Types of studies

We will include primary studies whose designs enable attribution of causation as per the guidance of Cochrane Effective Practice and Organisation of Care (EPOC) (EPOC 2021). We will use a broader set of study designs, as randomised controlled trials (RCTs) are likely to be limited for complex public health interventions on snakebite. This is because of the logistical complexity and resource scarcity in the conduct of controlled studies. Using non‐randomised trials will also increase the external validity for knowledge users, because they include a wider set of geographies or populations, or both. We will include the following study designs.

• Randomised controlled trials: where participants were randomly assigned, individually or in clusters (cRCT).

• Non‐randomised controlled trials: where individuals or clusters were allocated to different interventions using methods that were not random.

• Controlled before‐and‐after (CBA) studies: where allocation to intervention groups and control groups was not made by study investigators; outcomes were measured in both intervention and control groups at baseline and endpoint; and appropriate methods were used to control for selection bias and confounding, such as statistical matching (e.g. propensity score matching or covariate matching) or regression adjustment (e.g. difference‐in‐differences, instrumental variables).

• Interrupted‐time‐series (ITS)studies: where outcomes were measured in the intervention group at least three time points both before and after the intervention is implemented. We will exclude studies that did not have a clearly defined point in time when the intervention occurred.

We will only include cluster RCTs, non‐randomised RCTs and CBA studies if they have at least two intervention sites and two control sites, as recommended by Cochrane EPOC.

Types of participants

We will include participants within studies in communities affected by snakebite, regardless of their age, gender and country.

Types of interventions

We will include any community‐based intervention (alone or as a part of a multi‐component intervention) that aimed to decrease snakebite, as defined previously (Description of the intervention and Table 1). We will also include holistic, community‐based interventions that integrate snakebite awareness into other community‐based programmes on the prevention of environmental, zoonotic or other diseases, provided a clear reporting of the component relevant to snakebite is available.

The included studies must have compared these interventions against no intervention or interventions that are non‐community based (including health systems or mass‐media interventions).

Types of outcome measures

When considering which outcomes to include in this review, we explored a range of outcomes that reflect the overall aim of the review. We decided that the outcomes that are at the impact level, as identified in our logic model (Figure 1), are the primary outcomes of interest in this systematic review. A broad and inclusive approach to define outcomes of interest was taken to reflect the diverse nature of intervention categories and components of community‐based interventions.

Electronic searches

We will search the following databases to retrieve reports of relevant studies:

• MEDLINE Ovid;

• Embase Ovid;

• Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library;

• Campbell Library;

• Education Resource Information Center (www.eric.ed.gov);

• AfricaBib (www.africabib.org);

• Scientific Electronic Library Online (SciELO) (www.scielo.org);

• Global Index Medicus (WHO, www.globalindexmedicus.net); and

• Global Health (EBSCO).

We have devised a draft search strategy for MEDLINE, which we display in Appendix 1. We will adapt this strategy to search other databases and provide all search strategies within the full systematic review. There will be no restrictions of the searches by language, date of publication or study setting.

We will also search the following clinical trials registries for ongoing studies:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov);

• World Health Organization International Clinical Trials Registry Platform (www.who.int/clinical-trials-registry-platform); and

• Trials Register of Promoting Health Interventions (www.eppi.ioe.ac.uk/webdatabases4/Intro.aspx?ID=12).

Searching other resources

We aim to identify other potentially eligible studies or ancillary publications by searching the reference lists of retrieved included studies as well as relevant overview of reviews. We will contact members of the Snakebite Research Network (through their mailing list) and people working on community interventions for snakebite to identify additional potentially relevant studies.

We will also search the following websites to identify grey literature:

• New York Academy of Medicine Grey Literature Catalogue (www.nyam.org/library); and

• 3ie (International Initiative for Impact Evaluation) Development Evidence Portal (www.developmentevidence.3ieimpact.org).

Selection of studies

Two review authors (SB and SP or JJ) will independently screen titles or abstracts, or both, based on the eligibility criteria. Any record that is considered to be included by one author will be considered for inclusion in the next phase of screening. In the next phase of screening, we will retrieve the full text, which at least two review authors will independently assess. We will resolve any disagreements by discussion with a third review author (PK), who will act as an arbiter. We will document reasons for exclusion at full‐text level. We will use EndNote X7 to manage the screening process. We will use a PRISMA flow diagram to document the selection process (Page 2021).

Data extraction and management

At least two review authors (SB and SP or JJ) will independently extract the following data from the included studies in a standardised data extraction form.

• Study identification: authors and year of publication.

• Methods: study design, location, duration and date.

• Context: any related information reported on context, including setting (rural, semirural, urban, hilly, forested areas, coastal, desert, etc.) or weather (tropical, subtropical, high rainfall, low rainfall, etc.), or both.

• Participants: number of participants, mean age or age range, sex, inclusion and exclusion criteria.

• Community characteristics: size, resilience, cohesion, demographics (particularly age and gender), type of community (indigenous (tribal) or not; nomadic, subsistence farming, agricultural, aquacultural, pastoral, etc.), beliefs about snakes, snakebite and envenomation.

• Theoretical basis and aims of the intervention if reported.

• Interventions: description of intervention components (content, dose, duration, frequency), description of intervention implementers (gender, education, training, type of worker) and modifiable design characteristics. Similar data would be collected for any comparator and co‐intervention.

• Process metrics if reported, including any qualitative results related to process metrics that the included study reports.

• Outcomes: outcomes measured, measurement method used, the timing of measurement and numerical results.

• Data pertaining to risk of bias assessment: any information required to assess the risk of bias assessment.

• Additional information: conflicts of interest, source of funding.

The logic model informed the elements of data collection (Figure 1). We will data extract by suitably adapting the data extraction forms created by Cochrane Public Health and Cochrane Effective Practice and Organisation of Care (EPOC), inculcating elements of the logic model. We will pilot the form in the first few studies before we use it for all eligible studies.

We will resolve disagreements relating to data extraction by consensus with a third review author (PK), who will act as an arbiter.

Assessment of risk of bias in included studies

Two review authors (SB and JJ) will independently assess the risk of bias of each included study. We will resolve any disagreements by consensus with a third review author (SP or PK), who will act as an arbiter, as per the guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2022a; Higgins 2022b; Sterne 2021).

For RCTs and cRCTs, we will use Cochrane's RoB 2 for randomised controlled trials (Higgins 2022b; Sterne 2019). The tool evaluates bias in the following domains.

• Bias arising from the randomisation process.

• Bias due to deviations from intended interventions.

• Bias due to missing outcome data.

• Bias in measurement of the outcome.

• Bias in selection of the reported result.

• Overall risk of bias.

For cRCTs, we will also consider the additional domain of identification or recruitment bias (Eldridge 2021; Higgins 2022a).

We will use RoB 2 to assess bias for intention‐to‐treat (ITT) effects. For RCTs and cRCTs, we will categorise the risk of bias for each domain as either low risk, some concerns or high risk, using the signalling questions of RoB 2. We will present our risk of bias assessments using standard risk of bias summary figures. If we judge a trial to be at a low risk of bias in all domains, we will consider it to be at a low risk of bias overall. We will consider trials to be at high risk of bias if we judge them to be at high risk of bias for one or more domains, or if we judge the risk of selection bias or performance bias or detection bias to be unclear.

For non‐randomised controlled trials, controlled before‐and‐after studies and interrupted‐time‐series studies, we will use the ROBINS‐I tool (Sterne 2016; Sterne 2021). We will use an intention‐to‐treat (ITT) analysis for the purpose (Sterne 2016; Sterne 2021). We will restrict the ROBINS‐I assessments to primary outcomes and for the maximal time point reported. Due to the broad scope of the review (in terms of intervention), we cannot provide a full a priori list of co‐interventions at the protocol phase as part of the ROBINS‐I assessment (Sterne 2016), but health systems‐strengthening and mass‐media interventions are likely to be co‐interventions. A priori confounders relevant to all or most studies that we are likely to consider for ROBINS‐I assessment are community size, demographical factors (age and gender), educational levels and socioeconomic factors (income, indigenous or tribal people). If studies mention both adjusted and unadjusted effect estimates, we will use adjusted estimates. We will consider and report any other additional confounders and co‐interventions (e.g. strengthening of health systems) reported by the primary study authors. We will report any such deviation in the full review.

We will assess bias in the following domains:

• Bias due to confounding.

• Bias in the selection of participants into the study.

• Bias in classification of interventions.

• Bias due to deviations from intended interventions.

• Bias due to missing data.

• Bias in the measurement of outcomes.

• Bias in the selection of the reported result.

• Overall risk of bias.

We will use signalling questions as per the ROBINS‐I tool to rate each domain. The rating of overall risk of bias will lead to a categorisation of “low risk”, “moderate risk”, “serious risk”, “critical risk” or “no information” (Sterne 2016).

We will exclude studies that we judge to be at critical risk of bias from any numerical analysis. We will report assessments of RoB 2 and ROBINS‐I separately.

Measures of treatment effect

For dichotomous data, we will calculate risk ratios (RRs) with 95% confidence intervals (CI). For continuous data where studies measure the change in outcome using the same method, we will calculate the mean difference (MD) with 95% CI, as is it enables better interpretation. If different studies measure the same continuous outcome using different methods, we will calculate the standardised mean difference (SMD) with 95% CIs. For outcomes that are reported using both continuous and dichotomous data, we will present these as SMDs and will pool dichotomous and continuous outcome measures by calculating SMDs from odds ratios (ORs). If we encounter count data, we will extract the total number of events and analyse them as rates. We will express rate (or incidence) data as rate ratios with 95% confidence intervals (CI), according to the Cochrane Handbook (Deeks 2022; Higgins 2022c). We will import rate ratios and standard errors into Review Manager 5 and use the generic inverse variance method to calculate CIs.

For time‐to‐event outcomes where primary study authors used survival analysis (e.g. time to reach health facility), we will use hazard ratios (HR). If a study does not report HRs, we will attempt to estimate HRs using established statistical methods (Parmar 1998; Tierney 2007). If this is not possible, we will summarise the intervention effect descriptively.

For some secondary outcomes, we expect studies to report a mix of both change‐from‐baseline and post‐intervention values. For randomised studies, we will use post‐intervention values for meta‐analysis. For non‐randomised studies that use MDs, we will pool change‐from‐baseline values and post‐intervention values together but report them in subgroups, as recommended in Chapter 10 of the Cochrane Handbook (Deeks 2022). However, when the effect measure is SMD, we will not pool change‐from‐baseline and post‐intervention values; we will instead synthesise and report them separately. If studies do not report SDs of change, we will impute them as per Chapter 6 of the Cochrane Handbook (Higgins 2022c).

For ITS studies, we will extract data on time points of measurement and for each time point, we will extract data on pre‐interruption level and slope, post‐interruption change in level, post‐interruption slope, as reported. We will use WebPlotDigitizer, if required.

Unit of analysis issues

Our preferred unit of analysis will be the individual participant. If a cluster RCT is not appropriately analysed, we will — if feasible — use the following information to adjust for clustering (design effect), as per guidance in the Cochrane Handbook (Higgins 2022c).

• Number of clusters randomly assigned to each intervention, or average number of participants per cluster.

• Reported outcome data without considering the cluster design for all participants.

• Intracluster (or intraclass) correlation coefficient (ICC).

If we encounter a study with multiple comparisons groups and it is included in a meta‐analysis (thus resulting in multiple correlated comparisons), we will create single pair‐wise comparisons before pooling, as described in the Cochrane Handbook (Deeks 2022; Higgins 2022c).

Dealing with missing data

We will attempt to contact study authors to obtain any missing data. If there is no response from authors or we cannot establish contact, we will assume that participants with missing data did not develop the outcome of interest. If data are available in graphical format (with no numerical data reported), we will extract the numerical values based on review author consensus from the graphs or figures, or both. If trials report both intention‐to‐treat and per‐protocol data, we will only use intention‐to‐treat data; we will not impute missing data.

For continuous variables, we will present available data from the study reports or study authors and do not plan to impute missing data. Where measures of variance are missing, we will calculate these wherever possible. If calculation is not possible, we will contact the study authors. Reporting of time‐to‐event outcomes in trials is known to be poor. If studies do not report HRs, and when feasible, we will attempt to estimate HRs using other reported data through established statistical methods (Parmar 1998; Tierney 2007).

If insufficient data are available, we will not exclude the study from the relevant meta‐analysis. In the full review, we will transparently report information regarding any data requests made and responses obtained.

Assessment of heterogeneity

We will first consider clinical and methodological heterogeneity, i.e. we will consider the degree to which the included studies vary in terms of participant; intervention; outcome and other characteristics such as length of follow‐up, co‐intervention and community type. We are unable to pre‐specify the amount of clinical, methodological and statistical heterogeneity in the included studies, but we will only pool data to generate a forest plot if it is appropriate to do so. We will supplement the assessment of clinical and methodological heterogeneity with information on statistical heterogeneity. We will test heterogeneity of the intervention effects amongst the included trials by visually inspecting analysis graphs, the standard Chi² test (P value) and the I² statistic (Deeks 2022; Mckenzie 2022a). We will consider a P value of less than 0.10 as statistically significant in terms of heterogeneity. We will interpret the I² statistic for heterogeneity as follows:

• 0% to 40%: may not be important.

• 30% to 60%: represents moderate heterogeneity.

• 50% to 90%: represents substantial heterogeneity.

• 75% to 100%: represents considerable heterogeneity.

For ITS studies, we will assess quantitative heterogeneity by formally testing homogeneity and assessing the proportion of total variability attributable to heterogeneity rather than sampling error (I² statistic). We will also report the prediction interval of the pooled effect sizes.

Assessment of reporting biases

Reporting bias arises when the nature and direction of results influence the dissemination of research findings. Publication bias is one of several possible causes of 'small‐study effects', that is, a tendency for estimates of the intervention effect to be more beneficial in smaller RCTs. Funnel plots allow a visual assessment of whether small‐study effects may be present in a meta‐analysis. A funnel plot is a simple scatter plot of the intervention effect estimates from individual RCTs against some measure of each trial's size or precision (Sterne 2016). If we find more than 10 studies for a particular intervention‐comparison pair, we will assess reporting bias for primary outcomes using funnel plots (both the visual method and Egger test), as recommended by the Cochrane Handbook (Page 2019).

Selective outcome reporting, i.e. the bias in selection of the reported result (Page 2019), is a risk where information on outcomes or time points is collected but not reported in the study. We will contact study investigators in an attempt to get information on such outcome measures or time points. Based on the information available, we will assess risks qualitatively: for each study, we will note which outcomes were captured (from the methods section) and identify outcomes that were not reported (from the results section) or not obtained (after contact with study authors). We will compare the stated aims of each evaluation with the outcomes reported. We will appropriately report any suspected reporting bias, along with justification for our judgement.

Data synthesis

We will structure the comparisons according to the broad intervention categories identified by our logic model, and then subsequently by related pair‐wise comparator and outcome domains. We will group interventions as per their broad intervention category. For multi‐component interventions that map to different intervention categories, we will not group them with either of the categories; instead, we will create a single category of multi‐component interventions. We will create separate categories for non‐community‐based interventions, based on their key components. We will separately compare a particular intervention category with no intervention or non‐community‐based intervention.

We will conduct separate meta‐analyses depending on whether the study was based on an ITS or other study designs. For the latter, we will separately pool dichotomous (RR, OR) outcomes (by converting them to a common measure as appropriate), continuous outcomes (MD or SMD) and time‐to‐event outcomes (HR). If meta‐analysis is appropriate, we will use a random‐effects approach for meta‐analysis. We will use the Chi² test and the I² statistic to quantify heterogeneity, but we will not use these to guide the choice of model for meta‐analysis. We will exercise caution when meta‐analysing data in the presence of small‐study effects, as a random‐effects model might not be suitable in such a scenario. In this case or where there are other reasons that might lead us to question the selection of the random‐effects model as recommended by Deeks 2022, we will assess the impact of the approach using sensitivity analyses and compare results from alternate models (Mckenzie 2022a; Sterne 2016). We will report any evidence that suggests that the use of a particular model might not be robust.

For meta‐analysis of ITS studies, we will use a two‐stage approach, which encompasses the following process: extract effect estimates from each included ITS study and then meta‐analyse using a Hartung‐Knapp‐Sidik‐Jonkman (random‐effects) model (Turner 2021a; Turner 2021b). We will report the prediction interval of the pooled effect sizes. We aim to pool both the level‐change and the slope‐change across the studies. For level‐change (immediate intervention effect), we will allow for a buffer time based on what is most commonly reported in studies. For slope‐change, we will use a homogenous timescale based on what is most commonly reported across studies. We also plan to conduct another type of analysis where we aim to re‐analyse the primary studies and then pool the effect sizes. We will do so in order to have both effect sizes for all studies (when, for instance, primary studies reported only the level change or the slope change) and also to potentially account for autocorrelation and correct the original analysis if the model structure used was inappropriate (i.e. we will not re‐analyse if the included study is already analysed using strong methods). If we have to re‐analyse the primary ITS studies, we will digitise the graphs of the time‐series data presented, if possible. If data are not available or reported for re‐analysis, we will not include them in a meta‐analysis but rather descriptively present the results, noting methodological concerns. For ITS studies with control series, we will calculate the effect estimates adjusted for any difference observed in the control series. We will assess quantitative heterogeneity by formally testing heterogeneity and assessing the proportion of total variability attributable to heterogeneity rather than sampling error (I² statistic).

For included cRCTs, we will take account of clustering by adjusting the raw data for the design effect by using the effective sample size approach (i.e. the original sample size is divided by the design effect, which is 1 + (average cluster size ‐ 1) x intracluster correlation coefficient).

For comparisons where meta‐analysis is not appropriate, we will choose an approach in alignment with the Cochrane Handbook (McKenzie 2022b), and we will report the results as per Synthesis Without Meta‐analysis (SWiM) guidelines (Campbell 2020). Our approaches for the different expected scenarios are as follows.

• Limited evidence for prespecified comparison (i.e. meta‐analysis is not possible because there are no studies or only one study): modify planned groupings or comparisons (to explore if meta‐analysis then becomes possible), with clear reporting of posthoc changes. If limited evidence still persists, we will summarise individual study results in a structured manner.

• Incomplete reporting of outcome or intervention effect (i.e. all numerical data required for meta‐analysis are neither available nor calculable from available statistics): combine P values, use vote counting based on the direction of effect or report the range of results depending on the data available.

• Major concerns about bias in evidence: summarise intervention effects using structured tables.

• Clinical and methodological diversity: modify planned groupings or comparisons (to explore if meta‐analysis then becomes possible), with clear reporting of posthoc changes, including the direction of effect (where we categorise intervention effect as "beneficial effect", "no effect" or "detrimental effect"). If diversity persists, we will present individual study intervention effects in a structured summary.

If no empirically based minimally important difference is available for the domain, we will determine clinical relevance through consensus between review team members. We will transparently report this and use this information to guide interpretation of the results.

Subgroup analysis and investigation of heterogeneity

When pooling for meta‐analysis, we will consider any methodological and clinical differences between studies (Deeks 2022). We will only conduct meta‐analyses when we consider it appropriate. In the event that we observe substantial or considerable heterogeneity (I² statistic ≥ 50%), we will further explore subgroup analysis as follows.

• Setting (rural, semirural, urban, hilly, forested areas, coastal, desert, etc., as defined by the primary study authors).

• Size of the community (< 100 households, ≥ 100 households).

• Type of community (tribal or indigenous versus not, as defined by the primary study authors).

• Integrated programme for environmental, zoonotic and other diseases versus programme focussing on snakebite alone (categorical: yes or no).

• Duration of follow‐up (short term: up to 12 months; long term: more than 12 months).

The type of setting, size of the community and type of community affect not only the nature of community interaction but also the ease of implementation; thus, they are important effect modifiers. They are also of relevance for policymakers and those designing and managing community‐based interventions. We will assess differences among subgroups by using the formal statistical test outlined in the Cochrane Handbook (Deeks 2022). We will conduct subgroup analyses only for primary outcomes.

Should meta‐analysis not be possible, we will explore heterogeneity by ordering tables within each comparison with the same parameters as mentioned for subgroup analysis.

Sensitivity analysis

 We plan, where possible, to conduct appropriate sensitivity analyses in order to explore the effects of the following:

• removing studies determined to be at high risk of bias; and

• the method of meta‐analysis, i.e. comparing results of random‐effects and fixed‐effect models (if required).

Summary of findings and assessment of the certainty of the evidence

We will rate the evidence for all outcomes based on the GRADE criteria. We will rate the certainty of evidence according to the following four levels (Schünemann 2021).

• High certainty: implying we are very confident that the true effect lies close to that of the effect estimate reported in the systematic review.

• Moderate certainty: implying that the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low certainty: implying that the true effect estimate may be substantially different from the effect estimate reported in the systematic review.

• Very low certainty: implying that the true effect is likely to be substantially different from the effect estimate reported in the systematic review, and we have very little confidence in its results.

The GRADE categorisation of the certainty of a body of evidence takes into consideration within‐study risk of bias (methodological quality), indirectness, inconsistency (heterogeneity), precision of effect estimates and risk of publication bias. At the start of the GRADE process, we will consider that all studies provide high‐certainty evidence, irrespective of study design, as per the ROBINS‐I tool for non‐randomised controlled trials, CBA studies and ITS studies (Sterne 2016). The ROBINS‐I tool is used to facilitate the assessment of the risk of bias due to lack of randomisation (Mckenzie 2022a). We will downgrade evidence by two points for indicators if most of the evidence is from non‐randomised controlled trials, CBA or ITS studies (Murad 2017). We will downgrade evidence by one point if the evidence is from a single study only. For RCTs, we will use our overall RoB 2 judgement to feed into the GRADE assessment as per RoB 2 recommendations. We will conduct separate GRADE assessment for randomised trials only to understand the effect of diversity of study designs. We will downgrade for risk of bias only if the majority of outcomes are from studies that are at high risk of bias. For inconsistency, we will consider the formal I² statistic. If there is substantial heterogeneity, we will downgrade by one point, and if there is considerable heterogeneity, we will downgrade by two points.

If data are not pooled, we will present GRADE assessment of overall direction of effect of the intervention as per the approach laid out by Murad 2017, which takes into consideration methodological limitations, indirectness, imprecision, inconsistency, likelihood of publication bias and appropriateness of certainty ratings. We will assess the level of certainty that the intervention had a "beneficial effect", "no effect" and "detrimental effect" (see Data synthesis), and we will report on the identified range of effect sizes for interpretation (Hultcrantz 2017).

Two review authors (SB and JJ) will independently rate the evidence, based on GRADE criteria, justifying reasons for downgrading or upgrading in the footnotes. We will resolve any discrepancy in GRADE assessment by consensus. We will prepare a separate summary of findings table for each comparison, including results of the primary outcomes and the 'unintended adverse consequences of the intervention' outcome using GRADEpro GDT (www.gradepro.org). For all other secondary outcomes, we will report the GRADE assessments in the text of the results section, without presenting separate summary of findings tables.