Types of studies

We included randomised controlled trials (RCTs) and cluster randomised controlled trials (cRCTs). We also included non‐randomised studies because: 1. we did not expect to find many RCTs that would answer our question; and 2. to increase the external validity of the review findings. In these studies, observations are made before and after an intervention has been implemented or an exposure has occurred, both in an intervention and a control group. These types of studies are sometimes referred to as prospective analytical cohort studies or controlled before‐after studies. We collectively termed them prospective controlled studies (PCS). We planned to include interrupted time series (ITS), but found none. ITS studies observe the effects of an intervention at multiple time points before and after an intervention. ITS studies needed to have at least three time points both before and after the intervention in order to be included.

Types of participants

We included all population groups living in communities in LMICs exposed to community‐level interventions aiming to improve food access. For the purpose of this review, we defined a community as a group of people with diverse characteristics who are linked by social ties, share common perspectives and engage in joint action in geographical locations or settings (MacQueen 2001). We included both adults and children living in those communities, as well as disadvantaged groups within those communities. LMICs were defined according to the World Bank 2020.

Most interventions addressing food insecurity are usually implemented in areas and among populations at high risk for food insecurity, such as low‐income areas, unemployed people, women and children. We did not restrict studies on the basis of social and demographic characteristics, and reported these characteristics in the review.

We excluded studies which only included participants with specific diseases or conditions (e.g. severely malnourished children) as these types of participants require specialised approaches to address malnutrition caused by these diseases or conditions.

Types of interventions

We included community‐level interventions that aim to improve access to food, as detailed in our logic model (Figure 1). Community‐level interventions were defined as those in which the community was the setting where the intervention was implemented, with every member of that community potentially benefiting from it (McLeroy 2003). This includes interventions that are district‐, city‐ or village‐wide or interventions that take place within community institutions such as schools, neighbourhoods, churches or work sites. The intervention may involve individuals, households, organisations or public policy. Based on the literature in this field, and on the findings of our scoping review, we decided to include the following interventions that address access to food (Table 2):

• interventions that improve buying power (e.g. income‐generation opportunities, cash transfer schemes);

• interventions addressing food prices (e.g. policies, discounts, vouchers and subsidies);

• interventions addressing infrastructure and transport that affect physical access to food outlets;

• interventions addressing the social environment and social support (e.g. social support from family, neighbours or government).

We included studies that compared these interventions, individually or in combination, to no intervention or to other eligible interventions, including treatment as usual.

We chose this broad approach because we did not expect to find many eligible studies to include for each of the intervention types.

As we anticipated variability in the duration of included interventions, we included interventions of any duration.

Although we were interested in interventions that have measured access to nutritious food, we did not apply this as an inclusion criterion. Instead, we captured this information when extracting the details of included interventions, if this was available.

We excluded interventions that addressed transient food insecurity (e.g. food aid during natural disasters and wars) and that provided short‐term relief from food insecurity (e.g. one‐off food voucher, food banks or soup kitchens). We also excluded interventions that provided food in the form of food baskets or in‐kind transfers of food. These types of interventions, according to our logic model, fall under the groups of interventions addressing availability and were, therefore, excluded. Other types of in‐kind transfers (e.g. livestock, food vouchers, etc), that were not directly providing food to participants but contributed to their economic access to food, were eligible for inclusion. Interventions that involved agricultural production also typically fall under 'food availability', however, if their aim was specifically to generate income, they were included.

Types of outcome measures

Given the complex nature of food security, we assessed outcomes at different levels, namely at the community, household and individual levels.

The findings of our scoping review showed that the types of outcomes measured across food security interventions vary considerably. For this reason, we took a broad approach regarding the outcomes to include.

Given that our main interest was in determining whether these interventions improve access to food and, consequently, food security and nutritional status, we included only interventions that had measured outcomes related to food access or nutritional status, or that used a food security measurement tool. We included any study that had at least one of the outcomes listed below.

Electronic searches

We searched electronic databases from 1980 onwards for relevant studies. We applied no language or publication status limits. We chose the year 1980 as the starting point because it was around this time that the term 'food security', encompassing access to food, started being used (Masset 2011). The initial searches were conducted in September 2016 in the following databases:

• Ovid MEDLINE(R) Epub Ahead of Print 11 July 2016, Ovid MEDLINE 1946 to June week 5 2016, Ovid MEDLINE(R) In‐Process & Other Non‐Indexed Citations 11 July 2016, Ovid MEDLINE Daily Update 11 July 2016;

• Cochrane Central Register of Controlled Trials (CENTRAL): Issue 6, 2016 (the Cochrane Library/Wiley);

• Embase (Elsevier);

• GreenFILE (EBSCO);

• AfricaBib (africabib.org);

• AGRIS;

• AGRICOLA;

• AFRICAN HEALTHLINE, African Journals Online (via Africa‐Wide Information, EBSCO);

• Trials Register of Promoting Health Interventions (TRoPHI);

• WHO Global Index Medicus;

• Web of Science (Conference Proceedings Citation Index, Science Citation Index Expanded, Social Science Citation Index);

• Sociological Abstracts (ProQuest);

• International Bibliography of the Social Sciences (IBSS) (ProQuest);

• Global Health (EBSCO);

• ClinicalTrials.gov;

• WHO International Clinical Trials Registry Platform.

A combination of text words and controlled vocabulary terms related to the interventions and possible outcome measures were used to develop a sensitive search strategy. The search strategies for the different databases are available in Appendix 1, which is an adaptation of the search strategy for the Cochrane Review assessing interventions to improve food security in developed countries (Burns 2010). We applied a study design filter to the search that has been developed by Joy Oliver, the information specialist at Cochrane South Africa. The original search strategy for MEDLINE published with the protocol of this review had to be revised by a librarian and adapted for Ovid MEDLINE, as it retrieved an excessive number of results. The Ovid MEDLINE search strategy was then modified to be adapted for the other databases and reported as appendices in our full review. We recruited the Cochrane Public Health Group's information specialist to advise on and implement the search strategy.

The search was updated in April 2019 and February 2020. For the updates, we followed the recommendations of Garner 2016. The Cochrane Public Health Group's information specialist defined a minimum set of databases that would have identified the original included studies and optimised the remaining database searches to improve the balance of sensitivity and precision of the search strategies. We searched the following databases from 1980 onwards:

• Ovid MEDLINE(R) and Epub Ahead of Print, In‐Process & Other Non‐Indexed Citations, Daily and Versions;

• CENTRAL (the Cochrane Library/Wiley);

• Web of Science (Conference Proceedings Citation Index, Science Citation Index Expanded, Social Science Citation Index);

• Global Health (EBSCO);

• Sociological Abstracts (ProQuest);

• International Clinical Trials Registry Platform.

The search strategies for each database included in the latest search, which is the same as for the April 2019 search, are available in Appendix 1. Appendix 2 presents the search strategies of the original search strategy in September 2016.

Some of the electronic databases specified above index a combination of published and unpublished studies, such as doctoral thesis and conference abstracts. Therefore, the electronic searches captured some of the unpublished studies. For further searching for unpublished studies, see Searching other resources.

Searching other resources

We identified additional studies through searching reference lists of similar reviews or contacting authors of included studies. However, much of the additional searches we were planning to undertake at the protocol stage were not carried out. We provide reasons in the Differences between protocol and review section.

Selection of studies

Two author pairs (SD, AS, MV, AB, JO, VR, BS) independently screened all titles and abstracts retrieved to determine eligibility against the inclusion criteria. Full‐text copies of eligible titles and of those for which eligibility was unclear were retrieved for closer examination. Any disagreements regarding eligibility were resolved through discussion or through arbitration by a third author, if necessary. We recorded the reasons for excluding studies at the full‐text screening stage in the Characteristics of excluded studies table. We completed a PRISMA flow chart of study selection.

The initial title and abstract screening, from the first search, was carried out using Word documents. The full‐text screening and all subsequent screening was carried out using the Covidence platform.

Where we found relevant studies in a language other than English, Portuguese or Spanish, we planned to contact Cochrane Public Health for options for translations. We found studies in French, which a colleague reviewed against the eligibility criteria. As these were not eligible for inclusion, no translations were required. We found no studies in any other language that required translation.

We used EndNote X8 to manage the retrieved records and to remove duplicate reports of the same study. The study was considered the unit and all references related to the same study were grouped under the same identifier.

Data extraction and management

For each included study, author pairs (SD, AS, MV, AB, JO, VR, BS) extracted data independently and resolved disagreements through discussion or arbitration by a third author. We collected all data except those concerning outcomes using Covidence, using a standardised data collection form, which was piloted on two studies. One author extracted outcomes data using a standardised and piloted form in Microsoft Excel 2007 and a second author (a biostatistician; YB) checked all the data extracted. We based our data extraction form on the forms from Cochrane Public Health and Cochrane Effective Practice and Organisation of Care (EPOC), modified to suit our review. We extracted the following data.

• Study design and methods (recruitment of participants, representativeness of sample, number of intervention groups, randomisation procedure, statistical methods).

• Details about the participants, including PROGRESS‐Plus characteristics and number in each group at baseline and at the endpoint. PROGRESS‐Plus characteristics refer to characteristics of participants that can be used to identify disadvantaged groups and that allow us to differentiate the effects of the intervention across social categories (Tugwell 2010). These characteristics include: place of residence, race or ethnicity, occupation, gender, religion, education, socioeconomic status and social capital; and Plus characteristics include age). We extracted details about withdrawals and dropouts, if these were available.

• Details about the intervention, including process measures (e.g. aims; social and cultural context; comparison interventions; length of the intervention; duration of follow‐up; implementation factors such as amount of conditional cash transfers, number of times transport is given or total amount of food vouchers given to each individual), and whether the intervention was universal or targeted. This information aimed to provide insight on the factors that may impair or facilitate implementation of the intervention, which addresses the second objective of this review. We also extracted information on whether the intervention aimed to improve access to nutritious food, how nutritious food was defined, if specific nutritious foods were targeted for increased access and what types of food were accessed by participants.

• Description of outcomes used to measure effectiveness and how they were measured.

• Primary outcomes at the household and community level.

• Secondary outcomes at the individual level.

• Other process measures including intervention cost and sustainability.

• Source of study funding and sponsorship of the interventions.

We incorporated the Cochrane‐Campbell Methods Group Equity Checklist into our data extraction form (methods.cochrane.org/sites/methods.cochrane.org.equity/files/public/uploads/EquityChecklist2012.pdf); however, the included studies reported very little of this information.

We extracted information on potential confounders or moderators of the study outcomes. These included sociodemographic variables such as gender, ethnicity or race, and place of residence, and other PROGRESS‐Plus characteristics based on the details available in the studies.

When necessary, we contacted the authors of primary studies to for clarification or to seek missing information.

We used Review Manager 2014 for data management and analysis.

Assessment of risk of bias in included studies

Author pairs (SD, AS, MV, AB, JO, VR, BS) conducted the risk of bias assessment and resolved disagreements through discussion or arbitration by a third author. Risk of bias assessments were also carried out in Covidence.

We assessed the risk of bias for all RCTs and PCS using the EPOC risk of bias tool for studies with a separate control group (EPOC 2017). This tool assesses the same risk of bias domains as the Cochrane 'Risk of bias' tool for RCTs (Higgins 2011), namely sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessors, incomplete outcome data (including loss of clusters in the case of cRCTs), selective outcome reporting and other bias. It also includes additional domains to assess the risk of bias from inappropriate methods regarding: similarity of baseline outcome measurements, similarity of baseline characteristics and whether the study was protected against contamination. For other bias, we specifically assessed misclassification bias of the exposure, measurement bias and two domains related to cRCTs: incorrect analysis (i.e. whether the study adjusted for clustering) and recruitment bias. We assessed the risk of bias from lack of blinding of participants and personnel and of outcome assessors separately. We had planned to assess the risk of bias from lack of blinding separately for objective and subjective outcomes and to assess the risk of bias from incomplete outcome data separately for different outcomes. However, given the disparity and multiplicity of outcomes reported, we decided not to do this. However, we did consider whether the outcome was objective or subjective when assessing the risk of bias from lack of blinding.

We had planned to use the EPOC risk of bias tool for ITS study designs; however, we included no ITS studies.

For each item, we made a judgement of 'High risk', 'Unclear risk', or 'Low risk', with supportive information to justify these judgements provided in the Characteristics of included studies table. We incorporated the risk of bias assessment in the interpretation of our review findings, and we did not restrict analysis by degree of risk of bias. We presented a 'Risk of bias' graph and a summary figure.

To assess overall risk of bias at study level, we considered its risk of bias for two key domains: selection and attrition bias. For example, if a study was classified at high risk of either selection or attrition bias, it was classified as having overall high risk of bias.

Measures of treatment effect

Where data allowed, we conducted meta‐analysis using Review Manager 5 (Review Manager 2014). However, due to sparsely reported data, we were unable to conduct a meta‐analysis in many instances.

For binary outcomes, we planned to report the risk ratio (RR) of outcomes in the intervention group compared to the control group. Only one included study reported the RR as an overall effect measure for the intervention. The other 28 included studies that reported dichotomous outcomes reported the change in proportion using percentage points (pp) (68%) or using reported odds ratios (OR) (32%).

For continuous outcomes, and where baseline data were available, we reported the mean difference (MD) between the change in the intervention and control groups if the outcomes had been measured in the same way by all studies. If the continuous outcomes were measured in distinct ways in different studies in a comparison, we used the standardised mean difference (SMD) between the intervention and control groups. Where the change per group was not available, we used end values where randomisation was successful. If there was a reasonable risk of selection bias, and the change per group was not available, the study was not included in a meta‐analysis.

The included studies reported mostly estimates from regression or from difference‐in‐difference analyses, which were interpretable as an MD and thus were reported as such. None of the studies reported the effects per group, and in most cases the data were only available either for baseline or endline, and if it was available, often there was no measure of variance reported. Thus, we described the effect measures as reported in the included studies.

We reported 95% confidence intervals (CIs) alongside all effect estimates, when these were available or when it was possible to calculate them. Calculations of 95% CI were done in Review Manager (using the inverse variance option; Review Manager 2014) or using a Microsoft Excel 2007 spreadsheet with the formula to calculate the 95% CI from the regression estimate and standard error (SE) value. We report P values only where no 95% CI was reported or could be calculated to illustrate the strength of evidence for the effect size.

Unit of analysis issues

cRCTs that randomise groups rather than individuals to intervention groups and that report analyses at the individual level needed to also report the method used to account for clustering. A biostatistician (YB) checked all studies to ensure that the clustering effect had been accounted for correctly. If they had not taken the clustering effect into account in their analyses, we would have requested individual participant data, calculated an intracluster correlation coefficient (ICC), and re‐analysed the data appropriately. If we had been unable to obtain primary data, we would have attempted to find an appropriate ICC from the literature and adjust the sample size accordingly. We had planned to meta‐analyse the effect estimates and SEs from cRCTs using generic inverse‐variance methods in Review Manager 2014. If we had re‐analysed the data, we would have clearly marked the results as re‐analysed and we would have stated where re‐analysis had not been possible. However, we did not have to re‐analyse the data for included cRCTs as they all correctly accounted for clustering.

In cases where the outcomes were measured at multiple time points, we had planned to group the outcomes measured at similar time points where this was possible. For any particular outcome, if most studies were reporting a specific time point and only one study reported multiple time points, we reported the most commonly reported time point. In most cases, the time points were similar and, for the few instances where this was not the case, we extracted measures from all time points but reported the latest time point. Taking into account that the minimum duration after implementation at which we extracted outcomes was three months, the short‐term time point was three to six months.

We only considered outcomes reported immediately at the end of the intervention, not postintervention follow‐up.

In many cases, studies reported multiple outcome measures for the same outcome domains. To prioritise the outcomes, we selected the measure that provided the largest scale measure of the domain (i.e. the most comprehensive outcome). For example, in cases where individual and composite measures for the same outcome domain were reported for the same study, we preferentially reported composite measures as these are probably more useful to decision‐makers. For anthropometry, we did not report effects on weight and height units, but rather reported z‐scores for weight‐for‐age and height‐for‐age, in which weight and height are assessed against a reference standard. All outcomes reported in a study are presented in the Characteristics of included studies table, as well as an indication of which were selected for synthesis.

For interventions with multiple comparison groups, all groups that met this review's inclusion criteria were included. If there were more than two relevant comparison groups for the same intervention, we attempted to combine the relevant experimental and control groups to make a single pairwise comparison. This was the case in three studies, for which two interventions groups were combined. If this was not possible, we made multiple pairwise comparisons between the relevant groups and divided the sample size of the shared intervention group evenly across the comparisons to avoid double counting of participants in a meta‐analysis. If a meta‐analysis was not possible and we could not combine the results of different groups, we presented the results of all relevant groups.

Dealing with missing data

If there were unclear or missing data related to study methodology, participants lost to follow‐up, outcome data or statistics, we contacted the study's primary author via email. We recorded all communications with authors in Appendix 3.

We recorded all missing outcome data in the data extraction form and in the Characteristics of included studies table. If it was not possible to obtain missing outcome information after attempting to do so, we would have excluded these studies from the meta‐analysis. We did not exclude any studies due to missing outcome data.

Five included studies did not report the number analysed for at least one outcome (for which the number (n) is stated as not reported (NR)) (Ahmed 2019a; Ahmed 2019b; Andaleeb 2016; Ferre 2014; Hoddinott 2013). This lack of reporting reduces our confidence in the estimated treatment effect as we are unable to assess if the study was powered to detect an effect, analysed accounting for any clustering or if attrition bias was likely. In addition, it has been shown that trial sample sizes can influence treatment effect, with smaller studies reporting larger effect estimates (Dechartres 2013). With no sample sizes reported, it is difficult to ascertain whether this bias exists.

Assessment of heterogeneity

Where we were able to meta‐analyse, we assessed heterogeneity, or the variability among the studies included in a meta‐analysis, by visual inspection of overlap of CIs, and by assessing statistical heterogeneity with the Chi² statistic (P < 0.1) (Deeks 2019). We calculated the I² statistic to quantify heterogeneity; with an I² statistic of 75% and above indicating substantial heterogeneity. We also calculated Tau², which reflects the extent of variation among intervention effects in different studies, to assess heterogeneity (Deeks 2019). However, in most cases, we were unable to carry out meta‐analyses or create forest plots due to heterogeneity. Instead, we assessed clinical, methodological and conceptual heterogeneity, through tabulation of characteristics of studies included in the same synthesis. For specific comparisons and outcomes, we assessed clinical or conceptual heterogeneity by considering variability in the participants and interventions, or co‐interventions, including study duration, intervention dosing and outcome assessment. We assessed methodological heterogeneity by considering the variability in study design and risk of bias (Deeks 2019; Singh 2017).

Assessment of reporting biases

We had planned to assess the likelihood of reporting bias through funnel plots for each outcome with 10 or more included studies in a meta‐analysis (Sterne 2019). We would have assessed the funnel plots visually for sources of asymmetry, such as small‐study effects, publication bias or other. If it was likely that asymmetry was caused by small‐study effects, we would have conducted sensitivity analysis to explore how this affected the results and conclusions of the meta‐analysis. However, we were unable to do this as none of the compared outcomes were assessed by at least 10 studies.

Data synthesis

In most cases, we were unable to include all studies reporting a specific outcome domain in a meta‐analysis. This was due to studies reporting multiple measures for the same domain that could not be combined, either because there was missing information regarding variance measures, or because the effect measures reported could not be converted to a standardised metric. Therefore, we synthesised the data from all studies reporting on the same outcome domain using vote counting based on the effect direction method (McKenzie 2019). The results of individual studies were presented in one of four categories: 1. 'favours control' if the point estimate favoured the control and the 95% CI did not cross the null; 2. 'unclear effect; potentially favouring the control' if the point estimate favoured the control but the 95% CI crossed the null; 3. 'unclear effect; potentially favouring the intervention' if the point estimate favoured the intervention and the 95% CI crossed the null; and 4. 'favours intervention' if the point estimate favoured the intervention and the 95% CI did not cross the null. Where no CI was provided or could be calculated, we decided whether the effects were 'clear' or 'unclear' based on provided P values. However, P values did not inform the effect direction reported. Although this is a useful method to synthesise data when meta‐analysis is not possible, there are some limitations associated with this method, for example, it does not provide information on the magnitude of effects, does not account for differences in the relative sizes of the studies and is a less powerful method than that used to combine P values (McKenzie 2019).

Regarding the effect direction synthesis, we reported the number of studies with results in the different effect categories for each outcome domain, and the probability of observing this based on the multinomial distribution (for outcome domains with two or more studies and assuming the true proportion is 0.25 for all categories). This information was reported in the first paragraph reporting results for a specific outcome in the effects of interventions section. If a meta‐analysis of all studies in the outcome domain was possible, the multinomial distribution P value was not reported. To visually display the results for key outcomes included in the 'Summary of findings' tables, we created harvest plots for each comparison. These harvest plots depict data both from RCTs and from PCS for key summary of findings outcomes. We presented the results of the effect direction synthesis separately for RCTs and for PCS, in the Effects of interventions section.

In some instances, we were able to carry out a meta‐analysis, either for all studies reporting on the same outcome measure (n = 35), or for a subset of studies that could be combined in a meta‐analysis (n = 8). We conducted meta‐analyses in Review Manager 2014 if the included studies were sufficiently homogeneous (I² < 75%) and if there was a minimum of two studies for any type of intervention being compared reporting the same outcome measure. Not pooling results in cases of high heterogeneity is an accepted approach in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2019). We also explored heterogeneity and reported this when there was high heterogeneity. We did not have sufficient data to carry out any subgroup analysis or meta‐regression to more formally explore heterogeneity. We carried out meta‐analyses separately for each outcome and type of study design, and we used the random‐effects model for all analyses to account for any existing heterogeneity. We generated forest plots for each comparison and outcome where meta‐analyses could be carried out (see Data and analyses).

In preparation for synthesis, we first grouped all studies assessing the same intervention categories to identify which studies could be grouped under each preplanned comparison, and no changes to prespecified grouping were required. The comparison groups were based on the pre‐specified types of interventions listed in table 2: cash transfers (unconditional; conditional), income generation interventions, food vouchers, food subsidies, and social support interventions. Under each comparison, we tabulated the available data and time frames reported for each outcome, which helped identify what data were available, and thus where meta‐analysis was possible and where we had to synthesise using effect direction. A meta‐analysis was possible if the effect and variance estimates were available for all studies or could be calculated from the available data, and if all effect estimates were of the same type (e.g. OR or MD) or could be converted for the comparison (e.g. OR to SMD). Where necessary, we converted OR to SMD, MD to SMD, or MD to SMD to OR.

We prepared two additional types of tables to aid visualisation of available data. One was the 'Overview of included studies' table, summarising main characteristics and reported outcomes of included studies for each comparison (McKenzie 2019). In this table, we organised studies first by study design, with RCTs first followed by PCS, and second according to their overall risk of bias (low, unclear and then high risk of bias). The second type were tables with the results for individual studies, for each comparison, for scrutiny by the reader. The studies in these tables were also ordered according to their overall risk of bias.

We had planned to assess and discuss the implementation factors common to effective interventions, if this information was reported in included studies or in published process evaluations that are mentioned in the study report. However, there was insufficient information from included studies on this.

Subgroup analysis and investigation of heterogeneity

We did not have enough data per outcome and comparison to carry out subgroup analyses. If data allowed, we would have conducted subgroup analysis to assess effectiveness for people at different levels of disadvantage. In updates of this review, we will include the following subgroups.

• Geographic location (e.g. urban versus rural, country or region).

• Sex (male versus female).

• Age (e.g. elderly people, adults, children, infants).

• Baseline nutritional status (e.g. underweight, overweight, micronutrient deficiencies).

We would also have assessed important implementation factors through subgroups analyses, including the following.

• Intensity of intervention (high intensity versus low intensity, e.g. in relation to amount of food vouchers or of conditional cash transfers).

• Length of study and follow‐up (e.g. three to six months, more than six months to less than two years, and two years and beyond).

• Whether the intervention specifically aimed to improve access to nutritious food.

These analyses would have allowed further exploration of heterogeneity. In order to compare the different subgroups with each other, we would have conducted a standard heterogeneity test in Review Manager 2014 across the subgroup results, by calculating the I² statistic. We would have made sure that the subgroup data being compared were independent.

Sensitivity analysis

We conducted a sensitivity analysis to assess risk of bias for outcomes with five or more studies. Studies with overall low risk of bias were included in the sensitivity analysis. We reported the results of study designs separately.

Summary of findings and assessment of the certainty of the evidence

The 'Summary of findings' tables include information regarding the number of participants and studies for key outcomes, a summary of the intervention effect and a measure of the certainty of evidence for each outcome according to GRADE considerations. GRADE is a system of rating certainty of evidence in systematic reviews (Guyatt 2010). We rated the overall certainty of evidence for a particular outcome on‐line with GRADEpro as high, moderate, low or very low. All RCTs started at high‐certainty evidence and the following factors were considered to downgrade the certainty: overall risk of bias, consistency of effect, imprecision, indirectness and publication bias. All PCS started at low‐certainty evidence and the following factors would have been considered to upgrade the certainty: large magnitude of effect, dose‐response gradient and effect of plausible residual confounding. We did not upgrade the certainty of evidence for PCS as there were existing reasons for downgrading (Schünemann 2019). As most of the evidence was not from pooled data, we used the 'Summary of findings' table format for narrative synthesis.

We had planned to include a 'Summary of findings' table for the primary outcomes of this review. However, we decided to also include some of the secondary outcomes. The choice of outcome categories and specific outcome measures to report in the 'Summary of findings' table were decided by the review author team through in‐depth discussion until consensus was reached, taking into consideration which outcomes would be useful to decision‐makers. The 'Summary of findings' tables included the following outcomes.

• Prevalence of undernourishment.

• Proportion of household expenditure on food.

• Proportion of households who were food secure.

• Dietary diversity.

• Stunting.

• Wasting.

• Cognitive function and development.

Three authors met to rate the evidence per outcome for each of the 'Summary of findings' tables. Decisions about whether to downgrade or not were made through discussion and reaching consensus. Evidence on different outcomes was available from different study designs. Where there was evidence for a particular outcome from both RCTs and PCS, we reported the data from the RCTs in the 'Summary of findings' table. When there were no data from RCTs for a particular outcome, we reported data from PCS that reported that outcome. We reported the certainty of the evidence in the Effects of interventions for outcomes which assessed with GRADE. For other outcomes, we report the risk of bias, as an indicator of the certainty of the evidence to consider when interpreting the findings.