|Protocol Component ||Theorising the causal contrast*||Strengthening causal claims*|
• Does the study include a precise and detailed description of the population who have/will feasibly be exposed to the intervention, with special focus on the boundaries of the intervention which may be fuzzy and/or may not overlap with boundaries of (routine) data collection or risk of the outcome?|
• Is a definition and description of the eligibility of potential control populations to ensure independence and exclude spill-over effects included? 
• Are potential issues of collider bias  or other forms of selection bias considered?
|• Consider broadening out the eligibility criteria for multiple control groups that differ in some consequential way ; to include, for example, comparable groups or areas from other geographical locations for sensitivity analyses.|
• Are the intervention, the dose and treatment regimes, and what it aims to affect, including when and where it is introduced defined?|
• Has the baseline timepoint been defined?
• Has the control condition (including the potential for reactions even if intervention was not received) in the post-intervention period been defined, and/or has the counterfactual been defined?
• Does the study describe the plausibility of the Stable Unit Treatment Value Assumption (SUTVA)? 
• Consider the possibility of pre-implementation changes resulting from anticipating the intervention (for example changes in behaviour or reactions from industry ).|
• Consider additional other, likely earlier, baseline timepoints to exclude anticipation behaviour in sensitivity analyses.
• Given that the assignment procedure of the intervention is not controlled by the researcher, has the assignment rationale and procedures been reported in detail?|
Note that the intervention group can also be the whole population (e.g. if exposed to the intervention at a well-defined timepoint). Further note that, in the absence of a suitable control population defined by a temporal or spatial boundary, that the control group can be a synthetic counterfactual
• Has the plausibility of as-if randomization of the assignment been discussed?
• Has conditional exchangeability been formally evaluated for observed factors? Note that this cannot be done for unobserved factors and requires knowledge about exposure allocation procedures.
• Has the parallel trends assumption been assessed prior to the intervention implementation (when analysis based on timeseries data)?
• Has the plausibility of intervention and control groups remaining in their allocation group throughout the study been discussed?
• Consider whether partial control of assignment of intervention is possible.|
• Consider the selection of controls that are geographically locally to the intervention units
• Consider selection of intact control groups that are matched to intervention units based on pre-intervention measures of the outcome
• Consider control groups for whom measurement of the exposure, outcome, and covariates is performed similarly to that for the intervention group .
• Consider inclusion of (additional) control groups or use of synthetic counterfactuals to improve assessment of conditional exchangeability for observed and unobserved factors .
• Consider the inclusion of additional controls hypothesized to not be affected by the intervention (negative controls)
|Follow-up period||• Has the follow-up period, which starts prior to assignment of intervention to groups, includes assignment, and ends after a priori defined period post-intervention, been described?||• Consider different follow-up periods to assess evidence of pulse impacts (short-term temporal effect followed by regression to the mean)|
|Outcome(s)||• Does the study describe the outcome (or outcomes) of interest in detail, and does the description include a priori hypothesized individual-level or population-level parameters at a priori defined period post-intervention or cumulative/average outcomes from start of intervention until a priori defined period post-intervention?||
Consider evaluation of additional outcomes:|
• also hypothesised to be affected by intervention (positive control)
• hypothesised to be unaffected by intervention (negative control)
|Causal contrasts of interest||
• Has the causal contrast, or contrasts, to be evaluated been precisely defined?|
• Has the causal contrast of interest been specified as an ‘average-treatment-effect’ (ATE) for the population, or as ‘average-treatment-effect-treated’ (ATT) for self-selected interventions? 
• Consider, and report, whether Natural Experiment Study enables the estimation of intention-to-treat effects and/or per-protocol effects (although in natural experiments the latter may be rarely available)|
• Consider additional causal contrasts, for example in subgroups
• Is there a pre-specified analytic plan?|
• Is the measure of the result specified as a relative and/or absolute measure?
• Is the measure of the result specified as the difference between post-intervention minus pre-intervention outcome of interest in intervention group and post-intervention minus pre-intervention outcome of interest in control group?
• Has the statistical methodology used to calculate the impact or effect of the event or intervention been described in sufficient detail to allow replication?
• Consider the inclusion of temporal falsification analyses by choosing different, randomly assigned, implementation times for the intervention|
• Consider the inclusion of spatial falsification analyses using different combinations of units, irrespective of true assignments
• Consider improving causal claims by methodological triangulation using different statistical methods [35, 36].