Fortification of condiments and seasonings with iron for preventing anaemia and improving health

  • Protocol
  • Intervention

Authors

  • Julie L Self,

    1. Emory University, Nutrition and Health Sciences, Atlanta, Georgia, USA
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  • Mary Serdula,

    1. Centers for Disease Control and Prevention, Division of Nutrition, Physical Activity and Obesity, Atlanta, Georgia, USA
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  • Therese Dowswell,

    Corresponding author
    1. The University of Liverpool, Cochrane Pregnancy and Childbirth Group, Department of Women's and Children's Health, Liverpool, UK
    • Therese Dowswell, Cochrane Pregnancy and Childbirth Group, Department of Women's and Children's Health, The University of Liverpool, First Floor, Liverpool Women's NHS Foundation Trust, Crown Street, Liverpool, L8 7SS, UK. t.dowswell@liverpool.ac.uk.

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  • Luz Maria De-Regil

    1. World Health Organization, Evidence and Programme Guidance, Department of Nutrition for Health and Development, Geneva, Switzerland
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Abstract

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

To determine the effects of condiment and seasoning fortification with iron alone or iron plus other micronutrients on iron deficiency and anaemia and health-related outcomes in populations at risk.

Background

Description of the condition

Vitamin and mineral deficiencies are prevalent throughout the world and contribute significantly to the global burden of disease (WHO 2009). It has been reported that iron, vitamin A and iodine deficiencies affect more than a third of the world's population, with iron deficiency and anaemia being the most prevalent (The Micronutrient Initiative 2009). Iron is present in a wide variety of plant and animal-based foods, but absorption of iron from plant-based diets - common in low income countries - is often inhibited by some dietary compounds such as phytates, tannins or phenols that are present in the same foods. Conversely, meat and meat by-products are the best sources of bioavailable iron but they may be inaccessible, culturally inappropriate, or unaffordable to many people.

Anaemia is a multifactorial condition that occurs mostly after prolonged iron deprivation (known as iron deficiency anaemia - IDA), although chronic inflammation, parasitic infections, inherited disorders of haemoglobin structure or other nutritional deficiencies such as that of folate, vitamin B12 and vitamin A, can all cause anaemia (WHO 2001). Anaemia affects approximately 1.6 billion people worldwide, particularly in Africa and Asia, and the most vulnerable populations are children and women of reproductive age, particularly during pregnancy. There is an inverse association between income and iron deficiency and anaemia status. In general, low-income countries have higher prevalence of anaemia (WHO 2008; Fall 2009). For example, in the WHO regions of Africa and South East Asia the prevalence of anaemia in school-age children is 67.6% and 65.5%, respectively, and 57.1% and 48.2% in pregnant women, respectively. In contrast, in Europe 21.7% of school-age children and 25.1% of pregnant women have anaemia (WHO 2008). This association between income and anaemia is also evident in high-income countries where people of low socioeconomic status are especially susceptible to iron and other vitamin and mineral deficiencies (Allen 2009; Cole 2010).

Iron deficiency and anaemia have several consequences throughout the life cycle that can affect physical and cognitive development in children, and work productivity and economic well-being in adults (WHO 2004). Before birth and during the first year of life, iron deficiency can result in permanent damage to an infant's central nervous system (Beard 2008); it affects growth, neurodevelopment and cognitive performance (Carter 2010; Lozoff 2006), and may increase susceptibility to infections (Oppenheimer 2001). In adults,  iron deficiency and anaemia cause loss of healthy and productive lives due to their effects on work and physical capacity (Haas 1996). Pregnant women with iron deficiency are at higher risk of suboptimal pregnancy outcomes, including complications at delivery, perinatal mortality, low birth weight and preterm birth (Scholl 1994; INACG 2002; WHO 2009). Postpartum iron deficiency is also associated with fatigue and general malaise which may impair infant development by negatively affecting  a healthy mother-child interaction (Murray-Kolb 2009; Armony-Sivan 2010).

Anaemia and iron deficiency can only be diagnosed by laboratory tests. Anaemia is assessed by measuring haemoglobin concentration, and is usually interpreted according to age, sex, pregnancy status, altitude and, if known, smoking status as these factors alter iron needs (WHO 2011a). Iron deficiency is assessed through several biochemical measurements including serum ferritin, serum iron, transferrin saturation, soluble transferrin receptor (sTfR), and erythrocyte protoporphyrin. Ferritin is the most used indicator to assess iron status and depletion, and there is a close relationship between the total amount of stored iron and the serum ferritin concentration in normal individuals, although this indicator is affected by inflammation (WHO 2011b). Assessing anaemia by measuring the haemoglobin concentration is a relatively inexpensive and feasible test, even in resource poor settings (WHO 2007).

Description of the intervention

Various strategies are employed to prevent and treat iron deficiency and anaemia in different populations. These include dietary diversification to improve iron intake and bioavailability; selective plant breeding or genetic engineering to increase the iron content or to reduce absorption inhibitors in dietary staple crops; oral iron supplementation with pharmacological doses; and fortification of industrially manufactured foods with iron (Hurrell 2010). Mantaining a varied diet that includes foods rich in bioavailable iron - such as animal sources - is often costly and difficult to obtain in resource-poor settings. Oral supplementation is probably the most used strategy, as it often improves micronutrient status quickly by providing the nutrient directly, in tablet or liquid form. While it may be effective, large programmes may not be sustainable to reach the needy population, and address only temporarily the underlying causes of nutrient deficiency (Allen 2006).

Fortification is the addition of micronutrients to foods during processing. Targeted fortification is often voluntary and means that the fortified food is commonly consumed by specific subpopulations, such as complementary foods for children (WHO/UNICEF 2003), or supplementary food for people living in emergency settings (WFP 2006). Market-driven fortification is a type of voluntary fortification in which food manufacturers decide to fortify their product for business reasons (e.g. breakfast cereals and infant formulas), while mass fortification involves fortifying staple foods that are consumed by the entire general population, such as corn and wheat flours, milk, salt, sugar and oils, and it often becomes mandated by a government (Allen 2006; Hurrell 2010). Among them, wheat and corn flours are some of the most frequently fortified staples, and more than 50 countries with mandatory fortification require the addition of iron and folic acid to flour, although other nutrients such as zinc or vitamin A might be also added (CDC 2008).

Iron fortification aims to improve the nutritional status of populations at risk of iron deficiency and anaemia without causing harm to other age groups such as men and postmenopausal women, who may consume more iron than they actually require. Due to its relatively low cost and potential for wide distribution, it has been identified as one of the most cost-effective of all health interventions (World Bank 1993). The use of fortified foods does not require knowledge, changes in dietary patterns nor individual decisions for adherence (Darnton-Hill 2002) as people are consuming the same basic foods and condiments. However, it is possible that fortified foods do not reach the poorest segments of the general population, who are at the greatest risk of vitamin and mineral deficiencies, because of low purchasing power, underdeveloped product distribution channels or because they produce their own food grown at home.

How the intervention might work

The selection of the food for a fortification programme requires consideration of both dietary habits of the target population and the cost of the intervention. In some situations, fortification of condiments or seasonings (e.g. soy and fish sauces, or curry powder) may be a useful alternative if they are consumed consistently by most of the population, as is the case in many Asian and African countries, developed or not. Fortification of condiments and seasonings, which are more specific to certain regions or ethnic groups, may also help target subpopulations that have different unmet dietary needs or risks, such as displaced people or those in emergency settings (Lamparelli 1987; Ballot 1989).

Fortification of condiments and seasonings is a relatively new strategy that may have several benefits, including feasibility, cost-effectiveness, sensory acceptability, targeting of subpopulations, and frequent and consistent use (Allen 2006). People in less advantaged groups tend to have little variety in their diet and a small number of foods account for most of the calories per day. In these cases, condiments and seasonings overcome monotony in diet and become staple, possibly reaching some people that cannot afford other fortified foods. In China, for example, soy sauce is almost ubiquitous; in 1999 it was estimated that 70% of the population consumed an average of 12.6 mg of soy sauce per day (Chunmigng 2003). In Singapore, the National Mental Health Survey of the Elderly reported that 46% of the population often eat curry (Ng 2006).

In addition to selecting a widely consumed food vehicle, it is necessary to overcome the inhibitory effect on iron absorption of components such as phytic acid, phenolic compounds or calcium, that may be part of the food vehicle or consumed as part of the overall diet. It is also important to select the most appropriate iron fortifying compound (Hurrell 2010). Iron compounds commonly used for fortification include salts such as ferrous sulphate, ferrous fumarate and protected (or chelated) compounds such as sodium iron EDTA (also known as NaFeEDTA or sodium iron ethylene diamine tetra acetate) or encapsulated ferrous sulphate (PAHO 2002). Careful selection of the type of iron compound for fortification is important due to differences in the bioavailability of iron or the way it may react with the fortified food, modifying its final sensory characteristics and consequently consumers' acceptance (Hurrell 1997; Benjamin-Bovell 1999).

The majority of condiment and seasoning fortification research has been conducted by adding NaFeEDTA to soy and fish sauces in Southeast Asian countries. This iron compound has been selected because of its high absorption rate (that compensates for the small quantities of food ingested), as well as the fact that it does not precipitate and has minimal impact on the appearance and taste of the sauces. Other sources of iron, such as ferrous fumarate, have been suggested as suitable fortificants because they are equally stable and less expensive to produce (Allen 2006Watanapaisantrakul 2006). Preliminary studies with iron-fortified soy and fish sauces show promising results in preventing anaemia in populations at risk, and this strategy may be feasible to implement on a large scale (Huo 2002; Thuy 2003; Chen 2005; Longfils 2008).

Despite the biological plausibility of this intervention to prevent and control anaemia in some settings, its success as a public health intervention will likely be determined by several factors related to policies and legislation regulations; production and supply of the fortified condiments; the development of delivery systems; the development and implementation of external and internal food quality control systems; and the development and implementation of strategies for information, education and communication for behaviour change among consumers. A generic logic model for micronutrient interventions that depicts the programme theory and plausible relationships between inputs and expected changes in outcomes is presented in Figure 1 (WHO/CDC 2011).

Figure 1.

WHO/CDC logic model for micronutrient interventions in public health (with permission from WHO)

Why it is important to do this review

Iron deficiency and anaemia are important public health concerns worldwide. In regions where condiments are frequently consumed, countries are now considering their use as potential vehicles for improving micronutrient intake. As with all fortification programs, everyone in the population is exposed to increased levels of micronutrients in food, irrespective of whether or not they will benefit from fortification, and the risk of excessive intake and possible adverse effects may be a concern and should be monitored. Additionally, provision of iron in malaria-endemic areas has been a long-standing controversy due to concerns that iron provision may exacerbate infections, in particular malaria given that the parasite requires iron for growth (Oppenheimer 2001). Although the daily doses given through fortification are minimal and theoretically do not represent a risk for the population, this issue merits attention.

To date there has been no systematic assessment of the safety and effectiveness of this intervention to inform policy making. The proposed systematic review will complement the findings of other ongoing Cochrane systematic reviews exploring the effects of using iron to fortify wheat flour (Albanese 2011), maize flour (Pasricha 2011) and rice (Ashong 2011) in public health programmes.

Objectives

To determine the effects of condiment and seasoning fortification with iron alone or iron plus other micronutrients on iron deficiency and anaemia and health-related outcomes in populations at risk.

Methods

Criteria for considering studies for this review

Types of studies

Fortification of condiments and seasonings 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 food fortification 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, with randomisation at either individual or cluster level;

  • quasi randomised trials (where allocation of treatment has been made, for example, by alternate allocation, date of birth, alphabetical order, etc);

  • non-randomised controlled trials;

  • observational studies that are prospective and have a control group;

    • cohort studies (prospective and retrospective),

    • controlled before and after studies,

    • interrupted time series with at least three measure points both before and after intervention (ITS).

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 and we will have separate meta-analysis estimates based on the different study designs.

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 results from these studies in a table but 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 co-morbidities.

Types of interventions

We will include interventions in the review in which condiments or seasonings have been fortified with any combination of iron and other vitamins and minerals, irrespective of the fortification technology used. We will include fortification of herbs, spices, seasonings and condiments (e.g. seasoning for instant noodles and bouillon cubes), sauces (soy sauce, fish sauce, Thai sauce), salt and its substitutes and any other substance intended to enhance the aroma and taste of food, including blends in powder or paste form (e.g. chilli seasoning, chilli paste, curry paste, curry roux and dry cures or rubs), onion salt, garlic salt, oriental seasoning mix (dashi), topping to sprinkle on rice (furikake, containing, e.g., dried seaweed flakes, sesame seeds and seasoning) (Codex 2011).

We will include studies with co-interventions i.e. fortified condiment or seasoning with education only if the comparison group also receive the education component in addition to the unfortified condiment or seasoning.

Comparisons to be made include:

  • condiments or seasonings fortified with iron versus unfortified condiments or seasonings;

  • condiments or seasonings fortified with iron versus no intervention;

  • condiments or seasonings fortified with iron plus other micronutrients versus unfortified condiments or seasonings;

  • condiments or seasonings fortified with iron plus other micronutrients versus no intervention.

We will not include comparisons of condiment or seasoning fortification versus other forms of micronutrient interventions (i.e. supplementation or dietary diversification).

We will not include fortification of sugar (which is classified as sweetener), or ketchup, mayonnaise, mustard or relishes, as these foodstuffs do not fulfil the definition of condiments and seasonings provided above. We will exclude studies examining other types of interventions such as biofortification, home fortification with multiple micronutrient powders or supplementation.

Types of outcome measures

Primary outcomes

Primary outcomes will be assessed in all age groups.

  1. Anaemia (as defined by trialists, depending on the age and gender and adjusted for altitude and smoking as appropriate);

  2. Haemoglobin concentration (g/L)

  3. Iron deficiency (as defined by trialists, based on a biomarker of iron status; for example ferritin less than 12 µg/L for preschool children and less than 15 µg/L for older populations)

  4. Iron status (as reported: ferritin, transferrin saturation, soluble transferrin receptor, soluble transferrin receptor-ferritin index, total iron binding capacity, serum iron)

  5. Any adverse effects (including constipation, nausea and vomiting, heartburn and diarrhoea, as measured by trialists)

Secondary outcomes

Secondary outcomes of interest may differ by participant group and we have listed these accordingly.

Children (2 to 11.9 years of age)
  1. Iron deficiency anaemia (as defined by trialists)

  2. Cognitive development

  3. Motor skill development

  4. Growth: height-for-age Z scores

  5. Growth: weight-for-height Z scores

  6. Malaria severity (only for malaria settings)

  7. Malaria incidence (only for malaria settings)

  8. Motor skill development

Adolescents (12 to 18 years of age)
  1. Iron deficiency anaemia (as defined by trialists)

  2. Malaria severity (only for malaria settings)

  3. Malaria incidence (only for malaria settings)

Pregnant women
  1. Iron deficiency anaemia (as defined by trialists)

  2. Premature delivery (less than 37 weeks)

  3. Very premature delivery (less than 34 weeks)

  4. Low birth weight (less than 2500 g)

  5. Any birth defects (neural tube defect, cleft lip, cleft palate, congenital cardiovascular defects and others as reported by trialists)

  6. Malaria severity (only for malaria settings)

  7. Malaria incidence (only for malaria settings)

Adults (male and females)
  1. Iron deficiency anaemia (as defined by trialists)

  2. Work capacity (as defined by trialists)

  3. Risk of iron overload (ferritin more than 150 mg/L)

  4. Malaria severity (only for malaria settings)

  5. Malaria incidence (only for malaria settings)

All groups

If the reports also present figures with combined data for all populations, we will also include them.

Search methods for identification of studies

Electronic searches

We will search the following international and regional sources.

International databases
  1. CENTRAL (The Cochrane Library);

  2. PubMed;

  3. EMBASE;

  4. CINAHL;

  5. Web of Science (both the social science citation index and the science citation index);

  6. POPLINE;

  7. AGRICOLA (http://agricola.nal.usda.gov/);

  8. BIOSIS;

  9. Food Science and Technology Abstracts (FSTA).

Regional databases
  1. IBECS (http://plip.eifl.net/negotiations/free-e-resources/spanish/ibecs-indice-bibliogra);

  2. Scielo (http://www.scielo.br/);

  3. Global Index Medicus - AFRO (includes African Index Medicus); EMRO (includes Index Medicus for the Eastern Mediterranean Region);

  4. LILACS;

  5. PAHO (Pan American Health library);

  6. WHOLIS (WHO Library);

  7. WPRO (includes Western Pacific Region Index Medicus);

  8. IMSEAR; Index Medicus for the South-East Asian Region;

  9. IndMED, Indian medical journals (http://indmed.nic.in/);

  10. Native Health Research Database (http://hsc.unm.edu/library/nhd);

For theses 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 also contact the Trials Search Co-ordinator of the Cochrane Public Health Group to search the Cochrane Public Health Group specialised register. The search will use keyword and controlled vocabulary (when available), using the search terms set out in Appendices and adapt them 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 restrictions. As condiment fortification is a relatively recent development we will limit the search from 1980 to present for all databases.

If we identify articles written in a language other than English, 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 assessment' 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) as well as the nutrition section of the Centers for Disease Control and Prevention (CDC), the United Nations Children's Fund (UNICEF), the World Food Programme (WFP), the Micronutrient Initiative (MI), Global Alliance for Improved Nutrition (GAIN), Hellen Keller International and Flour Fortification Initiative (FFI).

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; TD will screen titles and abstracts and the rest of the authors one-third 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; two review authors will independently assess each full text report. 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.

If studies are published only as abstracts, or if study reports contain little information on methods, participants or interventions, we will attempt to contact the authors to obtain further information. Failing this, we will place studies in the 'Awaiting assessment' until further information is published or made available to us. We will resolve disagreements at any stage of the eligibility assessment process through discussion and consultation with a third author where necessary.

Data extraction and management

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.

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, whether there were protocol deviations, and levels of compliance/use of condiments in different sites within studies.

We will use the PROGRESS (place, race, occupation, gender, religion, education, SES, social status) checklist to record whether or not outcome data have been reported by socio-demographic characteristics known to be important from an equity perspective. We will also record whether or not studies included specific strategies to address diversity or disadvantage.

For eligible studies, two review authors will independently extract data using the agreed form. One author (TD) will enter data into Review Manager software (RevMan 2011) and a second author will carry out checks for accuracy. We will resolve any discrepancies through discussion.

When information regarding any aspect of study design or results is unclear, we will attempt to contact authors of the original reports asking them to provide further details.

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.

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);

  • unclear.   

(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);

  • unclear.   

(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;

  • 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;

  • 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;

  • 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;

  • low, high or unclear risk of bias for personnel.

We will assess the risk of detection bias associated with blinding as:

  • low, high or unclear risk of bias for outcome assessors.

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;

  • 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;

  • 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 pre-specified outcomes and all expected outcomes of interest to the review have been reported);

  • high risk of bias (where not all the study’s pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest were reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported); or

  • risk of bias unclear.

(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 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:

  1. Was the intervention independent of other changes?

    1. 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;

    2. 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;

    3. unclear risk of bias.

  2. Was the shape of the intervention effect pre-specified?

    1. 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;

    2. hIgh risk of bias if it clear that these conditions were not met;

    3. unclear risk of bias.

  3. Was the intervention unlikely to affect data collection?

    1. 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);

    2. high risk of bias if the intervention itself was likely to affect data collection;

    3. unclear risk of bias.

Overall risk of bias

For all included studies, we will summarise the overall risk of bias by primary outcome within each study. Studies at high risk of bias will be those with high or unclear risk of bias in the following domains: allocation concealment, similarity of baseline outcome measurements, 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.  

If there is insufficient information in study reports for us to be able to assess risk of bias, studies will await assessment until further information is published, or made available to us.

We will set out the main findings of the review in summary of findings (SoF) tables prepared using GRADE profiler software (GRADEpro 2008). 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 (Balshem 2010), 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 express the results as one of four levels of quality (high, moderate, low or very low).

Measures of treatment effect

Dichotomous data

For dichotomous data, we will present proportions and, for two-group comparisons, results as average risk ratio or odds ratio with 95% confidence intervals.

Continuous data

We will report results for continuous outcomes as the mean difference with 95% confidence intervals if outcomes are measured in the same way between trials. Where some studies have reported endpoint data and other 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 with 95% confidence intervals 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

Cluster-randomised trials

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.

Cross over trials

From cross over trials, we will consider the first period of measurement only and we will analyse the results together with the parallel group studies.

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 and Tau2 statistics, and the Chi2 statistic to quantify the level of heterogeneity among the trials in each analysis. If we identify moderate or substantial heterogeneity, we will explore it by pre-specified subgroup effects analysis.

Heterogeneity may be a particular concern in non-randomised studies, and where there is evidence of 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).

Data synthesis

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 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 one 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 socio-demographic characteristics known to be important from an equity perspective based on the PROGRESS framework, where this information is available.

Subgroup analysis and investigation of heterogeneity

Where data are available we will carry out the following subgroup analyses:

  • by prevalence of anaemia among trial participants: less than 20%; 20% to 39%, 40% or higher;

  • by sex: males, females, mixed/unknown;

  • by type of condiment (as reported by trialists);

  • by type or iron compound (as reported by trialists);

  • by malaria endemicity at the time that the trial was conducted malaria setting versus non/unknown malaria setting;

  • by length of the intervention: less than six months, six months to one year, more than one year;

  • by dose of iron per 100 g of product.

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’ confidence intervals; non-overlapping confidence intervals suggesting a statistically significant difference in treatment effect between the subgroups. We will also use Borenstein 2008's approach to formally investigate differences between two or more subgroups. We will conduct analyses in Review Manager (RevMan 2011).

Sensitivity analysis

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 intra-cluster correlation values.

Acknowledgements

We would like to thank Amy Allison, Woodruff Health Sciences Library, Emory University and Christy Cechman, US Centers for Disease Control and Prevention, for their help in devising the search strategy.

Appendices

Appendix 1. Search terms

Search Strategy devised for MEDLINE (the strategy will be adapted for various different databases)

  1. exp Food, Fortified/

  2. exp Condiments/

  3. Spices

  4. exp Sodium Chloride, Dietary

  5. Flavoring agents

  6. ((fortif* or enrich or enhance*) adj3 (food* or iron)).ab,ti.

  7. ((salt or sodium chloride) adj (diet* or table or common) .ab,ti

  8. exp Iron/ andfortif*.ab, ti.

  9. NaFeEDTA.ab,ti

  10. (achar or anise or basil or caper or pepper or cardamom or cinnamon chilli or chives or clove*).ab,ti

  11. (coriander or cumin or Curcuma longa or cuceb or curry).ab.ti

  12. (dill or fennel or fenugreek or garlic or ginger).ab,ti.

  13. (majoram or masala or mint or nutmeg or oregano).ab,ti.

  14. (paprika or parsley or rosemary or sage or savory or sesame or sorrel).ab,ti.

  15. (tarragon or thyme or tumeric or vanilla or wasabi or vinegar*).ab,ti.

  16. (MSG or monosodium glutamate).ab,ti.

  17. ((condiment* or seasoning* or flavo?r* or sauce* or spice* or herb*) adj3 (fortif* or enrich* or enhance*)).ab,ti.

  18. (flake* or powder* or blend* or granule*).ab,ti.

  19. (Stock cube* or gravy cube* or bouillon* or instant noodle).ab,ti.

  20. or/1-19

  21. exp Ferritins/bl, df [Blood Deficiency]

  22. exp Anemia, Iron Deficiency/

  23. (an?emi* or iron deficien* or nonan?emic or h?emoglobin-free erythrocyte* or haemoglobin or h?emoglobin or serum ferritin).ti,ab

  24. exp Hemoglobins/

  25. exp Iron/bl, df [Blood Deficiency]

  26. 21 or 22 or 23 or 24

  27. 20 and 26

  28. exp animals/ not humans.sh.

  29. 27 not 28

Contributions of authors

Julie Self drafted an initial protocol with technical input from the rest of the authors. Luz Maria De-Regil and Therese Dowswell developed the methods of the protocol. All four review authors contributed to drafting the final text of the protocol.

Disclaimer: Luz Maria De-Regil is a full-time staff member of the World Health Organization. Mary Serdula is full staff member of the US Centers for Disease Control and Prevention. The authors alone are responsible for the views expressed in this publication and they do not necessarily represent the official position, decisions, policy or views of these organizations.

Declarations of interest

None known.

Sources of support

Internal sources

  • US Centers for Disease Control and Prevention (CDC), Division of Nutrition, Physical Activity, and Obesity, USA.

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

External sources

  • Goverment of Luxembourg, Luxembourg.

    WHO acknowledges the Government of Luxembourg for their financial support to the Micronutrients Unit for
    conducting systematic reviews on micronutrient interventions

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

    Dr Therese Dowswell received partial financial support from the Department of Nutrition for Health and Development for this work.

Ancillary