Experimental studies

1. Randomised controlled trials (RCTs) in which individuals are randomly allocated to a treatment arm and to a control arm. We will also accept cross‐over RCTs (Higgins 2019a).

2. Cluster‐randomised controlled trials (c‐RCTs) in which groups of people are allocated to different interventions by clusters such as school or area (Higgins 2019a). These may include stepped wedge RCTs. All c‐RCTs are required to have at least two intervention sites and two control sites.

Non‐randomised studies

We will also accept the following types of non‐randomised studies (NRS) because it is often impossible to randomise policy or program interventions. 

1. Quasi‐randomised studies. These controlled trials use inappropriate methods for allocating people to interventions (Reeves 2019).

2. Controlled before‐after studies (CBAs) in which measurements are taken from both an experimental and a control group before and after the intervention and in which the researcher has control over which people are allotted to which group.

3. Interrupted time series (ITS). ITS studies may use data routinely collected for monitoring and surveillance in 'natural experiments' (Petticrew 2005) or data collected for a specific intervention. ITS studies must include at least three observations before the intervention and three observations after the intervention.

4. Controlled cohort studies. A cohort study is an observational study design where groups are assembled according to whether or not exposure to the intervention has occurred (Armijo‐Olivia 2012; Thomas 2004).  Exposure to the intervention is not under the control of the investigators but under the control of others, such as decision‐makers. People may self‐select into the intervention. Controlled cohort studies can be either prospective or retrospective cohort studies. 

   1. Prospective cohort studies are those in which the intervention and control groups are assembled before the intervention and followed through time (Reeves 2019). 

   2. Retrospective cohort studies are those in which intervention and control groups are assembled based on past records.

To be included, all NRSs must be longitudinal and have at least two measurements of the outcome ‐ one near the start of the study and one just at the end of the intervention. We will not include NRSs that only have endpoint data.

Results for each type of study will be tabulated and analysed separately.

Low‐ and lower‐middle‐income countries

Higher‐income countries

Included

We will include interventions that include providing meals (breakfast or lunch), snacks (including milk), and/or take‐home rations in a school setting.

To be included in our review, the meal/snack given must meet at least 10% of the daily energy requirement and at least 10% of the daily protein requirement for that age group. 

If a multi‐armed study includes multiple independent comparisons, we will include all independent comparisons (Higgins 2019b). If a multi‐armed study includes several arms and one control group, we will choose the arm that is most relevant to our study question (Higgins 2019b). For example, if the study provides both in‐school feeding and take‐home rations, we will select the in‐school feeding arm. If the study has two intervention groups based on energy given, we will select the intervention group with the highest amount of energy given. 

Excluded

We will exclude the following interventions: micronutrient supplementation or fortification of existing meals alone, stand‐alone nutrition education in schools or at home, obesity prevention programs, breastfeeding programs, food stamps, modifications to school meals to change nutrient content, community kitchens, food banks, and feeding centres.

Because of the increasing emphasis on reducing obesity, programs built around school meals increasingly aim to enhance the nutritional content of children's diets by increasing availability of, and access to, low‐fat choices, fruits, and vegetables (Coleman 2005; Luepker 1996). However, the focus of this review is not on changing the content of school meals but on the effect of the provision of food to children. Thus, we will not include these types of interventions in this review.

Comparators

Comparators can be either no treatment or placebo (low‐calorie drinks/snacks). The placebos must contain less than 3% of the daily energy requirement and less than 5% of the daily protein requirement.

Main Comparisons

We will include the following five comparisons.

1. Meals only versus control.

2. Snacks only versus control.

3. Take‐home rations only versus control.

4. Meals and snacks versus control.

5. Meals and take‐home rations versus control.

Primary outcomes

1. Anthropometry (weight and height for age z‐scores and weight for height z‐scores).

2. Educational outcomes (reading, math, and science performance; school attendance; and enrolment).

3. Cognitive outcomes (verbal fluency, intelligence, reasoning, attendance, and memory assessed by a reliable and valid test).

4. Adverse outcomes (overweight/obesity and disruptive behaviour at school).

Secondary outcomes

1. Anthropometry (weight, height, and bone mineral density).

2. Physical health (nutritional status; vitamin A status; vitamin B12 status; zinc status; and haemoglobin and hematocrit as indices of anaemia, a condition in which the blood cannot carry enough oxygen, most often due to iron deficiency).

3. Behavioural outcomes (physical activity).

4. Adverse outcome (stigmatisation).

5. Consumption of healthier and unhealthier foods.

Timing of outcome measurement

We will consider both short‐term outcomes (less than three months) and longer‐term outcomes (three months or more) as some behavioural changes may be seen rapidly. Attention and behaviour are examples of short‐term outcomes. Longer‐term outcomes include growth, school achievement, and intelligence. 

Process variables

To address Objective 3, several process elements will be extracted. Our list was chosen to represent factors that could impact the effectiveness of these programs and includes the following. 

1. The intensity of the feeding (e.g. energy content of the meal/snack, percentage of average daily energy or protein requirement, and whether it is categorized as lower (interventions providing less than 15% of the average daily requirement for that age group) or higher (interventions providing 15% or more of the average daily requirement for that age group)).

2. Context (country and area).

3. Type of feeding (snack, meal, drink, and whether fortified or unfortified) and the time of day food was given.

4. Quality/acceptability of the food given.

5. The provider (who delivered the intervention).

6. Whether intake was monitored.

7. Child/youth adherence.

8. Substitution.

9. The cost of providing school meals.

Process evaluation

Contemporary research practice recommends process evaluation alongside empirical trials of complex interventions to identify how the intervention was implemented in practice, the mechanism by which it achieved its impact, and any local contextual issues that may have influenced outcomes (Calnan 2003; Campbell 2000). The process evaluation will be used to aid the interpretation of the findings. 

Process evaluation can also be undertaken as part of a systematic review by extracting, analysing, and synthesising any data from the included studies that may help explain the mechanism(s) of action, heterogeneity of outcomes, or both. Thus, when a complex social intervention appears to have had a significant effect in one trial but no effect (or a negative effect) in another, an analysis of the link between the context, intervention, and outcome aims to generate further hypotheses about the circumstances in which this intervention might be more or less successful.

Study quality may also impact findings; studies of lower quality will often show higher effect sizes than those of higher quality. For example, biased outcome assessment is possible in situations where those who assess the outcome variables are not blinded to the study group (i.e. intervention or control).

MO and MD will tabulate the effects for each study in Excel (Microsoft Excel 2019) and sort them by the possible process elements to better understand the influence of process factors. We will begin with the study type, quality, and high versus low energy food. Energy content is an important process element, which will be assessed by the team's nutritionists (SL and JK). If possible, we will also estimate the recommended dietary intake (RDI) for other nutrients.

Rules used in calculating the energy content

1. When the total energy content or percent of average daily energy requirement is provided in the text of the study, this value will be used. When the energy content is not provided, but the descriptions of food are sufficient (quantity and type of food), the energy content of the meal/snack will be estimated using Food Data Central (USDA 2021).

2. When meals/snacks with different energy contents are provided on different days (e.g. Powell 1983), a weighted average will be taken (e.g. if a meal with 400 kcal was provided three days a week and a meal with 60 kcal was provided two days a week, then the weighted average of 264 kcal would be used).

3. When the number of days on which different meals/snacks are given is not specified (Agarwal 1989) or when the energy content is different in year one than year two of the study (Neumann 2003), a straight average will be used for the energy content.

RCTs

To rate the risk of bias for RCTs, we will use the Cochrane RoB 2 tool (ROB2 2021; Sterne 2019a; Sterne 2019b) as outlined in Chapter Eight of the Cochrane Handbook for Systematic Reviews of Interventions (hereafter referred to as the Cochrane Handbook; Higgins 2019c). We will also use the Crib Sheet (Higgins 2019d) and the Excel implementation sheet to guide us in our decision‐making (RoB Excel Tool 2022).

1. Bias arising from the randomisation process (allocation sequence generation and allocation concealment, baseline differences).

2. Bias due to deviations from intended interventions (non‐protocol interventions, the effect of assignment, blinding, and appropriate analyses).

3. Bias due to missing outcome data.

4. Bias due to measurement of the outcome.

5. Bias due to selection of the outcome.

For each of these domains, we will judge the result as low risk of bias, some concerns, or high risk of bias. To reach this judgment, we will follow signalling questions, which will help us to decide on these levels. These signalling questions have five response options: yes, probably yes, no, probably no, and no information. 

Based on the judgments of the five domains, we will determine the overall risk of bias for each outcome within a study. This will be related to the highest risk in any domain; e.g. if all domains are low risk the overall ROB for that outcome will be low risk, but if any of the domains are judged to be of some concern the overall risk will be judged to be of some concern. If any of the domains are at high risk or if there are some concerns in multiple domains, the overall ROB for that outcome will be judged to be at high risk.

Cluster RCTs

For this, we will follow the criteria outlined in Chapter 23 of the Cochrane Handbook (Higgins 2019b). We will also as use the guidance document (Eldridge 2021), the Crib Sheet (Higgins 2019d), and the Excel Tool (RoB Excel Tool 2022).

The criteria are as follows. 

1. Bias due to timing of identification or recruitment of participants (recruitment before randomisation, preventing knowledge of assignment to clusters, baseline imbalance).

2. Bias due to deviations from intended interventions (awareness of trial and their assigned intervention, caregiver's awareness, deviations from intended intervention, and appropriate analyses).

3. Bias due to missing outcome data (data for all clusters, number of missing in each cluster, missingness related to outcome variable).

4. Bias due to measurement of the outcome (measurement of appropriate, measurement different between groups, participants blinded to trial, outcome assessor aware of assignment, assessment influenced by knowledge of assignment).

5. Bias due to selection of reported results.

The overall risk of bias for a study/outcome is judged as low, moderate, serious, or critical using the criteria in Chapter 23 of the Cochrane Handbook (Higgins 2019b).

Please note that this tool for cluster‐RCTs can also be used with stepped wedge trials, realising that it does not cover the need for adjusting data for time trends (Higgins 2019b). 

Crossover RCTs

To assess the ROB in a crossover trial, we will use the draft version of the ROB 2 tool for crossover trials (Higgins 2021). We will also use the Crib Sheet and Excel Tool. The criteria for crossover trials are as follows. 

1. Bias that arises from the randomisation process; here, the randomisation is to sequence A or B of the cross‐over trial.

2. Bias due to deviations from intended interventions (non‐protocol interventions, the effect of assignment, blinding, and appropriate analyses).

3. Domain S: Bias arising from period and carryover effects.

4. Bias due to missing outcome data.

5. Bias in the measurement of the outcome.

6. Bias in the selection of the reported result.

Criteria for controlled cohort studies and CBAs

We will assess the risk of bias for this group of studies using the ROBINS‐I tool for non‐randomised studies (Reeves 2019; Sterne 2016). The domains are as follows.

1. Bias due to confounding.

2. Bias in the selection of participants for the study.

3. Bias in the classification of interventions.

4. Bias due to deviations from intended interventions.

5. Bias due to missing data.

6. Bias in the measurement of outcomes.

7. Bias in the selection of the reported result. 

For each domain, there are five possible levels of bias: low, moderate, serious, critical, and no information. For each domain, signalling questions help the judgment of the level of bias. These signalling questions have five response options: yes, probably yes, no, probably no, and no information (Sterne 2016).

The judgment of the overall risk of bias will be the least favourable assessment across the domains. This judgment will be low risk of bias across all domains, some concerns in at least one domain but not at high risk of bias for any domain, or high risk of bias in at least one domain.

Criteria for ITSs

In assessing the methodological quality of ITS studies, we will use the Suggested risk of bias criteria for EPOC reviews (Cochrane EPOC 2022). The domains include the following.

1. Intervention is independent of other changes.

2. The shape of the intervention is prespecified.

3. Intervention unlikely to prevent data collection.

4. Knowledge of allocation.

5. Incomplete outcome data are adequately taken care of.

6. Selective outcome reporting.

7. Other risks of bias.  

We will rate each domain as having low risk, unclear risk, or high risk of bias as per the criteria outlined within.

RCTs 

CBAs and controlled cohort studies

ITSs

For these studies, we will use estimates from time series regression. We will examine the trends/slopes and changes in the outcome level before and after the intervention and the mean change in the outcome level.

Cluster studies (cRCTs, CBAs, and ITSs)

For c‐RCTs and non‐randomised studies (CBAs and ITSs), we anticipate that the study authors will have presented their results after appropriately controlling for clustering effects (robust SEs or hierarchical linear models). We will document clustering and analysis methods used within the studies to control for this. We will correct the design effect using the variance inflation factor (VIF) if needed.

Quantitative meta‐analyses

We will conduct meta‐analyses when we have a minimum of two studies that can be combined (e.g. same intervention, outcome, and study design, I² below 75). We will perform these meta‐analyses in RevMan Web (RevMan Web 2022). 

We will perform meta‐analyses separately for each type of study design (RCTs, cluster RCTs, cross‐over RCTs, NRCTs, CBAs, controlled cohort, and ITSs). We will also complete separate meta‐analyses for higher‐income and lower‐income countries. 

The generic inverse variance method will be used as the preferred method of meta‐analysis. Using this method, for continuous variables, we will enter unstandardised regression coefficients and SEs, which have been adjusted for relevant covariates. These statistics will be converted to the same units. For dichotomous outcomes, which may be adjusted for relevant covariates, we will enter the log of the RR and SEs, or the OR and SE. 

For each meta‐analysis, we will provide an estimate with 95% CI; we will also generate a forest plot. In many instances, we will need to derive SEs from CIs using the RevMan calculator (Drahota 2021). We will use a random‐effects model for all analyses (Higgins 2019a), as clinical and methodological heterogeneity between studies is anticipated in terms of the type and implementation of interventions, participant groups, or outcomes measured. We will discuss the extent of the evidence against homogeneity in each analysis.

For cross‐over RCTs, we will use a paired t‐test with generic inverse variance (Higgins 2019b).

As noted above, we will determine whether the interventions, participants, or outcomes are similar or too different to combine. We will not combine different types of study designs. If the I² for any meta‐analysis is > 75%, we will not combine all studies in the meta‐analysis.

Syntheses without meta‐analysis

If the effect sizes are given but do not have the variability estimate, we will summarise the data using medians and interquartile ranges.

We will also prepare an effect direction plot for studies that we could not use to conduct a quantitative meta‐analysis (Thompson 2013). We will narratively synthesise reports for studies based on effect direction as well, as suggested on page 327 in the Cochrane Handbook (Higgins 2019a). We will use the SWiM guidelines to ensure that we report our qualitative syntheses appropriately (Campbell 2020). These guidelines concern grouping studies together, the metric and transformation method used, the synthesis method used, priority setting, reporting of heterogeneity and certainty of the evidence, data presentation, and reporting results and limitations.

Drawing conclusions

When drawing our conclusions, we will consider the risk of bias, the certainty of the evidence, effect size, CI, statistical significance, and real‐world meaningfulness.

Avoiding dependency

To avoid dependency, we will be careful not to double‐count the same participants in the analyses. For multi‐arm studies, we will follow methods outlined in Chapter 23 in the Cochrane Handbook (Higgins 2019b).

Synthesizing data from process evaluations

We will follow a realist approach to synthesise the data collected from process evaluations. As recommended by the RAMESES methodological standards (Wong 2013), analysis and synthesis of findings will be an interpretive process, reached through reflection and discussion and requiring repeated reading and re‐reading of primary studies in light of the emerging synthesis. We will give particular attention to identifying and exploring the mechanisms by which study participants drew upon resources available to achieve the intended outcome.

This approach will result in a series of context‐mechanism‐outcome (CMO) configurations that represent hypotheses concerning which outcomes are generated through which mechanisms in which context (Rycroft‐Malone 2012). We will iteratively test theories and refined based on integrating evidence of effectiveness (i.e. what works) with evidence derived from process evaluations and implementation research (i.e. how and why it works). The effectiveness evidence will contribute to the outcome and mechanism components of a CMO, whereas the process/implementation evidence will contribute to the mechanism and context components of a CMO (Harden 2018). We will synthesise this data using the following steps.

1. Organization of extracted data into evidence tables. This may include the theory of change proposed by study authors, why they felt the intervention was needed and what they thought it would achieve, and authors’ conclusions about why the intervention had worked or not worked; differences in subgroups, and any explanations for these differences; and additional mechanisms proposed by authors.

2. Theming of context, mechanisms, and outcomes by individual reviewers.

3. Comparison of reviewers' themes for a specific article and formulation of chains of inference from the identified themes.

4. Linking of the chains of inference and tracking and linking of articles.

5. Hypothesis formulation (context, mechanism, and outcome configurations).

6. Integration of analysis of the underlying theories of how the feeding interventions are expected to bring about change, and ii) the findings of the trials and the process evaluations of how the theory worked or did not work in practice.

As an output of this synthesis, we will identify factors that enhance or reduce the effectiveness of school feeding programs. 

Subgroup analyses  

We will conduct subgroup analysis across SES, age, and sex for the three primary outcomes: physical health, educational, and cognitive outcomes.