problems with measurement and missing variables (Pattanayak and Pfaff, 2009). This makes it virtually impossible to attribute causality to the interventions.<sup>11</sup> So what are the key elements of today‘s standard for causal impact analysis required to assess the gender implications of interventions in the energy sector? First, the outcomes of interest – health, livelihoods, drudgery, time, employment, indoor air pollutants – would be measured for at least 4 sub-groups corresponding to women and men (separately) who are exposed to the policy and their control counterparts who are not exposed to the policy (program, project, intervention). Ideally, these measures would be before and after the intervention – i.e., before the sub-group used an improved cookstove or cleaner fuel. Second, each sub-group estimate would be derived from a relatively large sample of households and individuals so that we would have some degree of confidence in that estimate (i.e., the standard deviation would not be larger than the means).<sup>12</sup> Third, an experimental or quasi-experimental approach or rich multivariate regression would be used to address the likely endogeneity of the intervention.<sup>13</sup> Finally, in addition to being of sufficient size, the sample would have sufficient variation over policy-amenable variables (e.g., access to roads, quality of local institutions, mother‘s education) to support identification of why the program works under some conditions (or for some portion of the population) and not under others. Without the ability to identify the moderating influence of these factors that introduce heterogeneity, we cannot derive meaningful policy advice for scaling up and sustaining the impacts.

While all of the above elements are critical, we actually apply relatively inclusive screening criteria for the purposes of this report. Specifically, the preponderance of the evidence considered in this review comes from small sample studies, as long as they were large enough samples to support at least multivariate regression to control for key potential confounders. Thus, we include studies even if they had limitations with (a) design – not experimental or quasi-experimental, (b) single cross-section measures, instead of a before and after, and (c) proxy indicators of the direct welfare outcome – e.g., quantity of fuelwood collected, instead of time spent on fuelwood collection. Despite this approach and as presaged by the TOR, the empirical literature on the rigorous ―causal impacts‖ of household energy policies and programs is scattered, shallow, and patchy. The highest methodological standards are found in one-off academic ventures that may not be generalizable across all developing countries. There are very few studies with the ambition of the prospective RESPIRE trials in Guatemala (Smith et al.) or the careful retrospective quasi-experimental approaches to examine the household welfare impacts (Dinkelman, forthcoming; Edmonds, 2002; Mueller et al. 2011). Especially 11 The fields of environment and development, which is where household energy and gender concerns reside, are particularly lagging in the use of experimental and quasi-experimental designs, large samples and careful consideration of covariates to address the thorny but critical issue of causal impacts (Dinkleman, forthcoming; Duflo et al. 2008; Pattanayak et al., 2009; Peters 2009, Estache 2010, Bernard 2010). Ferraro and Pattanayak (2006) conjecture about attributes of resources, energy and environment that might cause this laggardness, but these arguments are no more compelling than in the field of disease control, education, poverty alleviation, and other sectors with ―soft‖ or amorphous outcomes, long ambiguous causal chains and impatient donors. Ravallion (2009) presents some alternative claims about political economy concerns and market failures in the supply of evaluations.

12 Most studies summarized in this review (except potentially those examining the impacts of electrification) are underpowered to detect gender differences; we have included these studies otherwise our empirical base would be virtually a null set. Future research should consider working with the large-scale household surveys such as DHS and LSMS with several thousand observations, some of which measure gender differentiated outcomes, in pursuing the kinds of impacts – health, time spent, forest products extracted – examined in this report.

13 Experiments use the power of randomization to ensure that potential confounders are balanced across intervention and control units and therefore any differences in the outcomes between the two can be attributed to the intervention. The quasiexperimental designs that use econometrics to compare intervention to ―controls‖ include: (a) matching—finding a control group that ―matches‖ important observable characteristics of the program group; (b) instrumental variables—using variables that are uncorrelated with the outcome but correlated with program participation to identify a control group; (c) difference-indifference—using repeated measures of the same individuals (units) to account for time-invariant differences between control and program groups; and (d) Heckman two-stage models—using covariates to predict who participates and using the predicted probabilities to correct bias when comparing controls to program groups (Ravallion 2007).

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