Wildﬁre exposure increases pro-environment voting
within Democratic but not Republican areas
Chad Hazlett1and Matto Mildenberger∗2
1Departments of Political Science and Statistics, University of California Los
2Department of Political Science, University of California Santa Barbara
One political barrier to climate reforms is the temporal mismatch between short-
term policy costs and long-term policy beneﬁts. Will public support for climate reforms
increase as climate-related disasters make the short-term costs of inaction more salient?
Leveraging variation in the timing of Californian wildﬁres, we evaluate how exposure
to a climate-related hazard inﬂuences political behavior, rather than self-reported at-
titudes or behavioral intentions. We show that wildﬁres increased support for costly,
climate-related ballot measures by 5 to 6 percentage points for those living within 5km
of a recent wildﬁre, decaying to near zero beyond a distance of 15km. This eﬀect is
concentrated in Democratic-voting areas, and nearly zero in Republican-dominated ar-
eas. We conclude that experienced climate threats can enhance willingness-to-act but
largely in places where voters are known to believe in climate change.
∗Authors are listed in alphabetical order and contributed equally. Thanks to Johannes Urpelainen,
M. Kent Jennings, Peter Howe, Leah Stokes, Paasha Mahdavi, Jennifer Marlon, Parrish Bergquist, par-
ticipants at the Environmental Politics & Governance workshop, the American Political Science As-
sociation conference, the UC Santa Barbara Environmental Politics Workshop, and three anonymous
reviewers for their comments on earlier versions of this manuscript. Corresponding author: milden-
email@example.com. Replication materials are available on the American Political Science Review Dataverse
Despite the severity of the climate threat, global climate policymaking remains ane-
mic. One political barrier to policy enactment has been the temporal mismatch between
short-term climate policy costs and long-term climate policy beneﬁts (Jacobs 2011; Levin
et al. 2012). However, as the time horizon for realized climate change moves closer, weather
extremes and climate-related hazards could reshape the politics of climate change by making
salient the costs of policy inaction. Already, climate change has begun to noticeably disrupt
economic, social, and environmental conditions across the globe, including in the United
States (Diﬀenbaugh, Swain, and Touma 2015; Abatzoglou and Williams 2016).
Yet, it remains unclear whether ﬁrst-hand climate change experiences are reshaping the
public’s climate policy preferences or political behaviors. Some scholars ﬁnd that climate
concerns modestly increase with experienced temperature extremes (Brooks et al. 2014;
Bergquist and Warshaw 2019). Others ﬁnd no eﬀects (Brulle, Carmichael, and Jenkins
2012; Mildenberger and Leiserowitz 2017), only ephemeral eﬀects (Egan and Mullin 2012;
Deryugina 2013; Konisky, Hughes, and Kaylor 2016), or that eﬀects are limited to particular
political subgroups (Hamilton and Stampone 2013). Evidence for the relationship between
climate-related hazards and reported attitudes is similarly mixed. Some studies ﬁnd that
experiencing hazards increases intention to engage in mitigation and adaptation policies
(Spence et al. 2011; Demski et al. 2017) and climate risk perceptions (Lujala, Lein, and Rød
2015). Others, though, ﬁnd little or no eﬀect of hazards such as ﬂooding or ﬁre (Whitmarsh
2008; Brody et al. 2008). It also remains unclear whether attitudinal shifts, even if they
do occur, translate into shifts in realized political behaviors (Rudman, McLean, and Bunzl
These mixed empirical ﬁndings reﬂect systematic diﬀerences in how climate threats and
responses are measured, and in approaches to causal identiﬁcation (Howe et al. 2019). They
also reﬂect diﬀerent theoretical expectations about political responsiveness to experienced
threat. From one perspective, experiencing climate-related hazards may heighten the salience
of related social and economic risks, irrespective of an individual’s political identity (Slovic
and Weber 2013). Alternatively, an individual’s response to experiencing a climate change
impact may be conditioned by pre-existing beliefs and identities (Howe and Leiserowitz 2013;
Myers et al. 2013), including party or ideological commitments (Marquart-Pyatt et al. 2014;
Hamilton et al. 2016) and beliefs in anthropogenic climate change (Brody et al. 2008; Cap-
stick and Pidgeon 2014). For example, wildﬁre exposure has a stronger eﬀect on climate
attitudes among respondents who believe in the scientiﬁc consensus around climate change
(Lacroix, Giﬀord, and Rush 2019). Alternatively, climate-related political behaviors may be
overshadowed by other factors that inﬂuence political preferences during crises, including
public evaluation of government performance (Malhotra and Kuo 2008; Bechtel and Hain-
mueller 2011) and political participation (Jenkins 2019). All the same, empirically many
members of the public have linked wildﬁres to climate change (Brenkert-Smith, Meldrum,
and Champ 2015), with a recent survey showing 69% of Californians believe that climate
change is making wildﬁres worse.1
Scholars have also examined the psychological mechanisms through which the public re-
sponds to climate-related threats. For example, a rich literature elaborates how individuals
and communities manage wildﬁre risks. These studies highlight response heterogeneity, in-
cluding as a function of community-level discourse, social interactions, and norms (Brenkert–
Smith, Champ, and Flores 2006; Brenkert-Smith et al. 2013; Dickinson et al. 2015). Result-
ing wildﬁre responses, in the aggregate, are not always eﬃcient. For example, government
wildﬁre management often responds to recent salient wildﬁre events rather the actual distri-
bution of future wildﬁre risks (Anderson et al. 2018; Wibbenmeyer, Anderson, and Plantinga
In this paper, we evaluate the links between experiencing a climate-related hazard and
realized political behavior. Our study oﬀers two major advances over prior work. First,
existing research on experienced climate change has exclusively used survey outcomes to
1. Jennifer Marlon and Abigail Cheskis. 2017. “Wildﬁres and climate are related – are Americans con-
necting the dots?,” Yale Project on Climate Change Communication. https://climatecommunication.
measure individual attitudes or behavioral intentions (Howe et al. 2019). By contrast, we
estimate the eﬀect of an actual climate-related hazard (wildﬁres) on a realized political
behavior that directly inﬂuences policy (ballot initiative support). Speciﬁcally, recognizing
limits to generalization, we study how wildﬁre exposure at the census block group-level
shapes voting outcomes on a series of Californian environmental ballot initiatives between
2006 and 2010. Second, we use location (block group) and year ﬁxed eﬀects in order to exploit
idiosyncratic variation in when wildﬁres are experienced by voters in each block group. As
a result, only time-varying confounders within block groups could bias the results, and only
when they cannot be explained by statewide change over time. Including observed time-
varying covariates expected to relate most strongly to wildﬁre risk and to attitudes (e.g.
rainfall, democratic vote share, population density, etc.) have no impact on our estimates.
Further, we use sensitivity analyses to show that even unobserved confounding multiple times
stronger than these covariates would not substantially alter our conclusions.
Overall, we ﬁnd that Californians who experience a wildﬁre within 5km of their census
block group are 5-6 percentage points more likely to vote for costly climate-related policy
reforms, relative to those at least the median distance away (35-40km). This eﬀect decays
with distance, falling below 1 percentage point beyond a distance of 15 km. Moreover, this
eﬀect is highly heterogeneous depending on partisan identity: it is concentrated in the block
groups that are most Democratic, while areas dominated by Republican voters show no
detectable eﬀect of wildﬁre. These ﬁndings are consistent with some survey-based work on
wildﬁre exposure in emphasizing heterogeneity in public responsiveness as a function of priors
about climate change (Lacroix, Giﬀord, and Rush 2019; Marlon et al. 2020); however, other
observational research has found mixed relationships between individual climate experiences
and climate-related beliefs and behaviors (Dessai and Sims 2010; Kreibich 2011; Howe et
al. 2019). For example, Javeline, Kijewski-Correa, and Chesler (2019) ﬁnd that both risk
exposure and adaptation intentions related to sea-level rise are independent of climate change
attitudes. By contrast, we ﬁnd that responsiveness to climate-related impacts is concentrated
in populations that, among other features, are far more likely to believe in anthropogenic
climate change (e.g. Dunlap, McCright, and Yarosh 2016). In turn, our results suggest
that as the impacts of climate change become more evident, support for climate mitigation
policies may remain weaker in areas with lower pre-existing climate beliefs.
We prepare an original panel of political and wildﬁre data in California. Electoral out-
come and voter registration data available from the California Secretary of State provide
precinct-level outcomes for all national elections between 2002 and 2010. The precinct level
is the smallest unit with electoral return data in California. However, Californian electoral
precinct boundaries and names change over time. We convert all data to 2000 census block
group geographies. Oﬃcial conversion ﬁles allow us to compute the overlap between election
precincts in each year and the 2000 census block groups. We then aggregate the electoral
precinct data to the 2000 census block groups. That is, for any variable expressed as a count
or total in each precinct (e.g. the number of votes in support of a ballot initiative), we sum
these values across the precincts that contribute to a given block group, weighting each by
the fraction of the precinct overlapping with that block group.
Measure of environmental support. Our dependent variable is the proportion of voters
supporting four pro-environment ballot initiatives in each block group, across three unique
elections. The four ballot measures we consider constitute all the measures that clearly
reﬂect support for costly climate-related policies. We review these brieﬂy. In 2006, Califor-
nians voted on Proposition 87, which proposed a new $4 billion dollar program to support
clean energy alternatives, funded by a 1.5% to 6% tax on Californian oil producers. It
was rejected 55% to 45%. In 2008, Californians voted on Proposition 10, which proposed
a support program for research, education and deployment of alternative fuel technologies,
and was rejected 59% to 41%. Californians also voted on Proposition 7, which proposed to
require increased utility purchases of renewable energy and was rejected by 64% to 34%. We
create a single measure of pro-environment voting behavior for 2008 by averaging support
for Proposition 10 and Proposition 7. In 2010, Californians voted on Proposition 23, which
sought to suspend California’s Global Warming Act of 2006 (rejected, 62% to 38%). Criti-
cally, we do not assume that support for these four initiatives measure the same thing, i.e.
that they would have similar levels of support in the absence of the treatment. In partic-
ular, we allow for an arbitrary intercept shifts in the level of support across proposals. In
Appendix A.1, we provide additional details on each proposition, including information on
the costs as presented contemporaneously to the public.
Treatment Measurement. We extract wildﬁre perimeter data from the Monitoring Trends
in Burn Severity (MTBS) dataset, an interagency US government eﬀort tracking large ﬁres
via Landsat satellite data. We then spatially merge the wildﬁre perimeter data to the census
block group data to determine each block group’s distance from wildﬁres. Our primary esti-
mates consider wildﬁres that burned at least 5000 acres, over each two-year period preceding
a federal election (see Appendix A.2 for details). The 5000 acre threshold covers 94% of the
state’s total burned area over this period; it was chosen after prior examination of separate,
satellite-based data to eliminate numerous smaller events too small to be threaten the public.
The two year window is used to correspond to the timing of election cycles and thus the
measurement of our outcomes as well as potential confounders.
Unconditionally, these wildﬁres do not occur at random with the same probability in
all census block groups; they are more common in rural and peri-urban areas—what ﬁre
scholars describe as the Wildland-Urban Interface (WUI). Overall, without conditioning we
see that block groups with wildﬁres have only one eighth the population density of those
without (t-stat = 83 for diﬀerence in means; see also Figure 7 in Appendix A.8). Areas
with wildﬁres are also more conservative on average: mean Democratic vote share among
areas with a wildﬁre as just deﬁned have is 42%, compared to 63% in areas without wildﬁres
(t-stat = 23 for diﬀerence in means). Naive estimates that merely compare voting behavior
in places that did and did not experience wildﬁres are thus uninformative as to the eﬀect of
wildﬁre, instead only showing how places more or less prone to wildﬁre tend to diﬀer (see
Confounding, Sensitivity, and Estimation. We minimize confounding through a strat-
egy of conditioning on block group and year, such that only time-varying covariates within
block groups and not already captured by the secular time trend can potentially generate
confounding bias. One type of time-varying potential confounder we might remain concerned
about is political attitudes, such as partisan preferences, that could certainly inﬂuence en-
vironmental support and may for unknown reasons also relate to ﬁre risk. We consider
Democratic vote share (DemVoteShare) as a proxy for such attitudes, and employ it with a
lag to avoid concerns that it was aﬀected by wildﬁre itself, though all results are similar with-
out lagging. Another source of potential time-varying confounding would be environmental
changes in ﬁre risk, particularly due to variation in precipitation, that could also poten-
tially eﬀect environmental attitudes directly. For this, in each block group we sum the total
precipitation over the two-years leading up to the election (Precip2yr). We also compute
the deviation from historical average rainfall, (PrecipDeviation).2Our approach does not
require an assertion of precisely zero confounding. Rather, we eliminate as much confound-
ing as possible through conditioning on block group and year (and optionally the covariates
just described), after which sensitivity analyses reveal how the estimate would vary under
postulated degrees of confounding, including confounding multiple times stronger than such
observed factors as precipitation or Democratic vote share.
Coming to estimation, consider a particular block group level voting outcome in a given
year, Yit. For each block group at each election, Wildﬁre2yrit equals 1if a wildﬁre occurred
2. PrecipDeviation is given by the rainfall in the prior two years, minus (twice) the average annual rainfall
over the years 1981 to 2010, divided by the latter. We also note that the eﬀect of rainfall or drought on
environmental support may be a causal question of direct interest, but here we are only concerned with its
potential for confounding the estimated eﬀect of wildﬁre.
within the block group’s spatial perimeter in the preceding two year period and equal to 0
otherwise. We estimate the eﬀect of wildﬁre exposure on voting outcomes using a (two-way,
ﬁxed eﬀects) model of the form,
Supportit =γi+ωt+αWildﬁre2yrit +β1DemVoteShareit+(1)
β2Precip2yr +β3PrecipDeviation +ηit,
where Supportit is environmental ballot measure support iin year t,γiare block group
ﬁxed eﬀects, ωtare election-year ﬁxed eﬀects, and ηit is the error term. The key parameter
of interest is α, the coeﬃcient on Wildﬁre2yrit. Including the Democratic vote share and
precipitation variables in these models does not change the result, while allowing them to
play useful roles as benchmarks for relative confounding in the sensitivity analysis below.
We ﬁnd that block groups exposed to a wildﬁre larger than 5000 acres have 6.0 percentage
point higher support for environmental ballot initiatives (t-stat=11.5, 95% CI [5.0,7.1]).3We
then examine how eﬀects vary with distance from the ﬁre with the same model but replacing
the wildﬁre variable with a series of indicators that measure the minimum distance between
each block group and a wildﬁre. The indicator variable for block groups near the median
wildﬁre distance (35-40km) is omitted, so that each coeﬃcient estimate reports a diﬀerence
relative to the median distance. Figure 1 plots these results. Experiencing a wildﬁre very
near one’s block group (0 to 5 km) has the largest estimated eﬀect on pro-environment
voting relative to the median distance (5.5 percentage points, t-stat = 24.8; 95% CI [5.1,
6.0]). This estimate decays monotonically down to just 0.4 percentage points (t=2.5) at 30
3. If all wildﬁres are analyzed regardless of size, the average eﬀect estimate is still substantial but, as
expected, somewhat smaller at 4.7 percentage points, t-stat=10, 95% CI [3.7,5.6]. If we instead examine
whether a wildﬁre occurred within the prior one year rather than two, the estimate is similarly 5.0 percentage
points with 95% CI [3.5, 6.4]).
Figure 1: Estimated eﬀect of wildﬁre exposure on pro-environment voting, by distance.
Estimates compared to response at the median distance (35-40km). All estimates derived
from a linear model with block group and year ﬁxed eﬀects and controlling for Democratic
vote share in Congressional elections four years prior. Error bars show 99% conﬁdence
intervals, using standard errors clustered on block group.
to 35 km away, the last group closer than the median distance (see Appendix A.4, Table
3 for numerical results). Figure 5 in A.5 re-expresses these results as the expected level of
support at each distance, i.e. a dose-response curve, to facilitate any chosen comparison
rather than comparing each distance to the median.
Finally, because wildﬁres are statistically rare, we have limited ability to investigate
whether the eﬀect varies based on the degree of prior exposure. However, Figure 6 in
Appendix A.6 shows the result when limited to the 293 block groups that had wildﬁres
prior to the 2006 electoral cycle, suggesting little or no eﬀect in this group, albeit with lower
precision due to the reduced sample size.
Heterogeneity by political ideology
A key question is what places are more or less responsive to this threat. Figure 2 shows the
estimated eﬀect of wildﬁre by distance from the same model as above, splitting the data into
Figure 2: Estimated eﬀect of experiencing a wildﬁre at various distances, by Democratic
vote share. Error bars show 95% conﬁdence intervals, using standard errors clustered on
three groups: those where Democratic vote share was lower (20-40%), middling (40-60%),
or higher (60-80%). The eﬀect of wildﬁre is heavily concentrated in the most Democratic
group, and near zero in the most Republican group, with the less extreme areas falling in
While the eﬀect of wildﬁre in each group is identiﬁable under the same assumptions as
the entire group, we emphasize that the diﬀerences between these lines cannot be attributed
to partisan preferences alone and may be due to other characteristics associated with Demo-
cratic vote share. One covariate of particular interest is population density, or various related
concepts for which we take it as a proxy. Figure 8 in Appendix A.8 shows that while there
are large diﬀerences in the eﬀect of wildﬁre depending on Democratic vote share, there is
little diﬀerence when further stratifying on population density.4
4. We also note that the strong correlation of population density with Democratic vote share in the overall
sample (r=0.35) vanishes entirely (r=−0.001,p= 0.98) when we look only at places with wildﬁres at some
time. Appendix A.8 explains why this occurs and shows that consequently the distribution of population
density is nearly the same for more Democratic and more Republican areas that have had wildﬁres.
Risks of confounding
For omitted time-varying variables to cause confounding bias in this setting, they must vary
over time within block group and not be captured by the statewide changes over time. The
potential time-varying confounders of greatest concern to us based on domain knowledge
were political attitudes, and changes in environmental conditions leading to wildﬁre risk,
particularly precipitation level and variation. We observe variables that speak to both:
Democratic vote share in each year, the level of precipitation in the prior two years, and
deviation in precipitation from the historical average. While these were included in the
above models to assuage concerns that they may be confounders, doing so did not appreciably
alter the estimates. Population density and total registered voters are also potentially time-
varying, albeit unlikely to change fast enough to have an impact on estimates. Including
these variables also has no impact on estimates.
We also consider a placebo outcome using support for ballot measures on housing bonds,
for which we expect little to no eﬀect of wildﬁre. In models otherwise identical to those
above, we ﬁnd that wildﬁre does not predict a change in support for housing bonds with a
coeﬃcients of -0.2 percentage points (t-stat=0.55, 95% CI [-1.0, 0.6]). See Appendix A.7 for
Finally, more worrying than observed covariates is the potential for unobserved con-
founders due to variables we could not think of or measure. It is not necessary to have
precisely zero confounding bias in order to arrive at our research conclusions, but it is im-
portant to determine how severe confounding would have to be to have meaningfully altered
our conclusions through sensitivity analysis. Following Cinelli and Hazlett 2020, the contours
in Figure 3 show the eﬀect estimate as adjusted for varying possible degrees of confounding.
Confounding is indexed by the proportion of residual variance in wildﬁre (the treatment)
it can explain (on the horizontal axis), and the proportion of residual variance in environ-
mental support it explains (vertical axis). The dashed line shows combination of these two
strengths at which confounding explains away the entire eﬀect, making the adjusted esti-
mate zero. Of particular note are the benchmark bounds (diamonds). These show how
confounding “as strong as” (able to explain as much of the treatment and outcome resid-
ual variation as) observed covariates would alter the estimate. Even confounding as strong
as precipitation in the prior two years (Precip2yr) or the deviation from historical rainfall
(PrecipDeviation) would bring the estimate approximately from the unadjusted value of 6
percentage points down to approximately 5 percentage points. Confounding as strong as
Democratic vote share—or even ten times as strong (10x dem. vote share)—would have a
still smaller impact. Therefore, any confounding able to substantially alter the conclusions
reached would need to explain far more of wildﬁre occurrence and environmental attitudes
than is explained by even these theoretically important variables.5
In summary, the haphazard and unpredictable nature of wildﬁre timing in California provides
an empirical opportunity to evaluate the eﬀect experienced environmental threats on real-
world climate-related political behavior. Block groups that experiences a wildﬁre within their
boundaries show higher support for environmental ballot initiatives in subsequent elections
by 6 percentage points relative to those without one. Block groups that are nearer to wildﬁres
experience larger estimated eﬀects than those farther away: those within 5km, 10km, or
15km of a wildﬁre boundary show estimated eﬀects of 5.5, 3.1, and 2.4 percentage points
respectively, each highly signiﬁcant (t-stat>11); while the eﬀect dissipates beyond 15km.
Moreover, the eﬀect of wildﬁre strongly varies with the political identities composing
these block groups. Voting behavior is most severely impacted by wildﬁre in the most
Democratic census block groups, and largely unaﬀected in the most Republican census block
groups. Experiences with climate change thus enhance willingess-to-act in groups that are
5. Note that the horizontal position of the benchmarks on this plot also provides a balance test, showing
that each variable has a very weak conditional relationship with wildﬁre. Measuring imbalance in this way
directly speaks to how worrying a potential imbalance would be by showing “how confounders as strong as
these covariates” would inﬂuence estimates provides.
Partial R2 of confounder(s) with the treatment
Partial R2 of confounder(s) with the outcome
0.00 0.05 0.10 0.15 0.20 0.25 0.30
0.00 0.05 0.10 0.15 0.20 0.25 0.30
10x dem. vote share
Figure 3: Eﬀect estimates at varying degrees of postulated confounding, with benchmark
more likely to be climate-concerned and to believe in human causes of climate change (see
also Zanocco et al. 2018). The same events did little to mobilize those in highly Republican
areas, who are expected to be more skeptical and less climate-concerned. Whether wildﬁre
exposure altered the outcomes of these particular ballot measures or not, climate impacts
thus appear to intensify the climate commitments of existing supporters rather than creating
new political supporters.
Fully investigating the mechanism by which this eﬀect occurs requires separate research
and a variety of designs. One conclusion we can reach, however, is that the eﬀect is not
through a change in turnout. Appendix A.9 shows the estimated eﬀect of wildﬁre on voter
turnout at varying distances. Wildﬁres within 15km appear to reduce turnout, but only by
approximately 1 percentage point. While substantively interesting unto itself, this is too
small an eﬀect on turnout to account for the observed eﬀect on environmental support.
By using realized vote share on costly ballot initiatives, these results capture the impact
of wildﬁre exposure on a real world political behavior that can directly inﬂuence policy. As
in any analysis of real world events, generalizing these results to other types of events or to
other places and time periods would require caution. However, we ﬁnd that climate-related
impacts have already shaped realized political behavior. In the case of Californian wildﬁres
between 2006 and 2010, wildﬁre exposure increased voting for costly climate-related policies,
an eﬀect that was concentrated among Democratic areas where voters were more likely to
believe in climate change.
Abatzoglou, John T, and A Park Williams. 2016. “Impact of anthropogenic climate change
on wildﬁre across western US forests.” PNAS 113 (42): 11770–11775.
Anderson, Sarah E, Ryan R Bart, Maureen C Kennedy, Andrew J MacDonald, Max A
Moritz, Andrew J Plantinga, Christina L Tague, and Matthew Wibbenmeyer. 2018.
“The dangers of disaster-driven responses to climate change.” Nature Climate Change 8
Bechtel, Michael M, and Jens Hainmueller. 2011. “How Lasting Is Voter Gratitude?” Amer-
ican Journal of Political Science 55 (4): 852–868.
Bergquist, Parrish, and Christopher Warshaw. 2019. “Does Global Warming Increase Public
Concern About Climate Change?” The Journal of Politics 81 (2): 686–691.
Brenkert–Smith, Hannah, Patricia A Champ, and Nicholas Flores. 2006. “Insights into wild-
ﬁre mitigation decisions among wildland–urban interface residents.” Society and Natural
Resources 19 (8): 759–768.
Brenkert-Smith, Hannah, Katherine L Dickinson, Patricia A Champ, and Nicholas Flores.
2013. “Social ampliﬁcation of wildﬁre risk: the role of social interactions and information
sources.” Risk Analysis 33 (5): 800–817.
Brenkert-Smith, Hannah, James R Meldrum, and Patricia A Champ. 2015. “Climate change
beliefs and hazard mitigation behaviors: homeowners and wildﬁre risk.” Environmental
Hazards 14 (4): 341–360.
Brody, Samuel D, Sammy Zahran, Arnold Vedlitz, and Himanshu Grover. 2008. “Examining
the relationship between physical vulnerability and public perceptions of global climate
change in the United States.” Environment and Behavior 40 (1): 72–95.
Brooks, Jeremy, Douglas Oxley, Arnold Vedlitz, Sammy Zahran, and Charles Lindsey. 2014.
“Abnormal Daily Temperature and Concern about Climate Change Across the United
States.” Review of Policy Research 31 (3): 199–217.
Brulle, Robert J, Jason Carmichael, and J Craig Jenkins. 2012. “Shifting public opinion on
climate change: An empirical assessment.” Climatic Change 114 (2): 169–188.
Capstick, Stuart Bryce, and Nicholas Frank Pidgeon. 2014. “Public perception of cold weather
events as evidence for and against climate change.” Climatic Change 122 (4): 695–708.
Cinelli, Carlos, and Chad Hazlett. 2020. “Making sense of sensitivity: Extending omitted
variable bias.” Journal of the Royal Statistical Society: Series B (Statistical Methodology)
82 (1): 39–67.
Demski, Christina, Stuart Capstick, Nick Pidgeon, Robert Gennaro Sposato, and Alexa
Spence. 2017. “Experience of extreme weather aﬀects climate change mitigation and
adaptation responses.” Climatic Change 140 (2): 149–164.
Deryugina, Tatyana. 2013. “How do people update? The eﬀects of local weather ﬂuctuations
on beliefs about global warming.” Climatic Change 118 (2): 397–416.
Dessai, Suraje, and Catherine Sims. 2010. “ Public perception of drought and climate change
in southeast England.” Environmental Hazards 9 (4): 340–357.
Dickinson, Katherine, Hannah Brenkert-Smith, Patricia Champ, and Nicholas Flores. 2015.
“Catching ﬁre? Social interactions, beliefs, and wildﬁre risk mitigation behaviors.” So-
ciety & Natural Resources 28 (8): 807–824.
Diﬀenbaugh, Noah S, Daniel L Swain, and Danielle Touma. 2015. “Anthropogenic warming
has increased drought risk in California.” PNAS 112 (13): 3931–3936.
Dunlap, Riley E, Aaron M McCright, and Jerrod H Yarosh. 2016. “The political divide on
climate change.” Environment: Science and Policy for Sustainable Development 58 (5):
Egan, Patrick J, and Megan Mullin. 2012. “Turning personal experience into political atti-
tudes.” The Journal of Politics 74 (3): 796–809.
Hamilton, Lawrence C, and Mary D Stampone. 2013. “Blowin’in the wind: Short-term
weather and belief in anthropogenic climate change.” Weather, Climate, and Society
5 (2): 112–119.
Hamilton, Lawrence C, Cameron P Wake, Joel Hartter, Thomas G Saﬀord, and Alli J
Puchlopek. 2016. “Flood realities, perceptions and the depth of divisions on climate.”
Sociology 50 (5): 913–933.
Howe, Peter D, and Anthony Leiserowitz. 2013. “Who remembers a hot summer or a cold
winter?” Global Environmental Change 23 (6): 1488–1500.
Howe, Peter D, Jennifer Marlon, Matto Mildenberger, and Brittany S Shield. 2019. “How
will climate change shape climate opinion?” Environmental Research Letters 14 (11).
Jacobs, Alan M. 2011. Governing for the Long Term: Democracy and the Politics of Invest-
ment. Cambridge, UK: Cambridge University Press.
Javeline, Debra, Tracy Kijewski-Correa, and Angela Chesler. 2019. “Does it matter if you
“believe” in climate change? Not for coastal home vulnerability.” Climatic Change 155
Jenkins, Matthew D. 2019. “Natural disasters and political participation: The case of Japan
and the 2011 triple disaster.” Journal of East Asian Studies 19 (3): 361–381.
Jost, John T, Jack Glaser, Arie W Kruglanski, and Frank J Sulloway. 2003. “Political con-
servatism as motivated social cognition.” Psychological Bulletin 129 (3): 339.
Konisky, David M, Llewelyn Hughes, and Charles H Kaylor. 2016. “Extreme weather events
and climate change concern.” Climatic Change 134 (4): 533–547.
Kreibich, Heidi. 2011. “Do perceptions of climate change inﬂuence precautionary measures?”
International Journal of Climate Change Strategies and Management 3 (2): 189–199.
Lacroix, Karine, Robert Giﬀord, and Jonathan Rush. 2019. “Climate change beliefs shape
the interpretation of forest ﬁre events.” Climatic Change 159:103–120.
Levin, Kelly, Benjamin Cashore, Steven Bernstein, and Graeme Auld. 2012. “Overcoming
the tragedy of super wicked problems.” Policy Sciences 45 (2): 123–152.
Lujala, Päivi, Haakon Lein, and Jan Ketil Rød. 2015. “Climate change, natural hazards, and
risk perception.” Local Environment 20 (4): 489–509.
Malhotra, Neil, and Alexander G Kuo. 2008. “Attributing blame: The public’s response to
Hurricane Katrina.” The Journal of Politics 70 (01): 120–135.
Marlon, Jennifer, Xinran Wang, Parrish Berguist, Katherine Hayhoe, Sharmistha Swain, Pe-
ter Howe, and Anthony Leiserowitz. 2020. “Hot, dry days increase perceived experience
with global warming.” SSRN Working Paper.
Marquart-Pyatt, Sandra T, Aaron M McCright, Thomas Dietz, and Riley E Dunlap. 2014.
“Politics eclipses climate extremes for climate change perceptions.” Global Environmen-
tal Change 29:246–257.
Mildenberger, Matto, and Anthony Leiserowitz. 2017. “Public opinion on climate change: Is
there an economy–environment tradeoﬀ?” Environmental Politics 26 (5): 801–824.
Myers, Teresa A, Edward W Maibach, Connie Roser-Renouf, Karen Akerlof, and Anthony
A Leiserowitz. 2013. “The relationship between personal experience and belief in the
reality of global warming.” Nature Climate Change 3 (4): 343.
Nail, Paul R, Ian McGregor, April E Drinkwater, Garrett M Steele, and Anthony W Thomp-
son. 2009. “Threat causes liberals to think like conservatives.” Journal of Experimental
Social Psychology 45 (4): 901–907.
Rudman, Laurie A, Meghan C McLean, and Martin Bunzl. 2013. “When truth is personally
inconvenient, attitudes change.” Psychological Science 24 (11): 2290–2296.
Slovic, Paul, and Elke U Weber. 2013. “Perception of risk posed by extreme events.” In
Regulation of Toxic Substances and Hazardous Waste, edited by Applegate, Gabba,
Laitos, and Sachs, 34–38. St. Paul, MN: Foundation Press.
Spence, Alexa, Wouter Poortinga, Catherine Butler, and Nicholas Frank Pidgeon. 2011. “Per-
ceptions of climate change and willingness to save energy related to ﬂood experience.”
Nature Climate Change 1 (1): 46.
Whitmarsh, Lorraine. 2008. “Are ﬂood victims more concerned about climate change than
other people? The role of direct experience in risk perception and behavioural response.”
Journal of risk research 11 (3): 351–374.
Wibbenmeyer, Matthew, Sarah E Anderson, and Andrew J Plantinga. 2019. “Salience and
the government provision of public goods.” Economic Inquiry 57 (3): 1547–1567.
Zanocco, Chad, Hilary Boudet, Roberta Nilson, Hannah Satein, Hannah Whitley, and June
Flora. 2018. “Place, proximity, and perceived harm: extreme weather events and views
about climate change.” Climatic Change 149 (3-4): 349–365.
Wildﬁre exposure increases pro-environment voting within
Democratic but not Republican areas
Chad Hazlett & Matto Mildenberger
A.1 Additional details on California ballot initiatives
In our analysis, we focus on four pro-environment ballot initiatives across three unique elec-
tions. Each of these measures involves costly climate-related policies. Here, we summarize
the anticipated costs of each, as reported to voters at the time.
The ﬁrst ballot initiative is California Proposition 87, from the 2006 election. (Oﬃcial Ti-
tle: Alternative Energy. Research, Production, Incentives. Tax on California Oil Producers).
The proposition involved $4 billion dollars in new program spending on clean energy, funded
by a 1.5% to 6% tax on Californian oil producers. The initiative proved highly contentious,
with advocates and opponents spending over $150 million on the initiative. The proposition
included language to prohibit direct cost pass-throughs to California consumers, opponents
vocally claimed that the measure would increase gas prices. The proposition would also have
imposed indirect economic costs. The oﬃcial Fiscal Impact Statement suggested it would
lead to state and local revenue reductions in the low tens of millions. Ultimately, Proposition
87 was rejected 55% to 45%.
The second ballot initiative is California Proposition 10, from the 2008 election. (Oﬃcial
title: The California Alternative Fuels Initiative). This proposition proposed a support
program for research, education and deployment of alternative fuel technologies, to be paid
for using $5 billion dollars in state bonds. The oﬃcial Fiscal Impact Statement estimated the
proposition’s total cost as $9.8 billion, including $4.8 billion to service the bonds. Support
and opposition focused on whether the state should be prioritizing these funds towards clean
energy needs. Ultimately, Proposition 10 was rejected 59% to 41%.
The third ballot initiative is California Proposition 7, also from the 2008 election. (Oﬃcial
title: Standards for Renewable Resource Portfolios). This proposition proposed to require
increased utility purchases of renewable energy by 2% annually, up to 40% in 2020 and
50% in 2025. The oﬃcial Fiscual Impact Statement emphasized broad uncertainty in costs.
It suggested that higher power rates would be likely in the short-term and uncertain in
the long-term. Opponents claimed the measure would increase consumer electricity costs
by 10%, including a $300 increase per household per year. Ultimately, Proposition 7 was
rejected by 64% to 34%.
The fourth initiative is California Proposition 23, from the 2010 election. This proposition
sought to suspend California’s Global Warming Act of 2006, one of the state’s primary
legislative packages to manage the climate crisis. According to the Fiscal Impact Statement,
the proposition (to eliminate climate policy) would have modestly increased state economic
activity. Proponents emphasized the measure would save a million jobs, would prevent $3800
in annual household cost increases, and would help protect public services by not imposing
economic hardship on the state. Ultimately, this proposition was rejected, 62% to 38%.
Note again, as discussed in text, that we do not assume that support for any of these
four initiatives measure the same thing, i.e. that they would have similar levels of support
in the absence of the treatment. In particular, we allow for an arbitrary intercept shifts in
the level of support across proposals.
A.2 Distribution of wildﬁres in California across electoral precincts
The electoral precinct level is the smallest unit with available electoral return data in Cal-
ifornia. However, Californian voting geographies and identiﬁers change on an election-by-
election basis constraining our ability to directly contrast voting precinct-level voting out-
comes across time. Between 2002 and 2014, the number of electoral precincts in the state
varied between a maximum of n=26,985 in 2008 and a minimum of n= 23,185 in 2014.
Figure 4: Perimeters of Californian wildﬁres larger than 5000 acres during each inter-election
periods are used for analysis
In the two years preceding each of these elections, between 0.3% and 1.3% of block
groups experienced a wildﬁre that burned at least 5000 acres (see Table 1). The perimeters
of wildﬁres in each two-year period are also visualized in Figure 4. Biannual elections occur
in early November. A small fraction of units labeled as experiencing wildﬁres actually did
so after the November election in even years; however, the number of such cases is small and
moreover, this error would bias our result slightly toward zero as it labels some units that
were not aﬀected (prior to the election) as if they were.
Election Block groups without wildﬁres Block groups with wildﬁres
2006 19717 88
2008 21353 273
2010 20939 66
Table 1: Frequency of wildﬁres burning at least 5000 acres, within boundaries of a census
block group, by election cycle.
A.3 Naive relationship between wildﬁres and political behavior
We begin by descriptively examining the cross-sectional relationship between wildﬁre and
environmental voting, separately in each year and in the pooled data. Results are shown in
Table 2 below.
Table 2: Cross-Sectional (Naive) Results for Environmental Outcome
2006 2008 2010 pooled pooled
(1) (2) (3) (4) (5)
wildﬁre2yr −0.108∗∗∗ −0.065∗∗∗ −0.118∗∗∗ −0.086∗∗∗
(0.010) (0.004) (0.011) (0.004)
YEAR=2008 −0.078∗∗∗ −0.080∗∗∗
YEAR=2010 0.155∗∗∗ 0.153∗∗∗
Constant 0.476∗∗∗ 0.398∗∗∗ 0.631∗∗∗ 0.476∗∗∗ 0.477∗∗∗
(0.001) (0.001) (0.001) (0.001) (0.001)
Observations 19,805 21,626 21,005 62,436 62,427
R20.006 0.012 0.005 0.430 0.431
F Statistic 115∗∗∗ 261∗∗∗ 110∗∗∗ 15,679∗∗∗ 15,736∗∗∗
∗p<0.1; ∗∗p<0.05; ∗∗∗ p<0.01
Note: Cross-sectional description of environmental voting in block groups with and without wildﬁre
in preceding two years. Models (1)-(3) show results separately by year. Model (4) pools cross-
sectional comparisons across years, adding year ﬁxed eﬀects so as to allow ballot initiatives in the
three years to diﬀer in their baseline levels of support. Model (5) is also pooled but uses a one
election (two year) lead of the treatment Wildﬁre2yr_f2. In all cases, the kinds of places that had
wildﬁre in the prior two years (Models 1-4) or in the subsequent two years (Model 5) are places
with signiﬁcantly lower support for environmental measures.
The estimates in columns (1) through (3) all simply show the correlation (as a regression
coeﬃcient) between wildﬁre and voting on the corresponding ballot measure(s) separately
for the three relevant elections. Each shows that wildﬁre is associated with approximately 7
to 12 percentage points lower support for environmental initiatives. The “pooled” version in
column (4) includes all the relevant elections/measures, with election ﬁxed eﬀects to allow
for diﬀerent baseline levels of support. It similarly shows a strong negative correlation, with
those areas experiencing wildﬁre having lower support by 9 percentage points. We take
these not as estimated eﬀects of wildﬁre on environmental voting, but as an indication that
the types of places where wildﬁres occur are those that tend to be generally less supportive
of environmental measures. That this relationship reﬂects largely “what type of units get
treated” rather than an eﬀect of treatment is made evident by replacing the wildﬁre variable
in these models with an indicator for wildﬁres in the next election cycle, which clearly
cannot eﬀect (past) support. Column (5) in Table 2 shows that future wildﬁres also predict
11 percentage point lower support.
These results were expected, as places with wildﬁres on the whole are likely to be more
rural, and more conservative. If true, we also expect to see similar or even larger “imbalances”
of this type on a measure of conservatism. The ideal measure for this is Democratic (or
Republican) vote share. Unfortunately, a meaningful measure of either is available only
until 2010. From 2012 onwards, California switched to run-oﬀ style elections where both
candidates running in many congressional districts were Democrats. However, where our
analysis requires a measure of Democratic vote share (e.g. as a reassuring but unnecessary
control variable, or for examining heterogeneous eﬀects), we wish to use a lagged measure
anyway to ensure it is pre-treatment. We thus lag Democratic vote share by two elections
both to ensure it is available where needed and is unaﬀected by the wildﬁre coded to the
same “row” in the data.
A.4 Details of regression for eﬀect by distance
To estimate the distance-varying eﬀects as in Figure 1, we estimate the model
Supportit =γi+ωt+α1Fire0to5km +... +α7Fire30to35km
+α8FireOver40km +βDemVoteShareit +ηit,(2)
where Fire0to5km, ..., Fire30to35km are indicators for block groups that experience the near-
est wildﬁre burning at least 5000km within those distances. The indicator for being 35 to
40km from a ﬁre (the median category) is omitted (and the FireOver40km category is in-
cluded) so that the median group is the omitted one and the coeﬁcient estimates for the
distance indicators thus represent the expected change in support at that distance relative
to the expected level of support at the median distance. Note that because the coeﬃcient on
FireOver40km will reﬂect the eﬀect of being farther away from a wildﬁre than the median,
it is expected to be (and is) opposite in sign.
Table 3: Regression results for analysis by distance
Estimate Std. Error t stat. p-value
ﬁre within 0-5km 0.055 0.002 24.775 0.000
ﬁre within 5-10km 0.031 0.002 16.853 0.000
ﬁre within 10-15km 0.024 0.002 13.397 0.000
ﬁre within 15-20km 0.007 0.002 4.102 0.000
ﬁre within 20-25km 0.004 0.002 2.766 0.006
ﬁre within 25-30km 0.007 0.002 4.021 0.000
ﬁre within 30-35km 0.004 0.002 2.508 0.012
ﬁre over 40km away -0.012 0.001 -9.942 0.000
Dem. vote share 0.025 0.003 7.164 0.000
precip.2yr 0.000 0.000 42.972 0.000
precip.deviation -0.194 0.005 -35.873 0.000
Note: Regression results for analysis of eﬀect of wildﬁre by distance using two-way (block group and
year) ﬁxed eﬀects model. Main indicators of interest (and those plotted in Figure 1) correspond to
indicators for being various distances to the nearest wildﬁre burning over 5000 acres. The indicator
for the median distance (35-40km) is omitted, so that each coeﬃcient is interpreted as a diﬀerence
in expected support, relative to the median distance.
A.5 Dose-response estimate
Wildﬁre is an unusual treatment in that all block groups experience wildﬁres at some dis-
tance. In analyzing the eﬀect of wildﬁre at diﬀerent distances, we thus do not compare
“having a wildﬁre X kilometers away to having no exposure at all”. Rather, distance-based
eﬀects are deﬁned as a contrast of the expected level of support at any two distances. While
Figure 1 in the main text compares the expected level of support for environmental initiatives
at the given distance to the level of support at the median distance, another natural quantity
of interest is the “dose-response” curve, i.e. the expected level of support (conditional on or
integrating over confounding variables) at each distance. To construct this, we ﬁrst estimate
Supportit =γi+ωt+α1Fire0to5km +... +α8Fire35to40km +βDemVoteShareit +ηit,
from which we compute expected levels of support at each distance. Creating actual esti-
mated levels of support requires choosing values of the other covariates – the year, the block
group, and the Democratic vote share. The choice matters little, as it results only in a con-
stant shift of all expected levels of support up or down.6We use the average DemVoteShareit,
and choose the average value of γi, thereby averaging the block group intercepts. We leave
out ωtthereby constructing a value that corresponds to the year 2006, the omitted category.
Results are shown in Figure 5.
A.6 Eﬀect in areas experiencing prior wildﬁres
As suggested by a reviewer, it would be desirable to know if the eﬀect varies depending on the
degree of prior exposure to wildﬁre. Because wildﬁres are statistically rare, the proportion of
places with multiple ﬁres is very small; among more than 22000 block groups included in our
6. In fact, the dose-response curve is equivalent to Figure 1, but vertically shifted by the response at the
median distance (the ﬁnal category, 35-40km).
Figure 5: Dose-response curve showing expected level of support for environmental intiatives
as a function of distance to nearest wildﬁre burning over 5000 acres. To produce these
estimates, the year is set to 2006, and the block group intercept shift is given by the average
block group ﬁxed eﬀect. Error bars show 99% conﬁdence intervals with standard error
estimates clustered on block group.
study, only 293 experienced a wildﬁre prior to the 2005-2006 electoral cycle. Repeating the
distance-based analysis in just these unit, Figure 6 shows that units that experienced prior
ﬁres may have a weaker response, though as expected the estimates are much less precise in
this reduced sample.
A.7 Placebo outcome: Support for housing bonds
Finding a suitable placebo outcome requires constructing an outcome from ballot measures
that (i) repeat a similar proposal across multiple years, and (ii) for which we expect little to
no eﬀect of wildﬁre, so that any estimated eﬀect of wildﬁre we ﬁnd most likely reveals bias
and not a true eﬀect. A particular concern of the latter type is that wildﬁres, as a source of
threat, may make people broadly more conserative in their thinking (see e.g. Jost et al. 2003;
Nail et al. 2009). This rules out many measures as useful placebos.
However, in an earlier project we had deemed one set of measures as having the least
Figure 6: Eﬀect estimate at varying distances for only the 293 units that experienced wild-
ﬁres prior to the electoral cycles used for form these estimates. Regression model controls
for Democratice vote share, precipitation in prior two years, and two year deviation from
ideological content: support for housing bonds as measured in Proposition 46 in 2002, and
Proposition 1C in 2006. Coding the outcome for both so that support is more positive,
we replicate the identical model to Equation 1 above but replacing the outcome variable
(environmental support) with the outcome for the housing measures. In that model we see
no detectable relationship between wildﬁre and support for housing bonds with a coeﬃcient
of only 0.2 percentage points (t-stat=-0.55, p=0.58, 95% CI: [-1.0, 0.58] percentage points).
A.8 Population density
Population density and Democratic vote share are strongly correlated (r= 0.35) in the
complete data. However conditioning on localities where wildﬁres occur, for example, breaks
this relationship (r=−0.001,p= 0.98). This may seem surprising but is to be expected.
Places with wildﬁre will have a certain distribution of population densities, strongly skewed
towards the lower density areas. This distribution of densities should look the same, however,
−15 −10 −5
0.0 0.1 0.2 0.3 0.4 0.5 0.6
most Republican with fires
most Democratic with fires
Figure 7: Distribution for the (log) population density, for all areas (solid lines) or for those
experiencing a wildﬁre (dashed line). For all locations, the distribution varies by Democratic
votes share (red vs. blue solid lines), with Democratic areas (blue) tending to have higher
density. For areas with wildﬁres however, the distributions of population density are similar
for more Republican and more Democratic areas (red vs. blue dashed lines), with the small
remaining diﬀerence pointing towards Democratic areas having slightly lower population
density (not signiﬁcant as a correlation).
whether we are examining more Democratic or more Republican areas. That is to say once
a ﬁre “knows” the population density of an area, it is unconcerned with whether it is more
Republican or Democratic.
Figure 7 shows this graphically. Looking at all block groups (whether they have ﬁres
or not) the relationship between Democratic vote share and density is strong, as expected.
But among block groups with wildﬁre (dashed lines), the relationship disappears entirely,
with the distribution of population densities for places (with wildﬁre) being nearly the same
regardless of party preference. The small remaining diﬀerences, which we expect are due
to chance, happen to produce slightly lower average density among the Democratic areas,
hence the small negative correlation.
Recalling that our estimates are driven by locations with wildﬁres (for example, the ﬁxed
eﬀect estimate depends only on locations that change wildﬁre status, which are places with
at least one wildﬁre), and that population density is almost unchanging within each location.
Hence, by conditioning on locations with wildﬁre, we are removing the relationship between
Democratic vote share and population density. Population density is thus not an explanation
for the diﬀerent eﬀects we ﬁnd by Democratic vote share in Figure 2.
This does not prohibit variation in population density from having an independent in-
ﬂuence on the eﬀect size. Figure 8 expands upon the analysis by taking the most and least
Democratic groupings and splitting them into the most and least population dense areas.
This ﬁnds weak evidence that among the most Republican areas, more dense areas may have
stronger eﬀects at some distances; there is very little indication of any such diﬀerence within
(a) Most Republican (b) Most Democratic
Figure 8: Eﬀect estimate at varying distances for block-groups with 20-40% Democratic vote
share (left) and 60-80% Democratic vote share (right), each now split into the most and least
population dense quartiles. Underlying regression model controls for precipitation in prior
two years, and two year deviation from historical precipitation as well as the two-way ﬁxed
A.9 Eﬀect of wildﬁre on turnout
We examine here whether wildﬁre has an eﬀect on turnout, and whether this is suﬃcient to
explain changes in support simply through the addition (or subtraction) of voters.
Continuing to assume an absence of time-varying confounders, we can estimate the eﬀect
of wildﬁre on turnout by the same approach used to estimate the eﬀect of wildﬁre on support,
changing only the outcome. We thus regress turnout on indicators for distances to wildﬁre
as above, intercepts for each census block group and for each time period, and (optionally)
including the two preciptation variables. As shown in Figure 9, the results suggest that
wildﬁre increases turnout by approximately 3 percentage points for distances of up to 25km.
This is a relatively large and politically relevant eﬀect in substantive terms, making this
another ﬁnding of interest to political scientists. For present purposes however, it also
suggests that the eﬀect of wildﬁre on support for ballot initiatives cannot be generated
solely by newly mobilized voters after wildﬁres, since the eﬀect of wildﬁre on support at each
distance exceeds the eﬀect on turnout several-fold. Of course, it does remain possible that
wildﬁre’s eﬀect occurs at least partially through changes in the composition of voters rather
than just “added voters”.
Figure 9: Estimated eﬀect of wildﬁre on turnout in the following election, at each distance
from the nearest wildﬁre that burned at least 5000 acres in the prior two years, relative to
the media distance. Error bars show 99% conﬁdence intervals with standard errors clustered
on block group.