTs;

  4. controlled before‐after (CBA) studies;

  5. interrupted time series (ITS) studies.

We will apply no language or publication status restrictions. We will attempt to obtain translations where possible if the review team is unable to translate papers in languages other than English.

Types of participants

We will include studies that assess the effectiveness of food fortification in the general population (including men, women and children). We will also include targeted fortification to specific populations (e.g. older people, pregnant women, women of reproductive age and children at school through institutions such as schools or care facilities). We will include food fortification studies from all countries regardless of their level of income and development.

Types of interventions

Intervention: MMN fortification (three or more micronutrients) of any food vehicle compared with single micronutrient, MMN fortification or no fortification.

We would not include studies evaluating point‐of‐use or home fortification of foods.

Types of outcome measures

Primary outcomes

  • Anaemia and iron‐deficiency anaemia.

  • Deficiency of specific micronutrients (e.g. vitamin A, zinc and iron).

  • Anthropometric outcomes (e.g. incidence of stunting, wasting and underweight).

  • Morbidity (e.g. infectious diseases such as pneumonia, sepsis and diarrhoea).

  • All‐cause mortality.

  • Cause‐specific mortality (as defined by study authors) due to pneumonia, diarrhoea or malaria.

Secondary outcomes

  • Potential adverse outcomes.

  • Serum concentration of specific micronutrients (zinc, retinol, ferritin, folate).

  • Serum haemoglobin levels.

  • Serum levels of various vitamins (e.g. vitamin B complex, vitamin C, vitamin E and vitamin D).

  • Neurodevelopmental and cognitive outcomes.

Search methods for identification of studies

Electronic searches

We will search the following electronic databases for primary studies. We will place no date or language restrictions.

  • Cochrane Central Register of Controlled Trial (CENTRAL), including the Cochrane Effective Practice and Organisation of Care (EPOC) Group Specialised Register and Cochrane Public Health Specialised Register;

  • MEDLINE and MEDLINE(R) In‐Process;

  • PubMed for the most recent six months to identify records that are 'Epub ahead of print';

  • EMBASE;

  • CINAHL;

  • PsycINFO;

  • ERIC;

  • LILACS;

  • AGRIS;

  • Science Citation Index and Social Sciences Citation Index;

  • Food Science and Technology Abstracts;

  • AgriCOLA;

  • Global Index Medicus ‐ AFRO;

  • EMRO;

  • PAHO (Pan American Health library);

  • WHOLIS (WHO Library);

  • WPRO;

  • IMSEAR (Index Medicus for the South‐East Asian Region);

  • 3ie Database of Impact studies;

  • EPPI centre databases ‐ DoPHER and TROPHI;

  • OpenGrey;

  • Index to Conference Proceedings;

  • ClinicalTrials.gov (clinicaltrials.gov/), and WHO International Clinical Trials Registry Platform (ICTRP; www.who.int/ictrp/en/).

We will adapt the MEDLINE search strategy (Appendix 1) for use in the other databases using the appropriate controlled vocabulary as applicable. We will handsearch the journals and the proceedings of major relevant conferences relating to food and nutrition. We will also handsearch the journals that the included studies appear most frequently in. We will search the top five journals (according to the number of included studies provided) for the previous 12 months.

Searching other resources

We will examine the reference lists of included studies and relevant systematic reviews for additional papers to consider for inclusion. We will contact the authors of relevant papers to request further published or unpublished work.

Data collection and analysis

Selection of studies

Two review authors (RK and JKD) will independently assess all the potential studies identified by the search strategy for inclusion. We will resolve any disagreement through discussion or, if required, we will consult a third review author (ZAB).

Data extraction and management

We will design a form to extract data. Two review authors (RK and RAS) will extract the data from eligible studies using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third review author (ZAB). We will enter data into Review Manager 5 (RevMan 2011), and check for accuracy by double data entry having one review author entering data into a separate file and comparing the results. If studies report outcomes at multiple time points, we will extract data for each time point and will pool studies reporting similar outcomes at similar time points. When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.

We will use the PROGRESS (place, race, occupation, gender, religion, education, socioeconomic status, social status) checklist to record whether outcome data were reported by sociodemographic characteristics known to be important from an equity perspective. We will also record whether studies included specific strategies to address diversity or disadvantage.

Where available, we will extract data on costs and process/implementation and we will also extract source of funding of the primary studies. We will present these details in the 'Characteristics of included studies' table and will use them to explore and make inferences for the results. We will use the data pertaining to costs and process/implementation for deriving implications for implementation and future research.

Assessment of risk of bias in included studies

Two review authors (ZSL and RAS) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will use the Cochrane Effective Practice and Organisation of Care (EPOC; EPOC 2009) nine‐point criteria for non‐RCTs and CBA studies and seven‐point criteria for ITS studies to determine the quality of all eligible studies. When information in the studies is not sufficient, we will attempt to contact the study authors to request further details. We will report risk of bias for each study in the 'Characteristics of included studies' table. We will not exclude studies on the grounds of their quality, but will clearly report methodological quality when presenting the results of the studies.

Random sequence generation (checking for possible selection bias)

For each included study, we will describe the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups. We will assess the method as:
• low risk of bias (any truly random, e.g. random number table, computer random number generator);
• high risk of bias (any non‐random process, e.g. odd or even date of birth, hospital or clinic record number);
• unclear risk of bias.

Allocation concealment (checking for possible selection bias)

For each included study, we will describe the method used to conceal allocation to interventions prior to assignment and will assess whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as:
• low risk of bias (e.g. telephone or central randomisation, consecutively numbered sealed opaque envelopes);
• high risk of bias (e.g. open random allocation; unsealed or non‐opaque envelopes, alternation; date of birth);
• unclear risk of bias.

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

For each included study, we will describe the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes. We will assess the methods as:
• low, high or unclear risk of bias for participants;
• low, high or unclear risk of bias for personnel.

Blinding of outcome assessment (checking for possible detection bias)

For each included study, we will describe the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess methods used to blind outcome assessment as:
• low, high or unclear risk of bias.

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

For each included study and for each outcome or class of outcomes, we will describe the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the total randomised participants), reasons for attrition or exclusion where reported and whether missing data were balanced across groups or were related to outcomes. Where sufficient information is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses that we undertake. We will assess methods as:
• low risk of bias (e.g. no missing outcome data, missing outcome data balanced across groups);
• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; 'as treated' analysis done with substantial departure of intervention received from that assigned at randomisation);
• unclear risk of bias.

Selective reporting (checking for reporting bias)

For each included study, we will describe how we investigated the possibility of selective outcome reporting bias and what we found. We will assess the methods as:
• low risk of bias (where it is clear that all of the study's pre‐specified outcomes and all expected outcomes of interest to the review were reported);
• high risk of bias (where not all the study's pre‐specified outcomes were reported; one or more reported primary outcomes were not pre‐specified; outcomes of interest were reported incompletely and so could not be used; study did not to include results of a key outcome that would have been expected to have been reported);
• unclear risk of bias.

Other bias

For each included study, we will describe any important concerns we have about other possible sources of bias. We will assess whether each study was free of other problems that could put it at risk of bias:
• low risk of other bias;
• high risk of other bias;
• unclear whether there is risk of other bias.

Overall risk of bias

We will make explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will assess the likely magnitude and direction of the bias and whether we consider it is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses.

Measures of treatment effect

Dichotomous data

For dichotomous data, we will present results as summary RR with 95% CI.

Continuous data

For continuous data, we will use the mean difference (MD) and 95% CI if outcomes are measured in the same way between trials. We will use the standardised mean difference (SMD) and 95% CI to combine trials that measure the same outcome, but use different methods.

Unit of analysis issues

Cluster‐randomised trials

We will include cluster‐randomised trials in the analyses along with individually randomised trials. We will adjust their standard errors using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), using an estimate of the intracluster correlation coefficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster‐randomised trials and individually randomised trials, we plan to synthesise the relevant information. We will consider it reasonable to combine the results from both if there is little heterogeneity between the study designs and we consider the interaction between the effect of intervention and the choice of randomisation unit to be unlikely. We will also acknowledge heterogeneity in the randomisation unit and perform a subgroup analysis to investigate the effects of the randomisation unit.

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 for Systematic Reviews of Interventions to avoid double‐counting of 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 of the participants.

Dealing with missing data

We will describe missing data, including drop‐outs. Differential drop‐out rates can lead to biased estimates of the effect size, and bias may arise if the reasons for dropping out differ across groups. We shall report the reasons for drop‐out. If data are missing for some cases, or if the reasons for dropping out are not reported, we will contact the study authors. For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis. For all outcomes, we will carry out analyses, as far as possible, on an intention‐to‐treat basis (i.e. we will attempt to include all participants randomised to each group in the analyses, and all participants will be analysed in the group to which they were allocated, regardless of whether they received the allocated intervention). The denominator for each outcome in each trial will be the number randomised minus any participants whose outcomes are known to be missing.

Assessment of heterogeneity

We will determine clinical heterogeneity, and we have identified a priori factors that may contribute to heterogeneity and will explore these as part of the subgroup analysis (see Subgroup analysis and investigation of heterogeneity below). We shall evaluate methodological heterogeneity on the basis of factors such as the method of sequence generation, allocation concealment, blinding of outcome assessment and losses to follow‐up. We will assess statistical heterogeneity in each meta‐analysis using the T2, I2 and Chi2 statistics. We will regard heterogeneity as substantial if the I2 statistic is greater than 30% and either the T2 statistic is greater than zero, or there is a low P value (< 0.10) in the Chi2 test for heterogeneity; under these circumstances.

Assessment of reporting biases

If there are 10 or more studies in the meta‐analysis, we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually, and use formal tests for funnel plot asymmetry. For continuous outcomes, we will use the test proposed by Egger 1997, and for dichotomous outcomes, we will use the test proposed by Harbord 2006. If any of these tests detect asymmetry or visual assessment suggests asymmetry, we will perform exploratory analyses to investigate it.

Data synthesis

We will carry out statistical analysis using the Review Manager software (RevMan 2011) using the random‐effects meta‐analysis model. We will combine data where it is reasonable to assume that studies are estimating the same underlying treatment effect (i.e. where trials are examining the same intervention), and the trials' populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, we will perform subgroup analysis. We will present the results as the mean treatment effect with 95% CI, and the estimates of the T2 and I2 statistics. We will set out the main findings of the review in 'Summary of findings' tables prepared using the GRADE approach (Guyatt 2008), using GRADE profiler software. We will list the primary 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, which involves consideration of within‐study risk of bias (methodological quality), directness of evidence, heterogeneity, precision of effect estimates and risk of publication bias. We will rate the quality of the body of evidence for each key outcomes as 'high', 'moderate', 'low' or 'very low'.

Subgroup analysis and investigation of heterogeneity

We will conduct subgroup and sensitivity analyses to consider whether an overall summary is meaningful. We plan to carry out the subgroup analyses on the basis of the following:

  • study design (RCTs/non‐RCTs, CBA/ITS);

  • population (children, women of reproductive age, adults);

  • baseline micronutrient status (malnourished, normal);

  • various combination of MMNs (e.g. different number and types of micronutrients used);

  • low‐to‐middle income countries versus high‐income countries;

  • duration of intervention (zero to six months, six to 12 months, more than 12 months);

  • food vehicle used for fortification;

  • studies with and without commercial funding.

We will assess differences between subgroups by interaction tests, and by inspection of the subgroups' CIs; non‐overlapping CIs indicate a statistically significant difference in treatment effect between the subgroups. Inferences for clinical relevance will be based on these subgroup analysis, where possible. This will ensure recommendations considering specific contextual factors in relation to food vehicle, target population and dose, among others.

Sensitivity analysis

We will perform sensitivity analyses to examine the effect of removing studies at high risk of bias (studies with high or unclear risk of bias according to method and adequacy of allocation concealment; blinding status of the participants; percentage lost to follow‐up or with an attrition of 20% or greater; and random‐effects model of the primary analysis). Moreover, we will perform sensitivity analyses based on different ICC values.