Policy Uncertainty, Political Capital, and Firm Risk-Taking∗
Pat Akey†
Stefan Lewellen‡
University of Toronto
London Business School
November 3, 2015
Abstract
We link the cross-section of firms’ sensitivities to economic policy uncertainty to their subsequent political activity and post-election risk-taking behavior. We first show that firms with a
high sensitivity to economic policy uncertainty donate more to candidates for elected office than
less-sensitive firms. Using close election outcomes for identification, we then compare differences
in post-election risk-taking and performance for firms that experience the same close-election
political capital shocks and the same general policy uncertainty shock but that differ in their
ex-ante sensitivities to policy uncertainty. We find that policy-sensitive firms’ investment, leverage, operating performance, Tobin’s Q, option-implied volatility, and CDS spreads respond more
sharply to the resolution of uncertainty than policy-neutral firms. However, these effects are
largely restricted to firms experiencing a negative political capital shock, suggesting that political connections are an imperfect hedge against shocks to the economic policy environment.
Our results highlight many new links between political capital shocks and firms’ subsequent
decision-making and represent the first attempt in the literature to link firms’ policy uncertainty sensitivities to their political activities and subsequent risk-taking and performance.
∗
The authors would like to thank Ling Cen, Olivier Dessaint, Art Durnev, Nicholas Hirschey, Chay Ornthanalai,
Mike Simutin, Vania Stavrakeva, and Pietro Veronesi for valuable comments.
†
University of Toronto. Phone: +1 (647) 545-7800, Email: [email protected]
‡
London Business School. Phone: +44 (0)20 7000 8284. Email: [email protected]
1
1
Introduction
Government policy represents a large source of uncertainty for many corporations, yet there is
currently little research on the question of how economic policy uncertainty affects firms’ operating
decisions and performance. In this paper, we use firms’ political activities as a lens through which
to study the relationship between economic policy uncertainty and firms’ risk-taking behavior.
We do so by first linking economic policy uncertainty to firms’ donations to candidates in U.S.
congressional elections. We then examine how the resolution of uncertainty following election
outcomes affects firms’ subsequent risk-taking and performance, and in particular, how risk-taking
and performance differ between (ex-ante) policy-sensitive and policy-neutral firms following shocks
to these firms’ political capital bases stemming from close election outcomes.
Our focus on political activities is driven by the observation that, much as firms can hedge
against other forms of uncertainty such as price uncertainty or weather uncertainty, firms can also
“hedge” against economic policy uncertainty by actively attempting to influence the policy-making
process. Moreover, firms that are highly sensitive to changes in government policy arguably have a
stronger incentive to engage in the political process than similar, policy-neutral firms.1 Hence, in
order to accurately measure the effects of economic policy uncertainty on firms’ subsequent risktaking, we must also account for firms’ attempts to influence the policy-making process through
the accumulation and deployment of political capital. This intuition – which to our knowledge is
new to the literature – also suggests that firms may participate in the political process due to policy
uncertainty considerations alone, which represents a sharp contrast to the “increased government
handouts” and “increased credit availability” political participation channels that are popular in
the literature on political connections.
The most basic form of political capital is a direct connection between firms and policymakers.
As such, we focus on firms’ campaign contributions to candidates for elected office as our measure
1
While there are no theories (to our knowledge) that link together uncertainty, political connections, and firm
risk-taking, we can appeal to the literature on hedging to support this argument (see, e.g., Holthausen (1979)). In
the presence of financing frictions, taxes, bankruptcy costs, or other types of frictions, a positive shock to uncertainty
will increase the demand for hedging holding the firm’s production function constant. All else equal, this implies that
the marginal value of an extra hedging unit will be larger for firms exposed to greater levels of uncertainty.
2
of political capital. We identify a subset of firms that are particularly sensitive to economic policy
uncertainty within a given U.S. congressional election cycle and then track these firms’ subsequent
donation activities. Consistent with the intuition that the marginal value of a political connection
is greater for policy-sensitive firms, we find that policy-sensitive firms are more likely to make
(or increase) political campaign contributions relative to policy-neutral firms. Using close election
outcomes as a plausibly exogenous shock to firms’ political capital bases, we then examine how
shocks to a firm’s political capital stock impact the firm’s subsequent risk-taking behavior. In
particular, by examining differences in subsequent risk-taking across policy-sensitive and policyneutral firms that are subject to the same political capital shocks, we can directly isolate the effect
of economic policy uncertainty on risk-taking after controlling for firms’ own abilities to influence
the policy-making process. Furthermore, by comparing outcomes across policy-sensitive (or policyneutral) firms that experience different political capital shocks, we are able to measure the marginal
effects of an extra political connection on firm risk-taking and performance and are able to isolate
differences in these effects across policy-sensitive and policy-neutral firms. This latter set of tests
is important because it allows us to link our findings on the marginal value of political connections
to the existing political connections literature.
Our empirical design allows us to overcome many of the difficulties associated with identifying
the relationship between policy uncertainty and firm outcomes. First, as noted previously, our focus
on firms’ political donations allows us to directly control for firms’ “hedging” activities, thereby
allowing us to compare policy-sensitive (policy-neutral) firms that experience similar political capital shocks. Second, our sample of close congressional elections in the United States allows us to
identify true “shocks” to donating firms’ political capital stocks (since by definition, close elections
are not decided until election day).2 By limiting our focus to the sample of firms that actively
donated money to candidates in close elections, we are also able to mitigate concerns related to the
endogeneity of firms’ decisions to participate in the political process. Furthermore, we use ex-ante
measures of policy uncertainty sensitivity to avoid the simultaneity problems caused by firms’ joint
2
Our primary identifying assumptions are that close election outcomes are unknown at the times of firms’ donations, and that firms’ donations themselves are not sufficient to sway election results. While neither assumption is
directly testable, we present evidence later in the paper that is consistent with both assumptions.
3
management of their policy uncertainty sensitivities and their political capital activities. Finally,
most of our specifications include firm-election cycle fixed effects (that is, a separate fixed effect exists for each firm during each election cycle). This allows us to control for any unobserved variation
within each firm-election cycle pairing that may be driving our results.3
To estimate the relationship between economic policy uncertainty and risk-taking, we begin
by sorting firms into “policy-sensitive” and “policy-neutral” buckets six months before each U.S.
federal election using data from the previous 18 months. We identify firms as being policy-sensitive
based on a regression of firm stock returns on the Economic Policy Uncertainty index developed by
Baker, Bloom, and Davis (2015) and various control variables. Within each election cycle, we then
define the magnitude of the ex-post political capital shock for firm i as the difference between the
number of ultimate winners and losers that the firm supported in close elections during that cycle.4
We define a firm as receiving a “lucky” political capital shock if, in a given election cycle, the
firm’s close-election candidates win more elections than they lose.5 Consistent with our primary
identifying assumptions, the median political capital shock in our sample is exactly zero. The
risk-taking and performance variables that we examine include market-driven variables (such as
option-implied volatility, CDS spreads, and Tobin’s Q) and firm-driven investment and operating
variables (such as investment, leverage, R&D spending, operating profitability, and sales growth).6
We then employ a differences-in-differences design with multiple treatment groups to examine
how “lucky” and “unlucky” shocks to firms’ political capital bases affect their subsequent risk-taking
behavior.7 We also use triple-difference specifications to examine whether the effects we observe for
3
Our results are also robust to the use of industry-cycle fixed effects.
For example, Coca-Cola donated to two winning candidates and five losing candidates in close elections during
the 2004 election cycle, so we compute the shock to Coke’s political capital during the 2004 cycle as 2 - 5 = -3. In
contrast, Coke supported seven close-election winners and four close-election losers during the 2006 election cycle, so
Coke’s political capital shock in the 2006 cycle would be defined as 7 - 4 = 3.
5
This approach implicitly assigns an identical weight to every election. In reality, some elections may be more
important than others. However, there is no reason to believe that this approach induces a systematic bias in our
measurement of political capital shocks, which would be required in order for this concern to affect our results. As
a further robustness check, we also limit our sample to firms that make donations prior to September 1st within a
given election cycle (federal elections take place in the United States on the first Tuesday of November). All of our
results remain quantitatively and qualitatively unchanged.
6
These variables have been used before (in different contexts) within the existing literature on political connections.
7
Standard difference-in-difference designs contain a treatment group and a control group. Here, both groups are
treated: one experiences a positive shock while the other experiences a negative shock. This experimental design is
arguably better suited than standard difference-in-difference designs for causal inference, since, in the words of Cook
and Campbell (1979), “the theoretical causal variable has to be rigorously specified if a test is made that depends on
4
4
“lucky” winners versus “unlucky” losers differ between policy-sensitive and policy-neutral firms.
Hence, in total, we are able to isolate the effects of political capital shocks on firm risk-taking
for four different types of firms: “lucky” policy-sensitive firms, “unlucky” policy-sensitive firms,
“lucky” policy-neutral firms, and “unlucky” policy-neutral firms. This decomposition allows us to
directly test the relationships between policy uncertainty, political capital, and firms’ subsequent
risk-taking and performance.
Our analysis yields four main results, all of which are new to the literature. First, holding
policy sensitivity fixed, we find that “lucky” political capital shocks are associated with a subsequent
reduction in firms’ risk-taking (as measured by variables such as implied volatility and CDS spreads)
and an improvement in firms’ operating performance (as measured by variables such as Sales and
ROA). We also find that “lucky” political capital shocks are associated with increases in firm
value (as measured by Tobin’s Q). These effects are opposite in sign but are roughly symmetric in
magnitude for “lucky” versus “unlucky” firms, supporting our identifying assumption that election
outcomes were unknown at the time of firms’ campaign contributions in our sample of close elections.
We next compare the magnitudes of the differences between “lucky” and “unlucky” shocks
across firms with different ex-ante policy sensitivities. Consistent with the marginal value of a
political connection being larger for policy-sensitive firms, we find that the differences we observe in
post-election outcomes across “lucky” and “unlucky” policy-sensitive firms are larger in magnitude
than the differences we observe across “lucky” and “unlucky” policy-neutral firms. The economic
magnitudes of these differences are significant: for example, we observe a 10% relative difference
in investment levels, a 2% relative difference in leverage, a 13% relative difference in Tobin’s Q,
a 12% relative difference in one-month option-implied volatilities, and a 10% relative difference
in one-year CDS spreads. These findings confirm our intuition that policy-sensitive firms respond
more sharply to political capital shocks relative to policy-neutral firms.
To estimate the effects of policy uncertainty sensitivity on risk-taking, we examine the differone version of the cause affecting one group one way and another group the [opposite] way...[i]t is the high construct
validity of the cause which makes [this] design potentially more appropriate for theory-testing research than the
[standard difference-in-difference] design.” Empirically, the recovered treatment effects from our design are identical
to the treatment effects that would arise from a standard (and properly-specified) difference-in-difference analysis.
5
ences in treatment responses across policy-sensitive and policy-neutral firms experiencing the same
political capital shock. In other words, we examine differences in outcomes between “lucky” policysensitive firms and “lucky” policy-neutral firms (and vice versa). These firms differ in their ex-ante
policy sensitivities, but both firms experience similar political capital shocks. As such, we are able
to estimate the differential response of policy-sensitive versus policy-neutral firms to changes in
policy uncertainty after controlling for the effects of political capital shocks.
Interestingly, we find that the resolution of policy uncertainty has an asymmetric impact on
firms’ risk-taking and performance depending on whether firms are hit with a lucky or unlucky
political capital shock. Policy-sensitive firms that are hit with an unlucky political capital shock
have lower investment, higher leverage, lower Q, worse operating performance, and higher implied
volatility and CDS spreads than policy-neutral firms hit with a similarly unlucky shock. Hence,
consistent with intuition, we find that unlucky political capital shocks hurt policy-sensitive firms
particularly badly relative to their policy-neutral brethren. However, even when hit with a positive
political capital shock, we find that policy-sensitive firms invest less, have higher CDS spreads,
and have higher implied volatilities than policy-neutral firms hit with similarly positive shocks
(though the magnitudes are significantly smaller). Hence, we find that the effects of policy uncertainty on risk-taking and performance are asymmetric: firms hit with a bad political capital shock
suffer greatly, while firms hit with a good shock are still negatively impacted, though to a lesser
degree. These findings suggest that political connections serve as an imperfect hedge against policy
uncertainty, since even the “gains” associated with improved political connections do not allow
policy-sensitive firms to completely offset the effects of being sensitive to future economic policy
changes. Nevertheless, the differences in the magnitudes of the treatment responses across policysensitive and policy-neutral firms still suggest that on the margin, an extra political connection is
still more valuable for policy-sensitive firms than for policy-neutral firms.
Finally, we examine the term structure of political capital shocks using data on long-dated
options and CDS contracts. We find that political capital shocks seem to have long-lasting effects
on firms’ (expected) risk-taking: 6-month implied volatilities and 10-year CDS spreads drop signif-
6
icantly following elections for “lucky” firms, and the magnitudes of the drops are consistent with a
multi-year shock to firms’ risk-taking. We also find that implied volatility slopes and CDS slopes
steepen modestly for “lucky” firms following close elections, which suggests that the “half-life” of
the effects of political capital shocks on firm riskiness is potentially long. These results are largely
consistent with our other findings reported above.
Our results also point to a “policy uncertainty” channel of political capital accumulation that is
distinct from the channels that have been previously documented in the literature. For example, a
growing literature points to firms’ abilities to secure government funds through “bailouts” (Faccio,
Masulis, and McConnell (2006); Duchin and Sosyura (2012)) or through other forms of government
spending (Cohen and Malloy (2014)) as the primary channel through which firms benefit from
political connections. While we cannot rule out this channel, most of our results suggest that
risk-taking declines and operational performance improves following a positive political capital
shock, which is not consistent with the existing literature on the “increased government handouts”
channel.8 Another channel argues that politically-connected firms benefit from increased credit
availability (often through loans made by politically-connected banks), potentially reducing these
firms’ financial constraints (see, e.g., Khwaja and Mian (2005) and Claessens, Feijen, and Laeven
(2008)). However, our findings suggest that firms’ average leverage decreases following positive
political capital shocks, which is not consistent with the “increased credit availability” story. In
short, while the ultimate motives behind firms’ political donation decisions are unobservable, our
results line up most closely with the idea that corporations cultivate political connections in an
attempt to influence policy implementation on issues that are particularly relevant to the firm.
2
Related Literature
A recent strand of literature examines the effects of aggregate policy or political uncertainty on firm
outcomes and asset prices. Pástor and Veronesi (2012, 2013) model how asset prices and risk premia
respond during times of high aggregate political uncertainty. Kelly, Pástor, and Veronesi (2014)
8
We also test the “sticky-government-contracting” hypothesis explicitly and find no evidence that governmentdependent firms are driving our results.
7
find that political uncertainty is priced in options markets. Julio and Yook (2012) and Durnev
(2010) find that investment levels and stock price-investment sensitivities decrease during periods
of high political uncertainty, while Boutchkova, Doshi, Durnev, and Molchanov (2012) document
that export-oriented industries, industries dependent on contract enforcement, and labor-intensive
industries exhibit higher volatility during periods of political uncertainty. Finally, Gulen and Ion
(2015) find that investment and policy uncertainty are negatively related, particularly for firms that
have high investment irreversibility and dependence on government revenues. To date, however,
this strand of the literature has not looked at how economic policy uncertainty interacts with firms’
political connections.
Our paper is also related to two strands of the literature on political connections. One strand
focuses on the link between political connections and firm value. In particular, Fisman (2001),
Faccio (2004), Faccio and Parsley (2009), Cooper, Gulen, and Ovtchinnikov (2009), Goldman,
Rocholl, and So (2009), Acemoglu, Johnson, Kermani, Kwak, and Mitton (2013), Akey (2015),
and Borisov, Goldman, and Gupta (2015) all find evidence that stronger political connections are
associated with increases in firm value.9 Consistent with this literature, we find that unexpected
positive shocks to firms’ political capital stocks are associated with increases in firm value (as
measured by Tobin’s Q).
A second strand of the political connections literature is focused on identifying the underlying
rationale for firms to establish connections with politicians in the first place. Faccio, Masulis,
and McConnell (2006) and Duchin and Sosyura (2012) show that politically-connected firms are
more likely to receive government bailouts than non-connected firms, while Cohen and Malloy
(2014) find that government-dependent firms (who are likely to be politically-connected) have
lower investment, lower R&D spending, and lower sales growth than non-government-dependent.
Relatedly, Kim (2015) finds that firms with strong political connections have lower investment,
lower R&D spending, and lower patent citations (but higher government sales) relative to firms with
weak political connections. These findings are largely consistent with the theoretical predictions of
9
In contrast, Agarwal, Meshke, and Wang (2012) and Coates IV (2012) find that political connections may
indicate agency problems in connected firms. However, the overwhelming majority of studies has found that political
connections have a large and positive impact on firm value.
8
Murphy, Shleifer, and Vishny (1993) and Shleifer and Vishny (1994).10 In contrast, Khwaja and
Mian (2005) and Claessens, Feijen, and Laeven (2008) find that politically-connected firms benefit
from increased credit availability and a potential reduction in financial constraints. In addition,
Do, Lee, and Nguyen (2013) finds that firms invest more in physical capital, while Hanouna,
Ovtchinnikov, and Prabhat (2014) find that CDS spreads on average tend to be lower for politicallyconnected firms. Finally, a number of studies have found that political connections lead to higher
future sales (Amore and Bennedsen (2013), Goldman, Rocholl, and So (2013), Tahoun (2014),
Akey (2015)). However, none of these papers examines the effects of policy uncertainty on political
capital and firms’ subsequent risk-taking.
There is one other paper in the literature (Ovtchinnikov, Reza, and Wu (2014)) that links policy uncertainty to political connections and political connections to firm outcomes (in this case,
innovation). In particular, Ovtchinnikov, Reza, and Wu (2014) find that firms’ innovation increases
following positive political capital shocks, which they argue is due to a reduction in policy uncertainty amongst politically-connected firms. Our paper differs from Ovtchinnikov, Reza, and Wu
(2014) along many dimensions: we use a different identification strategy, our sample consists of
a different set of political connections, and we measure different outcome variables. Furthermore,
Ovtchinnikov, Reza, and Wu (2014) do not explicitly test whether policy uncertainty is directly
impacting political connections or risk-taking. Nevertheless, the key message of their paper – that
politically-connected firms may benefit from a reduction in policy uncertainty – nicely complements
the main findings of our paper.
3
Economic Setting and Identification Strategy
3.1
Economic Setting and Testable Implications
Our goal is to study the interaction between firms’ sensitivity to economic policy uncertainty, their
subsequent political activities, and their ultimate response to the resolution of policy uncertainty
10
Johnson and Mitton (2003) find that politically-connected firms benefit from foreign capital controls and suffer
when these controls are removed, consistent with the predictions of Rajan and Zingales (1998). These findings are
also in the spirit of Murphy, Shleifer, and Vishny (1993) and Shleifer and Vishny (1994).
9
following U.S. federal elections. Our basic argument consists of four main components. First,
some firms are more exposed (or sensitive) to economic policy uncertainty than other firms. For
example, financial institutions and auto manufacturers may have been more exposed to policy
uncertainty ahead of the 2008 elections than, say, textile producers. We are agnostic as to the
source of firms’ exposure to policy uncertainty – for example, firms’ exposure may stem from a
“shock” to the policy environment or may reflect firms’ own decision-making. We simply wish to
argue (and document) that prior to each U.S. federal election in our sample, some firms are more
exposed to policy uncertainty than others. We label firms with high exposure to policy uncertainty
as “policy-sensitive firms.”
We next conjecture that policy-sensitive firms are more likely to make (or increase) political
campaign contributions than less-policy sensitive firms (which we refer to as “policy-neutral” firms).
In other words, to the extent that political connections have value to firms, we posit that the
marginal value of a political connection is higher for policy-sensitive firms than for policy-neutral
firms. As noted in the introduction, this hypothesis is consistent with the literature on firms’
hedging behavior under uncertainty in the presence of market frictions. Our hypothesis leads
immediately to our first testable prediction, which is that policy-sensitive firms will contribute
more to candidates for elected office than policy-neutral firms within a given election cycle.
Having linked policy uncertainty sensitivity to firms’ campaign donations, we next link firms’
donation choices to the outcomes of U.S. federal elections. Economic policy uncertainty tends to
rise before U.S. federal elections and declines following these elections (Baker, Bloom, and Davis
(2015)). One interpretation of this finding is that a significant proportion of existing (ex-ante)
policy uncertainty is related to a given set of elections and is resolved by the outcomes from these
elections. Under this interpretation, the uncertainty faced by policy-sensitive firms should decline
following elections, and should decline more so than for non-policy sensitive firms. As such, we
posit that the previously-documented tendency for firms to “wait” on the outcomes of elections
(Julio and Yook (2012), Pástor and Veronesi (2013), Kelly, Pástor, and Veronesi (2014)) will lead
to sharper post-election changes in firm operating behavior for policy-sensitive firms relative to
10
non-policy sensitive firms. This is another prediction that is directly testable in our sample.
Election outcomes resolve two types of uncertainty: uncertainty related to future government
policies, and uncertainty regarding a firm’s stock of political connections or political capital. As
such, firms’ responses to the resolution of policy uncertainty may depend in part on whether the
firm’s own stock of political capital has been strengthened or weakened. Under the assumption that
firms’ campaign contributions are linked to its policy objectives, this implies that firms experiencing
a “lucky” election draw (i.e. an election where many of the firms’ contributions went to victorious candidates) will respond differently to the resolution of political uncertainty relative to firms
whose contributions primarily went to losing candidates. For example, “winning” firms may decide
to increase investment, while “losing” firms may decide to postpone investment.11 Furthermore,
policy-sensitive firms should be expected to increase or decrease investment (or other variables)
even more than their non-policy sensitive brethren. These two predictions are also directly testable
and arguably represent the main contribution of this paper.
One last question remains, however, and that is how firms should respond to the resolution of
uncertainty given a favorable or unfavorable election draw. The answer to this question depends in
part on the goals that firms have when they make political contributions to candidates for elected
office. For example, if a firm establishes political connections for the purpose of securing future
“bailouts” or other types of hedges against bad economic states of nature, this implies that a positive
shock to a firm’s political capital base may be followed by an increase in risk-taking behavior.
Alternatively, if a firm establishes political connections for the purpose of securing government
contracts, a positive political capital shock might be followed by a reduction in risk-taking behavior,
since extra risk could plausibly put the firm in jeopardy of securing future contractual agreements
with the government (or, as another possibility, firms may simply kick back and enjoy the “quiet
life”). Finally, if a firm establishes political connections in order to simply influence the policymaking process (perhaps because the firm is policy-sensitive), then a positive shock to political
11
The expected signs of these effects are theoretically ambiguous. For example, moral hazard arguments suggest
that stronger political connections should be linked to an increase in firm risk-taking. In contrast, government
contracting considerations may cause firms to decrease risk-taking following positive political capital shocks because
government funding may crowd out the firms’ own investment activities.
11
capital is likely to improve the probability of the firm obtaining its policy objectives, which in turn
may lead the firm to either increase or decrease its subsequent risk-taking behavior depending on
the firm’s specific policy objectives.
We formally test each of these three “channels” – along with the broader links between policy
uncertainty, campaign contributions, election outcomes, and subsequent risk-taking – using an identification strategy that exploits plausibly exogenous variation in close U.S. congressional elections.
We now describe this approach.
3.2
Identification and Empirical Approach
Estimating the causal effect of political capital shocks on ex-post firm outcomes is extremely challenging. First, firms endogenously choose whether to be politically active and which politicians
to form connections with. Second, certain types of firms may be more likely to donate to certain
types of candidates who are themselves more or less likely to be elected (for example, powerful
incumbents). Third, the results of most elections are effectively determined months before the
actual election date, making it difficult to isolate the timing of any political-capital-related shocks
on market prices. Fourth, the causality could go in the other direction; that is, firms’ operating
decisions or riskiness may affect the outcome of elections and/or create shocks to the firm’s political
capital ledger.12 Finally, other sources of unobserved heterogeneity may account for any observed
relationship between political capital shocks and firms’ riskiness and operating decisions. For example, a disruptive technology shock may jointly affect firms’ operating decisions as well as the
outcome of political elections in the state(s) most affected by the change.
To overcome these challenges, we focus on a subset of firms that donate to candidates in “close”
U.S. congressional elections from 1998-2010.13 Our primary identifying assumption is that election
outcomes at the time of firms’ donations are plausibly exogenous in our sample of close elections.
Our claim of plausible exogeneity requires two key assumptions to be met: first, firms cannot
12
For example, financial institutions’ behavior prior to the recent crisis may have affected the outcome of elections
and/or the firms’ political capital.
13
Following Akey (2015), Do et al. (2012), and Do et al. (2013), we define a close election as an election that is
ultimately decided by a voting margin of 5% or less. In other words, for an election with two candidates, we define
a close election as one in which the winner receives 50.01% - 52.5% of the total vote.
12
accurately predict close-election winners at the time of their donations, and second, firms’ donations
themselves cannot materially affect a candidate’s chances to win an election. While neither of
these assumptions are directly testable, anecdotal evidence strongly supports the view that election
outcomes in our sample are plausibly random conditional on firms’ donation decisions. In particular,
we find that the median firm in our sample supports exactly the same number of close-election
losers as close-election winners during each congressional election cycle. Consistent with this fact,
Figure 1 shows that the distribution of firms’ net close-election political capital shocks is centered
around zero, is effectively unimodal, and has relatively symmetric tails. Under the assumption that
firms would rather donate to winning candidates than losing candidates, these results suggest that
election outcomes are largely unpredictable in our sample of close elections and that a given firm’s
donations are not sufficient to sway election outcomes. Furthermore, by looking within the set of
firms that made close-election donations, we are able to effectively control for the fact that donation
patterns are not random, since all of the firms in our sample felt that it was optimal (for whatever
reason) to donate to one or more close-election candidates. Finally, close elections are generally
decided on election day (or very soon before), making it easier to isolate the timing associated with
a market response to political capital shocks.
Our identification strategy allows us to examine outcome differences between firms who donated
to a politician that just won a close election relative to firms who donated to a politician that just
lost a close election in the time periods before and after each election. Our implicit assumption is
that these “random” election-day outcomes represent positive or negative shocks to the political
capital of donating firms. If political capital shocks have an effect on firms’ riskiness or operating
decisions, we should see firms (and markets) respond to election-day political capital shocks in the
ensuing days, weeks, and months following U.S. federal elections. In the context of the economic
setting that was discussed in the previous section, these shocks can be interpreted as an increase
or a decrease in connectedness. This hypothesis forms the basis for our empirical strategy, which
we describe below.
We begin by defining Close W insi,t (Close Lossesi,t ) as the number of close-election winners
13
(losers) that firm i donated to during election cycle t. For example, since Coca-Cola donated to
two close-election winners and five close-election losers during the 2004 election cycle, we would
set Close W ins = 2 and Close Losses = 5 for Coke during the 2004 cycle. We next define
N et Close W insi,t as the difference between Close W ins and Close Losses. This variable captures
a firm’s overall political capital gain in close elections during a given cycle. For Coke in 2004, this
variable would be defined as N et Close W ins = 2 − 5 = −3. We also create a dummy variable
(Close Election Dummy) that takes the value of one if firm i’s overall political capital gains are
greater than the sample median of zero (i.e. where N et Close W insi,t > 0) during a given election
cycle, and takes the value of zero otherwise. For example, since Coke donated to more close-election
losers than winners in 2004, we would set Close Election Dummy equal to zero for Coke in 2004.
Importantly, our close-election measures are not strongly correlated with general election outcomes: for example, in the 2006, 2008, and 2010 elections (which were “dominated” by Democrats,
Democrats, and Republicans, respectively), our Close W ins variable suggest that more of the close
winners in 2006 and 2008 were Republicans, while there is no clear pattern in 2010. As such, our
close election results do not appear to be picking up “general” election trends. This helps to rule
out the possibility that our close-election results are simply picking up “general” election shocks
that tend to benefit firms that donated (nearly) exclusively to the party that “won” the election,
perhaps because of similar ideological positions on government policy priorities.
The variables Close W ins, Close Losses, N et Close W ins, and Close Election Dummy form
our primary measures of political capital shocks. We will use all four variables in our subsequent
tests. Panel A of Table 1 presents summary statistics for each of these measures (with the exception
of Close Election Dummy, which is an explicit function of the sample median).
With our political capital measures in hand, we can now turn to our empirical framework. We
employ a differences-in-differences framework to estimate the effects of a political capital shock on
14
firm outcomes.14 Specifically, we estimate the following model:
Outcomei,t =α + β1 P ost Electiont + β2 Capital Shocki,t × P ost Electiont +
(1)
+ Γ0 Controlsi,t + F irm × Election Cycle F E + i,t ,
where Capital Shocki,t represents one of our political capital shock measures described above.
Unlike standard differences-in-differences tests, there is no separate term for Capital Shocki,t in
the equation above because the granularity of our data allows us to include firm-election cycle fixed
effects (Capital Shocki,t is defined at the firm-cycle level, so it is swept up by our fixed effects). As
such, our results can be interpreted as looking within a firm and given election cycle.
Our primary coefficient of interest is β2 in the equation above. If β2 is positive, this signifies that
a “lucky” positive political capital shock for firm i is associated with an increase in the outcome
variable of interest relative to another firm j that experienced an “unlucky” negative political capital
shock during the same election cycle. The null hypothesis for all of our tests is that β2 = 0; that
is, political capital shocks have no effects on our outcome variables.
We also identify a subset of firms as sensitive to economic policy using a procedure that we
describe in detail below and define an indicator variable, P olicy Sensitive, to take a value of 1 if
the firm is sensitive and 0 otherwise. We then use a triple-difference framework to study whether
the effects of these political capital shocks differ for firms that are more sensitive or less sensitive
to policy uncertainty. Formally, we estimate the following model:
Outcomei,t = α + β1 P ost Electiont + β2 Capital Shocki,t × P ost Electiont +
(2)
+ β3 P osti,t × P olicy Sensitivei,t + β4 P ostt × P olicyi,t × Capital Shocki,t +
+ Γ0 Controlsi,t + F irm × Election Cycle F E + i,t ,
In this specification, the coefficient β4 captures the differential effect of being policy-sensitive
14
Julio and Yook (2012) and Durnev (2010) also use a differences-in-differences framework to estimate the effects
of political uncertainty on firm outcomes; however, most of their dependent variables and settings are very different
than the variables and settings we consider in this paper.
15
on outcomes given the same political capital shock. If, for the sake of argument, both β2 and β4
are negative, than policy sensitive firms had an even larger negative reaction in the outcome to the
same political capital shock than their policy-neutral peers.
3.3
3.3.1
Data
Political Connections Data
Firms contribute money to political candidates in the United States through legal entities known as
Political Action Committees (PACs). PACs solicit contributions from employees of the sponsoring
firm and donate these contributions to one or more political candidates.15 Rather than donating
money directly to candidates’ personal accounts (which is illegal in the United States), firms’ PACs
typically donate money to another PAC set up by a candidate for elected office (known as “Election
PACs”). Firm PAC contributions to Election PACs therefore constitute our measure of political
connectedness linking firms to candidates for elected office.16
We obtain election contribution and election outcome data from the U.S. Federal Election
Commission (FEC) for all federal elections from 1998-2010.17 Panel A of Table 1 presents summary
statistics for our political contributions and election data. United States general elections are held
annually in November. However, all House of Representative and Senate general elections occur in
even numbered years, while Presidential elections occur in years divisible by four.
3.3.2
Options Data
We obtain daily implied volatility data from OptionMetrics from 1997-2011. OptionMetrics computes implied volatility from at-the-money call options using the Black-Scholes model. We use data
for call options with 1 - 6 month maturities. All results are robust to using put options. Panel A
of Table 1 presents summary statistics for our implied volatility data. All of our implied volatility
15
Importantly, most decisions regarding which candidates to support are typically left to one or more officers of
the sponsoring company and frequently to a political specialist such as the PAC chair.
16
Firm PAC contributions to Election PACs are legally capped at $10,000 per election cycle.
17
FEC data is transaction-level data organized by election cycle. Political contribution data is available from the
FEC, the Center for Responsive Politics, or the Sunlight Foundation. The latter two organizations are non-partisan,
non-profit organizations who assemble and release government datasets to further the public interest.
16
tests use daily data from six months prior to federal election dates to six months after the election
takes place.
3.3.3
Credit Default Swap Data
We obtain daily CDS data from Markit from 2001 to 2011. Since CDS spreads are not available
prior to 2001, all tests involving CDS spreads only focus on election cycles from 2002 to 2010.
We focus on 1-year, 5-year, and 10-year CDS spreads on senior unsecured U.S.-dollar-denominated
debt. Following Hanouna, Ovtchinnikov, and Prabhat (2014), we take the natural log of the CDS
spread for each firm and use this as a dependent variable in our tests. Panel A of Table 1 presents
summary statistics for our (untransformed) CDS data. All of our CDS tests use daily data from
six months prior to federal election dates to six months after the election takes place.
3.3.4
Economic Policy Uncertainty Data
We use the monthly Economic Policy Uncertainty (EPU) index created by Baker, Bloom, and Davis
(2015) as a proxy for aggregate economic policy uncertainty. This index measures the frequency
of articles that mention economic or policy related uncertainty in 10 major US newspapers. The
authors suggest that this series predicts declines in aggregate investment and output along with
increases in volatility.
3.3.5
Other data
We also obtain quarterly accounting data from COMPUSTAT, daily stock returns from CRSP, and
stock return factors from Ken French’s website. Definitions of all variables used in our tests are
contained in Appendix A.
4
Results
The argument we outlined in section 3 consists of four main components. First, firms differ from
one another in the cross-section and the time series in the extent to which they are sensitive to
17
uncertainty related to economic policy. Second, all else equal, the marginal value of an extra
political connection is larger for policy-sensitive firms, and hence, these firms are more likely to
make campaign contributions relative to policy-neutral firms. Third, shocks to firms’ political
capital bases will lead to changes in firm outcomes following elections. Finally, to the extent that
firms make campaign contributions in support of their privately-optimal policy objectives, policysensitive firms will respond more forcefully to a positive political capital “shock” (i.e. a marginal
political connection) than policy-neutral firms. These arguments are discussed in detail in the
subsections below.
4.1
Firms’ Sensitivities to Economic Policy Uncertainty
Our first task is to document that firms differ in their sensitivities to economic policy uncertainty
(EPU). We seek to understand, among other things, what fraction of firms have a high sensitivity
to EPU, how persistent this sensitivity is across time, and whether sensitive and less-sensitive firms
differ significantly along observable measures such as size, leverage, and industry classification.
In order to examine these questions (and the other questions in this paper), we need to define a
time-varying, firm-specific measure of firms’ sensitivity to economic policy uncertainty.
We use the Economic Policy Uncertainty index developed by Baker, Bloom, and Davis (2015)
as our primary measure of economic policy uncertainty.18 The EPU index is an aggregate timeseries index that measures the frequency of newspaper articles containing words which indicate
uncertainty about economic policy.19 We are not interested in the index level per se, but rather in
agnostically identifying firms that seem to be the most sensitive to economic policy uncertainty.
To identify policy-sensitive firms, we run OLS regressions of the Baker, Bloom, and Davis (2015)
EPU index on each firm’s monthly stock returns in the 18 months leading up to an election. We
18
Other measures of economic policy uncertainty exist as well. For example, Whited and Leahy (1996) and Bloom,
Bond, and Reenen (2007) examine the link between general uncertainty and investment and use share price volatility
as a firm-specific measure of uncertainty. However, this measure seems to be too general to capture policy-specific
uncertainty as opposed to other types of uncertainty. Several authors also use elections to measure time periods when
policy uncertainty is high (see, e.g., Gao and Qi (2013) and Julio and Yook (2012)), but this measure cannot be used
to produce ex-ante (i.e. pre-election) cross-sectional variation in policy uncertainty sensitivity at the firm level.
19
Brogaard and Detzel (2015) study the general asset-pricing implications of this index and conclude that EPU is
an important risk factor for equities. In contrast, we look at the correlation between firms’ stock returns and this
index at various point in time to identify firms that are sensitive to policy uncertainty.
18
run a separate regression for each firm and each election cycle, so our measure of policy sensitivity
is defined at the firm-election cycle level. We then extract the p-value of the regression coefficient
on the EPU index. We define a firm as being sensitive to economic policy uncertainty during a
given election cycle if the p-value is less than or equal to 0.1. In other words, we define a firm as
being policy-sensitive if the absolute value of its loading on the EPU index is large, regardless of
whether the loading is positive or negative.
Using this procedure has benefits and drawbacks. The main benefit is that we are able to
be agnostic about exactly how uncertainty and returns are related. However, there are at least
two potential drawbacks: (i) we could simply be picking up random variation that is unrelated
to policy sensitivity, and (ii) we are relying on a short time series (18 monthly observations) for
each estimation, which can lead to power problems. However, if we were simply picking up random
variation, we would expect that in a large sample of firms, we would find that roughly 10% of
firms would be sensitive to EPU since this is the p-value cutoff we have defined. Instead, however,
we find that significantly greater than 10% of all firm-cycle observations have p-values lower than
0.1. Hence, we do not appear to be capturing purely noise. Furthermore, all of our main results
remain quantitatively and qualitatively unchanged when we include the market, size, value, and
momentum factors as controls. Finally, all of our main results are robust to varying our sensitivity
cutoff (p-value < 0.1) and the length of our estimation period (18 months).
Panel B, C, and D of Table 1 present summary statistics regarding the fraction and type of firms
that are policy sensitive according to the measure described above. Panel B shows that 18% of the
firm-years in our sample appear to be policy sensitive. Panel B also shows that there is time-series
variation in the fraction of firms that are defined as sensitive to EPU; for example, the 2008 and
2004 political cycles have the largest proportion of sensitive firms/years (48 and 22% respectively)
while 2010 has the lowest proportion (8%).20
Panel C examines the potential persistence of policy sensitivity. In particular, it may be that
20
Since our EPU correlations are computed using 18 months worth of data prior to each election, the increase
in sensitivity in 2008 is not likely to be simply capturing the U.S. government’s response to the recent financial
crisis since it is computed using data from May 2007 – October 2008, which was roughly the beginning of the U.S.
government’s response to the crisis.
19
some firms (or industries) are always policy-sensitive in every election cycle, while other firms are
never policy-sensitive in any election cycle. However, Panel C shows that this does not appear to
be the case; in fact, there are fewer cases of “persistent” policy sensitivity than we would expect
even if policy sensitivity were i.i.d. across each election cycle period. Finally, Panel D presents
the proportion of firms in each of the Fama-French 49 industries. Again, one might think that
some industries may persistently be policy-sensitive, while other industries may almost never be
policy-sensitive. However, Panel D shows that this is not the case: firms in the most policy-sensitive
industry (real estate) are themselves only policy-sensitive approximately 22% of the time, while
firms in the least policy-sensitive industry (agriculture) are still policy-sensitive around 11% of the
time.
We next look at how comparable firms that are policy sensitive are to firms that are not policy
sensitive. Table 2 contains the results of our tests. Panel A examines univariate differences in firm
characteristics such as size, leverage, investment, asset intensity, firm profitability, and Tobin’s Q
(as proxied for by the M/B ratio). The panel shows that policy-sensitive firms tend to be larger,
have higher leverage, and have lower asset intensity (PP&E/assets) relative to policy-neutral firms.
However, while these results are statistically significant, their economic magnitudes are quite small.
For example, policy-sensitive firms have leverage and asset intensity levels that are around 3% and
5% higher and lower than less-sensitive firms, respectively. Hence, while policy-sensitive firms
are not identical to less-sensitive firms along every dimension, neither group stands out as being
substantively different from the other along most observable measures.
We test this proposition more formally in Panel B. This panel presents the results of a logit
regression where the dependent variable is a binary variable taking the value of one if a given firm
is policy-sensitive in a given election cycle, and zero otherwise. Our independent variables are the
same firm characteristics that we studied in Panel A. Panel B shows that with the exception of
book leverage, none of the variables in Panel A appear to be strongly correlated with whether or
not a firm is policy-sensitive in a given election cycle.
The results we have presented thus far indicate that policy uncertainty sensitivity varies both
20
within election cycles and within firms. In particular, the lack of persistence within firms and
the relatively similar observable characteristics of sensitive versus non-sensitive firms suggest that
policy sensitivities most commonly represent distinct “shocks” that are specific to a given election
cycle. While policy sensitivities are not determined randomly, this evidence suggests that it is
unlikely that the effects we document elsewhere are purely driven by “fundamental” differences
between policy-sensitive and policy-neutral firms.
4.2
Policy-Sensitive Firms and Campaign Contributions
Having documented that some firms are more sensitive to policy uncertainty than others, we now
turn to our conjecture that policy-sensitive firms will be more likely to donate (and/or will give
larger amounts) relative to policy-neutral firms. Intuitively, the marginal value of a political connection should be larger for policy-sensitive firms, creating a stronger incentive for policy-sensitive
firms to donate money to candidates for elected office.21
We examine this proposition formally in Table 3, where we regress policy uncertainty sensitivity on a firm’s total political contributions. The main independent variable of interest is
P olicy Sensitive, which is a binary variable that takes the value of one if a firm is policy-sensitive
in a given election cycle, and is zero otherwise. Column (1) in the table documents a positive univariate relationship between firms’ policy sensitivity and their total (log) campaign contributions:
on the whole, policy-sensitive firms appear to donate more to political candidates than policyneutral firms. In columns (2), (3), and (4), we introduce firm and industry-election cycle fixed
effects and add firm-level control variables such as (log) size, leverage, profit margin, and the firm’s
scaled cash holdings. In all three specifications, the relationship between policy sensitivity and
total political contributions persists: policy-sensitive firms donate more to candidates for elected
office than non-policy sensitive firms in a given election cycle. In columns (5) and (6), we further
split each firm’s political contributions into contributions made to candidates in close elections
and contributions made to candidates in other (non-close) elections. The table shows that while
21
Throughout the paper, we are agnostic as to whether contributing firms are attempting to (i) directly influence
election outcomes, (ii) secure influence with politicians conditional on the politician winning their respective races,
or (iii) both.
21
firms contribute more to both types of races when they become policy-sensitive, the increase in
contributions seems to be larger in close election races.
If becoming policy-sensitive leads firms to increase their campaign contributions to candidates
in close elections, one might be concerned that these firms may be able to forecast election outcomes
more accurately than non-policy sensitive firms (which donate less). If firms are able to systematically predict the winners of close elections, this would invalidate the main identifying assumption
of our remaining empirical analysis since close election outcomes would not be unpredictable at the
time of firms’ donations. We test for this possibility by using our main political shock variable (the
net number of close-election victors supported by each firm) as the dependent variable in the final
two specifications in Table 3. Columns (7) and (8) show that policy-sensitive firms do not appear
to have better forecasting power than their policy-neutral peers when it comes to predicting the
winners of close U.S. congressional elections.
4.3
Implied Volatility
We are now ready to explore the link between political donations, election outcomes, and firms’
subsequent risk-taking.
We begin by examining the implied volatility of firms’ options following political capital shocks.
A number of recent studies have examined the impact of political capital shocks on firms’ stock
returns (see, e.g., Cooper, Gulen, and Ovtchinnikov (2009), Cohen, Diether, and Malloy (2013),
Belo, Gala, and Li (2013), and Addoum, Delikouras, Ke, and Kumar (2014)). Nearly all of these
studies find that positive political capital shocks are associated with higher subsequent firm returns.
To our knowledge, however, no one has linked the results on returns to changes in firms’ risktaking. In particular, if we assume that long-run returns are increasing, then standard asset pricing
models such as the CAPM will predict that the increase in expected returns should be caused
by a corresponding increase in the firm’s risk. In light of the existing literature on returns, this
logic suggests that we should expect to see an increase in firms’ risk-taking (as proxied by implied
volatility) if the standard relationship between risk and return continues to hold in our sample.
22
However, Panel A of Table 4 shows that implied volatility decreases for “lucky” firms relative
to “unlucky” firms following election dates. The first six columns in the table examine the implied
volatility on one-month, three-month, and five-month options. Columns (1), (3), and (5) contain
the results from our baseline diff-in-diff setup, while columns (2), (4), and (6) add the underlying
firm’s daily stock return and the stock return on the firm’s value-weighted industry as control
variables.22 These columns show that the drop in idiosyncratic volatility for “lucky” firms is quite
large; for example, the implied volatility on one-month call options declines by approximately
12% following elections for “lucky” firms (Close W in Dummy = 1) relative to “unlucky” firms
(Close W in Dummy = 0). Columns (7) - (9) repeat the analysis using the continuous measure of
a firm’s political capital shock. In unreported results, we confirm that there are opposite effects
of similar magnitude for connections to winning and losing candidates. That is, a firm’s implied
volatility goes down when it gains political connections and increases when it fails to gain such
connections.
Our implied volatility results complement the results of Kelly et al. (2014), who examine the
relationship between implied volatility and political uncertainty. They find that implied volatility
goes up for all stocks during the period just before elections, when political uncertainty is likely to
be the highest. To our knowledge, however, no one has examined the link between implied volatility
and the cross-section of politically-active firms.
We next examine how implied volatility changes differ between firms that are sensitive to policy uncertainty versus those that are not. Formally, we use a difference-in-difference-in-difference
methodology and examine how this effect varies for firms that have a “lucky draw” and are sensitive
to policy uncertainty compared to those firms that are sensitive to policy uncertainty and have an
“unlucky draw.” Panel B of Table 4 presents this analysis. The primary coefficient of interest in
specifications (1) – (6) is P ost × P olicy × Close W in Dummy and P ost × P olicy × N et Close W ins
in specifications (7) – (9), which captures the differential effect for policy-sensitive firms. The triple
interaction term is negative and highly significant in all specifications. The magnitude of the triple22
Industry returns are computed using three-digit SIC codes. All results in the table are robust to different industry
definitions such as one-digit or four-digit SIC codes, Fama-French 49 industry definitions, or GICS definitions.
23
difference estimator is larger than the simple difference-in-difference estimator in all specifications,
which suggests that a large fraction of the reduction in implied volatility comes through better connections to politicians in times when the firm is more sensitive to policy uncertainty. For example
in the 5 month option specifications ((5) and (6)), the connection effect for policy-sensitive firms
is 2.5 larger than for non-sensitive firms (-.0572 vs. -.0220).
4.4
Credit Default Swaps
Our second measure of firm riskiness is credit default swaps. CDS spread results are contained in
Table 5. We proceed in the same fashion as for implied volatility — we first conduct a differencein-difference analysis for firms that have “lucky draws” and firms that have “unlucky draws” before
and after the election and next perform a triple difference analysis to see how these effects vary
for policy-sensitive firms versus policy-neutral firms. An increase in CDS spreads indicates an
increase in the (expected) credit risk associated with a firm, while a decrease in CDS spreads
indicates a decline in expected credit risk. Panel A presents the simple difference-in-difference
results. Consistent with our previous results, we find that “lucky” shocks to political capital are
associated with lower firm riskiness. The first six columns in the table examine the effects of
political capital shocks on one-year, five-year, and 10-year CDS spreads. Columns (1), (3), and (5)
contain the results from our baseline difference-in-difference specification, while columns (2), (4),
and (6) add a host of control variables to the specification. All six columns shows that CDS spreads
drop significantly for “lucky” firms in the six months following U.S. federal elections. The drop in
firms’ expected credit risk for “lucky” firms is substantial; for example, one-year log CDS spreads
decline by more than 30% for “lucky” firms (Close W in Dummy = 1) relative to “unlucky” firms
(Close W in Dummy = 0).
Panel B presents the results of the triple-difference analysis. Consistent with our analysis of
implied volatility, we find that there is a larger reduction in risk for policy-sensitive firms that had
a “lucky draw” than for policy-neutral firms compared to their peers that had “unlucky draws.”
The economic size of this differential impact is even larger than the effect we found for implied
24
volatility: the smallest relative difference between policy-sensitive and policy-neutral firms is about
3.5 (specification (3)), while the largest difference is 7.5 (specification (2)). These results strongly
suggest that most of the reduction in CDS spreads comes from increases in firms’ political capital
stocks at times when the firm is more exposed to policy uncertainty.
In a contemporaneous paper, Hanouna, Ovtchinnikov, and Prabhat (2014) also examine the
link between political connections and CDS spreads. However, Hanouna et al. (2014)’s tests are
primarily focused on the more general link between political activity and CDS spreads. In essence,
they compare CDS spreads between firms that invest in political capital and firms that do not invest
in political capital, and find that CDS spreads are lower for firms that invest in political capital. In
contrast, we focus on the impact of a political capital shock on risk-taking across a subset of firms
that are all investing in political capital, and we focus on how firms’ post-election risk-taking differs
among policy-sensitive and policy-neutral firms. We also examine the effects of political capital
shocks on the term structure of CDS spreads, which Hanouna et al. (2014) do not examine. In
addition to addressing different questions, the two papers also have different identification strategies
and interpret their results differently. Hence, while both sets of results suggest that CDS spreads
are sensitive to a firm’s investment in political capital, we view our results as being both distinct
and complementary to the results in Hanouna et al. (2014).
4.5
The Term Structure of Political Capital Shocks
While a large literature has found that political capital shocks have an immediate impact on stock
prices, there is no current evidence in the literature regarding the term structure of political capital
shocks. To what extent are the benefits of political capital shocks transitory instead of permanent?
What is the expected half-life of a positive political capital shock? The goal of this section is to
provide some preliminary answers to these questions.
Figures 2 and 3 plot the term structure of political capital shocks for implied volatility and
CDS spreads, respectively. There are two takeaways from the figures. First, the impact of political
capital shocks appears to be long-lasting. For example, Figure 3 shows that 10-year CDS spreads
25
respond (negatively) to positive political capital shocks almost as much as 1-year CDS spreads.
This suggests that the market anticipates the effects of political capital shocks to be long-lasting.
Second, the figures shows a pronounced upward “slope” effect for “lucky” firms. That is, relative to
unlucky firms, lucky firms’ long-dated CDS spreads and option-implied volatilities respond slightly
less emphatically to positive political capital shocks relative to their short-dated brethren.
Teasing out the “half-life” of political capital shocks is not straightforward, but a simple credit
risk example can help to shed light on how the two results in the graph are informative about
the term structure of political capital shocks. Suppose the annual probability of a credit event is
10%. Then the probability of an event occurring in the next five years is 1 − (1 − 0.10)5 ≈ 0.41
(assuming independence across years, which we assume for the purpose of simplicity despite its
unrealistic nature).23 Now suppose that the probability of an event occurring in the first year only
jumps from 0.10 to 0.05. The new probability of an event occurring within five years now drops
to 1 − (0.95 × (1 − 0.1)4 ≈ 0.38. In contrast, suppose that the probability of an event occurring
now decreases to 0.05 not only in the first year, but across all five years. Then the cumulative
probability that an event occurs within five years is 1 − (1 − 0.05)5 ≈ 0.23. In other words, the
difference between the original default probabilities (1-year = 0.1; 5-years = 0.41) and the new
default probabilities (temporary case: 1-year = 0.05, 5-years = 0.38; permanent case: 1-year =
0.05, 5-years = 0.23) is significantly greater when the shock to default probabilities is long-lasting
in nature, particularly at the long end of the maturity spectrum. As such, this implies that a longlasting political capital shock should lead to a relative steepening of CDS slopes when compared
with a short-lasting shock.24
This example highlights two points. First, the fact that CDS spreads drop significantly even
for long-dated contracts suggests that the market anticipates a large downward change in the
probability of default extending for periods beyond a single year. In the example above, when
the political capital shock only affects default probabilities in the first year, the effect on 5-year
default probabilities is muted. In contrast, figure 3 shows that there is a very large change in
23
In future iterations, we will use a hazard model for this example.
Importantly, in absolute terms, the CDS slope is now flatter; in the original case, the slope was 0.41 - 0.1 = 0.31;
in the case of a permanent shock, the absolute slope is now 0.23 - 0.05 = 0.18.
24
26
CDS spreads for long-dated contracts, suggesting that the effects we are capturing have lengthy
maturities. Second, in the example above, a sustained change in default probabilities creates a
steeper change in CDS slopes than a single-year change. Figure 3 shows that CDS slopes indeed
steepen modestly for “lucky” firms following positive political capital shocks. As such, figure 3
presents visual evidence that the effects of a political capital shock appear to have long-dated
effects on expected firm riskiness.
We test this proposition formally in Table 6. Panel A of the table presents results on the effect
of political capital shocks on implied volatility slopes. Specifications (1) – (3) repeat the differencein-difference estimation, while specifications (4) – (6) repeat the triple difference specification.
Specifications (1) – (3) suggest that there is in fact an upwards sloping term structure of these
shocks unconditionally. However, specifications (4) – (6) suggest that these patterns do not persist
for the firms that are policy sensitive. Panel B of the table presents results on the effect of political
capital shocks on CDS slopes. In contrast with the implied volatility slopes, in all six specifications
in the panel, “lucky” firms’ CDS slopes steepen by as much as 15% relative to “unlucky” firms
following close elections. These effects are stronger for policy-sensitive firms, and may in fact
completely explain these results, since the coefficients on P ost × Close W in Dummy lose economic
and statistical significance in the triple-difference estimation. When combined with the results from
Table 5, these results support the idea that the effects of political capital shocks have a long-term
(expected) effect on firms’ credit risk.
4.6
Firms’ Investment and Operating Decisions
Tables 4 and 5 suggest that market-driven proxies for firm risk-taking decline following positive
political capital shocks, and decline particularly strongly (in magnitude) in the case of policysensitive firms. However, these tables do not shed light on how firms’ risk-taking might be changing
following positive political capital shocks. To address this question, Tables 7 and 8 examine how
firms’ investment, leverage, R&D spending, profitability, and operational performance respond to
“lucky” political capital shocks. As in tables 4 and 5, we begin by examining the differential
27
response of “lucky” winners versus “unlucky” losers following the outcomes of close elections. We
then further split our sample based on whether firms are particularly sensitive to economic policy
uncertainty during a given election cycle.
Table 7 examines how firms’ investment, leverage, and R&D spending behavior respond to political capital shocks. The results in Panel A suggest that firms do not appear to significantly adjust
their investment, leverage, or R&D spending policies in response to a political capital shock: the
interaction term between the post-election and “lucky” close-election dummy variables is statistically zero in every specification. The fact that we do not find a differential post-election change in
leverage between “lucky” and “unlucky” firms contrasts with Claessens, Feijen, and Laeven (2008),
who find that leverage increases following positive political capital shocks in Brazil. Our findings
of no differential effects on investment and R&D also contrast with Do, Lee, and Nguyen (2013),
Ovtchinnikov, Reza, and Wu (2014), and Kim (2015), who report evidence that political capital
shocks have significant effects on investment and innovation (though in different directions).
However, when we segment our sample further based on firms’ differing sensitivity to economic
policy uncertainty, we find that policy-sensitive firms’ investment and leverage do respond strongly
to political capital shocks. In particular, Panel B shows that policy-sensitive firms respond to
a “lucky” political capital shock by increasing investment and decreasing leverage following close
election outcomes, though we do not find any effects on firms’ R&D spending. Our investment
and leverage results are economically large; holding all else equal, “lucky” policy-sensitive firms’
investment increases by about 11% and leverage decreases by about 2% relative to similarly “lucky”
firms that are less sensitive to economic policy shocks. These results are even stronger when
we compare policy-sensitive “lucky” winners versus other policy-sensitive firms that experienced
“unlucky” political capital shocks. Hence, the resolution of political uncertainty appears to have a
significantly different impact on the investment and leverage choices of policy-sensitive firms based
on whether these firms’ experienced positive or negative political capital shocks.
Table 8 extends the tests in Table 7 to examine how firms’ operating performance and profitability respond to political capital shocks. Panel A present difference-in-difference results, while Panel
28
B presents triple-difference results. The results in Panel A suggest that “lucky” firms experience
higher sales, higher returns on assets, and higher M/B ratios than “unlucky” firms following close
election outcomes. These results are largely in line with the existing literature.25
However, Panel B shows that these results are largely driven by policy sensitive-firms. For
example, Columns (1) and (3) of Panel B show that the increases in sales and M/B documented in
Panel A accrue almost exclusively to policy-sensitive firms who experience a “lucky” political capital shock. Furthermore, Panel B shows that “lucky” policy-sensitive firms also experience higher
asset growth, higher gross profit margins, and higher net profit margins than other “lucky” winners.
These effects are also economically significant; for example, the COGS/Sales ratio decreases by 6%
for “lucky” policy-sensitive firms relative to other lucky firms, and by 10% relative to “unlucky”
policy-sensitive firms. Collectively, the results in Table 8 indicate that shocks to political connectedness are associated with significantly stronger future operating performance and profitability,
particularly for policy-sensitive firms. While other studies have shown that sales positively respond
to an increase in political connectedness, all of the other results in Table 8 are new.
5
Alternative Mechanisms
Firms’ differential sensitivity to economic policy uncertainty appears to be a driving factor behind
many of our results. However, the literature has proposed alternative theories that link political
capital shocks to firm risk-taking. One possibility is that firms establish political connections to
insure themselves against future shocks — a bailout story. One would expect that if this were
the case, then an increase in political connectedness would be followed by an increase in firms’
ex-ante risk-taking. A second possibility is that firms establish political connections to increase
the probability of winning future government contracts (e.g. Cohen and Malloy (2014)). Since
the government may be less likely to award contracts to a distressed firm, these “governmentdependent” firms may want to reduce risk-taking following a positive shock to political capital in
order to lock in the expected gains from future government contracts. We test these both of these
25
For example, Akey (2015), Goldman, Rocholl, and So (2013), Tahoun (2014), and Amore and Bennedsen (2013)
find evidence that sales growth increases following an increase in political connectedness.
29
potential mechanisms below.
5.1
Bailout Likelihood
One would expect that if firms were establishing political connections to hedge against adverse
future states that they would take on additional risk when they were able to form more political
connections. Acharya, Pedersen, Philippon, and Richardson (2010) propose a measure of ex-ante
risk taking (systemic risk) in the context of the financial crisis — Marginal Expected Shortfall
(MES). MES measures a firm’s expected loss given that the market has a large negative return. A
smaller (more negative) value of MES indicates higher ex-ante risk. To examine the link between
political capital shocks and MES, we run the same differences-in-differences specification as in
previous tests. Table 9 presents the results of this analysis. All specifications indicate that MES
increases for better politically connected firms relative to the less connected peers in post election
years. This result in and of itself cannot rule out a “bailout” story: risk-taking could still be
increasing while the “price” of risk could be decreasing more, leading to an overall decrease in
MES despite an increase in risk-taking. However, we find little evidence of increased risk-taking
elsewhere in our tests; for example, our differences-in-differences tests show little evidence that
firms increase investment or leverage following positive political capital shocks. Hence, while we
cannot rule out a “bailout” story, we view this story as being unlikely to explain our results.
5.2
Government Contractors
The other potential channel that has been described in the literature is a “sticky-governmentcontracting” channel. Intuitively, firms that rely more on government contracts for their sales
have a stronger interest in supporting political candidates who can help them to earn future sales.
Conditional on having established political connections, these firms also have a strong incentive to
stay in business – loosely speaking, if a firm donates money to candidate X and candidate X is then
elected, the firm will not want to do anything to jeopardize its ability to profit from its relationship
with candidate X going forward. As such, this story implies that large government contractors
may respond to a positive political capital shock by reducing their risk-taking in anticipation of
30
obtaining future government contracts. Alternatively, firms experiencing a positive political capital
shock (and hence, a higher probability of obtaining government contracts) may simply kick back
and enjoy the “quiet life,” since their future earnings streams are less subject to market competition.
Cohen and Malloy (2014) find evidence consistent with this argument: they find that investment
is lower and operating performance is worse at government-dependent firms.
To test this story, we download segment data from COMPUSTAT and classify firms as being
“government-dependent” in a given quarter if they list the U.S. Government as one of their operating
segments. We then examine whether our previous results on risk-taking are being driven primarily
by government-dependent firms.
Before continuing, it is important to note that we identify government-dependent firms differently than Cohen and Malloy (2014). They examine regulatory filings to find firms who obtain more than 10% of sales from the U.S. government, whereas we simply examine firms that
have a separate operating segment for government sales. While it is not clear which approach is
more “correct,” it is possible that our identification procedure mis-classifies government-dependent
firms as non-government-dependent firms. This could bias our results against finding an effect for
government-dependent firms, and may also reduce our power to detect an effect for such firms. As
such, we view our findings below as simply descriptive.
Table 10 contains the results of our tests. In the table, we have chosen to focus on CDS
spreads; however, we obtain similar results for our other tests. Columns (1) - (3) of the table
show that the CDS spreads of government-dependent firms do indeed respond more negatively to
positive political capital shocks than non-government-dependent firms (e.g. the loading on the
triple-interaction term P ost × Close Election Dummy × Gov Contractor is negative). However,
this result is not statistically significant. Furthermore, the table shows that our primary effect
does not appear to be coming from government-dependent firms: columns (7)-(9) confirm that our
main result goes through even after excluding government-dependent firms from our sample. In
fact, columns (4)-(6) show that even within the sample of government-dependent firms, we obtain
qualitatively similar results to our prior results using all firms; that is, we still find that CDS
31
spreads drop more following elections for firms experiencing a positive political capital shock, with
similar magnitudes to our findings for non-government-dependent firms. Hence, our results do not
appear to be fully explained by the “sticky-government-contracting” hypothesis.
5.3
Firm versus Industry Effects
We also run a series of tests to ensure that we are not simply picking up industry-specific effects in
our results. For example, it may be that firms in the defense industry tend to support Republicans
while firms in the technology industry tend to support Democrats. One concern might be that
we are simply capturing the fact that, say, defense contractors tend to vote for Republican party
candidates and Republicans happened to fare well in a given election cycle. In this case, all defense
contractors may have large “political capital shocks” in years where Republican candidates fare
well, whereas the same firms will have low political capital shocks in years where Republicans do
poorly. While this scenario does not violate our primary identifying assumptions, it does present an
alternative explanation for our results on firm risk-taking. In particular, this scenario suggests that
our “political capital shocks” may not be stemming from actual shocks, but may instead simply be
picking up longstanding political affiliations between certain industries and certain political parties.
Table 11 tests this idea formally by examining whether our main results in Tables 4 through 8
are robust to different specifications that examine the effects of political capital shocks on firm
risk-taking by looking within industries as opposed to within firms. In particular, we replace the
firm-election cycle fixed effects that were used in Tables 4 through 8 with a combination of firm fixed
effects and industry-election cycle fixed effects (where industry definitions are based on Fama and
French (1997)’s 49-industry classification system). These tests examine whether positive political
capital shocks are associated with lower firm risk-taking within a given industry and election cycle.
In other words, even if all defense contractors had positive political capital shocks in a given cycle
(say, 2002), this test tells us whether defense contractors that received more positive political
capital shocks than other defense contractors in this election cycle are still more likely to reduce
their risk-taking following the outcome of the election.
32
Table 11 shows that the answer to this question is yes: all of our main results are qualitatively
and quantitatively similar regardless of whether we look within industry-election cycles (as in
Table 11) or within firm-election cycles (as in our earlier tests). Hence, the effects we document in
this paper are not simply picking up firms from certain industries or longstanding industry-specific
political affiliations.
6
Robustness
We perform a variety of tests to ensure the robustness of our main results. We begin by constructing
placebo tests for our main difference in difference specifications where we artificially move the actual
election dates in our sample forward to verify that there are no “pre-trends” in the data for our two
groups of firms. These robustness checks are detailed in our Internet Appendix and are available
to review upon request.
We also verify that the parallel trends assumptions behind our differences-in-differences specifications are met empirically. One major concern, in particular given that much of our data is
observed on a daily frequency, is that news about the likelihood of close election outcomes becomes
available and some firms strategically re-allocate their contributions to support candidates that are
now more likely to win. If some firms do this, but other firms do not, this could create a violation
of the parallel trends assumptions. It is not immediately obvious that this is a problem because
firms frequently make small contributions to the same candidate at various time periods during
an election cycle, when the outcome is less likely to be predictable. However, in order to address
this concern, we recompute our connection measures excluding all contributions made in the two
months leading up to the election. On the one hand, this filter causes us to exclude about 20% of
the contributions that firms make, but on the other hand, the correlation between our connection
measures with and without these contributions is 80-90%. We replicate our main findings using
these results and find that nearly all of our results are quantitatively unchanged. Tables 1 and 2
of the Internet Appendix reproduce our results.
Finally, one potential concern for our MES results is that the financial crisis is driving our
33
results. We address this concern by removing the 2008 political cycle (years 2008 and 2009) from
our sample and replicating our MES results. All of the results in Table 9 are comparable in
significance and magnitude excluding the crisis. Table 3 of the Internet Appendix presents this
analysis.
7
Conclusion
We link the cross-section of firms’ sensitivities to economic policy uncertainty to their subsequent
political activity and post-election risk-taking behavior. We first show that firms with a high sensitivity to economic policy uncertainty donate more to candidates for elected office than less-sensitive
firms. Using a sample of close U.S. congressional elections, we then show that plausibly exogenous
positive shocks to policy-sensitive firms’ political capital bases produce large subsequent changes in
these firms’ investment, leverage, operating performance, CDS spreads, and option-implied volatility. These effects are weaker in magnitude among less policy-sensitive firms, suggesting that the
marginal value of a political connection is increasing in firms’ ex-ante sensitivity to policy uncertainty. We also examine the term structure of credit risk and implied volatility following political
capital shocks and find that these shocks are expected to be long-lasting in nature. Our results
cannot be explained by moral hazard or government contracting arguments and represent the first
attempt in the literature to shed light on the relationship between firms’ policy sensitivities and
their subsequent risk-taking behavior. While there are no existing theories (to our knowledge) that
link policy uncertainty to political capital and political capital to risk-taking, we view this as an
interesting prospective area for future research.
34
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37
Appendix A - Variable Definitions
Variable
Post Election
Close Wins
Close Losses
Net Close Wins
Definition
A binary variable that takes the value of 1 in all time
periods following an election.
The number of winning candidates involved in a close
general election that a firm donated to prior to the election
The number of losing candidates involved in a close general election that a firm donated to prior to the election
Close Wins - Close Losses
Post × Net Close
Wins
Post × Close Wins
Net Close Wins multiplied by Post Election
Post × Close Losses
Close Losses multiplied by Post Election
Close Win Dummy
A binary variable that takes the value of 1 if Net Close
Wins > 0
Close Win Dummy multiplied by Post Election
Post × Close Win
Dummy
CAPM Beta
CAPM Vol
MES
Log1y
Log5y
Log10y
Log5y1y
Log10y5y
Log10y1y
Slope5y1y
Slope10y5y
Slope10y1y
1-month
implied
volatility
3-month
implied
volatility
5-month
implied
volatility
3mo-1mo volatility
slope
5mo-3mo volatility
slope
5mo-1mo volatility
slope
Firm return
M/B
Close Wins multiplied by Post Election
A firm’s CAPM Beta
The standard deviation of residuals of a from annual Beta
regressions
A firm’s Marginal Expected Shortfall computed following
Acharya et al. (2010)
The natural log of a firm’s 1-year CDS spread
The natural log of a firm’s 5-year CDS spread
The natural log of a firm’s 10-year CDS spread
Log5y - Log1y
Log10y - Log5y
Log10y - Log1y
A firm’s unadjusted 5-year CDS spread minus the same
firm’s 1-year CDS spread
A firm’s 10-year CDS spread minus the same firm’s 5-year
CDS spread
A firm’s 10-year CDS spread minus the same firm’s 1-year
CDS spread
The implied volatility of a firm’s 1-month at-the-money
call options
The implied volatility of a firm’s 3-month at-the-money
call options
The implied volatility of a firm’s 5-month at-the-money
call options
3-month implied vol minus 1-month implied vol
Source
CRSP
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
Federal Election Commission
and Authors’ Computation
CRSP and Authors’ Computation
CRSP and Authors’ Computation
CRSP and Authors’ Computation
Markit
Markit
Markit
Markit
Markit
Markit
Markit
Markit
Markit
OptionMetrics
OptionMetrics
OptionMetrics
OptionMetrics
5-month implied vol minus 3-month implied vol
OptionMetrics
5-month implied vol minus 1-month implied vol
OptionMetrics
A firm’s daily (unless otherwise noted) stock return (variable: ret)
A firm’s market capitalization divided by its lagged book
value of equity (variables: prc, shrout, ceqq)
CRSP
38
CRSP, Compustat
VW ind return
Ln(Size)
Investment
R&D spending
Book leverage
Sales growth
Asset growth
EBITDA growth
Profit margin
COGS
SG&A
Cash
Current ratio
Scaled FCF
Profitability
The value-weighted return on a firm’s 3-digit SIC industry (weights are based on market capitalization)
The natural log of the firm’s book value of assets (variable: atq)
Quarterly capital expenditures divided by lagged net
PP&E (variables: capxy (adjusted), ppentq)
Quarterly R&D expenditure divided by book assets (variables: xrdq, atq)
Quarterly book value of debt divided by book assets
(variables: dlcq, dlttq, atq)
Quarter-over-quarter change in a firm’s sales (variable:
revtq)
Quarter-over-quarter change in a firm’s assets (variable:
atq)
Quarter-over-quarter change in a firm’s EBITDA (variable: oibdpq)
EBIT divided by sales (variables: oiadpq, revtq)
Cost of goods sold divided by sales (variables: cogsq,
revtq)
Selling, general, & administrative expenses divided by
sales (variables: xsgaq, revtq)
Cash & cash equivalents divided by book assets (variables: cheq, atq)
Current assets divided by current liabilities (variables:
actq, lctq)
EBITDA divided by lagged net PP&E (variables: oibdpq, ppentq)
EBITDA divided by assets (variables: oiadpq, atq)
39
CRSP
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Compustat
Figure 1: Net Close Wins Histogram
The figure below shows the distribution of N et Close W ins measured from 1998-2010.
40
Figure 2: Implied Volatility Term Structure
The figure below plots the Implied Volatility Term Structure for firms that have an above median draw. The solid
line plot the point estimate for implied volatility at different call option maturities. The dashed lines show the upper
and lower bounds of a 95% confidence interval.
Call Option Term Structure
Maturity of Call Option (Month)
-0.025
1
2
3
4
5
-0.03
-0.035
-0.04
-0.045
-0.05
-0.055
-0.06
Point Estimate
95% CI
41
95% CI
6
Figure 3: Credit Default Swap Spread Term Structure
The figure below plots the Credit Default Swap Spread Term Structure for firms that have an above median draw.
The solid line plot the point estimate for the CDS spread at different contract maturities. The dashed lines show the
upper and lower bounds of a 95% confidence interval.
CDS Spread Term Structure
1
Maturity of CDS Contract (Years)
5
10
-0.0015
-0.0025
-0.0035
-0.0045
-0.0055
-0.0065
-0.0075
Point Estimate
CI 95%
42
CI 95%
Table 1: Summary Statistics
Panel A presents summary statistics for (i) political connections data (taken from Federal Election Commission
filings), (ii) implied volatility data (OptionMetrics), and (iii) CDS spreads (Markit). Definitions of all variables
described in the panel can be found in the text and Appendix A. Panels B, C, and D report summary statistics for
firms that are sensitive to the Economic Policy Uncertainty (EPU) index of Baker, Bloom, and Davis (2015) based
on our estimation procedure (details of which can be found in the text). Panel B reports the number and proportion
of firms in each election cycle that are sensitive to the EPU index as well as the fraction of sensitive firms whose EPU
sensitivities are positive and negative, respectively. Panel C reports summary statistics on the number of election
cycles that a given firm is policy-sensitive according to our estimation procedure. Panel D reports summary statistics
regarding the industry distribution of policy-sensitive firms across our sample period (1998-2010).
Panel A — Political Connections, Implied Volatility, and CDS Spreads
Data Type
Variable
Mean
Median Std. Dev.
Political Connections N et Close W ins
0.13
0
2.37
Close W ins
2.85
2
3.22
Close Losses
2.71
2
2.77
T otal Contributions
$118,762
39,950
231,214
Close Election Contributions
$16,328
7,000
25,896
Other Contributions
$107,469
35,775
210,956
Implied Volatility
1 month implied volatility
0.4038
0.3495
0.2290
3 month implied volatility
0.3934
0.3453
0.2123
5 month implied volatility
0.3869
0.3423
0.2025
3mo/1mo slope
-0.0100
-0.0033
0.0465
5mo/3mo slope
-0.0060
-0.0016
0.0246
5mo/1mo slope
-0.0159
-0.0058
0.0572
CDS Spreads
1 year spread
0.0183
0.0035
0.0878
5 year spread
0.0214
0.0078
0.0569
10 year spread
0.0216
0.0094
0.0498
5yr/1yr slope
0.0036
0.0028
0.0255
5yr/1yr slope
0.0006
0.0014
0.0121
10yr/1yr slope
0.0043
0.0043
0.0341
Panel B — Firm Sensitivity to Economic Policy Uncertainty
Election
All
Policy-Sensitive Fraction
Positive
Cycle
Firms
Firms
Sensitive Std. Dev. Sensitivity
1998
10,211
1,463
0.143
0.350
29%
2000
9.698
1,248
0.129
0.335
41%
2002
8,195
938
0.114
0.318
43%
2004
7,376
1,586
0.215
0.411
93%
2006
7,462
905
0.122
0.326
32%
2008
7,646
3,689
0.482
0.500
7%
2010
7,203
568
0.079
0.270
39%
Total
57,791
10,397
0.180
0.382
35%
Number
7,838
7,838
7,838
5,433
3,988
5,398
842,190
840,089
830,831
840,089
830,831
830,831
354,697
387,287
358,344
353,271
356,658
342,762
Negative
Sensitivity
71%
59%
57%
7%
68%
93%
61%
65%
Panel C — Number of Policy-Sensitive Election Cycles Per Firm
(Sample restricted to firms present in all seven election cycles)
Number of Cycles where
Firm
Empirical Binomial Dist.
Firm is Policy-Sensitive
Count Distribution
(p = 0.180)
0 cycles
840
26.7%
25.0%
1 cycle
1,317
41.8%
38.3%
2 cycles
761
24.2%
25.2%
3 cycles
195
6.2%
9.2%
4 cycles
32
1.0%
2.0%
5 cycles
4
0.1%
0.3%
6 cycles
0
0.0%
0.0%
7 cycles
0
0.0%
0.0%
Test: Actual = Binomial
Chi-Square
p-Value
N
43
64.60
< 0.0001
3,149
Table 1: Summary Statistics (Continued)
Panel D — Number of Policy-Sensitive Firms Per Fama-French 49 Industry
Industry
Industry
Number Count Mean Std. Dev.
Real Estate
47
304
0.224
0.417
Computers
35
773
0.210
0.407
Electronic Equipment
37
2095
0.208
0.406
Non-Metallic and Industrial Metal Mining
28
208
0.202
0.402
Measuring and Control Equipment
38
657
0.199
0.4
Communication
32
1379
0.198
0.399
Precious Metals
27
350
0.191
0.394
Machinery
21
1006
0.191
0.393
Shipbuilding and Railroad Equipment
25
69
0.188
0.394
Chemicals
14
506
0.186
0.389
Fabricated Products
20
88
0.182
0.388
Candy and Soda
3
150
0.180
0.385
Business Services
34
2365
0.179
0.383
Transportation
41
794
0.179
0.383
Electrical Equipment
22
834
0.179
0.383
Trading
48
8344
0.175
0.38
Defense
26
63
0.175
0.383
Textiles
16
132
0.174
0.381
Construction
18
401
0.172
0.378
Apparel
10
349
0.172
0.378
Restaurants, Hotels, and Motels
44
685
0.171
0.377
Insurance
46
1176
0.169
0.375
Aircraft
24
149
0.168
0.375
Computer Software
36
2549
0.167
0.373
Tobacco Products
5
60
0.167
0.376
Steel Works
19
458
0.166
0.372
Medical Equipment
12
1049
0.166
0.372
Recreation
6
271
0.162
0.369
Petroleum and Natural Gas
30
1411
0.162
0.368
Almost Nothing
49
268
0.160
0.368
Printing and Publishing
8
351
0.160
0.367
Entertainment
7
444
0.158
0.365
Automobiles and Trucks
23
457
0.155
0.363
Business Supplies
39
368
0.155
0.362
Construction Materials
17
475
0.154
0.361
Wholesale
42
1407
0.154
0.361
Utilities
31
1043
0.153
0.361
Consumer Goods
9
339
0.153
0.361
None
None
850
0.152
0.359
Pharmaceutical Products
13
1965
0.149
0.356
Healthcare
11
626
0.141
0.348
Shipping Containers
40
100
0.140
0.349
Banking
45
4130
0.140
0.347
Coal
29
80
0.138
0.347
Retail
43
1610
0.137
0.344
Beer and Liquor
4
156
0.135
0.342
Personal Services
33
404
0.134
0.341
Food Products
2
483
0.124
0.33
Rubber and Plastic Products
15
205
0.117
0.322
Agriculture
1
104
0.106
0.309
44
Table 2: Economic Policy Uncertainty Sensitivity and Firm Characteristics
This table presents summary statistics for firms that are sensitive to Economic Policy Uncertainty and for those that
are not sensitive. Panel A presents univariate differences, while Panel B presents results from a Logit analysis with an
indicator variable that takes the value of one if a firm has been classified as sensitive to economic policy uncertainty
and 0 otherwise as the dependent variable. Details of this estimation procedure are found in the text. Standard
errors are presented in parentheses. The symbols *, **, and *** denote statistical significance at the 10%, 5%, and
1% levels, respectively.
Panel A — Univariate Differences
Book
Ln(Size)
Leverage
Other firms
9.057
0.684
(0.012)
(0.001)
22,668
22,415
Policy-sensitive firms
9.282
0.706
(0.027)
(0.004)
4,866
4,796
Difference
0.225***
0.021***
(0.028)
(0.004)
Panel B — Logit Analysis
(1)
PolicyVariable
Sensitive
ln(Size)
0.0595**
(0.0282)
Book Leverage
0.610**
(0.276)
It /Kt−1
-0.546
(0.844)
M/B
-0.00658
(0.0114)
P rof it M argin
0.0187
(0.0495)
N et P P &E/Assets
-0.222
(0.179)
ROA
1.460
(2.191)
Intercept
-2.324***
(0.299)
Fixed effects
None
Clustering
Firm
Observations
21,570
Pseudo-R squared
0.005
(2)
PolicySensitive
0.0580
(0.0467)
0.634
(0.439)
-0.511
(1.164)
-0.00906
(0.0170)
0.0149
(0.0582)
-0.207
(0.489)
1.857
(2.510)
-2.325***
(0.546)
None
FF-Cycle
21,210
0.005
Investment /
Capital
0.052
(0.001)
19,387
0.051
(0.001)
4,310
-0.001
(0.001)
Market /
Book
3.005
(0.024)
21,480
2.973
(0.059)
4,564
-0.031
(0.059)
Net PPE /
Assets
0.312
(0.002)
21,779
0.297
(0.004)
4,657
-0.015***
(0.004)
Profit
Margin
0.104
(0.005)
20,501
0.118
(0.004)
4,480
0.014
(0.011)
(3)
PolicySensitive
0.00672
(0.0373)
1.003***
(0.372)
-1.224
(1.084)
0.0115
(0.0133)
0.0529
(0.0723)
-0.223
(0.230)
1.410
(2.963)
-2.766***
(0.424)
Cycle
Firm
21,570
0.236
(4)
PolicySensitive
0.00356
(0.0437)
1.008**
(0.453)
-1.203
(1.283)
0.00880
(0.0162)
0.0488
(0.0753)
-0.190
(0.336)
1.552
(3.182)
-2.718***
(0.549)
Cycle
FF-Cycle
21,210
0.239
(5)
PolicySensitive
0.0284
(0.0484)
1.112**
(0.505)
-1.195
(1.242)
0.0170
(0.0178)
0.0781
(0.108)
0.0368
(0.416)
3.147
(3.518)
-16.59***
(3.832)
FF-Cycle
Firm
14,808
0.262
(6)
PolicySensitive
0.0284
(0.0586)
1.112*
(0.603)
-1.195
(1.421)
0.0170
(0.0203)
0.0781
(0.112)
0.0368
(0.442)
3.147
(3.475)
-16.59***
(1.205)
FF-Cycle
FF-Cycle
14,808
0.262
45
Return on
Assets
0.021
(0.001)
22,115
0.021
(0.001)
4,743
0.000
(0.001)
46
Table 3: Economic Policy Uncertainty Sensitivity and Political Contributions
Fixed effects
Clustering
Observations
R-squared
Intercept
Cash/Assets
M/B
P rof it M argin
Book Leverage
Ln(Size)
P olicy Sensitive
11.11***
(0.0467)
None
Firm
27,601
0.003
(1)
Ln(Total
Contributions)
0.207***
(0.0568)
11.11***
(0.00519)
Firm
Firm
27,601
0.857
(2)
Ln(Total
Contributions)
0.194***
(0.0293)
12.03***
(0.490)
Firm, FF-Cycle
Firm
27,190
0.905
(3)
Ln(Total
Contributions)
0.0792**
(0.0328)
(4)
Ln(Total
Contributions)
0.0749**
(0.0352)
0.433***
(0.0438)
-0.00583
(0.138)
0.0257
(0.0169)
0.00619*
(0.00362)
0.0348
(0.160)
8.293***
(0.614)
Firm, FF-Cycle
Firm
23,077
0.910
(5)
Ln(Close-election
Contributions)
0.136**
(0.0555)
0.411***
(0.0510)
-0.301
(0.193)
0.0218
(0.0172)
0.00713
(0.00444)
-0.145
(0.219)
4.124***
(0.874)
Firm, FF-Cycle
Firm
23,069
0.813
(6)
Ln(Other
Contributions)
0.0671*
(0.0384)
0.437***
(0.0470)
0.0936
(0.164)
0.0128
(0.0246)
0.00522
(0.00391)
0.172
(0.175)
8.080***
(0.607)
Firm, FF-Cycle
Firm
22,925
0.902
-0.540
(2.635)
Firm, FF-Cycle
Firm
27,190
0.515
(7)
Net CloseElection Wins
0.0657
(0.124)
(8)
Net CloseElection Wins
0.102
(0.136)
0.194*
(0.104)
0.0963
(0.404)
-0.0611*
(0.0367)
-0.0029
(0.0098)
-0.479
(0.483)
-2.222
(2.844)
Firm, FF-Cycle
Firm
23,077
0.531
This table documents the correlation between Economic Policy Uncertainty Sensitivity and Political Contributions. The dependent variable in columns (1) – (4)
is the natural logarithm of the amount a firm contributed to candidates in House and Senate races. This variable is then decomposed in Columns (5) and (6) into
contributions to candidates in close elections (Column 5) and contributions to candidates in other elections (Column 6). The dependent variable in columns (7)
and (8) is the net number of donation recipients who won their respective (close) elections within a given election cycle. All independent variables are defined in
the Appendix. Standard errors are reported in parentheses. The symbols *, **, and *** denote statistical significance at the 10%, 5%, and 1% levels, respectively.
47
Table 4: The Impact of Political Capital Shocks on Implied Volatility
0.395***
(0.00103)
Firm-Cycle
Firm-Cycle
841,514
0.748
Fixed effects
Clustering
Observations
R-squared
0.0349***
(0.00306)
-0.0494***
(0.00402)
Intercept
Industy Return
F irm Return
P ost × N et Close W ins
P ost × Close W in Dummy
P ost Election
Firm-Cycle
Firm-Cycle
841,169
0.750
-0.263***
(0.00943)
-0.162***
(0.0126)
0.395***
(0.00103)
0.0354***
(0.00308)
-0.0495***
(0.00403)
Panel A — Difference-in-Difference Analysis
(1)
(2)
1-Month
1-Month
Implied
Implied
Volatility
Volatility
Firm-Cycle
Firm-Cycle
839,403
0.788
0.384***
(0.000994)
0.0357***
(0.00297)
-0.0446***
(0.00386)
(3)
3-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
839,068
0.789
-0.176***
(0.00732)
-0.0606***
(0.00953)
0.384***
(0.000996)
0.0360***
(0.00298)
-0.0446***
(0.00386)
(4)
3-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
830,153
0.802
0.377***
(0.000962)
0.0350***
(0.00287)
-0.0421***
(0.00374)
(5)
5-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.803
-0.145***
(0.00664)
-0.0244***
(0.00852)
0.377***
(0.000963)
0.0352***
(0.00288)
-0.0421***
(0.00375)
(6)
5-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
841,169
0.751
-0.0117***
(0.000757)
-0.262***
(0.00945)
-0.163***
(0.0126)
0.395***
(0.00103)
0.0172***
(0.00215)
(7)
1-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
839,068
0.790
-0.0107***
(0.000749)
-0.176***
(0.00733)
-0.0614***
(0.00957)
0.384***
(0.000990)
0.0196***
(0.00207)
(8)
3-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.804
-0.0101***
(0.000728)
-0.145***
(0.00664)
-0.0251***
(0.00855)
0.377***
(0.000958)
0.0197***
(0.00200)
(9)
5-Month
Implied
Volatility
This table documents the effects of political capital shocks on implied volatility using data on firms’ donations to political candidates in close U.S. federal
elections. Panel A presents the difference-in-difference analysis for firms that have “lucky” political capital shocks before and after an election compared to those
that had “unlucky” shocks. Panel B presents a triple difference analysis that examines how this effect varies for firms that are sensitive to economic policy
uncertainty. Policy Uncertainty Sensitivity is measured using the correlation between a firm’s equity returns and the Baker, Bloom, and Davis (2015) economic
policy uncertainty index as defined in the text. Daily implied volatilities are taken from OptionMetrics and are computed using prices on at-the-money call
options. Each regression uses daily data from six months’ prior to a federal election to six months following the election. Our election data spans all biennial U.S.
federal elections from 1998-2010. All independent variables are defined in the Appendix. Standard errors are reported in parentheses. The symbols *, **, and
*** denote statistical significance at the 10%, 5%, and 1% levels, respectively.
48
0.395***
(0.000954)
Firm-Cycle
Firm-Cycle
841,514
0.759
Fixed effects
Clustering
Observations
R-squared
0.00527**
(0.00267)
0.134***
(0.00889)
-0.0299***
(0.00351)
-0.0495***
(0.0155)
Intercept
Industy Return
F irm Return
P ost × P olicy × N et Close W ins
P ost × N et Close W ins
P ost × P olicy × Close W in Dummy
P ost × Close W in Dummy
P ost × P olicy Sensitive
P ost Election
(1)
1-Month
Implied
Volatility
Panel B — Triple-Difference Analysis
Firm-Cycle
Firm-Cycle
841,169
0.761
-0.269***
(0.00947)
-0.174***
(0.0127)
0.395***
(0.000956)
0.00566**
(0.00267)
0.135***
(0.00894)
-0.0298***
(0.00351)
-0.0499***
(0.0156)
(2)
1-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
839,403
0.801
0.384***
(0.000914)
0.00599**
(0.00252)
0.135***
(0.00869)
-0.0244***
(0.00329)
-0.0552***
(0.0152)
(3)
3-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
839,068
0.802
-0.182***
(0.00733)
-0.0727***
(0.00962)
0.384***
(0.000916)
0.00623**
(0.00252)
0.136***
(0.00873)
-0.0243***
(0.00329)
-0.0555***
(0.0153)
(4)
3-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
830,153
0.815
0.377***
(0.000884)
0.00598**
(0.00242)
0.132***
(0.00843)
-0.0220***
(0.00320)
-0.0572***
(0.0146)
(5)
5-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.816
-0.151***
(0.00659)
-0.0370***
(0.00860)
0.377***
(0.000885)
0.00617**
(0.00242)
0.132***
(0.00846)
-0.0219***
(0.00320)
-0.0574***
(0.0147)
(6)
5-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
841,169
0.762
-0.00707***
(0.000706)
-0.0116***
(0.00248)
-0.269***
(0.00949)
-0.175***
(0.0127)
0.395***
(0.000952)
-0.00503***
(0.00188)
0.113***
(0.00731)
(7)
1-Month
Implied
Volatility
Table 4: The Impact of Political Capital Shocks on Implied Volatility (Continued)
Firm-Cycle
Firm-Cycle
839,068
0.802
-0.00590***
(0.000691)
-0.0129***
(0.00246)
-0.182***
(0.00734)
-0.0734***
(0.00963)
0.384***
(0.000912)
-0.00245
(0.00177)
0.111***
(0.00713)
(8)
3-Month
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.816
-0.00534***
(0.000667)
-0.0134***
(0.00238)
-0.151***
(0.00660)
-0.0377***
(0.00861)
0.377***
(0.000882)
-0.00165
(0.00171)
0.107***
(0.00686)
(9)
5-Month
Implied
Volatility
49
Table 5: The Impact of Political Capital Shocks on CDS Spreads
-5.523***
(0.0103)
Firm-cycle
Firm-cycle
355,735
0.898
Fixed effects
Clustered errors
Observations
R-squared
0.0439
(0.0322)
-0.309***
(0.0393)
Intercept
P rof itability
Current Ratio
Cash
Book Leverage
M/B
Ln(Size)
F irm Return
P ost × Close Losses
P ost × Close W ins
P ost × Close W in Dummy
P ost Election
Firm-cycle
Firm-cycle
249,129
0.895
0.484***
(0.0373)
-0.753***
(0.142)
-0.00831**
(0.00339)
2.939***
(0.434)
-0.776**
(0.370)
0.0549
(0.0484)
-1.016***
(0.379)
-0.250
(1.322)
0.0781**
(0.0359)
-0.355***
(0.0433)
Panel A — Difference-in-Difference Analysis
(1)
(2)
1-Year
1-Year
Log CDS
Log CDS
Spread
Spread
Firm-cycle
Firm-cycle
388,325
0.920
-4.747***
(0.00618)
0.0795***
(0.0189)
-0.187***
(0.0238)
(3)
5-Year
Log CDS
Spread
Firm-cycle
Firm-cycle
271,160
0.926
0.310***
(0.0241)
-0.414***
(0.0737)
-0.00248
(0.00162)
1.672***
(0.234)
-0.213
(0.220)
0.0188
(0.0287)
-0.900***
(0.250)
-1.919***
(0.694)
0.0917***
(0.0207)
-0.210***
(0.0254)
(4)
5-Year
Log CDS
Spread
Firm-cycle
Firm-cycle
359,382
0.917
-4.545***
(0.00542)
0.105***
(0.0161)
-0.161***
(0.0209)
(5)
10-Year
Log CDS
Spread
Firm-cycle
Firm-cycle
251,514
0.922
0.241***
(0.0238)
-0.249***
(0.0637)
-0.00496***
(0.00187)
1.400***
(0.202)
-0.0847
(0.197)
0.00271
(0.0235)
-0.538**
(0.211)
-3.089***
(0.601)
0.112***
(0.0174)
-0.173***
(0.0221)
(6)
10 Year
Log CDS
Spread
Firm-cycle
Firm-cycle
249,129
0.896
-0.0714***
(0.00695)
0.0767***
(0.00951)
0.484***
(0.0368)
-0.757***
(0.134)
-0.00840**
(0.00326)
2.791***
(0.417)
-0.768**
(0.365)
0.0517
(0.0488)
-0.890**
(0.398)
-0.121
(1.253)
-0.0672**
(0.0336)
(7)
1-Year
Log CDS
Spread
Firm-cycle
Firm-cycle
271,160
0.927
-0.0445***
(0.00444)
0.0411***
(0.00590)
0.307***
(0.0238)
-0.415***
(0.0697)
-0.00251
(0.00160)
1.594***
(0.227)
-0.210
(0.222)
0.0176
(0.0297)
-0.823***
(0.246)
-1.867***
(0.661)
0.0292
(0.0191)
(8)
5-Year
Log CDS
Spread
Firm-cycle
Firm-cycle
251,514
0.923
-0.0367***
(0.00388)
0.0352***
(0.00495)
0.240***
(0.0236)
-0.250***
(0.0614)
-0.00497***
(0.00176)
1.331***
(0.198)
-0.0919
(0.201)
0.00121
(0.0242)
-0.480**
(0.212)
-3.039***
(0.580)
0.0564***
(0.0167)
(9)
10-Year
Log CDS
Spread
This table documents the effects of political capital shocks on CDS Spreads using data on firms’ donations to political candidates in close U.S. federal elections.
Panel A presents the difference-in-difference analysis for firms that have “lucky” political capital shocks before and after an election compared to those that had
“unlucky” shocks. Panel B presents a triple difference analysis that examines how this effect varies for firms that are sensitive to economic policy uncertainty.
Policy Uncertainty Sensitivity is measured using the correlation between a firm’s equity returns and the Baker, Bloom and Davis (2015) economic policy uncertainty
index as defined in the text. Daily CDS spreads are taken from Markit for 1-year, 5-year, and 10-year tenors. All CDS spreads are then expressed in log form.
Each regression uses daily data from six months’ prior to a federal election to six months following the election. Our election data spans all biennial U.S. federal
elections from 1998-2010. All independent variables are defined in the Appendix. Standard errors are reported in parentheses. The symbols *, **, and *** denote
statistical significance at the 10%, 5%, and 1% levels, respectively.
50
-5.525***
(0.00916)
Firm-Cycle
Firm-Cycle
354,146
0.909
Fixed Effect
Clustered errors
Observations
R-squared
-0.235***
(0.0299)
0.911***
(0.0680)
-0.0797**
(0.0362)
-0.560***
(0.120)
Intercept
P rof itability
Book Leverage
Ln(Size)
M/B
F irm Return
P ost × P olicy × N et Close W ins
P ost × N et Close W ins
P ost × P olicy × Close W in Dummy
P ost × Close W in Dummy
P ost × P olicy Sensitive
P ost Election
(1)
1-Year
Log CDS
Spread
Panel B — Triple-Difference Analysis
Firm-Cycle
Firm-Cycle
298,366
0.911
0.367***
(0.0279)
-0.000624**
(0.000281)
-0.471***
(0.119)
1.954***
(0.362)
-1.084***
(0.344)
-2.248**
(1.116)
-0.238***
(0.0297)
0.945***
(0.0678)
-0.0807**
(0.0358)
-0.607***
(0.125)
(2)
1-Year
Log CDS
Spread
Firm-Cycle
Firm-Cycle
386,523
0.926
-4.750***
(0.00556)
-0.0765***
(0.0175)
0.517***
(0.0414)
-0.0667***
(0.0217)
-0.260***
(0.0767)
(3)
5-Year
Log CDS
Spread
Firm-Cycle
Firm-Cycle
325,005
0.931
0.251***
(0.0198)
-0.000295
(0.000189)
-0.280***
(0.0637)
1.179***
(0.202)
-0.889***
(0.203)
-2.858***
(0.601)
-0.0822***
(0.0173)
0.539***
(0.0410)
-0.0585***
(0.0211)
-0.307***
(0.0811)
(4)
5-Year
Log CDS
Spread
Firm-Cycle
Firm-Cycle
357,732
0.923
-4.547***
(0.00490)
-0.0280*
(0.0148)
0.435***
(0.0354)
-0.0599***
(0.0192)
-0.200***
(0.0660)
(5)
10-Year
Log CDS
Spread
Firm-Cycle
Firm-Cycle
301,983
0.926
0.200***
(0.0193)
-0.000189
(0.000180)
-0.151***
(0.0570)
0.995***
(0.179)
-0.533***
(0.184)
-3.796***
(0.540)
-0.0353**
(0.0146)
0.449***
(0.0352)
-0.0528***
(0.0186)
-0.236***
(0.0690)
(6)
10-Year
Log CDS
Spread
-0.0258***
(0.00733)
-0.0964***
(0.0181)
0.370***
(0.0276)
-0.000545*
(0.000283)
-0.474***
(0.117)
1.943***
(0.351)
-0.925**
(0.409)
-2.215**
(1.104)
-0.257***
(0.0209)
0.686***
(0.0583)
(7)
1-Year
Log CDS
Spread
Firm-Cycle
Firm-Cycle
298,366
0.911
Table 5: The Impact of Political Capital Shocks on CDS Spreads (Continued)
Firm-Cycle
Firm-Cycle
325,005
0.931
-0.0175***
(0.00438)
-0.0573***
(0.0117)
0.251***
(0.0196)
-0.000261
(0.000192)
-0.281***
(0.0628)
1.160***
(0.196)
-0.782***
(0.216)
-2.834***
(0.593)
-0.0974***
(0.0122)
0.398***
(0.0358)
(8)
5-Year
Log CDS
Spread
Firm-Cycle
Firm-Cycle
301,983
0.926
-0.0163***
(0.00387)
-0.0394***
(0.0103)
0.201***
(0.0192)
-0.000158
(0.000181)
-0.152***
(0.0567)
0.982***
(0.175)
-0.465**
(0.197)
-3.775***
(0.535)
-0.0487***
(0.0104)
0.342***
(0.0307)
(9)
10-Year
Log CDS
Spread
51
Table 6: Term Structure Effects of Political Capital Shocks
Fixed effects
Clustering
Observations
R-squared
Intercept
Industry Return
F irm Return
P ost × P olicy × Close W in Dummy
P ost × P olicy Sensitive
P ost × Close W in Dummy
P ost Election
Panel A — Implied Volatility
Firm-Cycle
Firm-Cycle
839,068
0.151
0.0870***
(0.00358)
0.101***
(0.00492)
-0.0114***
(0.000177)
0.000722
(0.000462)
0.00445***
(0.000741)
(1)
3mo - 1mo
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.191
0.0320***
(0.00188)
0.0313***
(0.00243)
-0.00628***
(0.000101)
-0.000633**
(0.000258)
0.00279***
(0.000429)
(2)
5mo - 3mo
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.222
0.119***
(0.00470)
0.132***
(0.00609)
-0.0176***
(0.000242)
0.000170
(0.000626)
0.00710***
(0.00102)
(3)
5mo - 1 mo
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.223
0.000788
(0.000686)
0.00759***
(0.00110)
-0.00281*
(0.00162)
-0.00656**
(0.00273)
0.119***
(0.00470)
0.132***
(0.00610)
-0.0176***
(0.000241)
(4)
3mo - 1mo
Implied
Volatility
Firm-Cycle
Firm-Cycle
839,068
0.151
0.000726
(0.000506)
0.00505***
(0.000803)
-1.97e-05
(0.00121)
-0.00504**
(0.00200)
0.0870***
(0.00357)
0.101***
(0.00492)
-0.0114***
(0.000177)
(5)
5mo - 3mo
Implied
Volatility
Firm-Cycle
Firm-Cycle
829,818
0.192
2.97e-06
(0.000280)
0.00269***
(0.000463)
-0.00289***
(0.000678)
-0.00164
(0.00115)
0.0322***
(0.00188)
0.0316***
(0.00243)
-0.00628***
(0.000101)
(6)
5mo - 1 mo
Implied
Volatility
This table documents the term structure effects of political capital shocks on CDS spreads and implied volatility. Political capital shocks are defined using data
on firms’ donations to political candidates in close U.S. federal elections. Panel A presents the analysis on implied volatility, while Panel B presents the analysis
on CDS Spreads. In both panels, Columns (1) – (3) present difference-in-difference analysis for firms that have “lucky” political capital shocks before and after
an election compared to those that had “unlucky” shocks. In both Panels, Columns (4) – (6) present the triple difference analysis that examines how this effect
varies for firms that are sensitive to economic policy uncertainty. Policy Uncertainty Sensitivity is measured using the correlation between a firm’s equity returns
and the Baker, Bloom and Davis (2015) economic policy uncertainty index as defined in the text. Each regression uses daily data from six months’ prior to a
federal election to six months following the election. Our election data spans all biennial U.S. federal elections from 1998-2010. Implied volatility data is sourced
from OptionMetrics. Daily CDS spreads are taken from Markit for 1-year, 5-year, and 10-year tenors. Slopes are defined as the difference in log CDS spreads
(columns (1)-(6)) or the difference in raw CDS spreads (columns (7)-(9)) between contracts with different tenors. All independent variables are defined in the
Appendix. Standard errors are reported in parentheses. The symbols *, **, and *** denote statistical significance at the 10%, 5%, and 1% levels, respectively.
52
Observations
R-squared
Intercept
P rof itability
Book Leverage
Ln(Size)
M/B
F irm Return
P ost × P olicy × Close W in Dummy
P ost × P olicy Sensitive
P ost × Close W in Dummy
P ost Election
Panel B — CDS Spreads
248,167
0.761
-0.159***
(0.0197)
0.333***
(0.0811)
0.00215*
(0.00119)
-1.173***
(0.220)
0.220
(0.206)
-1.643**
(0.747)
0.0180
(0.0169)
0.135***
(0.0215)
(1)
5yr - 1yr
Log CDS
Spreads
250,470
0.805
-0.0703***
(0.00815)
0.144***
(0.0315)
0.00104*
(0.000533)
-0.363***
(0.0824)
0.157*
(0.0827)
-0.923***
(0.286)
0.0220***
(0.00569)
0.0402***
(0.00764)
(2)
10yr - 5yr
Log CDS
Spreads
241,401
0.814
-0.238***
(0.0234)
0.464***
(0.111)
0.00315*
(0.00169)
-1.574***
(0.291)
0.298
(0.274)
-2.404**
(1.015)
0.0370*
(0.0217)
0.184***
(0.0275)
(3)
10yr - 1yr
Log CDS
Spreads
297,260
0.790
0.151***
(0.0156)
0.0212
(0.0197)
-0.383***
(0.0304)
0.271***
(0.0570)
-0.103***
(0.0142)
0.196***
(0.0673)
0.000305***
(7.08e-05)
-0.738***
(0.185)
0.285
(0.205)
-0.676
(0.634)
(4)
5yr - 1yr
Log CDS
Spreads
300,548
0.816
0.0574***
(0.00540)
0.00350
(0.00712)
-0.117***
(0.0105)
0.0868***
(0.0208)
-0.0565***
(0.00677)
0.101***
(0.0261)
0.000121***
(3.43e-05)
-0.218***
(0.0703)
0.163**
(0.0814)
-0.631***
(0.242)
(5)
10yr - 5yr
Log CDS
Spreads
Table 6: Term Structure Effects of Political Capital Shocks (continued)
289,325
0.840
0.209***
(0.0197)
0.0304
(0.0248)
-0.506***
(0.0389)
0.357***
(0.0729)
-0.164***
(0.0170)
0.284***
(0.0913)
0.000424***
(0.000103)
-0.983***
(0.243)
0.380
(0.272)
-1.158
(0.850)
(6)
10yr - 1yr
Log CDS
Spreads
53
Table 7: The Impact of Political Capital Shocks on Investment, Capital Structure, and R&D Spending
0.00002
(0.000591)
0.00103
(0.000880)
0.156***
(0.0224)
Yes
Firm-cycle
Firm-cycle
18,368
0.691
Controls
Fixed effects
Clustered errors
Observations
R-Squared
Intercept
P ost × P olicy × Close W in Dummy
P ost × P olicy Sensitive
P ost × Close W in Dummy
P ost Election
(1)
Investment
0.00210***
(0.000674)
-0.000622
(0.000972)
-0.00844***
(0.00139)
0.00538**
(0.00237)
0.164***
(0.0225)
Yes
Firm-cycle
Firm-cycle
18,368
0.693
Panel B — Triple-Difference Analysis
Controls
Fixed effects
Clustered errors
Observations
R-Squared
Intercept
P ost × Close W in Dummy
P ost Election
It
Kt−1
Panel A — Difference-in-Difference Analysis
(1)
Investment
(2)
Investment
0.000855***
(0.000244)
-0.000511
(0.000353)
-0.00268***
(0.000536)
0.00168**
(0.000839)
0.0662***
(0.00896)
Yes
Firm-cycle
Firm-cycle
18,368
0.784
0.000194
(0.000218)
0.000001
(0.000320)
0.0635***
(0.00892)
Yes
Firm-cycle
Firm-cycle
18,368
0.783
It
Assetst−1
(2)
Investment
(3)
Book Leverage
0.00252
(0.00183)
0.00183
(0.00255)
0.0177***
(0.00438)
-0.0134**
(0.00671)
0.516***
(0.0781)
Yes
Firm-cycle
Firm-cycle
18,267
0.948
0.00675***
(0.00172)
-0.00177
(0.00239)
0.534***
(0.0788)
Yes
Firm-cycle
Firm-cycle
18,267
0.947
Liabilitiest
Assetst
(3)
Book Leverage
(4)
Book Leverage
-0.00246
(0.00167)
0.00204
(0.00261)
0.0151***
(0.00375)
-0.0167***
(0.00556)
-0.0252
(0.0706)
Yes
Firm-cycle
Firm-cycle
18,267
0.941
0.00114
(0.00148)
-0.00162
(0.00235)
-0.0113
(0.0706)
Yes
Firm-cycle
Firm-cycle
18,267
0.941
Debtt
Assetst
(4)
Book Leverage
(5)
R&D Spending
0.000690*
(0.000403)
-0.000146
(0.000578)
-0.000445
(0.000826)
-0.000794
(0.00137)
0.0780***
(0.0268)
Yes
Firm-cycle
Firm-cycle
6,573
0.721
(6)
R&D Spending
0.00430*
(0.00240)
-0.00864
(0.00727)
-0.00420
(0.00651)
0.00575
(0.0118)
0.734**
(0.309)
Yes
Firm-cycle
Firm-cycle
6,570
0.752
0.00322
(0.00214)
-0.00745
(0.00579)
0.728**
(0.310)
Yes
Firm-cycle
Firm-cycle
6,570
0.752
R&D Expenset
Salest
R&D Expenset
Assetst
0.000572*
(0.000318)
-0.000192
(0.000510)
0.0771***
(0.0270)
Yes
Firm-cycle
Firm-cycle
6,573
0.721
(6)
R&D Spending
(5)
R&D Spending
Panel A presents differences-in-differences tests that examine how “lucky” firms’ investment, leverage, and R&D spending change following a positive shock to
the firms’ political capital. Panel B presents a triple-difference analysis that examines how the effect of a “lucky” political capital shock varies for firms that are
highly sensitive to economic policy uncertainty within a given election cycle. Policy Uncertainty Sensitivity is measured using the correlation between a firm’s
equity returns and the Baker, Bloom and Davis (2015) economic policy uncertainty index as defined in the text. Each regression is based on quarterly data from
CRSP/Compustat from four quarters prior to each election date to four quarters after each election date. All independent variables are defined in the Appendix.
Control variables include firm size, M/B, free cash flow / assets, and net PP&E / assets for investment and R&D regressions, plus operating profitability and
the firm’s current ratio for leverage regressions. Banks and firms missing industry classification codes are excluded from the sample. Investment and M/B are
trimmed at the 1% and 99% levels. The sample is also restricted to firms with leverage ratios between zero and one (inclusive). Standard errors are reported in
parentheses. The symbols *, **, and *** denote statistical significance at the 10%, 5%, and 1 % levels, respectively.
54
Panel C — Triple-Difference Analysis with Continuous Treatment
(1)
(2)
(3)
Investment
Investment
Book Leverage
P ost Election
0.00187***
0.000647***
0.00325**
(0.000500)
(0.000175)
(0.00144)
P ost × N et Close W ins
-0.000127
-0.000064
0.000239
(0.000185)
(5.85e-05)
(0.000508)
P ost × P olicy Sensitive
-0.00605*** -0.00191***
0.0120***
(0.00114)
(0.000404)
(0.00334)
P ost × P olicy × N et Close W ins
0.00148***
0.000451**
-0.00309**
(0.000459)
(0.000201)
(0.00140)
Intercept
0.164***
0.0662***
0.516***
(0.0225)
(0.00893)
(0.0781)
Controls
Yes
Yes
Yes
Fixed effects
Firm-cycle
Firm-cycle
Firm-cycle
Clustered errors
Firm-cycle
Firm-cycle
Firm-cycle
Observations
18,368
18,368
18,267
R-Squared
0.693
0.784
0.948
(4)
Book Leverage
-0.00169
(0.00125)
0.000378
(0.000536)
0.00810***
(0.00282)
-0.00393***
(0.00109)
-0.0257
(0.0706)
Yes
Firm-cycle
Firm-cycle
18,267
0.941
(5)
R&D Spending
0.000629**
(0.000268)
-0.000014
(7.75e-05)
-0.000703
(0.000663)
-0.000093
(0.000259)
0.0780***
(0.0269)
Yes
Firm-cycle
Firm-cycle
6,573
0.721
(6)
R&D Spending
0.00461
(0.00287)
-0.000533
(0.000629)
-0.00146
(0.00410)
0.000077
(0.00190)
0.729**
(0.309)
Yes
Firm-cycle
Firm-cycle
6,570
0.752
Table 7: The Impact of Political Capital Shocks on Investment, Capital Structure, and R&D Spending (continued)
55
Table 8: The Impact of Political Capital Shocks on Operating Performance and Profitability
Fixed effects
Clustered errors
Observations
R-Squared
Intercept
P ost × P olicy × Close W in Dummy
P ost × P olicy Sensitive
P ost × Close W in Dummy
P ost Election
(1)
Sales
0.0699***
(0.00592)
-0.00697
(0.00947)
-0.132***
(0.0146)
0.106***
(0.0214)
7.146***
(0.00212)
Firm-cycle
Firm-cycle
22,296
0.984
Panel B — Triple-Difference Analysis
Panel A — Difference-in-Difference Analysis
(1)
Sales
ln(Salest )
P ost Election
0.0402***
(0.00567)
P ost × Close W in Dummy
0.0198**
(0.00880)
Intercept
7.146***
(0.00216)
Fixed effects
Firm-cycle
Clustered errors
Firm-cycle
Observations
22,296
R-Squared
0.984
(2)
Assets
0.0885***
(0.00625)
-0.0214**
(0.00882)
-0.0628***
(0.0112)
0.0421**
(0.0188)
8.864***
(0.00194)
Firm-cycle
Firm-cycle
22,353
0.993
(2)
Assets
ln(Assetst )
0.0743***
(0.00532)
-0.00955
(0.00783)
8.864***
(0.00195)
Firm-cycle
Firm-cycle
22,353
0.993
(3)
M/B
-0.0953**
(0.0403)
0.0692
(0.0589)
-0.525***
(0.106)
0.365**
(0.159)
2.953***
(0.0139)
Firm-cycle
Firm-cycle
21,152
0.858
(3)
M/B
M/Bt
-0.213***
(0.0387)
0.169***
(0.0557)
2.953***
(0.0140)
Firm-cycle
Firm-cycle
21,152
0.857
-0.000225
(0.0152)
0.00389
(0.0165)
0.688***
(0.00462)
Firm-cycle
Firm-cycle
22,190
0.607
-0.00243***
(0.000366)
0.00238***
(0.000521)
0.0234***
(0.000132)
Firm-cycle
Firm-cycle
21,913
0.695
(5)
COGS
-0.00753
(0.0194)
0.0124
(0.0207)
0.0323
(0.0222)
-0.0427*
(0.0239)
0.688***
(0.00462)
Firm-cycle
Firm-cycle
22,190
0.607
COGSt
Salest
EBITt
Assetst−1
(4)
ROA
-0.00158***
(0.000380)
0.00166***
(0.000557)
-0.00379***
(0.00102)
0.00265**
(0.00134)
0.0234***
(0.000131)
Firm-cycle
Firm-cycle
21,913
0.696
(5)
COGS
(4)
ROA
(6)
SG&A
-0.00971
(0.0102)
0.000478
(0.0119)
0.0141
(0.0105)
-0.00717
(0.0125)
0.216***
(0.00253)
Firm-cycle
Firm-cycle
15,837
0.746
-0.00629
(0.00778)
-0.00222
(0.00952)
0.216***
(0.00253)
Firm-cycle
Firm-cycle
15,837
0.746
SG&At
Salest
(6)
SG&A
(7)
Profit Margin
0.0184
(0.0295)
-0.0172
(0.0310)
-0.0568*
(0.0316)
0.0563*
(0.0333)
0.0994***
(0.00692)
Firm-cycle
Firm-cycle
22,184
0.679
0.00556
(0.0230)
-0.00440
(0.0244)
0.0994***
(0.00692)
Firm-cycle
Firm-cycle
22,184
0.679
EBIT DAt
Salest
(7)
Profit Margin
Panel A presents differences-in-differences tests that examine how “lucky” firms’ operating performance and profitability change following a positive shock to the
firms’ political capital. Panel B presents a triple-difference analysis that examines how the effect of a “lucky” political capital shock varies for firms that are
highly sensitive to economic policy uncertainty within a given election cycle. Policy Uncertainty Sensitivity is measured using the correlation between a firm’s
equity returns and the Baker, Bloom and Davis (2015) economic policy uncertainty index as defined in the text. Each regression is based on quarterly data from
CRSP/Compustat from four quarters prior to each election date to four quarters after each election date. All independent variables are defined in the Appendix.
Banks and firms missing industry classification codes are excluded from the sample. M/B is trimmed at the 1% and 99% levels. Standard errors are reported in
parentheses. The symbols *, **, and *** denote statistical significance at the 10%, 5%, and 1 % levels, respectively.
56
Panel C — Triple-Difference Analysis with
(1)
Sales
P ost Election
0.0666***
(0.00469)
P ost × N et Close W ins
0.000716
(0.00187)
P ost × P olicy Sensitive
-0.0839***
(0.0113)
P ost × P olicy × N et Close W ins
0.0270***
(0.00463)
Intercept
7.146***
(0.00211)
Fixed effects
Firm-cycle
Clustered errors
Firm-cycle
Observations
22,296
R-Squared
0.984
Continuous
(2)
Assets
0.0803***
(0.00452)
-0.00397**
(0.00166)
-0.0446***
(0.00918)
0.0108***
(0.00352)
8.864***
(0.00194)
Firm-cycle
Firm-cycle
22,353
0.993
Treatment
(3)
(4)
M/B
ROA
-0.0654**
-0.000933***
(0.0303)
(0.000289)
0.00308
0.000282***
(0.0113)
(0.000105)
-0.370***
-0.00235***
(0.0803)
(0.000692)
0.104***
0.00114***
(0.0371)
(0.000378)
2.953***
0.0234***
(0.0139)
(0.000131)
Firm-cycle
Firm-cycle
Firm-cycle
Firm-cycle
21,152
21,913
0.858
0.696
(5)
COGS
-0.00167
(0.0114)
-0.000928
(0.00146)
0.0118
(0.0133)
-0.00900*
(0.00495)
0.688***
(0.00461)
Firm-cycle
Firm-cycle
22,190
0.607
(6)
SG&A
-0.00946
(0.00626)
-7.75e-05
(0.000600)
0.0103
(0.00655)
-0.00248**
(0.00112)
0.216***
(0.00253)
Firm-cycle
Firm-cycle
15,837
0.746
(7)
Profit Margin
0.0107
(0.0172)
0.000167
(0.00162)
-0.0317*
(0.0185)
0.0105**
(0.00493)
0.0995***
(0.00691)
Firm-cycle
Firm-cycle
22,184
0.679
Table 8: The Impact of Political Capital Shocks on Operating Performance and Profitability (continued)
Table 9: Political Capital Shocks and Marginal Expected Shortfall
The following table presents regression estimates of various connection measures on firm Marginal Expected Shortfall
(MES). MES, which is defined in Acharya, Pedersen, Philippon, and Richardson (2010), represents the conditional
expected return on a stock given a left-tail market return realization. A more negative MES number indicates a
greater exposure to systemic/tail risk. All independent variables are defined in the Appendix. All regressions include
firm-election cycle fixed effects. Standard errors clustered by firm are reported in parentheses. *, **, and *** denote
statistical significance at the 10, 5, and 1 % levels respectively.
Political Capital Shocks and MES
(1)
Marginal
Expected
Shortfall
P ost Election
P ost × N et Close W ins
-0.00174***
(0.000206)
0.000566***
(9.86e-05)
(2)
Marginal
Expected
Shortfall
(3)
Marginal
Expected
Shortfall
(4)
Marginal
Expected
Shortfall
(5)
Marginal
Expected
Shortfall
(6)
Marginal
Expected
Shortfall
-0.00134***
(0.000168)
0.000446***
(8.07e-05)
-0.00250***
(0.000275)
-0.00189***
(0.000224)
-0.00102***
(0.000299)
-0.000817***
(0.000238)
0.00205***
(0.000457)
0.00150***
(0.000365)
0.000506***
(9.67e-05)
-0.000767***
(0.000119)
8.45e-05
(0.000845)
-0.0276**
(0.0129)
0.000402***
(7.99e-05)
-0.000592***
(9.42e-05)
-0.00202**
(0.000825)
-0.0230***
(0.000698)
-0.000295
(0.000320)
0.0268**
(0.0130)
Firm-cycle
Firm
7,792
0.882
Firm-cycle
Firm
7,720
0.925
P ost × Close W in Dummy
P ost × Close W ins
P ost × Close Losses
M arket Cap
4.36e-05
(0.000845)
Intercept
-0.0270**
(0.0129)
-0.00203**
(0.000827)
-0.0231***
(0.000699)
-0.000274
(0.000320)
0.0271**
(0.0130)
Fixed effects
Clustered errors
Observations
R-squared
Firm-cycle
Firm
7,792
0.881
Firm-cycle
Firm
7,720
0.924
CAP M Beta
CAP M V olatility
57
0.000118
(0.000845)
-0.0281**
(0.0129)
-0.00200**
(0.000828)
-0.0231***
(0.000700)
-0.000305
(0.000320)
0.0266**
(0.0130)
Firm-cycle
Firm
7,792
0.881
Firm-cycle
Firm
7,720
0.924
58
Table 10: Government Contractors and CDS Spreads
Fixed effects
Clustered errors
Observations
R-squared
Intercept
P ost × Close Election Dummy × Gov
Gov × Close Election Dummy
P ost × Gov Contractor
P ost × Close Election Dummy
Gov Contractor
P ost Election
Dependent Variable:
Sample:
Firm-cycle
Firm-cycle
395,968
0.891
0.022
(0.027)
-0.209
(0.193)
-0.302***
(0.036)
0.165
(0.204)
0.0695
(0.213)
-0.193
(0.228)
-5.507***
(0.010)
(1)
All
Firms
1-Year
Spreads
Firm-cycle
Firm-cycle
438,640
0.918
0.072***
(0.016)
-0.185
(0.116)
-0.186***
(0.022)
0.133
(0.122)
0.139
(0.129)
-0.177
(0.138)
-4.730***
(0.006)
(2)
All
Firms
5-Year
Spreads
Firm-cycle
Firm-cycle
401,202
0.915
0.100***
(0.014)
-0.101
(0.099)
-0.161***
(0.019)
0.0464
(0.105)
0.117
(0.109)
-0.129
(0.116)
-4.535***
(0.005)
(3)
All
Firms
10-Year
Spreads
Firm-cycle
Firm-cycle
9,452
0.974
-5.516***
(0.154)
-0.240
(0.308)
0.045
(0.254)
(4)
Gov
Firms
1-Year
Spreads
Firm-cycle
Firm-cycle
10,327
0.981
-4.619***
(0.102)
-0.227
(0.208)
0.084
(0.164)
(5)
Gov
Firms
5-Year
Spreads
Firm-cycle
Firm-cycle
9,597
0.982
-4.410***
(0.0857)
-0.276*
(0.165)
0.087
(0.143)
(6)
Gov
Firms
10-Year
Spreads
Firm-cycle
Firm-cycle
304,938
0.891
-5.599***
(0.010)
-0.338***
(0.040)
0.036*
(0.033)
(7)
Non-Gov
Firms
1-Year
Spreads
Firm-cycle
Firm-cycle
333,515
0.915
-4.809***
(0.006)
-0.202***
(0.024)
0.088***
(0.020)
(8)
Non-Gov
Firms
5-Year
Spreads
Firm-cycle
Firm-cycle
308,605
0.910
-4.604***
(0.005)
-0.170***
(0.021)
0.109***
(0.176)
(9)
Non-Gov
Firms
10-Year
Spreads
The following table presents regression estimates of various political connection measures on log CDS spreads for “government-dependent” versus “non-governmentdependent” firms. Specifications (1) - (3) are run on the full sample of firms. Specifications (4) - (6) are run on the sample of Government Suppliers (see text for
details), while specifications (7) - (9) exclude government suppliers. All independent variables are defined in the Appendix. All regressions include firm-election
cycle fixed effects. Standard errors clustered by firm-election cycle are reported in parentheses. The symbols *, **, and *** denote statistical significance at the
10, 5, and 1 % levels respectively.
59
Table 11: Industry Robustness Tests
Clustered errors
Observations
R-Squared
Fixed effects
Intercept
P ost × P olicy × Close W in Dummy
P olicy × Close W in Dummy
P ost × P olicy Sensitive Dummy
P ost × Close W in Dummy
P olicy Sensitive Dummy
Close W in Dummy
P ost Election
(1)
5-year
CDS
Spreads
-0.0761***
(0.0176)
0.000972
(0.0334)
-0.249***
(0.0439)
-0.0634***
(0.0218)
0.515***
(0.0414)
0.0393
(0.0742)
-0.267***
(0.0772)
-4.706***
(0.0196)
Firm,
FF-Cycle
Firm-Cycle
379,503
0.853
(2)
3-month
Implied
Volatility
-0.0037**
(0.0018)
0.0030***
(0.0009)
-0.0555***
(0.0064)
-0.0060***
(0.0007)
0.1099***
(0.0071)
0.0047**
(0.0022)
-0.0123***
(0.0024)
0.3939***
(0.0459)
Firm,
FF-Cycle
Firm-Cycle
828508
0.693
0.000679
(0.000623)
-0.001775*
(0.000962)
0.004516***
(0.001530)
-0.000126
(0.000886)
-0.007280***
(0.001258)
-0.002455
(0.002456)
0.005228**
(0.002232)
0.074579***
(0.014451)
Firm,
FF-Cycle
Firm-Cycle
20458
0.526
(3)
Investment
0.000689
(0.001687)
0.003993
(0.003593)
-0.003181
(0.005225)
0.002555
(0.002551)
0.009918***
(0.003425)
0.005116
(0.008340)
-0.011221**
(0.005387)
0.213552***
(0.068447)
Firm,
FF-Cycle
Firm-Cycle
22353
0.848
(4)
Leverage
-0.0706*
(0.0396)
-0.1625**
(0.0762)
0.2481**
(0.1259)
0.0374
(0.0577)
-0.4974***
(0.1017)
0.1212
(0.2101)
0.4318***
(0.1573)
0.2173
(1.1879)
Firm,
FF-Cycle
Firm-Cycle
21152
0.685
(5)
M/B
0.0672***
(0.0058)
0.0002
(0.0160)
0.0553**
(0.0218)
-0.0053
(0.0091)
-0.1299***
(0.0140)
-0.0183
(0.0330)
0.0941***
(0.0207)
6.8751***
(0.4740)
Firm,
FF-Cycle
Firm-Cycle
22296
0.958
(6)
Sales
0.0868***
(0.0061)
0.0456***
(0.0153)
0.0354
(0.0228)
-0.0190**
(0.0086)
-0.0644***
(0.0109)
-0.0356
(0.0346)
0.0338*
(0.0190)
8.0019***
(0.3430)
Firm,
FF-Cycle
Firm-Cycle
22353
0.972
(7)
Assets
-0.0014***
(0.0004)
-0.0022***
(0.0006)
0.0015*
(0.0009)
0.0014***
(0.0005)
-0.0039***
(0.0010)
0.001
(0.0014)
0.0025*
(0.0013)
0.0395***
(0.0122)
Firm,
FF-Cycle
Firm-Cycle
21913
0.551
(8)
ROA
This table examines the robustness of the tests in Tables 4 - 8 to different types of industry controls. Specifically, the regressions below all include firm and
industry-cycle fixed effects. As such, these tests look within an industry within a given election cycle for identification. Standard errors clustered by firm-election
cycle are reported in parentheses. The symbols *, **, and *** denote statistical significance at the 10, 5, and 1 % levels respectively.