Evolution vs. Creationism in the Classroom: The Lasting Effects of Science Education^*

Abstract

Anti-scientific attitudes can impose substantial costs on societies. Can schools be an important agent in mitigating the propagation of such attitudes? This article investigates the effect of the content of science education on anti-scientific attitudes, knowledge, and choices. The analysis exploits staggered reforms that reduce or expand the coverage of evolution theory in U.S. state science education standards. I compare adjacent student cohorts in models with state and cohort fixed effects. There are three main results. First, expanded evolution coverage increases students’ knowledge about evolution. Second, the reforms translate into greater evolution belief in adulthood, but do not crowd out religiosity or affect political attitudes. Third, the reforms affect high-stakes life decisions, namely, the probability of working in life sciences.

I. Introduction

Anti-scientific attitudes can impose substantial costs on public health, the environment, and the economy. Misinformation about the danger of COVID-19 and a lack of trust in scientists have undermined compliance with social distancing measures and vaccination recommendations, prolonging the pandemic (Bursztyn et al. 2020; Algan et al. 2021; Brzezinski et al. 2021; Jin et al. 2021). Climate change denial has reduced the support for policies cutting greenhouse gas emissions, contributing to environmental and economic damage (Akter, Bennett, and Ward 2012; Linden et al. 2015). The rejection of evolution theory has been used to justify white supremacy and racism in the United States (Marks 2012) and has contributed to anti-scientific agricultural policies and associated food shortages in the former Soviet Union (Graham 2016).¹ While there is broad understanding of the societal costs of anti-scientific attitudes, evidence on its determinants is surprisingly scant despite the relevance for effective policy responses.

This article isolates the content of science education in high school as one determinant of anti-scientific attitudes that is directly subject to policy makers.² To study whether the content of science education has a lasting impact on individuals beyond attitudinal outcomes, the study also analyzes how it affects scientific knowledge and life decisions. Specifically, I estimate the causal effect of students’ exposure to the teaching of evolution theory in science education on (i) their knowledge about evolution at the end of high school, (ii) their belief in evolution in adulthood, and (iii) the probability that they work in life sciences.

The focus is on evolution theory because of its fundamental role in science and its controversy in the population and the education system. Evolution can scientifically explain the existence of all species, including our own. The American Association for the Advancement of Science (2021) states that “the foundation of all life sciences is biological evolution.” Ninety-eight percent of its members express support for the statement that humans have evolved over time (Pew Research Center 2015). In contrast, evolution is a highly charged topic among the U.S. population with only 65% agreeing that humans have evolved over time. Prior to World War II and up to the present day, this controversy has been reflected in heated debates and legal battles on whether evolution is supposed to be taught in schools.³ Teachers and school districts have been convicted for not following the education standards’ stance on evolution. Even today, there is substantial variation across U.S. states and over time in how evolution is covered in education standards.

To isolate exogenous variation in students’ exposure to the teaching of evolution, this article exploits staggered state-level reforms of the coverage of evolution in U.S. State Science Education Standards (Science Standards). In the study period from 2000 until 2009, 15 states reduced the coverage of evolution in their education standards, and 22 states expanded it. I argue that the political and institutional processes leading to these reforms, particularly the predetermined timing of gubernatorial elections in combination with the tenure of members of state Boards of Education, create idiosyncrasies in the determination of the precise reform years. This setting allows for the estimation of causal effects in two-way fixed-effects models with state and cohort fixed effects, overcoming the identification problem that the content of science education is generally correlated with scientific, religious, and political attitudes of the students’ environment, which independently affect student outcomes.

Beyond the theoretical argument that the reform timing is determined by institutional idiosyncrasies, my empirical setup explicitly accounts for a range of endogeneity concerns by comparing adjacent cohorts around sharp reforms of the Science Standards. Specifically, the performed two-way fixed-effects estimations can rule out as confounding factors (i) time-invariant state-specific differences (such as education levels), (ii) cohort-specific national differences (such as national changes in attitudes across time), (iii) time-varying state-specific shocks that affect adjacent cohorts similarly (such as natural disasters or state-level political or religious shocks that do not differentially affect children of different cohorts), and (iv) time-varying state-specific shocks that affect adjacent cohorts differentially but smoothly (such as state-specific trends in science skepticism or science prestige), in a robustness test that includes state-specific time trends. I account for potential biases in staggered two-way fixed effects designs from time-varying treatment effects (Callaway and Sant’Anna 2021). To conduct the analyses, I link state-level data on the evolution coverage in Science Standards with three individual-level data sets.

First, this article shows that the evolution coverage in Science Standards affects what students learn about evolution in school. Specifically, I use the National Assessment of Educational Progress (NAEP) to demonstrate that students exposed to a more comprehensive evolution coverage in high school are more likely to correctly answer knowledge questions on evolution by the end of high school. This finding exemplifies how the content of education standards can foster scientific knowledge, an outcome of direct economic importance given its effects on innovation, earnings, and economic growth in the long run (Lucas 1988; Barro 2001; Hanushek and Woessmann 2008, 2012).⁴

Second, this study demonstrates that the evaluated reforms have lasting effects on attitudes. To that end, I make use of the General Social Survey (GSS) to show that evolution teaching affects the probability of believing in the concept of evolution in adulthood. There are no effects on religiosity and political attitudes. Being exposed to a comprehensive evolution coverage in the education standards in high school compared to no evolution coverage increases evolution belief in adulthood by 57% of the sample mean, corresponding to a persuasion rate of 79% (DellaVigna and Gentzkow 2010). Effects are largest for mainline Protestants. This analysis underscores that reform effects persist long after students have left high school. This result exemplifies how science education can promote scientific attitudes, which can be directly relevant for improving public health, the environment, and the economy (Brzezinski et al. 2021; Martinez-Bravo and Stegmann 2022).

Third, I show that the evaluated reforms affect high-stakes choices, namely, occupational choice. It seems plausible that if people know more about and believe more in a particular theory, they are also more interested in working in the field that was founded on it. After all, skills and interest are important determinants of occupational choice (Speer 2017). Specifically, I hypothesize that learning about evolution, the fundamental theory of life sciences, affects the probability of working in life sciences in adulthood. Using the American Community Survey (ACS), I demonstrate that high school exposure to a comprehensive evolution coverage in the education standards compared with no evolution coverage increases the probability of working in life sciences in adulthood by 23% of the sample mean. This effect mostly comes from the subfield of biology, the subject in which evolution is typically taught. This finding exemplifies how science education can attract future STEM workers, which not only raises wages at the individual level (Hastings, Neilson, and Zimmerman 2013; Kirkeboen, Leuven, and Mogstad 2016; Deming and Noray 2020) but also has wider economic consequences through fostering innovation, technological change, labor productivity, and economic growth (Griliches 1992; Jones 1995; Kerr and Lincoln 2010; Peri, Shih, and Sparber 2015). In all three analyses, I consistently find that effects are larger in absolute terms for the subgroup of reforms that reduce the evolution coverage compared with the subgroup that expands it.

This article provides evidence on how learning about evolution theory—the fundamental theory of the evolution of life that explains the existence of humans—actually shapes humans. Specifically, I show that evolution teaching not only affects the related knowledge of students but also translates into evolution belief in adulthood. This implies that scientific beliefs can be “taught” in school and persist into adulthood. This finding complements seminal research on the effects of non–science-related school curricula reforms on financial decision making (Bernheim, Garrett, and Maki 2001), identity (Clots-Figueras and Masella 2013), labor market participation and employment (Fuchs-Schündeln and Masella 2016; Costa-Font, García-Hombrados, and Nicińska 2024), political and economic preferences (Cantoni and Yuchtman 2013; Cantoni et al. 2017), civic values (Bandiera et al. 2019), and religiosity (Bazzi, Hilmy, and Marx 2020).⁵

This study further demonstrates that attitudinal changes induced by science school curricula reforms translate into high-stakes choices of individuals. Specifically, the finding on occupational choice enhances our understanding of how to increase the share of STEM graduates, which is a policy goal with widespread support in many societies.⁶ Occupational sorting is influenced by demand-side factors such as expected earnings and nonpecuniary job benefits (Wiswall and Zafar 2018; Arcidiacono et al. 2020), perceived ability (Stinebrickner and Stinebrickner 2014; Arcidiacono et al. 2016), and heterogeneous tastes (Wiswall and Zafar 2015). Supply-side factors such as grading policies (Butcher, McEwan, and Weerapana 2014), admissions systems (Bordon and Fu 2015), affirmative action policies (Arcidiacono, Aucejo, and Hotz 2016), and the provision of role models (Porter and Serra 2020) can also play a role; see Altonji, Arcidiacono, and Maurel (2016) for an overview. I demonstrate that the content of science education in high school can be an effective policy tool to attract STEM graduates.

This article speaks to the emerging literature on the determinants of religiosity (Iannaccone 1998; Iyer 2016; McCleary and Barro 2019). Finding null effects on religious outcomes demonstrates that expanding the scientific content of science education neither reduces the belief in nor the belonging to a religion.⁷ This is true despite the fact that being raised as Evangelical is a large negative predictor of evolution belief. While a number of studies have found a positive relationship between education and religiosity (McCleary and Barro 2006a, 2006b; Glaeser and Sacerdote 2008; Meyersson 2014), other research suggests that education can decrease religiosity (Hungerman 2014; Becker, Nagler, and Woessmann 2017). In the specific setting of evolution teaching in the United States, religiosity is not crowded out.

Finally, this work contributes to the literature on the effects of the content of education on students’ knowledge. While there is broad understanding about the effects of topic-specific instruction time (Cortes and Goodman 2014), minimum high school course requirements (Goodman 2019), advanced placement courses (Conger et al. 2021), and the interaction of curricula and internet penetration (Sen and Tucker 2022), this article shows that the content of education standards affects the knowledge of students on the topic in question in the intended direction. The effects of the content of education standards last until adulthood. In sum, this study demonstrates that high school curricula exert a lifetime influence on students.

The article proceeds as follows. Section II outlines the institutional background of the teaching of evolution. Section III provides information on the data measuring the coverage of evolution in Science Standards and the micro data sets. Section IV describes the identification strategy. Section V presents the results. Section VI discusses robustness tests. Section VII concludes.

II. Institutional Background

II.A. The Battle for Teaching Evolution in U.S. Public Schools

For at least a century, the teaching of evolution in public schools has been a contested issue in the United States. Before World War I, evolution teaching was rare (Beale 1941). In the 1920s, more than 20 states considered bills to ban the teaching of evolution. Among other states, such a bill became law in Tennessee, resulting in the famous “monkey trial” where a biology teacher was convicted for having taught evolution.⁸ This law was overturned in 1967, and similar decisions followed in other states. In 1987, another law requiring that equal time must be spent on teaching evolution and creation was ruled unconstitutional by the U.S. Supreme Court. In short, the legislative and adjudicative decisions of the second half of the twentieth century have paved the way for evolution to be taught in public schools (Moore, Jensen, and Hatch 2003b). Still, there continues to be substantial variation across states and years in the twenty-first century, as the subsequent analysis of the evolution coverage in Science Standards demonstrates.

II.B. State Science Education Standards

In general, Science Standards define the scientific knowledge and skills that students are supposed to master in a grade in public schools. The scientific teaching a student is ultimately exposed to also depends on local school curricula; the selection of textbooks (Adukia et al. 2023); the knowledge, ability and ideology of teachers; testing formats; and other factors. However, Science Standards form the basis of many of these factors. For instance, they affect how local curricula and teachers’ lesson plans are written (Lerner 2000b). Furthermore, science textbooks are arranged to match the content laid out in Science Standards. Statewide standardized exams often directly test the content set out in the Science Standards. Lerner (2000b, ix) summarizes that Science Standards “are meant to serve as the frame to which everything else is attached, the desired outcome that drives countless other decisions about how best to attain it.” With regard to evolution, 88% of a nationwide representative sample of U.S. public high school biology teachers state that they focus heavily on what students need to know to meet Science Standards when teaching evolution, see Online Appendix Figure A.1.

Science Standards cover many topics. However, the reforms evaluated herein primarily concentrate on evolution. In Online Appendix A.1, I present evidence from a text analysis of the Science Standards, demonstrating that while the reforms modify the coverage of many topics, the treatment of evolution is altered to a significantly greater extent.

II.C. The Adoption Process of Reforms of Science Standards

How do reforms of Science Standards come into existence? In each state, they are decided by majority vote of the members of the state Board of Education. The selection process for these members differs across states. In some states, members are appointed by the governor, sometimes with the consent of the legislature (e.g., in California and Florida). In other states, members are elected by the public (e.g., in the District of Columbia and Texas). A few states combine these selection mechanisms by appointing some members and electing others (e.g., Louisiana and Ohio). Before the final vote of the Board of Education, Science Standards are typically drafted by advisory committees. These consist of a panel of teachers and other stakeholders such as parents, scientists, and religious representatives. Moreover, the Boards of Education hold public hearings.

This process implies that these reforms happening at some point is not random. Instead, it reflects changing views, expressed either by the election of a governor or by direct election of the Board of Education members.

However, the exact reform year in a given state can be regarded as as good as random due to institutional idiosyncrasies. If beliefs in evolution change among the population in a certain year, it will take an arbitrary number of years until this results in a reform of Science Standards. In states where the Board of Education is appointed by the governor, the year of a reform crucially depends on the governor's year of election, as determined by the legislation period lasting four years in general. In states where the Board of Education is directly elected, the reform year depends on the elections, which typically take place in a staggered manner across districts and years. Further idiosyncrasies are induced by the fact that the tenure of board members differs across states, which can last up to nine years as in West Virginia. Even after a new majority in the Board of Education is in power, drafting, hearing, and voting on new standards can take months or years.⁹ In sum, there may be a great number of years between a shock and a reform of the Science Standards. However, it can also be small if election dates and tenure expiration of a marginal board member occur shortly after a shock. I identify from this arguably exogenous reform timing.

Online Appendix A.2 provides anecdotal evidence on the political processes leading to reforms in Florida and Texas. While Florida expanded the evolution coverage in 2008, Texas reduced it in 2009; neither reform following a partisan change in government.

Online Appendix A.3 provides quantitative evidence on the exogenous timing of the reforms. I regress state-by-year characteristics, such as (i) unemployment rate, partisan composition, and school resources, and (ii) Google search frequencies of keywords specific to evolution and creationism, on the evolution coverage in the Science Standards, in models with state and year fixed effects. All estimates are insignificant and close to zero. This suggests that the timing of the reforms is independent of (i) economic, political, and educational conditions, and (ii) the interest of the population in evolution and creationism.

II.D. The Implementation of Reforms of Science Standards

After new Science Standards are adopted, their implementation in the classroom tends to be rather swift. In general, widely publicized lawsuits convicting school districts for not implementing the teaching of evolution as outlined in Science Standards contribute to a fast implementation.¹⁰ Newspaper articles and policy reports suggest that the content of textbooks, lesson plans, and standardized testing questions was changed because of the reforms, while there is no indication of new teachers being hired.¹¹ In Florida in 2008, for example, school districts were supposed to adjust their lessons by comprehensively including evolution as outlined in the newly adopted Science Standard within one year. Evolution was required to become part of standardized testing in Florida from 2012 onward. In the 2009 Texas reform, the evolution coverage of the new Science Standard had to be in textbooks from 2011 onward. These dates are likely the upper end of the implementation timeline, as in reality teachers have to implement many changes earlier to allow for a smooth transition of classroom activities before the deadline. Still, some people coded as exposed to the post-reform treatment may have been exposed to some pre-reform treatment. This dilutes the treatment-control contrast and implies that any effects should be interpreted as lower-bound estimates.

III. Data

III.A. Coding of Reforms of Science Standards

To measure the coverage of evolution in Science Standards, I make use of the “evolution score” provided by Lerner (2000a) and Mead and Mates (2009). The evolution score is a composite index based on an evaluation of whether the word “evolution” appears in a Science Standard; of the respective coverages of biological, human, geological, and cosmological evolution; and of the connection of the different aspects of evolution. The absence of creationist jargon and creationist disclaimers in textbooks is also taken into account. The evolution score is defined between 0 and 1, with 0.01 increments. An evolution score of zero indicates no or a creationist coverage of evolution, and a score of one indicates a very comprehensive coverage of evolution. Notably, the creationist jargon in all standards evaluated in this article is never openly religious, which would be unconstitutional. However, there is large variation in the emphasis of (alleged) weaknesses and critique of evolution theory, creating or removing scope for teachers wishing to teach creationist content.¹²

The evolution score is available for all states for 2000 and 2009, provided by Lerner (2000a) and Mead and Mates (2009), respectively. They also provide information on the evolution score’s year of reform for each state between 2000 and 2009 (if there was any reform). If more than one reform took place between 2000 and 2009 in a given state, there is information on the last reform.¹³ The evolution score serves as a treatment variable in this article. When merging it with individual-level data sets, each individual is defined as being exposed to the evolution score from 2000 if she started high school before the reform year in her state and to the evolution score from 2009 if she started high school in the year of the reform or later in her state. The high school entry year is the pertinent year, as most of the teaching on evolution takes place at the beginning of high school.¹⁴

To illustrate the identifying variation, Figure I depicts the state-level evolution score difference between 2000 and 2009.¹⁵ The evolution score decreased in 15 states (implying a negative evolution-score difference) and increased in 22 states (implying a positive evolution-score difference) between 2000 and 2009. In the remaining 14 states, it remained unchanged. The states with the largest evolution-score decreases are Connecticut, Louisiana, and Texas. The largest evolution-score increases are found in Kansas, Mississippi, and Florida. By construction, the changes partly depend on the baseline level, in the sense that Science Standards covering evolution very comprehensively in 2000 cannot expand the coverage by much by 2009, and vice versa. However, by identifying from changes within states, I control for fixed differences between states. Overall, the evolution-score changes are fairly well spread over the United States, with each census region having at least one state in which the evolution coverage became less comprehensive, more comprehensive, and remained unchanged, respectively.

Figure I

Map of Evolution-Score Difference between 2000 and 2009

The map depicts the evolution-score difference, which I define as the evolution score of 2009 minus the evolution score of 2000. A positive (negative) difference implies an increase (decrease) in the evolution score between 2000 and 2009, as indicated by blue plain coloring (orange striped coloring). White plain coloring indicates no change of the evolution score between 2000 and 2009. The years reported below the two-letter state codes mark the respective reform years. A list of the evolution-score differences and reform years underlying this map is provided in Online Appendix Table A.XI. Data sources: Lerner (2000b), Mead and Mates (2009).

III.B. Micro Data

This subsection describes the three micro-level data sets used in this article. Each repeated cross-sectional data set is standardized and hence comparable across states and cohorts, making it suitable for analyses with state and cohort fixed effects. In all three data sets, I keep students in the sample who start high school after 1990 and before 2010. Thereby, I balance temporal proximity to the reform years and having sufficient years to estimate pre-trends and fixed effects credibly (and with statistical power in general).¹⁶ This approach also prevents identification from the adoption of the Next Generation Science Standards, which started in 2013.

1. NAEP (Evolution Knowledge in School)

To estimate the effect of students’ exposure to the teaching of evolution in high school on their knowledge about evolution by the end of high school, I link the evolution score with the restricted-use individual-level National Assessment of Educational Progress (NAEP) (U.S. Department of Education 2020). NAEP is a standardized student achievement test, measuring the knowledge of U.S. students in various subjects since 1990. I use the NAEP test for science in grade 12 because it contains questions on evolution. Students are coded as exposed to the Science Standard in place in the year and state of their high school entry, assuming they started high school three years before taking the test in grade 12 in the same state.

The main outcome variable, evolution knowledge, is defined as the share of correctly answered questions on evolution. The nine categories of scientific knowledge on topics other than evolution include reproduction, climate change, or the universe, and are defined analogously. In addition, the NAEP student surveys provide rich student-level control variables, such as subsidized lunch status or home possessions, to approximate the socioeconomic status.

The main sample consists of more than 14,000 students who were asked at least one question on evolution. It contains only public school students, as Science Standards have never been binding for private schools. The average evolution score equals 0.65, implying that the sampled students were on average exposed to a “satisfactory” evolution coverage.¹⁷ The mean of the main outcome variable evolution knowledge equals 0.32. The fact that on average, not even a third of the questions on evolution are answered correctly underscores the questions’ difficulty. Online Appendix A.4.1 provides descriptive statistics, correlations, sample questions, and further information.

2. GSS (Evolution Belief in Adulthood)

To estimate the effect of students’ exposure to the teaching of evolution in high school on their belief in evolution in adulthood, I link the evolution score with the restricted-use individual-level General Social Survey (GSS) (Smith et al. 2017). The GSS is a biennial cross-sectional survey that monitors societal change by interviewing a nationally representative sample of adults in the United States since 1972. Since 2006, respondents have been asked about their belief in evolution. The GSS also provides the state of residence at age 16 and the birth year. I assume that respondents started high school in this state at age 14 and merge the evolution score for this state-year combination accordingly. Hence, I can link individuals’ belief in evolution in adulthood to the evolution coverage of the Science Standard they were exposed to as students, even if they moved to other states after finishing school.

The main outcome variable evolution belief is based on the question “Human beings, as we know them today, developed from earlier species of animals. Is that true or false?”¹⁸ The corresponding indicator variable is set to one if the answer “true” was given and zero if any other answer option was reported such as “false,” “don’t know,” or “no answer.” The GSS asks a broad range of questions on other scientific topics and on religious and political attitudes. Variables capturing dimensions of the childhood environment serve as controls, including the religion a respondent was raised in.

The GSS is sampled from the entire U.S. adult population, irrespective of type of school attendance. This makes it impossible to differentiate between public and private school attendance. Instead, one can estimate effects net of endogenous sorting across school types, including homeschooling. The estimation sample of individuals who were asked the question on evolution belief contains more than 1,800 individuals; 58% of this sample believe in evolution, which largely corresponds to other surveys at the time (Pew Research Center 2009). Further descriptive statistics, raw correlations, and data background are provided in Online Appendix A.4.2.¹⁹

3. ACS (Occupational Choice)

To estimate the effect of students’ exposure to the teaching of evolution in high school on their probability of working in life sciences during adulthood, I link the evolution score with the individual-level IPUMS American Community Survey (ACS) (Ruggles et al. 2020). The ACS is a large-scale demographic survey that draws from a national random sample of the U.S. population. Responding and providing correct information is required by U.S. law. The ACS contains detailed information on the respondents’ occupational field. It also elicits the state and year of birth. I assume that students start high school in this state at age 14 and accordingly merge the evolution score for this state-year combination.

Given that evolution is a fundamental theory of life sciences, the occupational field of primary interest in this study is life sciences. The main outcome variable, working in life sciences, is coded as an indicator variable equal to one if the respondent works in life sciences and zero otherwise. It can be divided into the subfields biology, agriculture and food, conservation and forestry, and medical and other.

Like in the GSS, the ACS is sampled from the entire U.S. population, which also includes individuals who went to private school and homeschoolers. The estimation sample of individuals who are older than 18 years (i.e., who typically completed secondary education) consists of more than 6 million individuals. Further information, including descriptive statistics, is provided in Online Appendix A.4.3.

IV. Identification Strategy

The analyses presented in this article are based on the following two-way fixed-effects (TWFE) model. The model exploits the different timing of reforms of the evolution coverage in Science Standards across states and the fact that some of the reforms reduced the coverage of evolution, while others extended it, and a third group of states did not reform the evolution coverage. It compares outcomes of cohorts who went to high school in states where the evolution coverage was reformed with previous cohorts from the same states prior to reforms, relative to how outcomes of these cohorts changed in states that did not reform at the time, after accounting for fixed differences between states and birth cohorts. The baseline TWFE model is specified as follows:

$$\begin{eqnarray} Y_{istu}= \beta \cdot Evolution\_Score_{st} + \gamma \cdot \mathbf {X_{i}} + \delta _{s} + \lambda _{t} + \theta _{u} + \epsilon _{istu}, \end{eqnarray}$$

(1)

where |$Y_{istu}$| is the outcome of interest of individual i, who started high school in state s and year t, and completed the test or survey in year u. The treatment variable |$Evolution\_Score_{st}$| measures the intensity of the evolution coverage in the Science Standard in state s and year t. Hence, the treatment status is based on the evolution score in force in the state and year in which an individual enters high school. |$\beta$| is the parameter of interest capturing the effect on the outcome of being exposed to a very comprehensive coverage of evolution (⁠|$Evolution\_Score_{st}$| = 1) as compared to being exposed to no or a creationist coverage of evolution (⁠|$Evolution\_Score_{st}$| = 0). The vector |$\mathbf {X_{i}}$| contains individual-level control variables. State fixed effects |$\delta _{s}$|⁠, birth cohort/high school entry cohort fixed effects |$\lambda _{t}$|⁠, test/survey year fixed effects |$\theta _{u}$|⁠, and an error term complete the model.²⁰ Standard errors are clustered at the state level to account for the potential correlation of error terms across cohorts within states (Abadie et al. 2023; Athey and Imbens 2022).

The key identifying assumptions are that in the absence of the evolution coverage reforms, the outcomes of students attending high school in different states would have evolved along parallel trends, and that treatment effects are homogeneous over time.

The TWFE model allows me to rule out various concerns about the ability to estimate causal effects of the evolution coverage in Science Standards. First, one might be concerned that state-level differences in scientific, religious, or political attitudes are correlated with the evolution coverage in Science Standards and affect scientific knowledge, beliefs, and occupational choice. The state fixed effects absorb all differences in outcomes that are constant between states. In addition, one might be worried that national trends, such as attitudinal trends on scientific, religious, or political topics, might erroneously appear as reform effects. To counter this concern, the cohort fixed effects eliminate all national differences between cohorts.

Moreover, the state fixed effects rule out time-varying state-specific shocks as long as they affect adjacent cohorts equally. This is as the empirical setup exploits cross-cohort variation within a narrow time window around the evolution curriculum reforms and identifies from reforms that affect adjacent cohorts in different ways. Specifically, a reform adopted in a given state and calendar year primarily affects the new high school entry cohort (and younger cohorts in the following years when they start high school), see Section III.A.²¹ I argue that many potential shocks that one might typically be concerned about (such as state-specific church scandals or shocks that affect the prestige of science) do not discontinuously affect different high school cohorts.²² Furthermore, a robustness specification with state-specific linear and quadratic time trends accounts for time-varying state-specific shocks that affect adjacent cohorts differentially but smoothly. This specification is particularly demanding in terms of statistical power, as reform effects are only detectable as “jumps” from the cross-cohort trend. For example, this specification accounts for changes in trust in science that could develop differently in the various states and change smoothly across cohorts.

Because the evolution-score treatment variable is continuous, the parallel-trends assumption has to hold in its strong form. The average potential outcomes for individuals exposed to a reform of the evolution coverage have to be the same at each level of evolution coverage. This excludes selection into a particular level of dosage (evolution coverage) (Callaway, Goodman-Bacon, and Sant’Anna 2021). Following Cook et al. (2023), I probe the plausibility of this assumption by testing for correlations between the evolution score and covariates. Specifically, I regress the evolution score on predetermined observables and find little evidence of systematic correlations.²³ I also show in robustness analyses that reform effects hold when transforming the continuous evolution-score variable into binary variables. Moreover, I note (i) that active selection into exposure to a different state Science Standards requires moving across states, which seems unnecessarily costly in most cases as students can simply switch to a private school (or do homeschooling),²⁴ and (ii) that the institutional idiosyncrasies determining the exact reform timing, as discussed in Section II, make it difficult to proactively select into certain evolution coverages. Last, I probe robustness on a smaller sample without individuals belonging to the top and bottom 20% of the evolution-score distribution. Following an idea by Marie and Zwiers (2022), this approach alleviates concerns about selection into evolution coverage, as individuals from the extremes of the evolution coverage distribution, with arguably the most diverse potential outcomes and the strongest incentive to move, are excluded from the sample.

To further probe the plausibility of the parallel-trends assumption, I estimate an event study version of equation (1), in which the reform of the evolution coverage in Science Standards in a given state and year is referred to as the “event.” This approach now views every reform as a discrete event and ignores differences in the intensity of the reform as indicated by the evolution score used in the baseline TWFE model, as follows:

$$\begin{eqnarray} \quad Y_{istu}= \sum _{k=-7}^{5} 1(t_{is}=t_{s} + k) \beta _{k} + \gamma \times X_{istu} + \delta _{s} + \lambda _{t} + \theta _{u} + \epsilon _{istu}. \end{eqnarray}$$

(2)

I estimate the effect of exposure to a reform of the evolution coverage in Science Standards in year |$t_{s}$| on outcomes of students starting high school k years before and after the evolution coverage reform, as captured by the parameter vector |$\beta _{k}$|⁠. All event-study regressions are estimated by grouping two years together in one bin to smooth the number of observations across bins as not all micro data are collected in every year (see Section III).²⁵ This model allows us to examine nonlinear pre-reform trends in outcome variables and disentangle effects that directly occur at the time of the reforms from those that phase in gradually after the reform. Note that the event-study estimations yield changes in outcomes induced by the average reform. This requires running the event-study models separately for the sets of states that reduce and expand the evolution coverage, respectively, because joint event-study models would cancel out effects from opposing reforms. In each set of states, the regression coefficients can be interpreted as changes in outcomes induced by the average reform of the evolution coverage in that set.

Even in the absence of confounding trends or shocks, consistent estimation of reform effects requires homogeneity in treatment effects. The treatment effect from the baseline TWFE model is a weighted average of all possible 2 × 2 difference-in-differences comparisons between treated and untreated groups as well as groups treated at different points in time (Goodman-Bacon 2021). In settings with staggered treatment timing, time-varying treatment effects can bias results away from the true effect if already-treated students act as controls for later-treated students, which also applies to the event studies (Sun and Abraham 2021).

To test whether my TWFE OLS event-study regressions are immune to this bias, I run the CS estimator (Callaway and Sant’Anna 2021), which excludes those 2 × 2 difference-in-differences comparisons in which already-treated students act as controls from the sample. Because I run the event-study models separately for the sets of states that reduce and expand the evolution coverage without never-treated states, the CS estimator uses not-yet-treated students as controls. To alleviate concerns about the multicollinearity of dynamic treatment effects and time fixed effects (Borusyak, Jaravel, and Spiess forthcoming), I bin both endpoints, which allows for separate identification even when using not-yet-treated units only (Schmidheiny and Siegloch 2023). In robustness analyses I also add a set of never-treated states to the sample.²⁶

V. Results

In three steps, this section shows that the evolution coverage in Science Standards affects students' knowledge about evolution, the belief in evolution in adulthood, and the probability of working in life sciences.

V.A. Evolution Knowledge in School

1. Baseline Estimates

To assess reform effects on student knowledge about evolution, I regress the share of questions on evolution answered correctly in the 12th-grade NAEP science test on the evolution coverage in Science Standards and different sets of control variables, following equation (1).

As shown in Table I, Panel A, column (1), the raw correlation is positive. This could imply that a comprehensive coverage of evolution increases students’ evolution knowledge (reform effect), that evolution knowledge raises the probability of states adopting Science Standards that cover evolution comprehensively (e.g., because students might not accept creationist content; reverse causality), or that third variables such as socioeconomic status affect both (omitted variable bias). To isolate reform effects, I add control variables in columns (2)–(4). The full model in column (4) is the preferred specification because it exploits the idiosyncratic timing of reforms of Science Standards as a source of arguably exogenous variation. I find that being exposed to an evolution score of one (very comprehensive coverage of evolution) compared with an evolution score of zero (no or a creationist coverage of evolution) increases the share of questions on evolution answered correctly by 6.5 percentage points (p-value = .005). Given that, on average, students answer 32% of the questions on evolution correctly, the reported effect amounts to 20% of the sample mean.

TABLE I

The Effects of Evolution Coverage in Science Standards

	Controls: No	Controls: Yes	Controls: No	Controls: Yes
	State FE: No	State FE: No	State FE: Yes	State FE: Yes
	Cohort FE: No	Cohort FE: No	Cohort FE: Yes	Cohort FE: Yes
	(1)	(2)	(3)	(4)
Panel A: Outcome: Evolution knowledge in school
Evolution score	0.039**	0.035***	0.074**	0.065***
	(0.018)	(0.012)	(0.028)	(0.022)
Mean of dep. var.	0.32	0.32	0.32	0.32
Std. dev. of dep. var.	0.42	0.42	0.42	0.42
Adj. R-squared	0.001	0.035	0.015	0.041
Observations	14,080	14,080	14,080	14,080
Panel B: Outcome: Evolution belief in adulthood
Evolution score	0.122***	0.084**	0.235*	0.333***
	(0.042)	(0.036)	(0.125)	(0.107)
Mean of dep. var.	0.58	0.58	0.58	0.58
Std. dev. of dep. var.	0.49	0.49	0.49	0.49
Adj. R-squared	0.006	0.088	0.038	0.107
Observations	1,801	1,801	1,801	1,801
Panel C: Outcome: Working in life sciences
Evolution score	0.039**	0.035**	0.035**	0.035**
	(0.018)	(0.013)	(0.014)	(0.014)
Mean of dep. var.	0.15	0.15	0.15	0.15
Std. dev. of dep. var.	3.84	3.84	3.84	3.84
Adj. R-squared	0.000	0.000	0.000	0.001
Observations	6,460,650	6,460,650	6,460,650	6,460,650

Notes. The table shows TWFE OLS coefficients and standard errors clustered at the state level in parentheses from estimating equation (1), for different sets of control variables and fixed effects as indicated in the column header. Each entry is from a separate regression model. Panel A, dependent variable: the share of questions about evolution that are answered correctly. Controls: indicator variables for gender, races/ethnicities, subsidized lunch status, home possessions (separate indicator variables for computer and books), birth month, test session, and test year. Data source: U.S. Department of Education, National Center for Education Statistics, National Assessment of Educational Progress (NAEP), 1996–2009 Science Assessments for Grade 12. Panel B, dependent variable: belief in evolution (“Human beings, as we know them today, developed from earlier species of animals—Is that true or false?,” indicator variable, 1 = true, 0 = false; don’t know). Controls: indicator variables for gender, races/ethnicities, parents born abroad, parental education, having lived with parents in adolescence, raised in a rural area, religion raised in (indicator variables for mainline Protestantism, evangelical Protestantism, Catholicism, no religion, Judaism, Buddhism, Hinduism, other Eastern, Islam, orthodox Christian, Christian, Native American, inter/nondenominational, other religion), and survey year. Data source: General Social Survey. Panel C, dependent variable: probability of working in life sciences (multiplied by 100 for interpretability). Controls: indicator variables for gender, races/ethnicities, and survey year. Data source: American Community Survey. * p < .10, ** p < .05, *** p < .01.

2. Event-Study Graphs

To test for parallel trends and to study the dynamics of treatment effects, I conduct event-study regressions following equation (2).

Figure II, Panel A, depicts the event-study graph of evolution knowledge in school for the set of states where the reform reduces the evolution coverage in Science Standards. The TWFE OLS coefficients of pre-reform years are all close to zero: the largest pre-reform point estimate is smaller than 0.018, which is less than a third of the smallest post-reform coefficient. All pre-reform coefficients are individually and jointly insignificant, even at the 10% level (F-test of joint significance: F = 0.27, p = .844). These findings are consistent with the idiosyncratic timing of the reforms and the parallel-trends assumption. After the reform, we observe immediate, stable, and significant changes in evolution knowledge. The second post-reform coefficient is the largest and amounts to 9 percentage points (p-value = .025).

Figure II

Event-Study Graphs for the Effect of Evolution Coverage in Science Standards on Evolution Knowledge in School

The figure shows point estimates and 95% confidence intervals from estimating equation (2). Dependent variable: share of questions about evolution answered correctly. In Panel A, the outcome variable is multiplied by −1 (inverted outcome due to inverted reform, to allow for comparability across results). TWFE OLS is shown in blue (color version available online) with circle markers. Controls: indicator variables for gender, races/ethnicities, subsidized lunch status, home possessions (separate indicator variables for computer and books), birth month, test session, and fixed effects for state, cohort, and test year. CS estimates (Callaway and Sant’Anna 2021) are depicted in red with diamond markers, using doubly robust inverse probability weighting and not-yet-treated observations as controls. Numbers on the horizontal axis refer to the final year of respective two-year bins; that is, −1 = last two years prior to treatment. Inference: clustering at the state level. Data source: National Assessment of Educational Progress.

To account for heterogeneous treatment effects in the presence of staggered treatment timing, I complement the OLS estimates with CS estimates (Callaway and Sant’Anna 2021). The CS pre-reform and post-reform coefficients are similar to the OLS coefficients in terms of size and significance, which implies that the OLS results are immune to bias from time-varying treatment effects. Specifically, all CS pre-reform coefficients are individually and jointly insignificant, and all post-reform coefficients are individually and jointly significant (the last two individual coefficients at the 1% level). The corresponding simple aggregate CS estimates based on the discrete reforms are also mostly significant (see Online Appendix Table A.IV).²⁷

Figure II, Panel B, depicts the event-study graph of evolution knowledge in school for the set of states where the reform expands the evolution coverage in Science Standards. I can formally reject the significance of pre-reform coefficients and document some significant post-reform coefficients. However, the reform effects are more pronounced for the states that reduce the evolution coverage (this pattern consistently reemerges in the analyses on evolution belief and occupational choice). Why is this the case? Plausible reasons include the disproportionate threat of lawsuits against teachers who do not adhere to Science Standards after evolution was removed from the standards, given the long history of anti-evolution advocacy groups litigating against teachers who “illegally” teach evolution. Another plausible reason is the disproportionate media attention that such reforms typically garner, which may heighten the awareness of teachers and other stakeholders and contribute to a swift implementation.²⁸

3. Further Classroom Outcomes

Beyond reform effects on evolution knowledge, I present supporting analyses on a range of other classroom outcomes related to evolution and biology. Using teacher survey data, I show suggestive evidence that high school biology teachers who are exposed to a more comprehensive coverage of evolution in the Science Standards spend more time teaching evolution (see Online Appendix A.5). Other teaching strategies including the expression of teachers’ personal opinions on the validity of evolution remain unaffected.

Moreover, I demonstrate that the reforms do not affect the probability of students’ selection of high school biology courses, see Online Appendix Table A.V.

V.B. Evolution Belief in Adulthood

The second analysis shows that teaching evolution has a lasting impact on attitudes in adulthood, shedding light on the persistence of effects of scientific educational content. At the same time, it examines whether the effect on evolution knowledge translates into neutral settings during which the scientifically correct answer is not encouraged. It could well be that students exposed to evolution content are both willing and able to answer science exam questions correctly to gain points in an exam but are not convinced of the correctness of evolution theory.

1. Baseline Estimates

Table I, Panel B, presents the GSS results from regressions of evolution belief in adulthood on the evolution score in high school, conditional on different sets of control variables. The evolution score estimate of the full model presented in column (4) shows that individuals who were exposed to an evolution score of one, as compared to an evolution score of zero, are 33.3 percentage points more likely to believe in evolution in adulthood (p-value = .003). This effect amounts to 57% of the sample mean, making it larger than the corresponding effect on evolution knowledge.

To benchmark the effect size relative to other determinants of attitudes, I calculate persuasion rates (DellaVigna and Gentzkow 2010). I define the persuasion rate induced by a reform changing the evolution score from zero to one as the average treatment effect on evolution belief divided by the share of students who do not believe in evolution in the entire sample.²⁹ The corresponding persuasion rate equals 79%. This is larger than the persuasion rates Cantoni et al. (2017) report for a Chinese school textbook reform on a range of outcomes.³⁰ It is also on the upper end of the persuasion rate distribution of media, which includes rates from 3% to 8% (DellaVigna and Kaplan 2007) to 65% (Enikolopov, Petrova, and Zhuravskaya 2011) for different media, settings, and outcomes. Reasons for the large persuasion rate of evolution teaching may include the large amount of time dedicated to evolution teaching,³¹ the credibility of the persuader,³² and the difficulty of avoiding exposure.³³

In terms of effect heterogeneities, I observe significantly larger reform effects on evolution beliefs among individuals raised as mainline Protestants compared to those raised nonreligiously, as well as among Blacks compared with Whites and among those raised in urban areas compared to rural areas. These heterogeneity results, along with others from the analyses on evolution knowledge and occupational choice, are discussed in more detail in Online Appendix A.6.

2. Event-Study Graphs

The event-study graphs for reform effects on evolution belief are presented in Figure III.

Figure III

Event-Study Graphs for the Effect of Evolution Coverage in Science Standards on Evolution Belief in Adulthood

The figure shows point estimates and 95% confidence intervals from estimating equation (2). Dependent variable: belief in evolution (“Human beings, as we know them today, developed from earlier species of animals—Is that true or false?”, indicator variable, 1 = true, 0 = false; don’t know). In Panel A, the outcome variable is multiplied by −1 (inverted outcome due to inverted reform, to allow for comparability across results). TWFE OLS estimates are depicted in blue with circle markers. Controls: fixed effects for state, cohort, and survey year. CS estimates (Callaway and Sant’Anna 2021) are depicted in red with diamond markers, using doubly robust inverse probability weighting and not-yet-treated observations as controls. Numbers on the horizontal axis refer to the final year of respective two-year bins; that is, −1 = the last two years prior to treatment. Inference: clustering at the state level. Data source: General Social Survey.

For the set of states reducing the evolution coverage shown in Figure III, Panel A, the pre-reform TWFE OLS coefficients are close to zero and individually and jointly insignificant, even at the 10% level (F-test of joint significance: F = 0.75, p = .540). After the reform, I observe immediate and significant changes in evolution belief. The first post-reform coefficient is the largest; it amounts to 31 percentage points (p-value = .017). The CS results are similar to the OLS results, both in terms of size and significance, for the pre- and post-reform coefficients. These findings are consistent with the idiosyncratic timing of the reforms and the parallel-trends assumption, and with the absence of contamination by time-varying treatment effects of the OLS. As before, reform effects are more pronounced for the states that reduce evolution coverage (Panel A) compared with the states that expand it (Panel B).

V.C. Occupational Choice

The third analysis reveals that teaching evolution translates into real-world high-stakes outcomes beyond attitudinal outcomes. Specifically, I focus on occupational choice as one high-stakes life decision in which an individual’s attitudes, values, and beliefs may be revealed. We know from the literature that skills and interest are important determinants of occupational choice (Speer 2017). If education standards are able to change students’ knowledge about and belief in a given theory, they could also change the desire to work in the area built on this theory. I hypothesize that exposure to evolution theory (and hence to the fundamental scientific theory about the existence of life) affects individuals’ probability of choosing to work in life sciences.

1. Baseline Estimates

Table I, Panel C shows that being exposed to a more comprehensive teaching of evolution in school increases the probability of working in life sciences during adulthood. The full model presented in column (4) demonstrates that individuals who were exposed to an evolution score of one, as compared to an evolution score of zero, are 0.035 percentage points more likely to work in life sciences as adults (p-value = .016). This effect is numerically small; however, it amounts to 23% of the sample mean. In absolute terms, it corresponds to more than 90,000 workers (approx. 260,000,000 adults in the United States × 0.00035). Because the life science industry faces a severe shortage of skilled workers, an addition of 90,000 workers would yield a substantial contribution.³⁴ This is also of wider economic relevance, given the significance of the life science industry for growth, innovation, employment, and trade.³⁵ Not least, the COVID-19 pandemic underscored the importance of the life science sector and its innovations (Barro 2022).

Subfield analysis reveals that the overall effect on the life sciences is mostly coming from the subfield of biology, see Figure IV.

Figure IV

The Effect of Evolution Coverage in Science Standards on the Probability of Working in Life Sciences, by Subfields of Life Sciences

The figure shows TWFE OLS coefficients and 95% confidence intervals of the effect of evolution coverage in Science Standards on the probability of working in life sciences (multiplied by 100 for interpretability), by subfields of life sciences as indicated along the vertical axis from estimating equation (1). Sample sizes of subfields are in parentheses (raw value). Controls: indicator variables for gender and races/ethnicities, and fixed effects for state, cohort, and survey year. Inference: clustering at the state level. Data source: American Community Survey.

The effect on biology is large in relative size, amounting to more than 39% of the sample mean (p-value = .001). It is significantly different from the effects on agriculture and food as well as conservation and forestry (with reform effects on all non-biology subfields themselves being indistinguishable from zero). This subgroup pattern underpins that it is indeed the evolution teaching that drives reform effects, in line with the fundamental relevance of evolution for biology,³⁶ and given that evolution is being taught in biology.

2. Event-Study Graphs

Figure V depicts the event-study graph of the probability of working in life sciences.

Figure V

Event-Study Graphs for the Effect of Evolution Coverage in Science Standards on the Probability of Working in Life Sciences

The figure shows point estimates and 95% confidence intervals from estimating equation (2). Dependent variable: the probability of working in life sciences (multiplied by 100 for interpretability). In Panel A, the outcome variable is multiplied by inverted outcome due to inverted reform, to allow for comparability across results). TWFE OLS estimates are depicted in blue with circle markers. Controls: indicator variables for gender and races/ethnicities, and fixed effects for state, cohort, and survey year. CS estimates (Callaway and Sant’Anna 2021) are depicted in red with diamond markers, using doubly-robust inverse probability weighting and not-yet-treated observations as controls. Numbers on the horizontal axis refer to the final year of respective two-year bins; that is, −1 = the last two years prior to treatment. Inference: clustering at the state level. Data source: American Community Survey.

For the states reducing evolution coverage depicted in Figure V, Panel A, the pre-reform TWFE OLS coefficients are close to zero as well as individually and jointly insignificant, even at the 10% level (F-test of joint significance: F = 0.17, p = .912). After the reform, I observe changes in the probability of working in life sciences that peak at the second post-reform coefficient of 0.052 percentage points (p-value = .008). We repeatedly observe in this article that reform effects do not reach their peak immediately after reform adoption (with the OLS event study on evolution belief for the set of states reducing evolution coverage shown in Figure III, Panel A, being an exception to this pattern). In general, this pattern aligns with reports of slight delays in the implementation of reforms, likely attributable to adjustments in lesson plans, curricula, textbooks, and standardized testing, as discussed in Section II. Also, note that in Figure V, Panel A, the CS results are similar to the OLS results in terms of size and significance. As before, reform effects are more pronounced for the states that reduce the evolution coverage (Panel A) compared with the states that expand it (Panel B).

VI. Robustness

This section shows additional analyses on placebo reforms, other outcome variables, event-study figures, and a range of further checks including estimations that control for state-specific trends and that run on a set of states with closely elected governors.

VI.A. Placebo Tests

As an alternative way of inference, I randomly reshuffle the reform years across the different reforming states. For the analysis on evolution knowledge, the density plot of the baseline TWFE OLS placebo coefficients based on 1,000 permutations shows that the baseline estimated reform effect on evolution knowledge is larger than the 95th percentile of the distribution of the 1,000 placebo reform effects; see Online Appendix Figure A.IV. The baseline effect on evolution belief is also larger than the 95th percentile of the placebo reform effect distribution (see Online Appendix Figure A.V), and the baseline effect on the probability of working in life sciences is larger than the 90th percentile of the placebo reform effect distribution (see Online Appendix Figure A.VI). These findings suggest that all three main effects of this article are unlikely to be spurious.

VI.B. Other Outcomes

Beyond evolution knowledge and belief, I estimate reform effects on knowledge of non-evolution scientific topics at the end of high school and attitudes about non-evolution scientific, religious, and political topics in adulthood. In principle, these outcomes could interact with each other and react to the reforms.

As is visible in column (2) of Online Appendix Table A.VI, there is no effect of the evolution coverage in Science Standards on the average student knowledge in the non-evolution scientific topics (I reject the equality of coefficients with evolution knowledge at the 10% level; p-value = .058). The coefficients for the nine non-evolution topics are all numerically smaller than that of evolution, but I only reject the equality of coefficients of evolution and “motion” at the 10% level (p-value = .086), and “energy” at the 5% level (p-value = .034). As is visible in Online Appendix Tables A.VII, A.VIII, A.IX, and A.X, respectively, there is no effect of the reforms on non-evolution scientific, religious, and political outcomes.³⁷ In sum, the reform effects are neatly tied to the topic of evolution in independent data sets and outcomes therein.

How could the null finding on religious outcomes arise? For some subgroups, such as those raised as Evangelicals and nonreligious, there is no reform effect on evolution belief. For those, we do not expect to observe a “crowding out” of religious beliefs. But what about the other subgroups? For some of those, evolution may not be contradictory to their religious beliefs, for example, if they follow “theistic evolution” (the belief that God does not interfere with the laws of nature after creation). For some others where evolution and religion contradict, compartmentalization, a mechanism whereby a person separates conflicting beliefs from each other, could be at work. Furthermore, religious beliefs may be harder to change by the school curriculum compared with evolution beliefs, for example, due to the relatively early exposure to religiosity during childhood (Huber 2007), the connection of religious activities to social groups (Levy and Razin 2012), and the social pressure to maintain religious beliefs (Edgell, Gerteis, and Hartmann 2006; Wiles 2014). Finally, if the impact of evolution teaching on religiosity manifests at a later stage in life compared with its effect on evolution belief, my data structure may not be capable of detecting religiosity effects. (Note that I do not have data on older postreform cohorts, as the evaluated reforms occurred between 2000 and 2009).

VI.C. Event-Study Graphs

I assess the sensitivity of the event-study estimates to violations of parallel trends. Following Rambachan and Roth (2023), I compare the confidence intervals of my main event-study estimates from Figures II, III, and V with confidence intervals that account for the precision of pre-trends and allow for per period deviations from linear trends up to parameter M. These confidence sets correct for the unintuitive property of standard pre-trend testing that zero pre-trends are less likely to be rejected if they are estimated less precisely (Roth 2022; Roth et al. 2023).

For the states reducing the evolution coverage shown in Panel A of Online Appendix Figures A.VII, A.VIII, and A.IX, the 95% confidence intervals become smaller and exclude zero when assuming linear trends (M = 0) in all three analyses. Confidence intervals gradually increase with larger deviations from linearity, and exclude zero for values of M up until 0.002, 0.11, and 0.005, respectively. These thresholds correspond to 8%, 94%, and 33% of the standard error of the respective coefficient of interest. This indicates that the finding on belief in evolution is most robust against low power of pre-trends and nonlinear violations of parallel trends, followed by the result on the probability of working in life sciences, while the finding on knowledge of evolution only demonstrates robustness against relatively smooth nonlinear trends. Note that these estimates are conservative because I do not impose any restriction on the sign or monotonicity of the differential trends. In contrast, reform effects for the states expanding the evolution coverage are not robust to nonlinear violations of parallel trends; see Panel B of Online Appendix Figures A.VII, A.VIII, and A.IX.

Moreover, I probe the robustness of the main event-study graphs to adding of a set of never-treated states to the sample. The event-study graphs do not change meaningfully; see Online Appendix Figures A.X, A.XI, and A.XII.³⁸

VI.D. Further Robustness

Table II covers a range of further robustness checks, including specifications that control for state-specific trends and that are estimated on a subsample of closely elected governors.

TABLE II

Robustness of the Effect of Evolution Coverage in Science Standards

	Close elections	Control: governor’s party	State-specific time trends	Dosage treatment	Only one reform event	Only large states	Only states with std. text	Sample start: 1995	Sample start: 2000	Probit	Outcome coding variation 1	Outcome coding variation 2
	(1)	(2)	(3)	(4)	(5)	(6)	(7)	(8)	(9)	(10)	(11)	(12)
Panel A: Outcome: Evolution knowledge in school
Evolution score	0.093***	0.066***	0.043	0.042	0.089***	0.056**	0.078***	0.048***	0.037	0.076**	0.058**	n/a
	(0.022)	(0.022)	(0.065)	(0.034)	(0.029)	(0.022)	(0.025)	(0.017)	(0.026)	(0.032)	(0.022)
Equality test w/	.265	.798	.533	.220	.314	.621	.340	.052	.014	.494	.153
base. coef. (p-value)
Panel B: Outcome: Evolution belief in adulthood
Evolution score	0.605***	0.332***	0.625***	0.177**	0.394**	0.433***	0.322**	0.257**	0.313*	0.329**	0.288**	0.426***
	(0.188)	(0.111)	(0.218)	(0.070)	(0.163)	(0.117)	(0.131)	(0.116)	(0.171)	(0.130)	(0.138)	(0.145)
Equality test w/	.072	.954	.042	.461	.582	.158	.893	.029	.852	.792	.323	.107
base. coef. (p-value)
Panel C: Outcome: Working in life sciences
Evolution score	0.039	0.036**	0.025	0.034**	0.031	0.040**	0.057***	0.036***	0.029**	0.035	n/a	n/a
	(0.025)	(0.014)	(0.025)	(0.016)	(0.021)	(0.017)	(0.016)	(0.013)	(0.012)	(0.026)
Equality test w/	.848	.731	.439	.963	.724	.663	.080	.982	.385	.984
base. coef. (p-value)

Notes. The table shows TWFE OLS coefficients and standard errors clustered at the state level in parentheses from estimating equation (1), for different robustness checks indicated in the column headers as follows. Column (1) sample only includes states where the members of the state Board of Education are appointed by the governor, and where the governor in office at the time of the reform was voted into office with a margin of less than 10 percentage points compared with the runner-up. Column (2) regressions control for the political affiliation of the governor ruling in the state and year of the student’s high school entry. Column (3) regressions include state-specific linear and quadratic time trends. Column (4) main evolution score is replaced by a weighted average of pre- and post-reform evolution scores, with weights corresponding to the number of pre- and post-reform high school years. Column (5) sample only includes individuals from states that had only one reform event between 2000 and 2009, see Online Appendix Table A.XI for more details. Column (6) sample only includes individuals from the 20 states with the largest population. Column (7) sample only includes individuals from states for which the text of the Science Standards is available for text analysis implemented in Online Appendix A.1. Column (8) sample only includes individuals who started high school after 1994. Column (9) sample only includes individuals who started high school after 1999. Column (10) coefficient reports the average marginal treatment effect of a probit specification. Column (11), Panel A: recoding of dependent variable: the share of questions about evolution answered correctly, indicator variable, 1 = true, 0 = false, missing = omitted/not reached/off-task/etc. (dependent on the question type); Panel B: sample excludes individuals whose dependent variable question on evolution replaces the words “human beings” with the word “elephants”; Panel C: n/a. Column (12), Panel A: n/a; Panel B: recoding of dependent variable: belief in evolution (“Human beings, as we know them today, developed from earlier species of animals—Is that true or false?”, indicator variable, 1 = true, 0 = false; missing = don’t know); Panel C: n/a. Each entry is from a separate regression model. “Equality test w/ base. coef. (p-value)” refers to the p-value of a test for equality between the coefficient reported in the given column and the corresponding baseline coefficient presented in Table I, column (4). Panel A: dependent variable: the share of questions about evolution answered correctly. Controls: indicator variables for gender, races/ethnicities, subsidized lunch status, home possessions (separate indicator variables for computer and books), birth month, test session, and fixed effects for state, cohort, and test year. Data source: U.S. Department of Education, National Center for Education Statistics, National Assessment of Educational Progress (NAEP), 1996–2009 Science Assessments for Grade 12. Panel B: Dependent variable: belief in evolution (“Human beings, as we know them today, developed from earlier species of animals—Is that true or false?”, indicator variable, 1 = true, 0 = false; don’t know). Controls: indicator variables for gender, races/ethnicities, parents born abroad, parental education, having lived with parents in adolescence, raised in a rural area, religion raised in (indicator variables for mainline Protestantism, Evangelical Protestantism, Catholicism, no religion, Judaism, Buddhism, Hinduism, other Eastern, Islam, orthodox Christian, Christian, Native American, inter/nondenominational, other religion), and fixed effects for state, cohort, and survey year. Data source: General Social Survey. Panel C: Dependent variable: probability of working in life sciences (multiplied by 100 for interpretability). Controls: indicator variables for gender and races/ethnicities, and fixed effects for state, cohort, and survey year. Data source: American Community Survey. Online Appendix Tables A.XII, A.XIII, and A.XIV provide further statistics of each regression including the mean and standard deviation of the dependent variable, adjusted R-squared, and the number of observations. * p < .10, ** p < .05, *** p < .01.

More information about these robustness checks, as well as other checks that account for multiple-hypothesis testing or which define treatment as a binary variable, is presented in Online Appendix A.7.1. Note that some of the point estimates are quite sensitive to the inclusion of control variables, which I mostly attribute to the relatively small number of observations in each state-cohort cell relative to the number of control variables added to some specifications (for example, compare the main results in Table I, columns (3) and (4), or the robustness check with state-specific time trends in Table II, column (3), to the main results in Table I, column (4)). The robustness test on the set of states with closely elected governors is particularly demanding because it reduces the sample size by around two-thirds, but reform effects are still robust (with the effects on the probability of working in life science being estimated less precisely, but yielding a similar point estimate).

Online Appendix A.7.2 assesses student movements between public schools, private schools, and homeschooling due to the reforms, and finds no evidence of meaningful changes to the sample composition by school type.

VII. Conclusion

This article shows that school curricula have lasting effects on students by affecting their knowledge, attitudes, and choices. To demonstrate this, I focus on the teaching of evolution theory in the United States. Exploiting institutional idiosyncrasies in the timing of reforms of the evolution coverage in Science Education Standards, I show that the teaching of evolution affects (i) students’ knowledge about evolution, (ii) their belief in evolution in adulthood, and (iii) the probability of working in the life sciences. To illustrate effect sizes, I calculate changes in outcomes that one would expect to observe if all states adopted Science Standards with a highly comprehensive evolution coverage relative to the average coverage in the sample. Naive linear extrapolation of the estimation results suggests that the evolution belief in the U.S. population would increase by 20% of the sample mean in such a scenario. Analogously, the number of adults working in life sciences (biology) would increase by 8% (13%) of the sample mean.

The three sets of results provide empirical support to important arguments raised in the policy debate about evolution teaching. As suggested by proponents of evolution teaching, the results indicate that teaching evolution has wider economic and societal benefits given the positive effects of scientific knowledge (Hanushek and Woessmann 2008), scientific attitudes (Brzezinski et al. 2021), and working in STEM occupations (Peri, Shih, and Sparber 2015) on individual and societal outcomes (although ultimate welfare implications also depend on other factors, such as substitution patterns). Furthermore, the results speak against a major concern brought forward by some skeptics of evolution teaching, namely, that teaching evolution might undermine students’ religiosity. The null findings on various religious outcomes imply that neither believing in nor belonging to a religion (Barro and McCleary 2003; McCleary and Barro 2019) is crowded out by teaching evolution. The same is true for political attitudes.

This study shows that the content of education standards is relevant for individuals in the short and long run. This conclusion challenges the notion that education standards have no meaningful effect on students. It has been argued that in reality, there is limited scope for education standards to affect teaching due to the dominance of other factors, such as the teachers’ own ideology (Moore, Jensen, and Hatch 2003a; Loveless 2021). Still, legal pressures on school districts to follow education standards, and the reflection of education standards in textbooks and standardized testing questions have arguably incentivized teachers to follow education standards. The analyses presented here provide empirical evidence that education standards indeed affect what students learn.

More broadly, this article shows that the content of school curricula and instruction shapes students over the long term. This is true even for a topic like evolution that is highly charged in political and societal debates. Despite its fundamental relevance for and overwhelming acceptance in science, people have strong partisan views on it. These views are likely to be determined by a multitude of factors. Still, what schools teach has long-lasting effects on individuals’ fundamental views and translates into high-stakes choices.

Beyond the reforms evaluated in this article, the findings indicate potential relevance of other education policies that increase the time teachers spend on teaching evolution, such as the adoption of the Next Generation Science Standards. Beyond the United States, the findings may also have a bearing for other countries where teaching evolution is controversial.³⁹ Beyond the topic of evolution, the findings of this study might also be relevant more broadly for further topics of science teaching, such as vaccinations, climate change, or trust in science in general. It is up to future research to study this explicitly.

Data Availability

The programs underlying this article are available in Arold (2024) in the Harvard Dataverse, https://doi.org/10.7910/DVN/HYLZUO.

Footnotes

*

I am very grateful to Elliott Ash, Ludger Woessmann, and Davide Cantoni for their support throughout this project. I also thank Robert Barro and Lawrence Katz, four anonymous referees, and Karun Adusumilli, Barbara Biasi, Luca Braghieri, Florian Ederer, Sarah Eichmeyer, Sergio Galletta, Eleonora Guarnieri, Eric Hanushek, Martina Magli, Rachel McCleary, Markus Nagler, Nathan Nunn, Paul Peterson, Matteo Sandi, M. Danish Shakeel, Claudia Steinwender, Joseph Stiglitz, Gregory Veramendi, Martin West, Brian Wheaton, Scott Williamson, Larissa Zierow, as well as the participants of the seminar in Religion and Political Economy (Harvard), the Graduate Workshop on Political Economy (Harvard), seminars at University of Cambridge, UC Riverside, ETH Zurich, UZH Zurich, LMU Munich, Mannheim, briq Institute Bonn, Luxembourg, Nuremberg, and the Lindau Nobel Laureate Meeting 2022, ASSA/AEA Annual Meeting 2022, ASREC Conference 2022, ifo-WZB EffEE Conference 2022, ESPE Conference 2021, EALE/SOLE/AASLE World Conference 2020, German Economic Association (VfS) Meeting 2020, and the AEFP Conference 2020. Clementine Abed Meraim, Shufan Ma, Caroline Michler, and Sophia Stutzmann provided excellent research assistance. I thank Paul Peterson, Antonio Wendland, and the Program on Education Policy and Governance at Harvard University for their hospitality while writing parts of this article. I gratefully acknowledge financial support by the DAAD through a one-year scholarship for doctoral students funding my stay at Harvard University. Financial support by the Leibniz Competition (SAW 2019) is also gratefully acknowledged. Some of the data used in this analysis are derived from Sensitive Data Files of the GSS, obtained under special contractual arrangements designed to protect the anonymity of respondents. These data are not available from the author. Persons interested in obtaining GSS Sensitive Data Files should contact the GSS at [email protected]. Similar requirements apply to NAEP. All errors are my own.

1.

The rejection of evolution theory by Trofim Lysenko, then president of the Academy of Agricultural Sciences of the Soviet Union and leading agricultural adviser to Joseph Stalin, has been held responsible for prolonging Soviet food shortages in the 1930s (Lysenkoism) (Joravsky 1962).

2.

In general, attitudes are shaped by a multitude of factors, many of which are rather shielded in the private domain. An extensive literature on the formation of attitudes and beliefs has emphasized the impact of intergenerational transmission in families (Bisin and Verdier 2001; Guiso, Sapienza, and Zingales 2008; Tabellini 2008). Other determinants include peers and social networks (Sacerdote 2001; Bailey et al. 2020), the media (Martin and Yurukoglu 2017), and political systems (Alesina and Fuchs-Schündeln 2007).

3.

For example, the New York Times published a report on controversies of the previous decade with the headline “Questioning Evolution: The Push to Change Science Class” (Haberman 2017).

4.

At the correlational level, Biasi and Ma (2022) show a direct link between higher education curricula and innovation.

5.

Scientific attitudes are arguably more challenging to change, as they pertain to the acceptance of knowledge rather than opinions. Note that the only scientific attitude addressed in the previous papers, environmental attitudes in Cantoni et al. (2017), did not change due to the curriculum reform (in contrast to political and economic attitudes).

6.

In the United States, increasing the number of STEM graduates is a central policy goal of the federal government’s strategic plan for STEM education 2018–2023 (National Science and Technology Council 2018). Similarly, the EU aims to increase the number of STEM graduates as one of its 12 policy goals of the European Skills Agenda 2020–2025 (European Commission 2020).

7.

The distinction of religious outcomes between believing and belonging follows Barro and McCleary (2003) who find in cross-country analyses that believing stimulates economic growth, while belonging tends to reduce economic growth at given levels of religious beliefs.

8.

This decision was later overturned on a technicality, see Larson (1999).

9.

In some cases, there are also idiosyncrasies induced by spillovers, in the sense that Science Standards reforms of one state affect the teaching in other states. This occurs, for example, because textbooks used in smaller states may follow Science Standards reforms of larger states. Building on this point, I show that reform effects also hold in a subsample of large states only, see Table II, column (6).

10.

For example, a lawsuit that received national attention was Kitzmiller v. Dover Area School District in 2005. The Dover Area School District had required biology teachers to teach intelligent design (a form of creationism attributing the creation of the world to an intelligent designer) as an alternative to evolution. This requirement contradicted the content of the Science Standard in force at the time and was ruled unconstitutional. Specifically, the verdict prohibited the district from requiring teachers to “denigrate or disparage the scientific theory of evolution, and from requiring teachers to refer to a religious, alternative theory known as intelligent design” (Kitzmiller v. Dover Area School District, 400 F. Supp. 2d 707, M.D. Pa. 2005).

11.

The likelihood of discussing evolution versus creationism in the household could be affected as well and would be a mechanism of the main results to the extent that it is specific to the treated cohorts.

12.

In 2000, Kansas received an out-of-range score of −0.18, as “it is a special case, unique in the extremity of its exclusion of evolution from statewide science standards” (Lerner 2000b, 16). In this article, I change this evolution score from −0.18 to 0 for ease of interpretability. All results using the original score of −0.18 for Kansas instead of 0 do not differ meaningfully (results available on request). Iowa had no Science Standards in 2000, which is coded as missing. The District of Columbia is treated as a state throughout this article. The evolution score was originally defined between 0 and 100, but I rescale it by dividing it by 100, again for ease of interpretability. More information about the scoring scheme is provided in Lerner (2000b, 10–17). I also estimate the effects of the different components of the evolution score separately on the relevant outcomes, but find that no component stands out in particular (these results are available on request).

13.

This implies that reforms before the respective last reform are not taken into account in the analyses. In theory, ignoring these prior reforms merely creates attenuation bias as long as these prior reforms are uncorrelated with the timing of the last reform in a given state. To explicitly test for this, I perform a robustness check restricting the sample to students from states for which careful examination of academic articles, legal documents, and state education websites indicates that they only had one reform between 2000 and 2009; see Table II, column (5).

14.

Although reforms of Science Standards are generally applicable to all cohorts from the year of adoption onward, the change in evolution coverage typically only affects the high school entry cohorts. This is because the standard high school curriculum typically features biology (the subject in which evolution is being taught) in the first year of high school. To account for the possibility that evolution could also be taught in other years, I run a dosage specification. Here, the main evolution score is replaced by the weighted average of the pre- and post-reform evolution scores, with the weights corresponding to the number of pre- and post-reform high school years; see Table II, column (4).

15.

Online Appendix Figure A.II also depicts the evolution score levels in 2000 and 2009.

16.

The results of this article do not depend on this specific sample cut; see Table II, columns (8) and (9).

17.

Lerner (2000b) classifies evolution scores between 0.60 and 0.79 as “satisfactory.”

18.

The words “human beings” are replaced by the word “elephants” for 10% of the questions on evolution belief. Table II, Panel B, column (11) shows that the results are robust to dropping those from the sample.

19.

Building on Barro (2022), I show for example that state-level averages of evolution belief and the evolution score correlate positively with COVID vaccination rates and negatively with Trump voting; see Online Appendix Tables A.I and A.II.

20.

In the analyses using NAEP, cohort and year fixed effects generally coincide as each cohort was examined in grade 12.

21.

To the extent that evolution is also being taught in higher grade levels, the difference in exposure to the teaching of evolution between pre- and post-reform cohorts is overstated in my coding. Hence, I interpret my results as lower-bound estimates because parts of the cohorts coded as exposed to pre-reform Science Standards would be partially treated by post-reform Science Standards in this scenario.

22.

See also Cantoni et al. (2017, 363), who exploit a cohort-specific introduction of a curriculum reform in models with state and cohort fixed effects and note: “This method of introducing the new curriculum considerably reduces concerns about omitted variables, as many time-varying, province-specific shocks seem unlikely to have very different effects across adjacent cohorts of students.”

23.

Each row of Online Appendix Figure A.III displays the estimate from a separate regression of the evolution score on the covariate defined along the vertical axis and survey-year fixed effects. The estimates show little correlation overall. The one notable exception is mainline Protestants, which, however, has the opposite sign as compared to other religious groups, such as Evangelicals and Catholics.

24.

The main regression estimates using the GSS and ACS are based on a sample of students from public school, private schools, and homeschoolers that are net of spurious selection across school types. For NAEP, the results hold on a sample of public and private schools, see column (4) of Online Appendix Table A.III, and there is no NAEP test for homeschoolers.

25.

Longer post-reform time horizons are not available in the micro data. Effects are estimated relative to the bin directly before the reform, that is, the bin that covers the years [−2, −1]. The bins at the beginning (end) of the domain additionally include the years before (after) the domain’s starting (ending) year. In event studies with GSS data, the individual-level covariates are dropped as the number of observations is particularly small relative to the number of covariates and estimated coefficients.

26.

I add the four never-treated states Nebraska, Oregon, Utah, and Wisconsin to the sample of states that reduce (or expand) the evolution coverage. These four states are selected to be largely representative for the United States and to be large enough to allow for separate identification of dynamic treatment effects and time fixed effects.

27.

They are stronger for the set of reforms that reduce the evolution coverage compared with those that expand it and stronger for the smaller sample without individuals belonging to the top 20% or bottom 20% of the evolution score (Marie and Zwiers 2022).

28.

For example, the reforms that reduce the evolution coverage in Texas and Louisiana received heightened media attention. For Texas, journalists published numerous local and national newspaper articles, for example in the New York Times (McKinley 2009), and even the film The Revisionaries (Gold 2012). For Louisiana, journalists published numerous newspaper articles as well, for example in the New York Times (Nossiter 2009), and teacher organizations (including the National Association of Biology Teachers) alongside 78 Nobel Prize laureates endorsed the repeal of this reform, further contributing to its visibility.

29.

Another definition of the persuasion rate would require dividing the treatment effect of the average reform by the share of individuals who do not believe in evolution and who studied before the evolution coverage was reformed. However, compositional differences by states and cohorts between individuals who studied before and after the reforms would bias results. Similarly, calculating the persuasion rate based on predicting treated and untreated students’ beliefs and subtracting the treatment effect from the treated students’ beliefs as in Cantoni et al. (2017) is not feasible because most students are treated to some extent even before the reforms, which then go in different directions with different intensities.

30.

They find the largest persuasion rates for the outcomes “not investing in a bond” (50% persuasion rate) and “trusting the local government” (47% persuasion rate).

31.

The number of hours a high school biology teacher in U.S. public schools spends on teaching evolution amounts to 14–20 hours on average; see Plutzer, Branch, and Reid (2020).

32.

Trust in public schools has exceeded trust in other persuaders such as newspapers and television news consistently throughout the past decades; see Gallup (2022).

33.

That is, the inability of students to “switch off” the teacher like a TV program conditional on being in class.

34.

In recent years, the number of unique vacancies has exceeded the number of new hires by about 40% in the life science industry, indicating a tight labor market (Cushman and Wakefield 2023). The report “How to Ensure That America’s Life-Sciences Sector Remains Globally Competitive” by the Information Technology and Innovation Foundation concludes, “Overall, we need more qualified STEM workers” (Kennedy 2020, 5).

35.

The life science industry accounts for 2.9% of U.S. GDP (or 7.3% when indirect effects are included) and has grown by an average of 7.8% per year over the past decade (Biotechnology Innovation Organization 2022). Furthermore, it plays a particularly crucial role in driving innovation in the United States, with about 20% of US patents originating from the life sciences (Cipher 2022). Moreover, the employment multiplier of the life science industry is estimated to be 4.82, implying that for every job in the life sciences, an additional 3.82 jobs are supported across the rest of the U.S. economy (Biotechnology Innovation Organization 2022). The export volume of U.S. biopharmaceutical goods has quadrupled between 2002 and 2022, amounting to almost US$90 billion in 2022 (U.S. Census Bureau).

36.

This can be illustrated by the well-known assertion by Dobzhansky (1973) that “nothing in biology makes sense except in the light of evolution.”

37.

Between the main outcome, evolution belief, and the average of the scientific topical outcomes, I reject the equality of coefficients at the 1% level (p-value = .0001). The analogous equality for the average of the broader science attitudes (interpreted as science prestige) is rejected at the 1% level as well (p-value = .004). The analogous equality for the average of the political and religious outcomes is rejected at the 1% level (p-value = .003), and at the 5% level (p-value = .022), respectively. Regarding the individual outcomes, I reject the equality of coefficients between evolution belief and the individual scientific topical outcomes for six out of nine comparisons and between evolution belief and the individual broader science attitudes for three out of three comparisons. For the individual religious and political outcomes, I reject the analogous equality for 8 out of 13 comparisons, and for 7 out of 17 comparisons, respectively.

38.

For the finding on the probability of working in the life sciences, I observe a positive pre-trend for the OLS estimator. This pre-trend completely disappears for the CS estimator that accounts for heterogeneous treatment effects.

39.

Examples include India, Israel, and Turkey, as illustrated by the news headlines “Indian education minister dismisses theory of evolution” by the Guardian (Safi 2018), “Israeli schools largely avoid teaching evolution” by the Times of Israel (Staff 2018), and “Turkey’s new school year: Jihad in, evolution out” by the BBC (Altunaş 2007).