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Although lawn signs rank among the most widely used campaign tactics, little scholarly attention has been paid to the question of whether they actually generate votes. Working in collaboration with a congressional candidate, a mayoral candidate, an independent expenditure campaign directed against a gubernatorial candidate, and a candidate for county commissioner, we tested the effects of lawn signs by planting them in randomly selected voting precincts. Electoral results pooled over all four studies suggest that signs increased advertising candidates’ vote shares. Results also provide some evidence that the effects of lawn signs spill over into adjacent untreated voting precincts.
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The effects of lawn signs on vote outcomes: Results from four
randomized eld experiments
Donald P. Green
, Jonathan S. Krasno
, Alexander Coppock
, Benjamin D. Farrer
Brandon Lenoir
, Joshua N. Zingher
Columbia University, USA
Binghamton University (SUNY), USA
Knox College, USA
High Point University, USA
Old Dominion University, USA
article info
Article history:
Received 8 July 2015
Received in revised form
28 October 2015
Accepted 15 December 2015
Available online 25 December 2015
Although lawn signs rank among the most widely used campaign tactics, little scholarly attention has
been paid to the question of whether they actually generate votes. Working in collaboration with a
congressional candidate, a mayoral candidate, an independent expenditure campaign directed against a
gubernatorial candidate, and a candidate for county commissioner, we tested the effects of lawn signs by
planting them in randomly selected voting precincts. Electoral results pooled over all four studies suggest
that signs increased advertising candidatesvote shares. Results also provide some evidence that the
effects of lawn signs spill over into adjacent untreated voting precincts.
©2015 Elsevier Ltd. All rights reserved.
1. Introduction
Lawn signs are one of the few campaign tactics deployed by
candidates for every level of government in the United States.
Inexpensive and relatively easy to deploy, lawn signs are a tactic
available to even the most obscure and underfunded candidate for a
down-ballot ofce. Indeed, the eforescence of roadside lawn signs
is often one of the few outward manifestations of a low-salience
Although campaign tactics ranging from door-to-door
canvassing to robotic phone calls have been evaluated by a vast
array of eld experiments conducted during the past fteen years
(for summaries of this literature, see Green and Gerber (2015),
Bedolla and Michelson (2012), and Green et al. (2013)), lawn
signs have largely escaped scholarly attention. Panagopoulos
(2009) nds that hand-held placards announcing Election Day
promote voter turnout, but hand-held placards involve a human
element that lawn signs lack, and non-partisan encouragements to
vote are different from efforts to build vote support for a candidate.
Current understanding of lawn signs derives largely from campaign
how-to guides, which offer anecdote-driven recommendations
from campaign professionals and candidates. However, these
guides are equivocal on the question of whether lawn signs are
effective. For example, The Political Campaign Desk Reference rec-
ommends planting signs as early as local election laws allow
(McNamara, 2012, p. 171), whereas Blodgett et al. (2008) dismiss
lawn signs as ineffective on the grounds that they do nothing to
persuade undecided voters (p. 130). Shaw (2009) describes a
number of campaigns that supposedly used lawn signs to great
effect but concedes that You never know what will work(p. 152).
The present study represents the rst rigorous evaluation of the
effectiveness of lawn signs. Working in collaboration with four
campaigns in different electoral contexts, we tested the effects of
lawn signs by planting them in randomly selected voting precincts.
The paper begins by describing the theoretical mechanisms by
which lawn signs are hypothesized to affect vote choice and how
those mechanisms may vary by electoral context. We then explain
the experimental design and its implications for statistical analysis.
We estimate a statistical model that allows for both direct exposure
The data and replication scripts for these experiments will be made available at The authors are grateful to David Frazier,
David Kirby, Brian Parvi, Aaron Ricks, Maoz Rosenthal, Kyle Seeley, and M. Steen
Thomas, who made possible the experiments we report.
*Corresponding author.
E-mail address: (D.P. Green).
Contents lists available at ScienceDirect
Electoral Studies
journal homepage:
0261-3794/©2015 Elsevier Ltd. All rights reserved.
Electoral Studies 41 (2016) 143e150
to signs in targeted voting precincts and indirect exposure to signs
in adjacent voting precincts. Although no single experiment is
conclusive statistically, electoral results from all four studies taken
together suggest that the signs signicantly increased advertising
candidatesvote margins. Results also indicate that the effects of
lawn signs spill over into adjacent untreated voting precincts.
Working within a Bayesian learning framework, we show that even
an initial skeptic would update her views in light of these four
2. Theoretical backdrop
Researchers have long observed that electoral outcomes are
correlated with exposure to signs (Kaid, 1977; Sommer, 1979). The
literature on campaign effects offers at least three theoretical rea-
sons for thinking that this relationship is causal, in other words,
that lawn signs increase the share of the vote won by the adver-
tising candidate.
In the context of low-salience elections or relatively unknown
candidates, lawn signs may help build name recognition. Recent
experiments suggest that mere exposure to candidates' names in-
creases their popularity among voters (Kam and Zechmeister,
2013), although the effect of mere exposure seems to dissipate
when voters are provided with other relevant information, such as
candidates' occupation or incumbency status. Indeed, Kam and
Zechmeister's quasi-experimental test of lawn signs on behalf of a
ctitious candidate for city council is the only study we are aware of
that directly assesses the effects of lawn signs on vote preference;
they nd that signs conveying only the candidate's name had a
large effect on vote intentions expressed in a survey they conducted
at the start of a low-salience election campaign (p.13). One testable
implication of the name recognition hypothesis is that signs should
have weaker effects in high-salience races, where name recognition
is widespread. This hypothesis suggests that we should expect to
nd weaker effects of signage in a hard fought governor's election
than in contests for lower ofce.
A second hypothesis is that the presence of signs is interpreted
as a signal of candidate quality or viability (Krasno, 1994). Lawn
signs suggest to voters that the advertising candidate's campaign
has the resources and stafng necessary to purchase and deploy
signage. Such costly signals are thought to inuence vote choice
(Potter and Gray, 2008) by creating bandwagon effects akin to those
set in motion by pre-election polls (Ansolabehere and Iyengar,
1994). These signaling effects are thought to be especially strong
when signs are displayed on private property because voters are
inuenced by their neighbors' candidate endorsements (Huckfeldt
and Sprague, 1992).
Finally, signs may convey information that guides vote choice.
Three of the four signs described below used text and graphics to
convey the ideological location or partisan afliation of the
advertising candidate. In electoral contexts where voters know
relatively little about the candidates, such cues may have strong
effects on vote choice (Mann and Wolnger, 1980; Popkin, 1994).
For example, in their experimental study Schaffner and Streb
(2002) found that surveys that merely included candidatesparty
afliations profoundly affected the distribution of vote preferences,
as this cue allowed respondents to better express their own party
preferences. Our theoretical predictions concerning the mecha-
nisms at play in each of the four experiments are summarized in
Table 1.
Are there theoretical reasons to be skeptical about the effects of
lawn signs? Two important caveats are suggested by the literature
on vote choice. First, lawn signs represent an impersonal mode of
campaign communication akin to direct mail or automated phone
calls, the persuasive effects of which have occasionally proven to be
signicant (Gerber, 2004; Rogers and Middleton, 2012) but have
just as often proven to be limited (Cardy, 2005; Shaw et al., 2012;
Cubbison, 2015). Second, the effects of signage may decay during
the time that elapses between exposure and the expression of vote
preference. The campaigns described below deployed signs in
residential precincts, not immediately outside polling locations. To
the extent that information diminishes in salience or is forgotten
altogether, the effects of signage may fail to manifest themselves in
the actual vote tally.
Taken together, these competing hypotheses offer compelling
reasons for believing either that lawn signs work or that they do
not, divergent conjectures reected in the campaign manuals cited
above. After presenting the results of our four experiments, we will
return to these prior beliefs about the efcacy of lawn signs and
update the views of optimists, skeptics, and agnostics in light of the
3. Experimental design
The unit of analysis in each of the experiments was the voting
precinct. Voting precincts are the lowest level of aggregation at
which voting choices are made public, so the effects of the lawn
signs on voterspolitical preferences can be measured directly.
Because voting precincts are relatively contained geographic areas,
the residents of a precinct can be thoroughly exposed to a large
dose of signs. Our design faced two relatively minor complications.
First, in Experiments 1, 2, and 4, some districts were designated
either as must-treator untreatable.Because these units could
not be randomly assigned to treatment conditions, they are
excluded entirely from our analyses. Second, in Experiments 1 and
4, we encountered some failure-to-treat: some units assigned to get
lawn signs did not receive them. We will conduct all analyses ac-
cording to treatment assignment, not treatment receipt.
Experiment 1 took place across two counties in upstate New
York containing a total of 97 voting precincts, 88 of which were
treatable. In Experiment 2, our initial sample size was 128 precincts
in the City of Albany. However, because some precincts were
regarded by the campaign as must-treatlocations, our experi-
ment was restricted to 69 precincts. Experiment 3 took place in 5 of
9 Fairfax County, Virginia districts, comprising a total of 131 pre-
cincts. Experiment 4 was conducted in 88 of Cumberland County,
Pennsylvania's 107 voting precincts, as the remainder were desig-
nated as untreatableby the campaign.
In all four experiments, precincts were assigned to treatment
conditions using restricted randomization (Morgan and Rubin,
2012). In order to address the issue of spillover, whereby voters
in one voting precinct are exposed to experimental lawn signs in a
neighboring precinct, the randomization protocol ensured that two
neighboring precincts could not be assigned to direct treatment at
the same time. The precise algorithm used to allocate treatment
assignments to units was different for each of the four experiments;
the Albany, Virginia, and Pennsylvania experiments also included
covariate information in the randomization protocols in order to
increase statistical power. These procedures induced differential
probabilities of assignments. For example, centrally located pre-
cincts are less likely to be directly treated.We address the statistical
complications of differential treatment probabilities by including
inverse probability weights. For complete descriptions of the
Our estimates therefore gauge the intent-to-treat effect, or the effect of
assigned (rather than actual) treatment (see Gerber and Green (2012, Chapter 5)).
The discrepancy between actual and assigned treatment is small, and therefore the
intent-to-treat effect understates the average treatment effect only by a factor of
22/23 ¼0.96 in Experiment 1 and 17/20 ¼0.85 in Experiment 4.
D.P. Green et al. / Electoral Studies 41 (2016) 143e150144
restricted randomization procedure used in each experiment, see
the appendix. The number of precincts in each condition in each
experiment is summarized in Table 2.
Our experimental treatments differed along two dimensions:
content and placement. Below we describe the signs and the
manner in which they were deployed (See Fig. 1).
3.1. Experiment 1: treatment
The lawn sign used in Experiment 1 was designed to be con-
ventional in all respects. The size and shape were the standard
18 24 inch rectangle. The colors were white type on a blue
background, which is a common format, especially for Democrats.
The candidate's last name commanded the largest font. Somewhat
smaller font was used for his rst name and the word Congress,
which appeared in blue type on a white background. The bottom of
the sign gave the candidate's campaign website. The sign contained
no graphics or photos.
Signs were deployed by researchers working with the campaign
two weekends prior to Election Day. When planting the lawn signs
in the treatment precincts, the guiding principle was to hew closely
to the procedures used by actual campaigns. This meant searching
for locations where the signs were likely to be seen by as many
potential voters as possible. Upon arriving in a treatment precinct,
the campaign team looked for public land around the largest in-
tersections and busiest roads. Given the paucity of public land in
some precincts, the team frequently placed clusters of signs -
usually around four or ve - in these high-prole locations. When
the most prominent areas had been treated with clusters of signs,
the team continued to place clusters of signs in other high-visibility
public locations until the allocation of 40 signs was exhausted. One
precinct assigned to treatment was not actually treated because the
campaign team could not nd any suitable roads on which to plant
3.2. Experiment 2: treatment
This experiment also used a conventional lawn sign. The size
and shape were the standard 18 24 inch rectangle. The colors
were white type on a blue and green background. The candidate's
last name is displayed in large type face with Democrat for Mayor
below in smaller font. No further information was included on the
An important difference between Experiment 2 and the other
experiments concerns the distribution of signs. In this study, signs
were given to supporters residing in treatment locations to display
on their own private lawns. This distinction is important for the
interpretation of the results, as signs planted on private land may
convey an endorsement by the landowner, whereas signs planted
by campaign workers do not necessarily imply support by local
residents. The signs in this campaign were placed by residents
during the last four weeks of the election.
3.3. Experiment 3: treatment
The sign used in the Virginia experiment was quite different eit
was a negative sign attacking an opponent rather than a positive
sign supporting a candidate. Moreover, the sign was visually
arresting, as it mimicked a For Salesign commonly used for
selling automobiles or houses. The text of the sign read: For Sale:
Terry McAuliffe. Don't Sellout Virgina [sic] on November 5.A
notice at the bottom indicated that the sign was Paid for by
FreedomWorks for America and not authorized by any candidate or
candidates' committee. FreedomWorks for America e202-942-
7642. The sign was designed to highlight the fact that the opposing
candidate was Democratic fundraiser before becoming a candidate
for higher ofce.
Three weeks prior to the election, the signs were placed in
clumps of ve in three locations within each treatment precinct.
Signs were successfully planted in all assigned treatment locations.
We were able to verify the exact placement of signs because the
volunteers placing them were instructed to take geotagged photos
of the clumps of signs with their smartphones.
3.4. Treatment: experiment 4
The sign used in Pennsylvania promoted two candidates for
County Commissioner: Gary Eichelberger and Rick Schin. It was
headlined, The Conservative Teamand featured an elephant
graphic to signal the candidatesRepublican afliation, though the
word Republicanis not on the sign. A total of 200 signs were
planted in the two weeks prior to election day by a campaign
worker. We encountered some failure-to-treat: three precincts
selected for treatment did not receive signs. We nevertheless
analyze the experiment according to the randomly assigned
treatments, ignoring noncompliance altogether.
4. Statistical model
One of the core assumptions required for unbiased causal
inference is the stable unit treatment value assumption (Rubin,
Table 1
Expected mechanisms.
Study Election context Election closeness Salience Sign type Expected mechanism
Experiment 1 General Contested Medium Road Sign Signs signal name recognition and viability
Experiment 2 Municipal Primary Landslide Low Yard Sign Signs signal name recognition, partisan endorsement, and support among neighbors
Experiment 3 General Toss up High Road Sign Signs signal ideological cues
Experiment 4 County Primary Contested Low Road Sign Signs signal name recognition, viability, and ideological cues
The sign used in Experiment 1 does not mention party or ideology, only the candidate's name. We expect that the sign operates primarily through the viability channel,
though given the medium salience of the election, it may also increase name recognition. In Experiment 2, the sign was planted in supporters' yards and mentioned the
candidate's name, party, and ofce sought. We expect the main mechanism triggered by the sign is the support among neighbors signal, though name recognition and party
endorsement may also be at work. The sign used in Experiment 3 was designed to mimic signs used for house or garage sales, suggesting that the advertising candidate's
opponent was For Sale.This sign primarily signals ideology. In Experiment 4, the sign displayed the candidates' names and ofce sought, with the text The Conservative
Team,including no direct mention of party beyond a graphic depicting an elephant. Given the low salience of the election, we expect that the sign operates through the name
recognition channel, though it may also signal viability and ideology.
Table 2
Treatment assignments.
Study Control Adjacent Treated Total
Experiment 1 16 49 23 88
Experiment 2 13 41 15 69
Experiment 3 25 76 30 131
Experiment 4 24 44 20 88
D.P. Green et al. / Electoral Studies 41 (2016) 143e150 145
1986), which implies that subjects are affected solely by the
treatment to which they are assigned; treatments assigned or
administered to others are assumed to be inconsequential. This
assumption is jeopardized when treatments spillover as the result
of communication or contagion. Because lawn signs can be seen by
anyone who passes by, untreated precincts may be affected by the
treatments that neighboring precincts receive. In effect, there may
be potential outcomes other than treatedand untreated; some
precincts may be partially treated. To reestablish stablepotential
outcomes, we must develop a model of potential outcomes that
includes this intermediate case.
Let Y
(d) be the potential outcome of each precinct i, where
dindicates one of three possible inputs: direct treatment with lawn
signs, indirect treatment because lawn signs have been planted in
an adjacent precinct, and no treatment. Following the language of
Aronow and Samii (2013), we are implementing an exposure model
in which the potential outcomes of each precinct can take on only
one of three values. Y
(d) is called a potential outcome because it is
the outcome that a precinct would manifest if it were to receive the
input d. Only one of the three potential outcomes is actually
observed, depending on the actual deployment of lawn signs; the
other two potential outcomes remain unknown. Nevertheless, we
can dene the causal effect of direct treatment versus no treatment
for each precinct as Y
(none) and the causal effect of
spillover treatment versus no treatment for each precinct as
(none). Although these precinct-level causal effects
cannot be observed or estimated, we may dene and estimate two
average causal effects across all precincts. The rst is the average
treatment effect of direct treatment versus control (i.e., the direct
treatment effect). The second is the effect of adjacency versus
control (i.e., the spillover effect).
Recovering these estimands from our experiment is complicated
by the fact that voting precincts have varying probabilities of
assignment to treatment and to adjacency-to-treatment. As dis-
cussed in Gerber and Green (2012, chapters 4 and 8), when
assignment probabilities vary, the effect of treatment cannot be
recovered using a comparison of unweighted average outcomes.
For example, comparing the average vote margin in precincts
assigned to receive the treatment to the average vote margin in
precincts assigned to the non-adjacent control group yields biased
and inconsistent estimates of the average effect of lawn signs. An
asymptotically unbiased estimation approach reweights the data
before computing group averages (see Gerber and Green, 2012,
chapter 3). The weight for each observation in experimental group
d2fdirect;spillover;nonegis the inverse of the probability of it
being assigned to group d. (Observations with probabilities of zero
or one, i.e., the untreatable or must-treat precincts, are necessarily
excluded.) When using regression to estimate average treatment
effects, we use weighted least squares rather than ordinary least
Our basic regression model is equivalent to comparing weighted
where Y
is candidate vote share, D
is an indicator variable scored
1 if the voting precinct is assigned to lawn signs, D
is an indicator
variable scored 1 if the voting precinct is adjacent to a precinct
assigned to lawn signs, and u
is the unobserved disturbance term.
represents the average effect of direct treatment
(compared to no direct or indirect treatment), and
represents the
average effect of spillover from an adjacent treatment (compared to
Fig. 1. Signs.
D.P. Green et al. / Electoral Studies 41 (2016) 143e150146
no direct or indirect treatment).
In order to improve the precision with which these causal pa-
rameters are estimated, we augment our regression model to
include covariates that are expected to be predictive of vote out-
comes. Different sets of covariates were available in each experi-
ment. We strove to include results from past elections of the same
type where possible (i.e., past congressional elections in Experi-
ment 1, a past mayoral election in Experiment 2, etc.) in addition to
past presidential vote margin. In Experiment 2, we also included
the campaign's measure of the number of registered Democrats in
each precinct. The full list of covariates used in each experiment is
listed at the foot of results tables below.
Equation (2) shows the covariate-adjusted specication used in
Experiment 1. The covariates included the vote margin for Barack
Obama in the 2008 presidential election (V
) and for the
Democratic congressional candidates in the 2006, 2008, and 2010
elections (V
, and V
The regression coefcients for the covariates (
, and
have no causal interpretation; the reason to include these cova-
riates is to reduce disturbance variability and eliminate chance
imbalances among experimental groups. The results below indicate
that these covariates were highly predictive of outcomes in
Experiment 1 and greatly improve the precision with which the
direct treatment and spillover effects are estimated. Covariates also
proved to be highly prognostic of outcomes in Experiment 3, which
also took place in a general election. Because the standard errors in
Experiments 1 and 3 are so much smaller after controlling for
covariates, our interpretation focuses primarily on the covariate-
adjusted estimates. In Experiments 2 and 4, the covariates were
less predictive of outcomes and do little to improve the precision of
our estimated treatment effects. We nevertheless focus our atten-
tion on the covariate-adjusted estimates when interpreting our
results and summarizing all four studies via xed-effects meta
When conducting hypothesis tests, we will focus exclusively on
randomization-based tests of the joint hypothesis of no direct or
indirect effects. The procedure is similar in all four experiments. We
rst obtain an observed F-statistic based on Equation (2), where the
restricted model constrains
to both equal zero. We then
simulate the distribution of this F-statistic under the sharp null
hypothesis of no effect by recomputing the F-statistic under 10,000
possible (restricted) random assignments. Our p-value reects the
proportion of random assignments in which the simulated F-sta-
tistic exceeds the observed F-statistic.
5. Results
5.1. Experiment 1: results
Table 3 shows the weighted regression estimate of the effects of
direct and indirect treatment using the regression specications in
Equations (1) and (2). Without covariates, the estimated effect of
direct treatment on vote share is 2.5 percentage points (robust
SE ¼2.7), and the estimated spillover effect is 3.7 percentage points
(robust SE ¼2.7). The estimates sharpen considerably when the
regression model is augmented with past vote outcomes as cova-
riates. The estimated effect of direct treatment remains 2.5 per-
centage points, but the standard error falls sharply (robust
SE ¼1.7). The estimated spillover effect decreases to 1.8 percentage
points, and its standard error falls to 1.6 percentage points. Using
randomization inference, we fail to reject the joint null hypothesis
of no direct or indirect effects (p¼0.22). The results suggest that the
signs exerted a direct treatment effect, although the effect falls
short of conventional levels of statistical signicance. The estimates
also provide some tentative evidence of spillovers from treated to
adjacent precincts.
5.2. Experiment 2: results
The Albany signs campaign was expected to produce especially
large effects, as the signs themselves were planted in supporters
yards rather than along public roadways. The statistical results,
however, turned out to be murky (Table 4). Without adjustment,
the signs appeared to increase vote share for Sheehan by 0.9 per-
centage points, but with adjustment, appeared to decrease her vote
share by 1.4 points. Ironically, controlling for covariates increases
our estimated standard errors. In either model, the standard errors
are so large that we come away without a clear sense of the average
treatment effects. Evidently, precinct-level studies in primary
elections require a much larger population of precincts because one
cannot rely on covariates to improve precision. The randomization
inference test of the joint hypothesis of no direct or indirect effect
yields a p-value of 0.90.
Table 3
Impact of lawn signs on vote share (Experiment 1).
Vote share
Model 1 Model 2
Assigned lawn signs (n ¼23) 0.025 (0.027) 0.025 (0.017)
Adjacent to lawn signs (n ¼49) 0.037 (0.027) 0.018 (0.016)
Constant 0.390 (0.020) 0.015 (0.031)
Covariate adjustment No Yes
0.031 0.823
Covariates: congressional vote margin 06, 08, 10 and presidential vote margin 08.
Standard errors in parentheses.
Table 4
Impact of lawn signs on vote share (Experiment 2).
Vote share
Model 1 Model 2
Assigned lawn signs (n ¼15) 0.009 (0.054) 0.014 (0.057)
Adjacent to lawn signs (n ¼41) 0.012 (0.046) 0.004 (0.045)
Constant 0.659 (0.039) 0.287 (0.131)
Covariate adjustment No Yes
0.001 0.253
Covariates: registered democrats and mayoral vote margin 05 and 09. Standard
errors in parentheses.
Table 5
Impact of lawn signs on vote share (Experiment 3).
Vote share
Model 1 Model 2
Assigned lawn signs (n ¼30) 0.042 (0.016) 0.018 (0.009)
Adjacent to lawn signs (n ¼76) 0.042 (0.013) 0.018 (0.007)
Constant 0.302 (0.011) 0.780 (0.025)
Covariate adjustment No Yes
N 131 131
0.094 0.825
Covariates: gubernatorial vote margin 09 and presidential vote margin 12. Stan-
dard errors in parentheses.
D.P. Green et al. / Electoral Studies 41 (2016) 143e150 147
5.3. Experiment 3: results
Table 5 reports the results of the anti-McAuliffe sign campaign.
To maintain consistency, we report the effects of the signs on the
vote share of McAuliffe's opponent, Ken Cuccinelli. The results
suggest, as expected, that the signs increased Republican vote
shares. The inclusion of covariates reduces the estimated standard
errors substantially, so we focus on those estimates. Cuccinelli's
vote share increased by 1.8 percentage points in treated precincts
and 1.8 percentage points in adjacent precincts. A randomization
inference test of the joint null hypothesis that neither direct nor
adjacent signs affected outcomes generates a p-value of 0.02.
5.4. Experiment 4: results
We expected that signs would be especially effective in the
Pennsylvania experiment, as name recognition of the candidates
was thought to be low.However, focusing on the covariate-adjusted
estimates in Table 6, directly treated precincts saw 1.2 percentage
points lower vote share for Eichelberger and Schin; indirect treat-
ment decreased vote share by 2.0 points. The standard errors
associated with both estimates are quite large because covariates
again fail to predict outcomes in this primary election. The
randomization inference test shows that we cannot reject the null
hypothesis no direct or indirect effects (p¼0.77).
5.5. Effects on turnout
We nd that lawn signs had essentially no effect on turnout.
Pooling the covariate-adjusted estimates according to Equation (3)
below, we nd that direct effect of lawn signs on total votes cast in a
precinct was 7.2 votes, with a standard error of 9.5 votes. We
interpret this null nding on turnout to mean that any positive
impact on vote share operates primarily though a persuasion
mechanism, not through mobilization.
6. Bayesian integration
Considered separately, each of the four experiments provides
equivocal evidence about the effects of lawn signs. That is not
surprising, given that each study is somewhat underpowered due
to the fact that relatively few precincts end up in the pure control
group after we allow for possible spillover effects from treated
precincts to adjacent precincts. One way to address the lack of
power, however, is to conduct a series of replication studies and to
pool the results.
This approach presupposes that the average of the
effects across the four studies is a quantity of interest. If, however,
the effects differ systematically depending on electoral context,
then this average might mask theoretically relevant variation. In
this analysis, we set aside differences in electoral context and fea-
tures of the signs themselves in order to answer the overarching
question of how well signs typically work across elections like the
four we have studied.
In order to estimate the pooled average treatment effect, we
conducted a xed-effects meta-analysis of the four studies
(Borenstein et al., 2009). This estimator is equivalent to the
precision-weighted average of the four estimated direct treatment
effects, where precisionin this context refers to the inverse of the
squared estimated standard error. Let the estimated standard error
of the jth study be denoted
; the weights are W
, and the
precision-weighted average of the four estimated average treat-
ment effects,
As shown in Table 7, the pooled estimate of average effect of
lawn signs in directly treated precincts is 1.7 percentage points,
with a standard error of 0.7 percentage points. The corresponding
pooled estimate for the average effect of adjacency is 1.5 percentage
points, with a standard error of 0.6 percentage points. It appears
that signs on average raise vote shares by just over one percentage
In order to quantify what one learns from this succession of four
studies, Fig. 2 traces the process by which three different observers
update their priors in light of the experimental evidence (Gill,
2002; Hartigan, 1983). The leftmost density plots display the
priors of an agnostic observer (row 1), an observer whose priors
make her optimistic about the effects of signs (row 2), and an
observer whose priors make her skeptical about the effects of signs
(row 3). The agnostic and the optimist are assumed to have diffuse
priors whose standard deviations are 5 percentage points, whereas
the skeptic's prior has a standard deviation of 1 percentage point,
reecting her condence that lawn signs have negligible effects.
Moving from left to right, the density plots show how these priors
evolve in the wake of each successive experiment. The rightmost
plots in each row show the posterior distributions for each
observer. Although the three observers' posteriors differ, they do
not differ by much; the experimental evidence has largely dis-
placed the prior views that these observers in advance of these
studies. The agnostic observer (row 1), concludes that there is a
98.8 percent chance that lawn signs increase the vote share of the
advertising candidate. The optimistic observer (row 2) puts this
probability at 0.991, and even the initial skeptic (row 3) concludes
that this probability is 0.966. Whichever prior view comes closest
to the reader's own priors, it seems apparent that the experimental
evidence contributes importantly to the posterior sense of the ef-
cacy of lawn signs, even if questions remain about the conditions
under which the effect tends to be larger or smaller.
7. Conclusion
Unlike prior research on lawn signs, which mainly described the
correlation between election outcomes and the prevalence of
Table 6
Impact of lawn signs on vote share (Experiment 4).
Vote share
Model 1 Model 2
Assigned lawn signs (n ¼20) 0.013 (0.028) 0.012 (0.026)
Adjacent to lawn signs (n ¼44) 0.023 (0.022) 0.020 (0.021)
Constant 0.548 (0.017) 0.532 (0.082)
Covariate adjustment No Yes
0.012 0.172
Covariates: gubernatorial vote margin 02, 06, 10 and presidential vote margin 00,
04, 08. Standard errors in parentheses.
Table 7
Meta-analysis: pooled vote share results.
Direct Direct SE Indirect Indirect SE
Experiment 1 0.025 (0.017) 0.018 (0.016)
Experiment 2 0.014 (0.057) 0.004 (0.045)
Experiment 3 0.018 (0.009) 0.018 (0.007)
Experiment 4 0.012 (0.026) 0.020 (0.021)
Pooled results 0.017 (0.007) 0.015 (0.006)
We do note, however, that the analytic choice to pool the results was not
specied ex ante in our preanalysis plans.
D.P. Green et al. / Electoral Studies 41 (2016) 143e150148
signage, this paper attempts to assess the causal effect of signs on
election outcomes using a randomized experimental design. Ex-
periments in which geographic units are the unit of assignment
present some special technical challenges insofar as random
assignment procedures require the use of GIS shapelesand
analytic tools. In order to assist researchers seeking to conduct this
type of research, we have made our data and accompanying code
available in the Supplemental materials.
Experiments of this type also present special estimation chal-
lenges given the possibility that the effects of signage spill over
from treated precincts to neighboring precincts. Unbiased estima-
tion requires the researcher to take account of the probability that
each precinct is exposed to spillovers, which in turn requires
simulating large numbers of possible random assignments. When
estimating spillover effects, we have taken a cautious design-based
approach, relying as much as possible on decisions made at the
design stage rather than on modeling choices made after results
have been obtained. Our randomization procedure assigned units
to two levels of treatment: precincts that receive signs and adjacent
precincts that otherwise are untreated. More gradations of spill-
overs are possible (e.g., adjacent to adjacent to treated), as are
precinct linkages that are guided by topography or road networks
rather than adjacency. These are directions for future work.
Although this series of experiments leaves many questions
unanswered, it is also apparent that the new evidence represents
an important advance over the conjectures that previously domi-
nated the discussion of campaign signs. Pooling over the four ex-
periments, it appears that signs typically have a modest effect on
advertising candidatesvote shares ean effect that is probably
greater than zero but unlikely to be large enough to alter the
outcome of a contest that would otherwise be decided by more
than a few percentage points. This nding puts lawn signs on par
with other low-tech campaign tactics such as direct mail that
generate reliable persuasion effects that tend to be small in
magnitude (Gerber, 2004).
From a theoretical standpoint, these ndings shed light on the
conditions under which voters are swayed by campaign commu-
nication. Clearly, further experimentation is needed to rene our
understanding of causal mechanisms, but for now we advance
some tentative conclusions. First, although signs may promote
name recognition, this mechanism does not seem to be a necessary
condition for signs to exert an effect on vote shares. Signs seem to
have been effective in the Virginia gubernatorial election, where
levels of name recognition were quite high, party cues were
abundant, and where the signs mentioned only the name of the
opponent. Second, signs do not seem to be especially effective
when they provide partisan or ideological cues. Signs appear to
have had weak effects in Pennsylvania, where ideological labels
were used, and Albany, where party labels were used. Conversely,
the congressional candidate in New York seemed to benet from
signs that made no mention of his party or ideology. Third, our one
test of yard signs found weak effects, suggesting that the cues from
neighbors failed to generate meaningful bandwagon effects. The
remaining hypothesis is that signs work because they signal
viability. The evidence here is ambiguous because all four signage
campaigns could be said to signal viability. Future investigation of
this causal mechanism might assess whether signs deployed near
polling places work especially well when randomly accompanied
Fig. 2. Bayesian integration of four lawn signs experiments.
Considering only the direct effect, we estimate the cost per vote across all four
experiments to be $3.18, with a 95% condence interval extending from $1.70 to
$13.71. This gure is calculated from total turnout (241,613), the direct effect (1.7
points), and the total cost ($13,045): $13,045/(241,613 * 0.017) ¼$3.18. If we include
indirect effects in this calculation, the cost per vote drops to $1.69.
D.P. Green et al. / Electoral Studies 41 (2016) 143e150 149
by signs in other areas of the same precincts, the latter signaling
substantial campaign effort and resources.
By conducting a series of experiments in different settings, we
have also sought to address questions of generalizability that
inevitably arise due to the many ways in which signseffects may
interact with features of the electoral context. Each of our studies
generated estimated average treatment effects that fall within the
margin of sampling variability of the other studies, suggesting that
meaningful systematic variation in treatment effects across con-
texts may be limited. Still, it remains to be seen whether the pattern
of results we obtained hold up when experiments are conducted
other contexts. Additionally, future experiments should be con-
ducted at a much larger scale, so that both average and heteroge-
neous effects can be estimated with greater precision. Given the
ubiquitous use of signage in campaigns worldwide, it is unfortunate
that it has so rarely been the object of eld experimental research.
We hope that the present studies will provide the substantive
impetus and methodological template for more work of this kind.
Appendix A. Supplementary data
Supplementary data related to this article can be found at http://
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IntroductionIndividual studiesThe summary effectHeterogeneity of effect sizesSummary points