factors, such as income, likely increase as a direct result of the education channel. This means our estimate is the bundled effect of education, including changes in income and other mediators, that come with an exogenous increase in schooling. In line with both of these points, Table A4 in the Online Appendix shows a strong first stage on education, while no statistically significant effect on other variables which should not be affected by CSL changes and would not operate through the education channel, such as gender or country of birth.

Our estimation strategy instruments for years of education using a series of indicators for whether each compulsory schooling law binds for a given cohort of individuals. We construct these indicators cumulatively, that is, the estimated effect of the current law is the marginal effect of the law relative to the prior law. We run a two-stage least squares regression where the second stage regresses our climate outcomes on predicted education based on the applicable compulsory schooling laws, controlling for time trends and country fixed effects.<sup>6</sup> For a given individual _i_ we estimate: where _CSLicyr_ is a binary indicator of whether an individual _i_ in country _c_ is a member of a cohort _y_ affected by the reform _r_ , and is therefore in the treatment group.<sup>7</sup> We estimate effects across multiple countries and reforms, with _CSLicyr_ representing a vector of binary indicators across all included reforms _r_ . In Equation (1) we estimate the first stage of the effect of CSLs on educational attainment _Eicy_ . Since educational attainment has trended upward over time, we condition on a linear country-specific time trend _Ty_ .<sup>8</sup> We include country fixed effects _δc_ given we analyze results in a unified cross-country framework.<sup>9</sup> We interact time trends and country fixed effects to produce country-specific time trends. Standard errors are clustered at the country-law (e.g., the CSL) level, which is the level of treatment assignment. We estimate Equation (2), the

> 6We further Winsorize educational attainment at the 1 percent level, to minimize outlier bias and address spurious coding in the ESS data of extreme values. With Winsorization, we have a minimum of two years of schooling and a maximum of 22 years. Without Winsorization, 414 respondents or 0.11% of our sample report at least 30 years of education, which clearly does not map to our standard notion of years of full-time education, even for individuals with a PhD, motivating Winsorization. Otherwise, the maximum reported education is 60 years of schooling which exerts undue leverage on the rest of the data. Nevertheless, our results also hold when using raw years of education or topcoding at 20 years of education instead.

> 7This is defined based on each respondents’ birth year and starting school age to derive when the reform would first take effect for a given individual.

> 8Higher order time trends consume too much of the variation caused by the instrument, leaving insufficient identifying variation. We believe that the model with a quadratic time trend is misspecified, as evidenced by the fact that such a model yields _negative_ and highly statistically significant effects of education on household earnings, contradicting the economic consensus that education causally increases earnings (Angrist and Krueger, 1991; Ashenfelter and Rouse, 1998; Card, 2001). In contrast, our model with linear country-specific time trends produces estimates more consistent with the literature.

> 9Omitted indicators are the earliest laws in each country, such that the earliest laws take the value of the country fixed effect, and each subsequent law has a positive _β_ estimate as long as the reform i increased education relative to the country’s time trend.

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