Do Firms Save Too Much Cash?Evidence from a Tax on Corporate Savings∗

Hwanki Brian KimBaylor University

Woojin KimSeoul National University

Mathias KronlundUniversity of Illinois at Urbana-Champaign

October 24, 2019

∗Hwanki Brian Kim is at Baylor University; Hankamer School of Business; One Bear Place; Waco, TX76798; U.S.A.; Email: Brian Kim6@baylor.edu. Woojin Kim is at Seoul National University; 1 Gwanak-ro,Gwanak-gu, Bldg 59; Seoul, 08826; Korea; Email: woojinkim@snu.ac.kr. Mathias Kronlund is at theUniversity of Illinois at Urbana-Champaign; Gies College of Business; 1206 South Sixth Street; Champaign, IL,61820; U.S.A.; Email: kronlund@illinois.edu. Yongseok Kim and SeongMyeong Kang provided excellentresearch assistance. We thank Heitor Almeida, Peter DeMarzo, Brent Glover, Kristine Hankins, and seminarand conference participants at the BYU Red Rock conference, ESSFM Gerzensee, the Korean SecuritiesAssociation, Seoul National University, the University of Illinois at Urbana-Champaign, and Virginia Techfor many helpful comments. A previous draft of this paper was circulated under the title “DiscouragingCorporate Savings”

Do Firms Save Too Much Cash?Evidence from a Tax on Corporate Savings

October 24, 2019

Abstract

Corporations have accumulated record amounts of cash. Are these savings optimal or

excessive? We examine this question by exploiting a Korean tax reform that sought

to discourage cash savings by imposing a surtax on earnings that were not paid out

to shareholders or invested. This tax applied only to firms with book equity above 50

billion wons or that belonged to a Chaebol. Difference-in-differences tests show that

the treated firms reduced cash savings and increased payouts, wages, and investments.

These additional investments appear profitable, and an event study analysis shows that

shareholders viewed the reform as value-enhancing. These results are consistent with

the accumulation of excessive savings before the reform, and we find evidence consistent

with both agency-based and behavioral channels underlying such excessive savings.

JEL category: G32, G35, G38

Keywords : Corporate cash, investment, wages, payout policy, natural experiment, tax

1 Introduction

Corporate cash balances have risen dramatically over the last few decades. In the United

States, cash on corporate balance sheets now totals over $3 trillion (Faulkender, Hankins,

and Petersen, 2019), and the trend toward growing corporate cash balances is prevalent also

in many other countries (Kalcheva and Lins, 2007; Pinkowitz, Stulz, and Williamson, 2015).

This phenomenon is often referred to as a “corporate savings glut” or “cash hoarding.”1 Still,

it remains an open question whether all of this cash represents excessive hoarding or optimal

savings.

It is challenging to determine whether corporations are saving too much and investing

too little, as the “cash hoarding” narrative would suggest. Corporate decisions about cash

policies, investments, and payouts are endogenously determined and driven by multiple factors

that are difficult to control for in empirical tests. To address the question of whether firms

save too much, we ideally need both a shock to firms’ cash policies—where some companies

exogenously change their savings behavior—and a way to measure the value impact of these

changes.

The main objective of this paper is to address this question through the lens of a recent

natural experiment in South Korea, where the government intentionally sought to stem the

tide of corporate cash by imposing a new 10% surtax on any “excess” cash savings above

a specific threshold of earnings.2 This tax reform became effective on January 1, 2015. A

crucial feature of the reform for identification purposes is that it applied only to firms that

had a level of shareholder’s equity above 50 billion Korean wons (equivalent to around $50

million USD), and to firms that were part of large business conglomerates (chaebol), whereas

non-chaebol firms below the 50-billion threshold were not subject to the new tax. This setting

1For example, a 2016 Financial Times article argued that “The failure of companies to invest their cashpile has frustrated investors who say companies are not plowing enough back into their underlying businesses,in research and development”; www.ft.com/content/368ef430-1e24-11e6-a7bc-ee846770ec15

2In the next section, we discuss the exact formula that determined the surtax and relevant exclusions.

1

allows us to study how the firms that were treated by the tax law changed their savings and

investment policies, and to measure the resulting consequences for firm value. This evidence

thus helps us assess whether saving less enhanced firm value, or whether the law merely

distorted corporate cash and investment policies.

Korean firms are among the most cash-heavy in the world: Compared with U.S. firms,

Korean firms hold three times more cash as a fraction of GDP: Corporate cash balances are

equivalent to 50% of GDP in Korea, compared with around 15% in the U.S..3 The law was

motivated by the idea that money sitting on corporate balance sheets could be used more

productively in the hands of shareholders or employees, or in the form of new investments.4

Our empirical strategy employs a difference-in-differences analysis, in which we compare

changes from two years before the tax reform (2013–14) to two years after (2015–16) in firms’

cash savings, payouts, and investments between the firms that were treated by this reform

versus firms that were not treated. An attractive feature of the 50-billion-wons threshold that

determined treatment is that this threshold is plausibly exogenous to firms’ future savings

and investment policies, and also unrelated to any other governmental reforms of which we

are aware that could have differentially affected the treated and non-treated firms around the

same time. Crucially, this surtax on cash savings was also significant in economic magnitude:

a ten-percentage-point surtax implies an almost 50% increase on top of the standard corporate

tax rate, which was 22% during our sample period.

Our results show that the treated firms responded by significantly cutting savings. The

economic magnitude of this effect is also large: the savings rate among the treated firms was

3This phenomenon is most evident among the largest business groups (chaebol). In 2017, the top fourchaebol together held the equivalent of around 500 Billion USD in cash. See The Economist, September 27,2014, at www.economist.com/leaders/2014/09/27/a-25-trillion-problem; and Financial Times, June 11, 2017,at www.ft.com/content/966fcbd8-4f13-11e7-bfb8-997009366969

4From an economy-wide perspective, money on corporate balance sheets is not “idle”; some of it is directlyinvested in other corporations’ stocks and bonds (Gilbert et al. 2017), and cash that is held as bank depositsis deployed as a source of lending.

2

cut by 0.3–0.6 percentage-points as a fraction of assets, compared with an average savings

rate of around 1 percent of assets.

A firm must necessarily either spend money that is not saved or pay it out to investors.

We show that the treated firms responded by significantly increasing payouts to shareholders.

Specifically, the treated firms pay out 0.2 percentage points more (as a fraction of assets)

after the reform, about a 30% increase relative to the sample mean of 0.7%. We also find

that the investment rate for the treated firms increased by around 20

To determine whether these actions were value-improving—and thus, whether the treated

firms’ savings before the reform might have been excessive—we next study the profitability

and valuation consequences for the treated firms. First, we show that the relative increases in

investments among the treated firms were especially concentrated among firms and industries

that exhibited high profitability before the reform. This implies that the marginal investments

were focused primarily in areas where these investments were likely to be more profitable.

Even if the additional investments by the treated firms were profitable; however, that does

not rule out the possibility that the shadow value of savings was even higher. We therefore

study the valuation consequences for the firms that were treated by the tax reform. Using

an event study design, we find that the cumulative abnormal returns (CAR) for the treated

firms around the days when the law was proposed and passed were positive. This finding is

consistent with investors believing that firms’ cash savings before the reform were excessive

and that saving less would raise firm value. The positive valuation effects are particularly

notable because a direct negative valuation effect for the treated firms is that they are subject

to higher taxes; this implies that investors viewed the responses by the treated firms as more

than outweighing these direct costs.

Cross-sectionally, we find stronger responses in terms of changes to savings, payout, and

investments among the firms that had high pre-reform earnings and that, therefore, would be

3

required to decrease their savings to the greatest extent to avoid the surtax. These firms also

experience more positive valuation effects around the passage of the law, which is consistent

with investors anticipating that these firms would change their behavior to the greatest

extent.

We finally explore two possible channels through which firms’ cash savings could have

been excessive before the reform and why being incentivized to save less might have improved

firm value. First, firms could have saved excessively because of agency conflicts (Bertrand and

Mullainathan, 2003; Gao, Harford, and Li, 2013; Nikolov and Whited, 2014). Second, firms

might have employed overly cautious cash policies because of behavioral biases (Malmendier,

Tate, and Yan, 2011); this would have occurred, for example, if managers have been scarred

by past crises such as the Asian Financial Crisis of 1997–98. In the final part of the paper, we

investigate these two possible mechanisms that might have induced firms to save too much,

and we find evidence consistent with both of these channels at work.

We conduct a battery of robustness tests for our findings. The crucial identification

assumption—as in any difference-in-differences design—is the “parallel trends” assumption.

To support this assumption, we show that there are no significant differential pre-trends

between the treated and control firms. We also conduct a “placebo” test by exploiting the

feature that the 50 billion threshold is relevant only for non-chaebol firms, by showing that

there are no effects around this threshold on firms that belong to chaebol and are therefore

treated regardless of their size. These results indicate that our results are not driven by

differential trends that might be related to a firm’s size.

We further show that our difference-in-differences regressions are robust to a variety of

controls, including controls for the distance to the treatment threshold (as in a regression

discontinuity), size, leverage, cash flow, and cash levels. The results are also similar when we

focus on a range around the threshold (firms with a shareholder’s equity between 10 and 90

4

billion wons). These tests also help ensure that any effects we find are not spuriously driven

by differential trends from the smallest or largest firms in Korea.

The Korean setting represents a unique opportunity to study the effects of a government

policy that was aimed at curtailing corporate savings. A historical episode involving a

similar reform was the “undistributed profits tax,” which raised taxes on retained corporate

earnings in the United States between 1936 and 1937. Poterba et al. (1987) show that the

undistributed profits tax resulted in more payouts. Christie and Nanda (1994) use an event

study methodology to show, similarly to our findings, that the undistributed profits tax was

associated with positive abnormal returns, and they argue that this tax also alleviated agency

problems whereby firms had been paying out too little of their profits. The recent experiment

in Korea has at least two primary benefits compared with studies of the undistributed profits

tax in the U.S. First, crucially, the Korean experiment has a control group of firms that were

not subject to the new tax, whereas the undistributed profits tax had no such natural control

group. Second, the Korean experiment takes place in recent times when the nature of firms’

balance sheets differ substantially from what it was in the 1930s.

Our study further contributes to the literature on the value of cash. Faulkender and

Wang (2006) estimate that the marginal value of cash on average is $0.94, but that this varies

across firms, depending on their financial constraints. Dittmar and Mahrt-Smith (2007) find

further that the value of cash is lower for poorly governed firms and Harford (1999) shows

that cash-rich firms tend to do more acquisitions of other firms and that these acquisitions

tend to be value-decreasing.5

We also contribute to the literature on the determinants of corporate cash. Studies

have cited several reasons that firms hold more cash than they once did, including more

precautionary savings (Opler, Pinkowitz, Stulz, and Williamson, 1999; Bates, Kahle, and

5However, Opler, Pinkowitz, Stulz, and Williamson (1999) do not find that excess cash predicts moreacquisitions, capital expenditures, or payouts.

5

Stulz, 2009), lower opportunity costs (Azar, Kagy, and Schmalz, 2016), increased competition

(Lyandres and Palazzo, 2016), costs of repatriating foreign earnings (Foley, Hartzell, Titman,

and Twite, 2007; Faulkender, Hankins, and Petersen, 2019), and higher levels of intangible

capital (Falato, Kadyrzhanova, Sim, and Steri, 2018).6 While most of this literature has

focused on cash levels rather than savings, two exceptions include Almeida, Campello, and

Weisbach (2004) and Riddick and Whited (2009), who examine what we can learn about

firms’ financial frictions from the sensitivity of firms’ savings to cash flows.

Finally, this experiment also relates to more recent studies on the “tax holiday” of the

“American Job Creation Act”(AJCA) of 2004, which allowed firms to repatriate foreign

earnings. Blouin and Krull (2009), Dharmapala, Foley, and Forbes (2011), and Faulkender

and Petersen (2012) examine what firms do after the ACJA when they enjoy (cheaper) access

to previously saved foreign cash. Blouin and Krull (2009) and Dharmapala, Foley, and Forbes

(2011) show that most of the money that was repatriated during the tax holiday was spent on

buybacks, while Faulkender and Petersen (2012) also find an increase in domestic investment

after the AJCA.

Our paper proceeds as follows. In the next section, we describe the legislative history

and the implementation of the law. In section 3, we describe our data on Korean firms and

summary statistics. In section 4, we present results on firms’ responses to the tax reform,

and in section 5, we describe several robustness tests. In section 6, we examine the valuation

effects. In section 7, we analyze cross-sectional variation in firms’ responses and valuation

effects; these tests shed light on the possible channels that could drive firms to save excessively.

We conclude in Section 8.

6The literature on the determinants of cash is surveyed by Almeida, Campello, Cunha, and Weisbach(2014).

6

2 Legislative History and Institutional Background

On July 16, 2014, the newly appointed then-Minister of Strategy and Finance in Korea, Choi

Kyoung-Hwan, announced in his inaugural address a plan for tax reforms. Among them was

the new tax on corporate savings. He pronounced that his team was considering taxes on

firms’ retentions of unspent earnings, with the aim of incentivizing corporate investments

and boosting domestic demand. The prevailing view was that money sitting on corporate

balance sheets could be put to more productive use if only firms were incentivized to spend

their cash on plants, equipment, labor, or payouts to shareholders.

The official proposal for the tax reform was made on August 6, 2014, the National

Assembly passed the law on December 2, 2014, and the law took effect on January 1, 2015.

The law did not target all firms but applied only to those that satisfied at least one of the

following criteria: 1) having shareholders’ equity greater than or equal to 50 billion Korean

wons as of the previous fiscal year, or 2) belonging to a large business group, i.e., a chaebol.

Firms that did not satisfy either criterion were not subject to the new tax.

For the treated firms, the reform imposed a 10% surtax on “excess saving,” defined as

earnings above a certain threshold after deductions for investments, wage increases, and

payouts to shareholders. The first surtaxes were assessed in April 2016 based on end-of-

2015-fiscal-year accounting information. Firms could choose between two separate rules for

determining the tax amount:

(Rule A): tax amount = [net profit×0.8

− (investments + wage increases + payouts)]×0.1

(Rule B): tax amount = [net profit×0.3 - (wage increases + payouts)]×0.1

7

For example, according to Rule A, treated firms that spent more than 80% of their net

income on investments, wage increases, or payouts during a given year would be fully exempt

from the tax, while treated firms that saved more than the threshold amount would be taxed

at 10% on the residual. Rule A was the relatively more favorable rule for firms that tend to

make substantial investments,7 whereas Rule B was more favorable to firms that do not make

large investments. Even though firms could choose which of the rules they would adhere to

initially, they were bound to their chosen rule for at least the next three years.8

This surtax was also significant in economic magnitude: A ten-percentage-point surtax

implies an almost 50% increase on top of the standard corporate tax rate, which was 22%

during our sample period. Also, note that this surtax was not a tax on cash balances, but

instead the tax applied to excessive accumulation of retained earnings as non-invested capital.9

The law made important exclusions related to the deductions for wage increases and

investments that were allowed. The law explicitly did not allow wage increases awarded to

top managers to count as deductions. Regarding the deduction for investments, there was a

concern that firms might seek to “store” money in the form of physical investments rather

than cash, such as by buying land. The law therefore required that firms taking a deduction

for buying land also would be required to start building facilities on the land by the end of

the year. The law further imposed a retroactive tax if a firm sold or leased any such land

for a period of up to two years after the completion of any construction on the land. While

payouts to shareholders was an allowed deduction, firms nevertheless were not allowed to

claim an equivalent deduction for paying back debt.

This reform was controversial and received significant pushback from the private sector.

On the one hand, an argument supporting the reform was that this measure was designed

7Specifically, for firms whose capital expenditures represents more than 50% of net earnings.8We do not have data indicating which rule each treated firm chose to follow, but we can nevertheless

calculate a lower bound on the tax amount based on the most favorable rule for each firm.9Cash balances already incur an implicit tax penalty because interest is subject to corporate taxes (e.g.

Gamba and Triantis (2008)).

8

to push corporate cash savings toward households through investments, wage increases, or

payouts. One concern quite broadly shared by politicians and policymakers was that Korean

firms had accumulated cash excessively after the financial crisis.10 A common view was also

that a corporate tax cut that had been passed in 2009 had resulted in even higher cash

accumulation in place of the intended effect of increasing investment activities. An implicit

assumption behind this argument was that firms were saving more cash than was optimal,

and that directing more of this cash towards households would result in higher aggregate

consumption.11

On the other hand, other observers raised doubts about the effectiveness of the new

tax. These views were based primarily on the assumption that retention rates are optimally

determined, and that any additional taxation or “forced” spending on payouts or invest-

ments would drive firms to make suboptimal decisions. It was also argued that the reform

would effectively increase the corporate tax rate, which would eventually suppress corporate

investment and growth.

3 Data and Empirical Strategy

In this section, we discuss our empirical strategy, sample construction, and variable definitions,

and we report summary statistics.

10As of 2014, Korean firms reported the second-largest corporate savings among OECD member nations asa fraction of GDP, trailing only Japan.

11For example, when he was a nominee as the minister, Choi emphasized in a press interview that he wouldmeasure success by welfare improvements for the household economy (https://thediplomat.com/2014/06/south-koreas-incoherent-economic-policy/).

9

3.1 Empirical strategy

Studying the effects of changes to corporate savings is generally challenging because it is

difficult to find a source of exogenous variation in savings across firms. To overcome this

challenge, we exploit the Korean tax reform as a natural experiment. We employ a difference-

in-differences strategy by comparing firms that were treated by this reform with firms that

were not treated, from two years before the reform (2013–14) to two years after (2015–16).

An important advantage of using the Korean reform as a natural experiment is that the

assignment of treatment is plausibly unrelated to omitted variables that could influence

changes in future corporate savings and investment policies and thereby invalidate the parallel

trends assumption.

We define an indicator variable ’Treated ’ to denote a firm that is treated by the tax reform,

and estimate the following baseline difference-in-differences model:

yi,t = θ + β0Treatedi + β1Aftert

+ β2Treatedi × Aftert + η′ · Xi,t + ϕi + τt + ψj,t + εi,t,

where i indexes firms, j indexes industries,12 and t indexes years. yi,t denotes outcome

variables, such as investments, wage increases, and payouts; After is an indicator variable

for the post-reform years; X is a vector of control variables based on firm characteristics.13

ϕi denotes firm fixed effects to control for unobserved time-invariant firm heterogeneity; τt

denotes year fixed effects to control for unobserved market-wide shocks for each year; and

12The Korean industry classification uses a six-digit code. To ensure that we have sufficiently many firms ineach industry classification, we use a five-digit industry code that roughly corresponds to two- or three-digitaggregation of industries using U.S. SIC codes.

13Because of a possible “bad controls” concern (Angrist and Pischke (2008), p. 64), we first report resultsfrom these difference-in-differences regressions without these additional control variables. We then report theresults with the control variables later for a robustness check.

10

ψj,t denotes industry-by-year fixed effects to control for unobserved industry-wide shocks for

each year.14

The main coefficient of interest is β2, which captures the average treatment effects for

each of the outcome variables. We cluster standard errors throughout at the firm level for

stand-alone firms or, alternatively, at the Chaebol level for firms belonging to a chaebol group.

All variables are winsorized at the 1% and 99% levels.

Because treatment is based on a firm’s shareholders’ equity, one may nevertheless be

concerned about the possibility that a firm’s equity size could be spuriously correlated with

differential trends; for example, suppose that larger firms tended to perform better after

the reform, but for reasons unrelated to the reform. To address this concern, we repeat

the baseline difference-in-differences estimation while limiting the sample to firms for which

the pre-reform shareholders’ equity is within a narrower bandwidth around the treatment

threshold of 50 billion Korean wons. Specifically, we employ a bandwidth that ranges between

10 billion and 90 billion Korean wons to make it sufficiently narrow so that firms are more

comparable and less likely to be affected by differential trends, while also maintaining a

reasonably large sample to ensure sufficient statistical power.

3.2 Data and sample construction

Most of the data for this study, including accounting information, stock prices (for firms

publicly listed on the stock exchange), and other firm characteristics, are collected from

DataGuide, which is a comprehensive database on both private and public firms in Korea.

To determine more precisely which firms are affiliated with chaebol groups, we manually

double-check the accuracy of our data using an annual report by the Korean Fair Trade

Commission. We obtain data on corporate governance scores from the Korea Corporate

14Because we include both firm fixed effects and year fixed effects in all specifications, the Treated andAfter variables are in practice subsumed by those fixed effects.

11

Governance Service, and data on the probability of default for public firms from the Risk

Management Institute of the National University of Singapore (NUS RMI).

Beginning with these data on all public and private firms in Korea, we employ several

filters to further refine the sample. We first eliminate firm-year observations for which data on

shareholders’ equity are missing, as this variable determines treatment. We further exclude

financial firms and utilities. We next screen out firms that have total assets of less than

1 billion Korean wons (approximately $1 million) and firms with very negative levels of

capital expenditures (less than -10% of total assets). As a final filter, we drop three specific

firms—Hyundai Motors, Kia Motors, and Hyundai Mobis—as these firms made a massive

investment in real estate during our sample period but that had been planned a long time

before the tax reform.15 After restricting our sample period to four years around the tax

reform, i.e. from 2013 through 2016, our final sample consists of 80,494 firm-year observations

across 20,916 unique firms.

3.3 Main variables and summary statistics

Because the tax reform was aimed directly at discouraging savings while encouraging payouts,

investments, and wage growth, we start our empirical analysis by studying changes to these

outcomes as dependent variables. Cash savings (∆Cash/assets), payouts (Payout), investment

(Investment), and wage growth (Wage increase), are defined, in turn, as changes in cash

holdings during the year, total cash dividends plus share repurchases, capital expenditures,

and changes in a firm’s wage bill for non-executive employees during the year.16 All of these

15Including these firms would make the estimated effects on investments stronger, but would less accuratelyreflect the impact of the tax reform.

16As described in section 2, wage increases for executives did not count as a deduction from the surtax.

12

variables are normalized by lagged total assets. Definitions for all variables are described in

Table A9 in the Internet Appendix.17

While the definitions of most variables are straightforward, it is worth paying extra

attention to that of our measures of share repurchases: We follow Fama and French (2001)

and Almeida et al. (2016) and focus on purchases of stock, because the tax reform did not

penalize sales of stock. In other words, we measure repurchases as purchases of stock if they

are not missing, and replace them with increases in common Treasury stock if stock purchases

are missing or zero and Treasury stock is not missing for the current and prior year. If neither

data on purchases of stock nor changes in Treasury stock are non-missing, repurchases are

set to zero.

Table 1 summarizes the panel data over our sample period (2013 through 2016). In Panel

A, we report summary statistics on firm characteristics.

Table 1 About Here

In Panel B of Table 1, we report statistics on how many firms were treated and not treated

by the reform by each criterion for treatment. Of the sample firms, 1,052 are chaebol -affiliated,

and 3,451 firms report shareholders’ equity that is greater than 50 billion Korean wons, while

599 firms are treated based on both of these dimensions. In total, 3,904 firms were treated,

i.e. subject to the tax reform. We will exploit this “two-dimensionality” of the treatment as

part of our identification strategy and in our “placebo” robustness tests.

17We multiply these asset-scaled variables by 100 throughout to aid interpretation, as this defines thevariables in percentage terms.

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4 Main Results

In this section, we employ the difference-in-differences methodology to study the effects that

this reform had on firms’ financial and investment policies. These results crucially show

whether the reform had any “bite” in affecting how firms save, and the results also shed light

about the margins along which firms respond most strongly. It is nevertheless important to

note that these results regarding how firms respond to the law do not tell us whether these

responses enhance firm value or not; we will turn to that crucial question in the following

section.

4.1 Effects on cash accumulation

We begin by studying how the reform affected corporate cash savings. In a simple theoretical

framework, firms should equate the marginal cost of increasing cash holdings and thus

potentially sacrificing valuable investment opportunities today with the marginal benefit

of having available internal cash to invest in the future (e.g., Opler et al. (1999); Almeida,

Campello, and Weisbach (2004)). The surtax raises the marginal cost of saving, so we might

naturally expect firms to save less.

This simple theoretical prediction is nevertheless made somewhat less evident because

the law provided no symmetric tax credit for dissaving (negative cash accumulation). The

reform thus creates a wedge between saving and dissaving: Saving above a certain threshold

of earnings is taxed, but payouts or investments that result in dissaving in another year does

not provide firms with an equivalent credit. As a result, we might expect treated firms to

smooth their savings to a greater extent and avoid years of dissaving. The overall effects of

the reform on savings are thus ambiguous.

In Table 2, we report difference-in-differences results on how the tax reform affected cash

savings in the treated firms. The dependent variable is defined as changes in cash holdings

14

scaled by total assets. In Columns 1 and 2 we report the results for the full sample and in

columns 3 and 4 we focus on firms that fall within a narrower bandwidth of shareholders’

equity around the treatment threshold (in a range between 10 and 90 billion wons). We

control throughout for firm fixed effects, as well as year or industry-by-year fixed effects.

Table 2 About Here

Our results show that treated firms responded by significantly reducing cash savings to

a greater extent than the non-treated firms after the tax reform: The coefficients on the

Treated × After interaction terms are significantly negative in all specifications. The economic

magnitude of this effect is also substantial: the savings rate among the treated firms was cut

by around 0.3 percentage points when normalized by assets, relative to an average savings

rate of around 1 percent. These results are qualitatively similar but slightly larger when we

focus on the narrower range of firms around the treatment threshold, as seen in columns 3–4.

In Panel A of Figure 1, we show this effect graphically. In this figure, we match each

treated firm to one non-treated control firm that is most similar (its “nearest neighbor”) before

the reform, and the figure shows that while these treated and control firms displayed similar

cash savings behavior in every year before the reform, the treated firms saved significantly

less in the years after the reform.18

Figure 1 About Here

18In the matching procedure, we require an exact match on industry, and further match on the pre-periodCash/assets, payouts, wage increases, and investment based on the Mahalanobis distance.

15

4.2 Effects on payout policy

In the previous section, we showed that the treated firms significantly reduced cash savings

after the tax reform. Given this reduction in cash accumulation, we now examine how firms

spent the cash that was not saved. We start by examining how payout policy is affected by

the reform, and in the following sections, we study effects on wage increases and investments,

respectively. It is nevertheless important to note that cash savings, payouts, wages, and

investments do not exhaust all the possible uses (or sources) of corporate cash flows, and

thus, the total effects on these alternative uses of savings do not necessarily add up precisely

to the estimated decrease in savings. We nevertheless study these specific effects as they are

the ones explicitly targeted by the law.

We measure payout as the sum of cash dividends and share repurchases scaled by total

assets (multiplied by 100, so that any effects can be interpreted as a percent fraction of

assets). Table 3 reports results. The results reported in columns 1 and 2 of Table 3 show

that the treated firms increased payouts following the tax reform: the economic magnitude

is around 0.2 percentage points of assets, which is around 30% of the sample mean payout

of 0.7%. In columns 3 and 4, we restrict the sample to a narrower bandwidth around the

regulatory threshold and find similar results. Panel B of Figure 1 also shows these results

graphically for the matched treatment-control sample.

Table 3 About Here

We next examine the components of payouts, i.e. dividends and repurchases separately.

The results reported in Table A1 in the Internet Appendix indicate that while both forms of

payout significantly increased for treated firms following the tax reform, dividends increased

more than repurchases in absolute magnitude. Guay and Harford (2000) and Jagannathan,

Stephens, and Weisbach (2000) argue that firms tend to use dividend increases to distribute

16

cash from relatively permanent shocks, whereas they use repurchases to distribute transitory

shocks. Thus, to the extent that dividends signal payouts that are more permanent, this result

suggests that the treated firms established a permanently higher level of payouts after the

surtax came into effect. The differences between the increases in dividends and repurchases

can also reflect the fact that dividends overall represent a much larger share of total payouts

in this sample, which in turn is related to the fact that the majority of the sample firms are

private. Average dividend levels equal 0.59% of assets, whereas average repurchases equal

only 0.1%, which means that the repurchases increased more in percent (by around 50%)

than dividends (30%).

4.3 Effects on wage increases and investments

We next focus on the effects on two real outcome variables: wage increases and investments.

Higher wages and investments were also among the outcomes that were explicitly targeted by

the tax reform, as these were allowed to offset the surtax on retained earnings.

In Table 4, we report how the growth in wage bills changed around the tax reform for

the treated firms. We measure wage increases as changes in firms’ non-executive wage bills

scaled by total assets. The results reported in columns 1 and 2 indicate that treated firms

increased wage bills. These results continue to hold when we consider the narrower sample

around the threshold (see columns 3 and 4).19

19For a subset of firms (around 10% of the sample), we have data on both the total wage bill and thenumber of employees, which further allows us to break down these wage bill changes into wages for new hiresand wage increases to existing employees. In Table A2 in the Internet Appendix, we report the results weobtain after separately examining the effects on these two outcome variables: wage per employee and thenumber of employees. These results are nevertheless not entirely conclusive. When we do not limit the samplebased on shareholder’s equity being relatively close to the threshold, the results indicate that the treatedfirms did raise wages to existing employees while there is no significant effect on the number of employees.On the other hand, when we consider the narrower sample around the treatment threshold, we instead findlarger effects on the number of employees.

17

Table 4 About Here

We next examine the effects on investments. We measure investments as changes in

tangible assets plus depreciation scaled by total assets. The results reported in columns

1 and 2 of Table 5 indicate that the treated firms increased their investments compared

with non-treated firms. The economic magnitudes are significant as the investment rate

for the treated firms relative to untreated firms increased by around 20%-30%. In columns

3–4, we report the results for the narrower sample around the treatment threshold, and

the estimated effects on investment here are even greater in magnitude. Panels C and D

of Figure 1 graphically show the results on wage increases and investment for the matched

treatment-control sample.

Table 5 About Here

One advantage of the data on Korean firms is that it further allows us to identify what

kinds of investments are made. When we focus on these separate components of capital

expenditures, we find that the treated firms increased investments about equally in Land,

Buildings, and Equipment. These results are reported in Table A3 in the Internet Appendix.20

Why did firms increase investments? On the one hand, these results are consistent

with firms’ having available positive-NPV projects that previously were unfunded (Fazzari,

Hubbard, and Petersen, 1988). If the treated firms had no such investments, they could

alternatively avoid any surtax by increasing payouts instead of increasing investments. The

fact that firms did invest more thus implies that firms viewed the value of these investments

as sufficiently high to outweigh the alternative of paying out more money to shareholders. On

20The results for the narrower sample are similar, but each of the separate components of investment is nolonger individually statistically significant.

18

the other hand, it is also possible that investing more could be a sign of an agency problem

in the form of “empire-building.” In Section 7.3, we examine this possibility in detail.

4.4 Other effects: Leverage and profitability

Saving less could potentially have negative consequences for a firm’s risk of finding itself

in financial distress. Did these changes contribute to higher risk? We find that the treated

firms have higher leverage after the reform went into effect and report the results in Table 6

(columns 1 and 2), which is consistent with higher risk. The economic magnitude is around

one percentage point in higher book leverage.

Table 6 About Here

Observing higher leverage for the treated firms is not surprising, as these firms start

saving less cash and paying out more.21 Whether or not this leverage increase is concerning

depends on the firms’ initial leverage, which nevertheless was relatively conservative at a

mean of 31% (with a median of 27%).

We see evidence of such muted effects on default risk when considering the estimated

treatment effects on the probabilities of default.22 That is, despite the higher leverage of the

treated firms, we observe an effect on the probability of default that is both economically

and statistically indistinguishable from zero. This result is similar if we measure distress risk

over a two-year horizon (see columns 3 and 4 of Table 6) and a three-year horizon (columns

5–6). If the trends in lower savings and higher payouts continue for the treated firms also

21The reform notably treated payments to debt and equity investors in a non-neutral way, as it does notallow debt repayment to count as a tax-reducible item.

22The probability-of-default measure is based on data from the NUS Risk Management Institute. Thismeasure is calculated based on their methodology, which is described in detail at http://www.rmicri.org. Onedownside of the probability of default data is that it is only available for a subset of the public firms.

19

in the long run, however, we would eventually expect the divergence in leverage to increase

further, potentially causing significantly added risks of distress.

What effect did these actions have on firms’ overall levels of profitability? In Table A4

in the Internet Appendix, we report results pertaining to the operating performance of the

treated firms, measured by Return on Invested Capital (ROIC, measured as EBITDA scaled

by total invested capital) as well as by profit margin (net sales less the cost of goods sold as

a percentage of net sales).

We find that the treated firms display improved profitability. These results suggest that

the actions that firms took in response to the law did not hurt profitability and that these

actions, if anything, improved their overall returns on capital. The economic magnitude of

these profitability changes is also meaningful. These results do not, however, by themselves

represent conclusive evidence that these actions were value-improving—a question that we

will analyze more formally in section 6.

5 Robustness

In this section, we conduct a battery of robustness tests of our findings.

We begin by exploiting the “double-dimensionality” in the assignment of treatment,

i.e., the fact that treatment was based on satisfying one of two inclusion criteria. As is

typical in a difference-in-differences setting, the key identification assumption is the “parallel

trends” assumption. One might nevertheless be concerned that particularly the chaebol firms

could follow different trends from the non-chaebol firms, which in turn could be spuriously

contributing to our results. To account for this possibility, in Panel A of Table 7 we report

results from the difference-in-differences tests while restricting the sample to only non-chaebol

firms that fall in the narrower range around the treatment threshold. For these firms,

“treatment” is based solely on whether shareholders’ equity is above 50 billion wons. The

20

results show that the economic magnitudes and statistical significance of the effects remain

largely similar to what we found with the full sample. Thus, chaebol firms do not drive the

overall effects, and these results are robust to examining effects within non-chaebol firms.

Table 7 About Here

Next, even within the relatively narrow range between 10 and 90 billion wons, we might

be concerned that the slightly larger firms above the 50 billion threshold might be following

a different trend that was unrelated to the reform, compared with the trend that the slightly

smaller firms below the threshold follow. To address this concern, we therefore limit the

sample to only chaebol firms in the 10–90 billion range and report the results in Panel B of

Table 7. This test thus serves as a “placebo” test, because the 50 billion threshold has no

impact on treatment for these firms. Consistent with this idea, we find no effect (or, in the

case of investment, even an effect that is the opposite of what we observe with our baseline

results) around the threshold across all of the dependent variables.

In sum, the results reported in Panels A and B of Table 7 show that the 50 billion

threshold predicts an effect among the non-chaebol firms while we find no effect within the

“placebo” sample that uses the same threshold among only the chaebol firms. These findings

reinforce the results according to which the documented effects are driven by the treatment

from the tax reform, and not spuriously driven by differences caused by a violation of parallel

trends that are related to shareholders’ equity or chaebol membership.

To examine whether the results for the full sample are robust to controlling for other

variables, we also report the results from separate specifications with additional control

variables, including Shareholder’s equity - 50 billion wons (i.e., distance to threshold, as in a

regression discontinuity design), size, cash flow, debt, and Cash/assets, and report the results

in Panel C. Here, the results show that the estimated effects remain the same or become

21

even stronger when we control for these additional firm characteristics. To address a concern

about “bad controls” that could confound these results (Angrist and Pischke, p. 64), we do

not use these results as our baseline specification.23

In Panel D, we report the results employing a difference-in-differences matching procedure.

For each treated firm, we pick one control firm that is most similar (the “nearest neighbor”);

we require an exact match on industry, and further match on the pre-period Cash/assets,

payouts, wage increases, and investment based on the Mahalanobis distance. Then, using the

sample of the matched treated-control pairs of firms, we estimate the baseline difference-in-

differences model. Panel D shows that this matching procedure generates similar estimated

treatment effects even despite using a smaller sample.

To further support the parallel trends assumption, in Table 8, we report results pertaining

to differences in “pre-trends” among our main outcome variables between the treated group

and the non-treated group. Panel A reports the results for all firms while Panel B focuses on

the firms that fall within the narrower range around the treatment threshold.

Table 8 About Here

These tests also show that our results are unlikely to be confounded by a violation of

the parallel trends assumption, as we do not observe any significant differential pre-trends

between the treated and untreated firms. This holds both across the full sample, and also

when we focus on the narrower range around the threshold. If anything, we typically observe

pre-trends that run in the opposite way of our main results; this is, for example, the case for

our investment variable in the narrow range, where the treated firms see slightly lower trends

in investment in the years leading up to the law.

23The full sets of the estimated coefficients from our baseline difference-in-differences specifications arereported in Table A5 in the Internet Appendix.

22

We may additionally be concerned about whether firms close to the threshold intentionally

shrink to avoid the tax, and whether such behavior may have an impact on our results.

We address this concern in two ways. First, we examine how many firms move across the

threshold to examine whether a large number of firms show behavior consistent with avoiding

the tax. We find little evidence that firms are shrinking to avoid the surtax; while 39 firms

move from above to below the threshold between 2014 and 2015, 185 firms move from below to

above (the fact that more firms are growing is consistent with overall growth in the economy

over this period). Second, we re-estimate our results using a “Donut RD” empirical strategy,

where we focus on the 10–90B wons range, but further exclude firms in the 45–55 billion

wons range for whom the incentives to shrink to avoid the tax may be the strongest. The

results, which are reported in Table A6 in the Internet Appendix, are similar, and if anything,

generally stronger than in our baseline tests.

Finally, we analyze whether these results differ depending on whether we focus on private

or public firms, or whether the results are unique to either of these groups of firms. Previous

research has shown that private firms overall tend to hold less cash than public firms (Gao

et al., 2013). We nevertheless find no significant differences between private and public firms

in their responses to the law.24

6 Valuation consequences

Our results thus far have shown that the treated firms responded to the reform by saving less

cash, paying out more to shareholders, and spending more on investments and wages. The

question nevertheless remains whether or not firms were saving optimally before the law, and

thus whether the treated firms’ responses to the tax reform represent an improvement or not.

In other words, whether discouraging savings is desirable from a policy perspective depends

24These results are not separately tabulated in the paper but available from the authors.

23

crucially on why firms are saving in the first place: If high savings rates before the law were

optimal, then using the tax system to discourage savings will merely destroy firm value by

distorting firms’ cash policies.25

Theoretically, firms should equate the marginal cost of saving cash with the marginal

benefit of doing so (e.g., Opler et al. (1999); Almeida, Campello, and Weisbach (2004)).

The main cost of saving involves potentially sacrificing profitable investment projects today

and a “double-taxation” penalty from earning interest, whereas a principal benefit is that a

cash buffer can enable firms to better weather recessions and respond to future investment

opportunities (Lins et al., 2010). This is especially true when a firm may face financial

constraints that can make internal financing significantly cheaper than external financing

(Almeida et al., 2004; Acharya et al., 2007). It is challenging to assess whether the treated

firms’ post-reform savings and investment behavior represent an improvement because it is

hard to measure the (shadow) value of cash savings and of any marginal investments. In this

section, we seek to address this question by employing an event study analysis around the

proposal and the passage of the law.

We analyze how investors viewed the valuation consequences of the law for the treated

firms, by employing an event study methodology around the date when the law was proposed

and the date when it was passed. The idea is that we may be able to distinguish between

excessive and optimal savings by looking at abnormal returns around the time the law was

passed. These returns can plausibly capture investors’ expectations regarding the long-term

consequences of the law for firm value, also accounting for expectations for how firms will

react to the law regarding any changes to their savings, payouts, and investments.26

25Previous empirical evidence (Brav et al., 2018; Kaplan, 1989) as well as agency theories (Jensen, 1986)might instead suggest that over-investment rather than excessive savings could be the larger problem.

26Studying announcement returns around several dates related to the passage of the same law in Koreathat we exploit for our study, Semaan (2017) finds that firms that were more likely to be subject to surtaxesexperienced negative abnormal returns, but that this effect was muted for firms that were more likely toengage in tax avoidance.

24

To the extent that high savings and high cash balances before the law were optimal, then

using the tax system to distort firms’ savings and investment policy must destroy firm value,

and we would expect any valuation effects for the treated firms to be negative. This negative

effect consists of two parts: an indirect effect from the tax change distorting corporate policies,

plus a direct effect from paying higher taxes to the extent that firms do not change their

policies sufficiently to avoid the surtax completely. On the other hand, if investors viewed

any changes that firms take in response to the reform to be value-improving, we might expect

somewhat less negative announcement returns to the extent that these indirect effects from

changes in firm policies cancel out the direct negative effects of higher taxes, or even positive

announcement returns if these indirect effects are viewed as sufficiently value-improving and

firms are able to make sufficiently large changes to mostly avoid any surtax. That is, if firms’

savings were excessive before the reform, then discouraging savings through the tax system

could result in improved firm outcomes, and possibly even higher firm values for the treated

firms despite the prospect of higher taxes.

To examine investors’ reactions to the tax reform, we compute the three-day cumulative

abnormal returns (CAR), from one day before to one day after the proposal of the law on

August 6, 2014, as well as the three-day-CARs around the passage of the law on December

2, 2014. We choose these two days because, even though rumors of such a law had existed

before the proposal, these are the first days when the information indicating which firms

would be treated and which firms would not be treated was released. We then take the sum

of these two CARs for each firm and regress it on the Treated indicator.

In Table 9, we report the results from the event study analysis.

Table 9 About Here

25

The results show that abnormal returns (CAR) for the treated firms around the days

when the law was proposed and passed were positive. This implies that investors believed that

the cash accumulation before the law was excessive and that encouraging firms to increase

payouts and investments enhances firm value. The economic magnitudes are estimated to be

around 2% of firm value. These effects are similar regardless of whether we include industry

fixed effects or not, whether we use the full or narrower sample, and whether we limit the

sample to only non-chaebol firms. These results are notably similar to the findings reported

by Christie and Nanda (1994), who find positive market reactions of about 1% around the

announcement of the undistributed profits tax of 1936–37 in the U.S.

The positive CAR for the treated firms is especially notable because the tax itself has a

direct negative valuation effect, as at least some treated firms are likely to pay higher taxes—

specifically, those firms that do not avoid the tax by increasing payouts and investments

sufficiently to avoid the surtax). The positive returns among the treated firms imply that

investors expected the treated firms’ responses to sufficiently enhance their value to more

than outweigh the direct negative effects from higher taxes. These results broadly support

previous findings regarding that investors tend to view a marginal dollar in the hands of

a corporation as being worth less than a dollar (Faulkender and Wang, 2006; Dittmar and

Mahrt-Smith, 2007).

7 Cross-sectional variation and channels

We next investigate whether firms that had high earnings before the reform responded

differently to the tax, as these firms were likely to be more heavily affected by the new surtax.

In the following sections, we use cross-sectional splits to study the mechanism through which

the tax reform affected corporate policies, which in turn can help shed light on why firms

might have been saving excessively in the first place.

26

7.1 High earnings

Firms with high earnings are more heavily affected by the new surtax, and the law also requires

these firms to effect relatively larger changes in their investment and savings behaviors to

minimize the surtax. We might thus expect these firms to change their savings and investment

policies to a greater extent around the reform.

To examine the differential effects on firms with high earnings, we split the sample based

on firms’ pre-reform earnings, measured as operating cash flows (the ratio of EBITDA to

total assets). We define a variable High earnings based on whether these earnings are above

the median. We then estimate triple-difference regressions for the effects on savings, payouts,

and investments, where we interact Treated and After with High earnings. We report the

results in Panel A of Table 10.

Table 10 About Here

Overall, we observe that the treatment effects on corporate policies are significantly more

pronounced for firms that garnered higher earnings in the pre-reform period.

Because the high-earnings firms change their savings and investment policies after the law

more extensively, we might also expect investors to react more strongly to the passage of the

law for these firms—assuming that investors correctly anticipate these reactions. Consistent

with this hypothesis, the results we report in Panel B of Table 10 show that the positive

valuation effects are indeed more pronounced for high-earnings firms.

7.2 Behavioral bias

We next study a possible channel that might explain why Korean firms prior to the enactment

of the law may have exhibited excessive savings in the first place, which is related to possible

27

behavioral biases caused by past experiences. Previous studies have documented links between

past experiences and future financial decisions. For example, Malmendier and Nagel (2011)

and Knupfer, Rantapuska, and Sarvimaki (2017) find that individuals who experienced

depression periods are more likely to be risk-averse in their investments in financial assets.

In the corporate setting, Dittmar and Duchin (2015) find that firms with CEOs who have

worked at a company that has undergone financial difficulties hold more cash.

We similarly examine the role of behavioral biases reflecting a “crisis mentality” among

firms and executives that might have been formed during the 1997 Asian financial crisis. The

idea is that if firms depended heavily on external financing and experienced the crisis, they

might have come out of the crisis with the belief that they need to build ample cash buffers to

weather the next crisis. The basic idea is that either a firm’s CEO may personally remember

the effects of the crisis, or even if the CEO has changed, the firm may have an “institutional

memory” from the crisis. Consistent with higher pre-reform savings for firms with memories

of a past crisis, in Panel A of Table A8 in the Internet Appendix, we report results supporting

a correlation between CrisisMemory and the pre-reform level of cash. Controlling for firm

size and cash flow, we observe in general that firms with a stronger memory from the crisis

did accumulate more cash before the tax reform.

To classify firms according to whether they may suffer from biases from a past crisis,

we define an indicator variable CrisisMemory as equal to one if either 1) the firm’s CEO

was an executive of a firm during the Asian crisis that was operating in an industry that

depends heavily on external financing, or 2) if the firm itself was established before the

crisis and operated in an industry marked by heavy dependence on external financing. The

degree to which firms in an industry depends on external financing is defined, following

Rajan and Zingales (1998), as capital expenditures minus operating cash flow; the use of this

measure within the specific context of the Asian financial crisis is based on Almeida, Kim,

and Kim (2015), who find that Korean firms that operate in industries that depend heavily

28

on external financing experienced more severe liquidity shocks during the crisis. We employ

triple-difference regressions and employ this indicator variable as an additional interaction

term in the baseline difference-in-differences. We hypothesize that firms that fit the definition

of the CrisisMemory variable were more likely to hoard cash excessively before the tax reform

and thus were more heavily affected by the new tax law.

We report the results of our analysis of the CrisisMemory variable in Table 11. In Panel A

we report the triple-difference results regarding the effects on savings, payouts, wage increases,

and investments. We see that firms with a crisis memory reduced cash savings to a greater

extent and also increase payouts, wages, and investments to a greater extent after the tax

reform, although some of these results are statistically significant at the 10% level only. This

suggests that the tax reform had a larger effect in terms of nudging these firms to change

their behavior.

Table 11 About Here

The results we report in Panel B in Table 11 show the differences in market valuation

responses around the law announcements for the crisis-memory firms vs. those firms without

such memories from the previous crisis. The results indicate that the positive announcement

returns (CAR) for treated firms are concentrated among firms with a crisis memory.

As a robustness test, we next confirm that our results capture not only industry-level

differences related to external financing needs, but are related specifically to a firm’s or CEO’s

memories from the past. In Table A7 in the Internet Appendix we report results from a

placebo test where we replace the CrisisMemory variable with a variable indicating whether

a firm operates in an industry with high dependence on external financing but either the

firm or CEO were not operating in 1997 when the Asian financial crisis hit. These placebo

tests show that there is no relationship between firm responses around the reform and their

29

dependence on external financing, but that the results in Table 11 are indeed driven by the

interaction of both being dependent on external finance and remembering the previous crisis.

The results we report in Table A7 similarly show that there are no effects merely involving

“old” firms or CEOs (defined as having been operating in 1997) unless the firm also relied

heavily on external financing.

The results discussed in this section together indicate that firms operating with a crisis

mentality saved more cash before the new reform, but also responded more strongly overall

to the reform, and moreover that these responses were viewed more positively by the market.

These results are consistent with a behavioral hypothesis whereby some firms and CEOs may

have been traumatized by the crisis and therefore engaged in excessive savings.

7.3 Corporate governance

Finally, we study the extent to which differences in firms’ levels of corporate governance

affected how firms and investors responded to the tax reform. Agency conflicts and poor

governance are one of the main reasons why we might expect firms to engage in overly

cautious precautionary savings before the reform (Bertrand and Mullainathan, 2003; Gao,

Harford, and Li, 2013; Nikolov and Whited, 2014). It is thus possible that the reform had

a larger impact on firms with relatively worse governance quality. The results we report in

Table A8 (Panel B) in the Internet Appendix show that poorly governed firms indeed tended

to carry more cash on their balance sheets before the reform.

To measure corporate governance quality, we employ a governance index score created by

the Korea Corporate Governance Service (KCGS). KCGS calculates these scores every year

for all public firms listed in the KOSPI market, and this measure is therefore limited to only

the subset of public firms. This governance score is calculated as a sum that encompasses

four distinct aspects of governance: 1) the protection of shareholder rights, which is given a

30

score between 0 and 81, 2) the internal workings and processes of the board, which is given a

score between 0 and 69, 3) the workings of monitoring organizations, which is given a score

between 0 and 43, and 4) transparency in disclosures, which is given a score between 0 and

47. These scores are then summed to create a total governance score. Note that higher scores

denote increasing governance quality, differing from the GIM-index or E-Index scores in

the U.S., which denote decreasing governance quality. We then define an indicator variable

High-G as equal to one if a firm is assigned an above-median total governance score.

In Panel A of Table 12 we first report results about how differences in corporate governance

quality affected post-reform changes in cash savings, investments, and payouts for the treated

firms.

Table 12 About Here

We find that there are no significant differences in changes in cash savings between poorly

governed and well-governed firms. That is, treated firms in both of these groups reduce their

savings equally after the law was enacted.

How firms used this money that was not saved differs in a predictable pattern, however,

depending on the quality of governance. The positive treatment effects on payouts are

concentrated among well-governed firms: treated firms demonstrating good governance on

average increase payouts following the tax reform by approximately 0.35 percentage points of

assets while poorly governed treated firms do not. On the other hand, the positive treatment

effects on investments and wage increases are much stronger among poorly governed firms.27

This evidence is broadly consistent with “empire-building” among these poorly governed

firms.

27The magnitudes of the average differences in the outcome variables between well-governed and poorlygoverned firms are quite large relative to those of our baseline treatment effects. This is partly a result of thefact that the magnitudes of the “baseline” treatment effects are even larger among this subsample of firms forwhich the governance score is available.

31

As seen in Panel B of Table 12, we further find that the investors’ value reaction to the

reform was much higher for the well-governed firms. This suggests that investors expected the

better-governed firms to respond more efficiently to the tax reform, apparently realizing that

the reform could encourage empire-building, particularly among poorly-governed firms. The

coefficients on the interaction term indicate that the announcement day CAR for a treated

firm is about 2% lower among poorly-governed firms.

This result thus reveals a dark side of the reform. Even if some firms were saving too

much, pushing firms to do something else with that money may not necessarily improve firm

value. For example, instead of hoarding cash, firms could alternatively overinvest or engage

in other forms of “empire-building,” which can result in even worse consequences.

8 Conclusion

Corporations all over the world have accumulated unprecedented levels of cash on their

balance sheets. Many observers say this trend has gone too far and increasingly criticize

firms for “hoarding” cash. Does this cash represents optimal precautionary savings by firms,

or could this money instead be put to more productive uses if firms saved less and instead

spent more on payouts, wages, or new investments? Can tax policy reduce corporate savings?

And if so, what are the consequences? To investigate these questions, we exploit a unique

tax reform in South Korea that explicitly sought to curb corporate savings by imposing a

surtax on excessive savings.

We employ a difference-in-differences methodology to exploit this natural experiment and

show that firms that were discouraged from saving instead spent more on payouts, wages, and

investments. Whether saving less and spending more on payouts and investments is desirable

depends on whether the treated firms’ savings and investment policies were optimal before

the law. Exploiting an event study methodology, we find that the valuation consequences

32

from being treated by the law were positive. This result suggests that investors expected

firms’ responses to the law to be value-improving, indeed sufficient enough to more than

outweigh the direct negative valuation consequences of facing higher taxes.

Overall, these findings are consistent with firms having saved excessively before the

law was enacted. When we investigate two channels that might explain why firms might

have been saving too much, we find evidence consistent with both behavioral biases and

agency conflicts as drivers of excessive savings prior to the reform. Both firms and investors

responded more strongly when a treated firm had a memory from the Asian financial crisis.

Merely encouraging internal investments instead of saving cash, however, is not a silver

bullet: poorly governed firms tend not to increase payouts and instead focus on investments,

and they experience lower valuation effects that are consistent with being perceived as

practicing inefficient empire-building. These findings contribute to the literature on the value

of corporate cash and offer important lessons for future policy.

33

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38

Figure ITime-series Trends in Outcome Variables

This figure plots differential trends over the years in cash savings (Panel A), payout (PanelB), wage increases (Panel C), and investments (Panel D) between treated and control firms.For each treated firm, we pick one control firm that is most similar (its “nearest neighbor”);we require an exact match on industry, and further matches on the pre-period ∆Cash/assets,payouts, wage increases, and investment based on the Mahalanobis distance. All outcomevariables are defined in Table A9 in the Internet Appendix.

39

Table 1Summary Statistics

In this table we report summary statistics. In Panel A we report firm-year-level statistics onfirm characteristics. In Panel B we report the number of firms in each combination of thetreatment criteria as of 2014. All variables are defined in Table A9 in the Internet Appendix.

Mean SD P1 P25 P50 P75 P99 N

Panel A. Firm characteristics (All firms)

Treated 0.17 0.37 0.00 0.00 0.00 0.00 1.00 80494After 0.53 0.50 0.00 0.00 1.00 1.00 1.00 804941{Equity ≥ 50 billion} 0.15 0.35 0.00 0.00 0.00 0.00 1.00 80494Chaebol 0.05 0.21 0.00 0.00 0.00 0.00 1.00 80494∆Cash/assets (%) 1.08 7.94 -23.67 -1.40 0.10 2.67 37.08 74016Payout (%) 0.75 2.38 0.00 0.00 0.00 0.00 16.03 74390

Dividend (%) 0.56 1.84 0.00 0.00 0.00 0.00 12.44 74390Repurchase (%) 0.10 0.61 0.00 0.00 0.00 0.00 5.04 74390

Wage increase (%) 0.36 1.46 -4.17 -0.13 0.14 0.67 7.30 71809Investment (%) 3.05 10.08 -16.20 -0.79 0.26 3.58 41.57 70592

Investment in land (%) 1.20 6.33 -15.83 0.00 0.00 0.00 38.21 72626Investment in building (%) 1.08 4.80 -9.29 0.00 0.00 0.16 30.18 72627Investment in equipment (%) 1.24 4.18 -11.20 0.00 0.00 1.07 24.33 72631

Earnings (%) 2.51 11.11 -43.36 -0.19 2.38 6.83 38.42 74322Size 24.23 1.15 22.44 23.41 23.92 24.78 28.31 80494Debt (%) 31.75 27.87 0.00 6.71 27.95 48.95 118.79 80494G-index 103.55 22.56 52.00 91.00 101.00 113.00 174.00 2513ROIC (%) 7.74 15.61 -44.68 1.50 5.65 11.79 81.80 74390Profit margin (%) 21.27 20.17 -37.29 9.75 17.03 28.83 91.77 73653PD in 2yrs (%) 0.38 0.55 0.00 0.06 0.20 0.46 3.25 6467PD in 3yrs (%) 0.58 0.72 0.00 0.13 0.36 0.73 4.04 6467CARproposal+CARpassage 0.01 0.07 -0.18 -0.03 0.00 0.04 0.23 6569

Panel B. Number of firms in each combination of treatment criteria

Chaebol Non-chaebol TotalSEQ ≥ 50 billion 599 2,852 3,451SEQ < 50 billion 453 17,012 17,465Total 1,052 19,864 20,916

40

Table 2Treatment Effects on Changes in Cash

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on changes in cash holdings. We use the entire sample to obtain theresults reported in columns 1 and 2 while for columns 3 and 4 we use firms in the narrowerbandwidth around the 50-billion-wons equity threshold. All variables are defined in Table A9in the Internet Appendix. We include firm and year or industry-year fixed effects as indicated.t-statistics (in parentheses) are calculated using standard errors that are heteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance atthe 1%, 5%, and 10% levels, respectively.

Dependent variable: ∆Cash/assets

(1) (2) (3) (4)

Sample All firms Firms in [10B, 90B]

Treated × After -0.282** -0.291* -0.449** -0.442**(-2.06) (-1.95) (-2.23) (-2.03)

Firm FE Yes Yes Yes YesYear FE Yes No Yes NoIndustry × Year FE No Yes No Yes

N 71,476 70,504 32,094 31,027R2 0.1910 0.2447 0.1880 0.2781

41

Table 3Treatment Effects on Payouts

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on total payouts. To obtain the results reported in columns 1 and 2 weuse the entire sample while for columns 3 and 4 we use firms in the narrower bandwidth aroundthe 50-billion-wons equity threshold. All variables are defined in Table A9 in the InternetAppendix. We include firm and year or industry-year fixed effects in the specifications. t-statistics (in parentheses) are calculated using standard errors that are heteroskedasticity-robustand clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the1%, 5%, and 10% levels, respectively.

Dependent variable: Payout

(1) (2) (3) (4)

Sample All firms Firms in [10B, 90B]

Treated × After 0.212*** 0.216*** 0.208*** 0.219***(5.27) (5.03) (3.12) (3.06)

Firm FE Yes Yes Yes YesYear FE Yes No Yes NoIndustry × Year FE No Yes No Yes

N 71,883 70,912 32,134 31,071R2 0.6206 0.6452 0.6275 0.6679

42

Table 4Treatment Effects on Wage Increases

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on wage increases. To obtain the results reported in columns 1 and 2 weuse the entire sample while for columns 3 and 4 we use firms in the narrower bandwidth aroundthe 50-billion-wons equity threshold. All variables are defined in Table A9 in the InternetAppendix. We include firm and year or industry-year fixed effects in the specifications. t-statistics (in parentheses) are calculated using standard errors that are heteroskedasticity-robustand clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the1%, 5%, and 10% levels, respectively.

Dependent variable: Wage increase

(1) (2) (3) (4)

Sample All firms Firms in [10B, 90B]

Treated × After 0.173*** 0.161*** 0.122*** 0.098***(8.02) (6.53) (3.68) (2.69)

Firm FE Yes Yes Yes YesYear FE Yes No Yes NoIndustry × Year FE No Yes No Yes

N 69,329 68,412 31,580 30,552R2 0.3889 0.4358 0.3946 0.4616

43

Table 5Treatment Effects on Investments

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on investments. To obtain the results reported in columns 1 and 2 weuse the entire sample while for columns 3 and 4 we use firms in the narrower bandwidth aroundthe 50-billion-wons equity threshold. All variables are defined in Table A9 in the InternetAppendix. We include firm and year or industry-year fixed effects in the specifications. t-statistics (in parentheses) are calculated using standard errors that are heteroskedasticity-robustand clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the1%, 5%, and 10% levels, respectively.

Dependent variable: Investment

(1) (2) (3) (4)

Sample All firms Firms in [10B, 90B]

Treated × After 0.494*** 0.480*** 0.694*** 0.712***(2.89) (2.69) (2.90) (2.59)

Firm FE Yes Yes Yes YesYear FE Yes No Yes NoIndustry × Year FE No Yes No Yes

N 65,887 64,934 30,447 29,416R2 0.4077 0.4461 0.3934 0.4575

44

Table 6Financial Distress

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on financial distress proxied by financial leverage or the probability ofdefault. To obtain the results reported in Panel A we use the entire sample while for Panel B weuse firms in the narrower bandwidth around the 50-billion-wons equity threshold. All variablesare defined in Table A9 in the Internet Appendix. We include firm and year or industry-yearfixed effects in the specifications. t-statistics (in parentheses) are calculated using standarderrors that are heteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗

indicate statistical significance at the 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4) (5) (6)

Dependent variable Leverage PD in 2yrs PD in 3yrs

Panel A: All firms

Treated × After 1.093*** 0.896*** 0.000 0.000 0.000 0.000(5.30) (3.74) (1.42) (0.89) (1.44) (0.80)

N 84,885 83,983 6,465 5,581 6,465 5,581R2 0.8713 0.8794 0.7253 0.7816 0.7398 0.7944

Panel B: Firms in [10B, 90B] (Discontinuity test)

Treated × After 0.581* 0.773** 0.000 -0.000 0.000 -0.000(1.90) (2.34) (0.64) (-0.09) (0.65) (-0.14)

N 35,744 34,714 3,187 2,449 3,187 2,449R2 0.8450 0.8625 0.6581 0.7629 0.6791 0.7776

Firm FE Yes Yes Yes Yes Yes YesYear FE Yes No Yes No Yes NoIndustry × Year FE No Yes No Yes No Yes

45

Table 7Robustness of the Treatment Effects

In this table we report the results of difference-in-differences (DID) regressions regarding thetreatment effects of the tax reform on each of our dependent variables across several combina-tions of samples and specifications: the baseline DID regressions within only non-chaebol firmsin the narrower bandwidth around the 50-billion-wons equity threshold (Panel A), a “placebotest” among chaebol firms around the 50 billion threshold within the narrower bandwidth(Panel B), the baseline DID regressions while controlling for additional firm characteristics,including distance to threshold, size, earnings, debt, and Cash/assets (Panel C), and matchingDID regressions where we match each treated firm with one control firm of the nearest neighbor(based on the Mahalanobis distance) on industry as well as on pre-period cash, payouts, wageincreases, and investments (Panel D). All variables are defined in Table A9 in the InternetAppendix. We include firm and industry-year fixed effects as indicated. t-statistics (in paren-theses) are calculated using standard errors that are heteroskedasticity-robust and clustered byfirm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the 1%, 5%, and 10%levels, respectively.

Dependent variable ∆Cash/assets Payout Wage increase Investment

(1) (2) (3) (4)

Panel A: Non-chaebol firms in [10B, 90B]

1{Equity ≥ 50 billion} × After -0.489* 0.250*** 0.082** 0.591**(-1.70) (3.16) (2.06) (1.97)

N 29,700 29,735 29,287 28,264R2 0.2794 0.6691 0.4589 0.4530

Panel B: Placebo, Chaebol firms in [10B, 90B]

1{Equity ≥ 50 billion} × After -0.104 -0.203 -0.060 -3.958**(-0.04) (-0.46) (-0.36) (-2.12)

N 758 758 730 623R2 0.4303 0.7523 0.6083 0.6914

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes Yes

46

Dependent variable ∆Cash/assets Payout Wage increase Investment

(1) (2) (3) (4)

Panel C: Additional control variables

Treated × After -0.737*** 0.289*** 0.074** 1.566***(-3.64) (4.89) (2.12) (6.06)

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes YesControls Yes Yes Yes Yes

N 70,517 70,611 68,340 64,862R2 0.6148 0.6488 0.4463 0.4790

Panel D: Matched treated-control pairs

Treated × After -0.447* 0.149** 0.081* 0.807***(-1.93) (2.48) (1.77) (2.69)

N 24,172 24,193 24,133 24,054R2 0.1908 0.6307 0.3970 0.3903

47

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48

Table 9Value Implication of the Tax Reform

In this table we report the differences in cumulative abnormal returns around the proposaland the passage of the law between treated and nontreated firms. To obtain the results re-ported in Panel A we use the entire sample while for Panel B we use firms in the narrowerbandwidth around the 50-billion-wons equity threshold. We include industry fixed effects inthe specifications. t-statistics (in parentheses) are calculated using standard errors that areheteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statis-tical significance at the 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4)

Dependent variable CARproposal+CARpassage (-1 to +1 days)

Sample Chaebol + Non-chaebol Non-chaebol only

Panel A: All firms

Treated 0.018*** 0.019*** 0.018*** 0.016***(4.62) (3.84) (4.53) (3.12)

Constant -0.006 -0.006(-1.59) (-1.59)

Industry FE No Yes No Yes

N 1,650 1,451 1,422 1,236R2 0.0158 0.2313 0.0165 0.2459

Panel B: Firms in [10B, 90B] (Discontinuity test)

Treated 0.017*** 0.020*** 0.016*** 0.017**(3.00) (2.63) (2.77) (2.34)

Constant -0.004 -0.004(-1.08) (-1.08)

Industry FE No Yes No Yes

N 811 641 786 616R2 0.0107 0.2411 0.0092 0.2544

49

Table 10Earnings and Treatment/Value Effects

In Panels A and B, respectively, we report the results of panel and cross-sectional regres-sions on the cross-sectional differences across firms regarding the treatment and value effectsdepending on whether a firm’s pre-reform earnings are above or below the median (High earn-ings) where earnings is proxied by earnings before interest, taxes, depreciation, and amorti-zation (EBITDA). t-statistics (in parentheses) are calculated using standard errors that areheteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statis-tical significance at the 1%, 5%, and 10% levels, respectively.

Panel A: Treatment effects and earnings

(1) (2) (3) (4)

Dependent variable ∆Cash/assets Payout Wage increase Investment

Treated × After 0.029 0.110** 0.060* -0.042(0.14) (2.55) (1.88) (-0.13)

High earnings × After -0.199 -0.065** -0.193*** -0.874***(-1.57) (-2.23) (-7.53) (-4.05)

Treated × After × High earnings -0.680** 0.184** 0.158*** 0.816**(-2.32) (2.51) (3.50) (1.97)

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes Yes

N 62,977 63,409 60,463 59,500R2 0.1722 0.6130 0.4009 0.3923

50

Panel B: Value implications and earnings

(1) (2)

Dependent variable CARproposal+CARpassage (-1 to +1 days)

Sample Chaebol + Non-chaebol Non-chaebol only

Treated 0.010 0.004(1.52) (0.64)

High earnings -0.005 -0.004***(-0.56) (-0.53)

Treated × High earnings 0.017* 0.021**(1.89) (2.20)

Industry FE Yes Yes

N 1,443 1,229R2 0.2383 0.2550

51

Table 11The Role of Crisis Mentality

In Panels A and B, respectively, we report the results of panel and cross-sectional regressions onthe cross-sectional differences across firms regarding the treatment and value effects dependingon whether a CEO or firm itself was operating in an industry featuring above-median externalfinance dependence (EFD) during the 1997 Asian financial crisis (CrisisMemory). t-statistics(in parentheses) are calculated using standard errors that are heteroskedasticity-robust andclustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the 1%,5%, and 10% levels, respectively.

Panel A: Treatment effects and crisis mentality

(1) (2) (3) (4)

Dependent variable ∆Cash/assets Payout Wage increase Investment

Treated × After -0.142 0.135** 0.108*** 0.371*(-0.98) (2.37) (2.75) (1.69)

CrisisMemory × After 0.189 0.057 0.014 -0.430**(0.47) (0.64) (0.21) (-2.54)

Treated × After × CrisisMemory -0.279* 0.146* 0.110** 0.599*(-1.86) (1.72) (1.98) (1.95)

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes Yes

N 71,083 71,358 68,885 67,067R2 0.1955 0.6281 0.4157 0.4153

52

Panel B: Value implications and crisis mentality

(1) (2)

Dependent variable CARproposal+CARpassage (-1 to +1 days)

SSample Chaebol + Non-chaebol Non-chaebol only

Treated 0.010 0.007(1.53) (0.97)

CrisisMemory -0.023** -0.026***(-2.42) (-2.77)

Treated × CrisisMemory 0.017* 0.018*(1.94) (1.90)

Industry FE Yes Yes

N 1,451 1,236R2 0.2316 0.2485

53

Table 12The Role of Governance

In Panels A and B, respectively, we report the results of panel and cross-sectional regressions onthe cross-sectional differences across firms regarding the treatment and value effects dependingon whether a firm’s governance score (G-index) is above the median or not (High-G). t-statistics(in parentheses) are calculated using standard errors that are heteroskedasticity-robust andclustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the 1%,5%, and 10% levels, respectively.

Panel A: Treatment effects and governance

(1) (2) (3) (4)

Dependent variable ∆Cash/assets Payout Wage increase Investment

Treated × After -0.601 0.050 0.298** 2.722*(-0.72) (0.61) (2.01) (1.91)

High-G × After 2.053 -0.283* 0.245** 2.586**(1.50) (-1.77) (2.11) (2.05)

Treated × After × High-G -1.777 0.350** -0.213** -2.661**(-1.26) (2.06) (-1.99) (-2.13)

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes Yes

N 2,521 2,521 2,514 2,471R2 0.1779 0.7595 0.4521 0.3707

54

Panel B: Value implications and governance

(1) (2)

Dependent variable CARproposal+CARpassage (-1 to +1 days)

Sample Chaebol + Non-chaebol Non-chaebol only

Treated 0.010 0.012(1.44) (1.54)

High-G -0.044 -0.038(-1.63) (-1.53)

Treated × High-G 0.021** 0.020**(2.05) (2.01)

Industry FE Yes Yes

N 494 342R2 0.3218 0.3577

55

Appendix

Table A1Treatment Effects on Payout Components

In this table we report the results of difference-in-differences regressions regarding the treat-ment effects of the tax reform on the components of total payouts: cash dividends (Panel A)and share repurchases (Panel B). To obtain the results reported in columns 1 and 2 we usethe entire sample while for columns 3 and 4 we use firms in the narrower bandwidth aroundthe 50-billion-wons equity threshold. All variables are defined in Table A9 in the Internet Ap-pendix. We include firm and year or industry-year fixed effects in the specifications. t-statistics(in parentheses) are calculated using standard errors that are heteroskedasticity-robust andclustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the 1%,5%, and 10% levels, respectively.

(1) (2) (3) (4)

Sample All firms Firms in [10B, 90B]

Panel A Dependent variable: Dividend

Treated × After 0.135*** 0.149*** 0.108** 0.117**(4.42) (4.81) (2.08) (2.16)

N 71,883 70,912 32,134 31,071R2 0.7121 0.7322 0.7115 0.7430

Panel B Dependent variable: Repurchase

Treated × After 0.037*** 0.031** 0.041** 0.041*(2.78) (2.16) (2.02) (1.84)

N 71,883 70,912 32,134 31,071R2 0.3603 0.3958 0.3519 0.4124

Firm FE Yes Yes Yes YesYear FE Yes No Yes NoIndustry × Year FE No Yes No Yes

56

Table A2Treatment Effects on Average Wages and Number of Employees

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on three employment-related variables: Wage per employee, defined asthe natural logarithm of total wage bills divided by the number of employees (columns 1 and2); Number of employees, defined as the natural logarithm of the total number of employees(columns 3 and 4); and N.employees/assets, defined as the total number of employees over totalassets multiplied by 1,000,000 (columns 5 and 6). We include firm and year or industry-yearfixed effects in the specifications. t-statistics (in parentheses) are calculated using standarderrors that are heteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗

indicate statistical significance at the 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4) (5) (6)

Dependent variable Wage per employee Number of employees N.employees/assets

Panel A: All firms

Treated × After 0.072*** 0.065** 0.018 0.036 0.006 0.006(3.27) (2.46) (0.90) (1.63) (1.37) (1.19)

N 8,219 7,353 8,249 7,381 8,249 7,381R2 0.9217 0.9331 0.9650 0.9674 0.9141 0.9285

Panel B: Firms in [10B, 90B] (Discontinuity test)

Treated × After 0.029 -0.013 0.035 0.063** 0.016*** 0.022***(1.02) (-0.37) (1.44) (2.15) (3.04) (3.28)

N 3,827 3,074 3,838 3,085 3,838 3,085R2 0.8722 0.8998 0.9237 0.9394 0.8977 0.9151

Firm FE Yes Yes Yes Yes Yes YesYear FE Yes No Yes No Yes NoIndustry × Year FE No Yes No Yes No Yes

57

Table A3Treatment Effects on the Components of Investments

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on each component of total investments, i.e. investments in land,building, and equipment. We include all firms in the sample. All variables are defined in TableA9. We include firm and year or industry-year fixed effects in the specifications. t-statistics(in parentheses) are calculated using standard errors that are heteroskedasticity-robust andclustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statistical significance at the 1%,5%, and 10% levels, respectively.

(1) (2) (3) (4) (5) (6)

Dependent variable Investment in land Investment in building Investment in equipment

Treated × After 0.210** 0.143 0.192** 0.197** 0.102 0.139*(2.25) (1.40) (2.48) (2.29) (1.28) (1.75)

Firm FE Yes Yes Yes Yes Yes YesYear FE Yes No Yes No Yes NoIndustry × Year FE No Yes No Yes No Yes

N 67,905 66,979 67,907 66,981 67,912 66,986R2 0.3063 0.3468 0.3105 0.3569 0.4512 0.4873

58

Table A4Operating Performance

In this table we report the results of difference-in-differences regressions regarding the treatmenteffects of the tax reform on operating performance, as measured by return on invested capital(ROIC ) and profit margin. To obtain the results reported in Panel A we use the entire samplewhile for Panel B we use firms in the narrower bandwidth around the 50-billion-wons equitythreshold. All variables are defined in Table A9. We include firm and year or industry-yearfixed effects in the specifications. t-statistics (in parentheses) are calculated using standarderrors that are heteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗

indicate statistical significance at the 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4)

Dependent variable ROIC Profit margin

Panel A: All firms

Treated × After 0.598*** 0.442* 0.839*** 0.586***(2.89) (1.91) (4.78) (3.13)

N 71,058 70,076 73,319 72,467R2 0.6412 0.6662 0.8702 0.8792

Panel B: Firms in [10B, 90B] (Discontinuity test)

Treated × After 0.809*** 0.820** 0.497* 0.491*(2.58) (2.35) (1.91) (1.85)

N 32,134 31,071 31,151 30,135R2 0.6744 0.7073 0.8983 0.9102

Firm FE Yes Yes Yes YesYear FE Yes No Yes NoIndustry × Year FE No Yes No Yes

59

Table A5Robustness of Treatment Effects: Controlling for Firm Characteristics

In this table we report the robustness results of difference-in-differences regressions regarding thetreatment effects of the tax reform while controlling for various firm characteristics including thedistance-to-the-equity-threshold, i.e. shareholders’ equity minus 50 billion wons. All variablesare defined in Table A9. We include firm and industry-year fixed effects, and firm characteristicsas control variables in the specifications. t-statistics (in parentheses) are calculated usingstandard errors that are heteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗,∗∗ , and ∗ indicate statistical significance at the 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4)

Dependent variable ∆Cash/assets Payout Wage increase Investment

Treated × After -0.737*** 0.289*** 0.074** 1.566***(-3.64) (4.89) (2.12) (6.06)

Equity - 50 billion wons 0.000** 0.000*** 0.000 0.000***(2.23) (3.40) (0.52) (4.39)

Size 5.063*** 0.032 0.568*** 9.030***(24.48) (0.61) (14.12) (28.00)

CF 0.128*** 0.017*** 0.020*** 0.135***(15.87) (7.90) (10.82) (13.13)

Debt 0.045*** 0.001 0.000 0.082***(13.92) (1.09) (0.53) (14.44)

Cash 1.078*** 0.012*** 0.005*** -0.092***(99.37) (4.39) (2.87) (-10.81)

Equity - 50 billion wons × After -0.000 -0.000 -0.000 0.000(-0.03) (-1.16) (-0.79) (0.16)

Size × After 0.057 -0.062*** 0.010 -1.044***(0.88) (-3.30) (0.75) (-10.51)

CF × After -0.070*** 0.004 -0.007*** -0.062***(-8.01) (1.60) (-3.75) (-5.75)

Debt × After -0.013*** -0.001** -0.003*** -0.033***(-5.19) (-2.15) (-5.23) (-8.91)

Cash × After -0.179*** 0.002 -0.001 0.017**(-17.39) (0.92) (-0.64) (2.26)

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes Yes

N 70,517 70,611 68,340 64,862R2 0.6148 0.6488 0.4463 0.4790

60

Table

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61

Table A7Placebo Tests on the Role of Crisis Mentality

Represented in panels A and B, respectively, are the results of panel and cross-sectional regres-sions on the cross-sectional differences across firms regarding the treatment and value effects.In each panel we report the results from two separate specifications: 1) we first split the ef-fects based on whether a firm operates in an industry featuring above-median external financedependence (HighEFD) while restricting the sample to firms established after the 1997 Asianfinancial crisis; 2) we also split the effects depending on whether a firm or a CEO was op-erating in a below-median EFD industry during the crisis (LowEFDcrisis) while using thesample of all firms. t-statistics (in parentheses) are calculated using standard errors that areheteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statis-tical significance at the 1%, 5%, and 10% levels, respectively.

Panel A: Treatment effects and crisis mentality

(1) (2) (3) (4)

Dependent variable ∆Cash/assets Payout Wage increase Investment

Sample Firms established post-crisis

Treated × After -0.713 0.256** 0.180*** 0.302(-1.64) (2.48) (3.49) (0.64)

HighEFD × After 3.663 0.682 -0.043 -8.673(1.33) (1.06) (-1.13) (-1.53)

Treated × After × HighEFD 0.487 0.043 0.028 0.841(0.87) (0.28) (0.34) (0.89)

N 37,753 38,065 35,984 35,242R2 0.2796 0.6407 0.4839 0.4551

Sample All firms

Treated × After -0.323 0.232*** 0.166*** 0.671***(-1.58) (4.60) (5.57) (2.81)

LowEFDcrisis × After 0.291 -0.005 0.208*** 0.779***(1.42) (-0.11) (5.59) (3.26)

Treated × After × LowEFDcrisis 0.072 -0.077 -0.060 -0.209(0.22) (-0.87) (-1.15) (-0.55)

N 70,082 70,431 68,137 66,928R2 0.2452 0.6457 0.4366 0.4153

Firm FE Yes Yes Yes YesIndustry × Year FE Yes Yes Yes Yes

62

Panel B: Value implications and crisis mentality

(1) (2)

Dependent variable CARproposal+CARpassage (-1 to +1 days)

SampleFirms established post-crisis

Chaebol + Non-chaebol Non-chaebol only

Treated 0.022* 0.022*(1.96) (1.81)

HighEFD -0.006 -0.009(-0.23) (-0.34)

Treated × HighEFD -0.019 -0.017(-1.05) (-0.88)

N 391 357R2 0.3417 0.3534

SampleAll firms

Chaebol + Non-chaebol Non-chaebol only

Treated 0.024*** 0.021***(3.85) (3.29)

LowEFDcrisis 0.005 0.005(0.55) (0.49)

Treated × LowEFDcrisis -0.013 -0.014(-1.30) (-1.42)

N 1,451 1,236R2 0.2329 0.2480

Industry FE Yes Yes

63

Table A8Crisis Mentality, Governance, and Pre-reform Cash Levels

In this table we report the results of cross-sectional regressions of the pre-reform level ofcash on (CrisisMemory) (Panel A), and governance index (Panel B), controlling for firmsize and earnings. t-statistics (in parentheses) are calculated using standard errors that areheteroskedasticity-robust and clustered by firm or chaebol -group. ∗∗∗, ∗∗ , and ∗ indicate statis-tical significance at the 1%, 5%, and 10% levels, respectively.

Panel A: Crisis mentality and pre-reform cash

Dependent variable Pre-cash/assets

CrisisMemory 0.781***(4.92)

Size -0.023(-0.42)

Earnings 0.254***(26.40)

Constant 6.426***(4.74)

N 18,135R2 0.0687

Panel B: Governance and pre-reform cash

Dependent variable Pre-cash/assets

High-G -1.188**(-2.39)

Size -0.634***(-2.73)

Earnings 0.180***(3.96)

Constant 23.483***(3.62)

N 637R2 0.0425

64

Table A9Variable Definitions

Treated An indicator variable that equals one if a firm belongsto the treatment group, i.e. either shareholders equityis greater than or equal to 50 billion Korean wons or thefirm belongs to a chaebol group.

After An indicator variable that equals one for year = 2015 or2016.

1{Equity ≥ 50 billion} A indicator variable equal to one if a firm’s shareholders’equity is greater than or equal to 50 billion Korean wons.

Chaebol An indicator variable that equals one if a firm belongsto a chaebol group.

∆Cash/assets [Cash(t) - cash(t-1)]/total assets(t-1)×100.

Payout (Cash dividend(t) + max(purchase of stock(t), treasurystock(t) - treasury stock(t-1)))/total assets(t-1)×100.

Dividend Cash dividend(t)/total assets(t-1)×100.

Repurchase max(purchase of stock(t), treasury stock(t) - treasurystock(t-1))/total assets(t-1)×100.

Investment [Tangible asset(t) - tangible asset(t-1) + deprecia-tion(t)]/total assets(t-1)×100.

Investment in land [Land(t) - land(t-1)]/total assets(t-1)×100.

Investment in building [Building(t) - building(t-1)]/total assets(t-1)×100.

Investment in equipment [Equipment(t) - equipment(t-1)]/total assets(t-1)×100.

Wage increase [Wage(t) - wage(t-1)]/total assets(t-1)×100.

Equity - 50 billion wons Shareholders’ equity - 50 billion Korean wons.

Earnings Net income/total assets×100.

Size Ln(total assets).

Debt Total debts/total assets ×100.

Cash/assets Cash/total assets ×100.

65

G-index Corporate governance score provided by the Korea Cor-porate Governance Service (KCGS). The KCGS scores(using integers) each of four aspects: 1) shareholderrights protections, ranging between 0 and 81; 2) boardoperations, ranging between 0 and 69; 3) monitoring or-ganization operations, ranging between 0 and 43; and 4)transparency in disclosures, ranging between 0 and 47.The four scores are then added together to obtain thetotal governance score.

ROIC EBITDA/Total invested capital = (sales - COGS -SG&A + depreciation + amortization)/(total debts +shareholder’s equity - cash)×100.

Profit margin (Sales - COGS)/sales×100.

PD in 2yrs Measure of the probability of default within two years,developed by the Risk Management Institute of the Na-tional University of Singapore (NUS RMI).

PD in 3yrs Measure of the probability of default within three years,developed by the Risk Management Institute of the Na-tional University of Singapore (NUS RMI).

CARproposal + CARpassage The sum of cumulative abnormal returns (-1 to +1 days)around the proposal of the law by the Korean govern-ment on August 6, 2014 and cumulative abnormal re-turns around the passage of the law by the NationalAssembly on December 2, 2014.

66