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Can Staggered Boards Improve Value? Evidence from the Massachusetts Natural Experiment
Robert Daines Shelley Xin Li Charles C.Y. Wang
Working Paper 16-105
Working Paper 16-105
Copyright © 2016, 2018 by Robert Daines, Shelley Xin Li, and Charles C.Y. Wang
Working papers are in draft form. This working paper is distributed for purposes of comment and discussion only. It may not be reproduced without permission of the copyright holder. Copies of working papers are available from the author.
Can Staggered Boards Improve Value? Evidence from the Massachusetts Natural Experiment
Robert Daines Stanford Law School
Shelley Xin Li University of Southern California
Charles C.Y. Wang Harvard Business School
Can Staggered Boards Improve Value?
Evidence from the Massachusetts Natural Experiment
Robert DainesStanford Law School
Shelley Xin LiUniversity of Southern California
Charles C.Y. Wang∗
Harvard Business School
October 2018
Abstract
We study the effect of staggered boards (SBs) on managers’ behavior and on long-run firmvalue using a natural experiment: a 1990 law that imposed a SB on all firms incorporated inMassachusetts. We find that the law led to an increase in Tobin’s Q, increased investmentin capital expenditure and R&D, more patents, less earnings management and higher ROA.These effects are concentrated at innovating firms—those firms that are early-life-cycle orengage in R&D spending—and especially at those facing Wall Street scrutiny. Collectively,the evidence suggests that early-life-cycle firms facing high information asymmetries benefitfrom staggered boards, in part because managers make more valuable long-term investmentsand reduce myopic behavior.
Keywords: Staggered board; entrenchment; life-cycle; Tobin’s Q; investments; profitabilityJEL: G18, G34, K22
∗First version: September 2015. Daines ([email protected]) is the Pritzker Professor of Law and Busi-ness at Stanford Law School and Professor of Finance (courtesy) at the Graduate School of Business. Li([email protected]) is an Assistant Professor at the USC Marshall School of Business. Wang([email protected]) is the Glenn and Mary Jane Creamer Associate Professor of Business Administra-tion at Harvard Business School. For helpful comments and suggestions, we are grateful to Renee Adams, YakovAmihud, Lucian Bebchuk, Sanjeev Bhojraj, Ryan Buell, Amanda Convery (GM conference discussant), RafaelCopat (FARS discussant), Fabrizio Ferri, Joseph Gerakos (Dartmouth discussant), Ron Gilson, Jeff Gordon, OliverHart, Paul Healy, Dan Ho, William Johnson, Marcel Kahan, Bob Kaplan, Louis Kaplow, Daniel Malter, GrantMcQueen, Lynn Paine, Krishna Palepu, Mark Roe, Tatiana Sandino, Holger Spamann, and Pian Shu, and toworkshop participants at the Cornell Johnson School of Management; the 2016 FARS conference; Yale School ofManagement; London Business School; Harvard Law School; Stanford GSB; Stanford Law School; the AmericanLaw and Economics Association Annual Meeting; the George Mason Conference on Investor Protection, CorporateGovernance, and Fraud Prevention; the 2016 Global Corporate Governance Colloquium; the Tsinghua InternationalCorporate Governance Conference; the Dartmouth Accounting Research Conference; Harvard Law, Economics, andOrganization Seminar; and Brigham Young University. We thank Natasha Dodge, Marc Fagin, Yiming Qian, KyleThomas, and Raaj Zutshi for excellent research assistance.
1 Introduction
No corporate-governance topic has been more heavily debated in recent years than the
impact of staggered (or “classified”) boards (SBs). SBs are considered the most important—
and some argue the only meaningful—common defense against hostile takeovers (Daines
and Klausner, 2001; Bebchuk, Coates, and Subramanian, 2002b; Klausner, 2013; Catan and
Kahan, 2016).1 No hostile bidder has ever taken over a firm protected by a staggered board
if directors opposed the merger; SBs allow incumbent directors to resist the will of even a
majority of shareholders and to delay changes of control for several years. To understand
the effects of insulating managers from the market for corporate control, therefore, one must
understand the effects of staggered boards. This paper provides such evidence in a quasi-
experimental setting by estimating the causal effects of SBs on firm value and managerial
behavior, including investment and reporting decisions.
Understanding the effects of staggered boards is important to understanding the effects
of managerial entrenchment. A large body of work examines the effect of takeover defenses
by exploiting the variation in state-level (e.g., Bertrand, 2004), or specific firm-level anti-
takeover provisions (e.g., such as poison pills, Bhojraj, Sengupta, and Zhang, 2017), or
composite indexes formed using both types of provisions (e.g., Gompers, Ishii, and Metrick,
2003). However, legal scholars have recently challenged the legal, institutional, and empirical
basis of these findings (e.g., Coates IV, 2000; Klausner, 2013; Catan and Kahan, 2016). For
these reasons, our study focuses on staggered boards, the most important variation in firms’
exposure to the market for corporate control.
Understanding the effects of staggered boards is especially important in light of investors’
growing opposition and the resulting trend of declassification. The Council of Institutional
Investors, major institutional investors (e.g., American Funds, BlackRock, CalPERS, Fi-
1Dual class common shares can provide nearly complete insulation from shareholder pressure, but arerelatively rare (Gompers, Ishii, and Metrick, 2010)
1
delity, TIAA-CREF, and Vanguard), and the two leading proxy advisors (ISS and Glass
Lewis) have all adopted voting policies opposing staggered boards. Shareholder activists
often press management to abolish the practice of staggered boards, and investors typically
vote to eliminate them when given the chance: shareholder proposals to de-stagger boards
have won more than 80% of votes cast in recent years. As a result, the number of Standard
& Poor 500 (S&P 500) companies with staggered boards has declined by 83%, from 300 in
the year 2000 to 50 in 2017.
Opponents argue that staggered boards harm shareholders by insulating directors and
managers from the beneficial disciplinary forces of shareholder control—leading to such
agency problems as shirking and empire building (a position known as “the entrenchment
view”) (Manne, 1965). SBs can also be used by self-interested agents to block acquisition
attempts (Easterbrook and Fischel, 1981) that would benefit shareholders (Grossman and
Hart, 1980). A body of empirical research generally supports this view.2
By contrast, supporters of SBs argue that directors (and under their supervision, man-
agers) can make better investment and other decisions when they are protected from share-
holder oversight.3 Directors have superior information about the firm’s prospects and may
rationally avoid making valuable investments if they can be ousted (or if the firm can be
taken over) before the value of those investments becomes apparent to shareholders (Stein,
1988, 1989). Because a staggered board protects the firm from takeovers in the short run
(before the value of some investments is realized), managers protected by a staggered board
2Bebchuk and Cohen (2005) document a strong and negative association between staggered boards andfirm value, measured by Tobin’s Q. A number of subsequent papers support this view: staggered boardshave been associated with lower market valuation (Guo, Kruse, and Nohel, 2008; Cohen and Wang, 2013),smaller gains to shareholders in completed takeovers (Bebchuk, Coates, and Subramanian, 2002a; Bebchuket al., 2002b), worse acquisition decisions (Masulis, Wang, and Xie, 2007), and weaker board monitoring(Faleye, 2007). See Section 3 below.
3See, for example, Wachtell Lipton Rosen & Katz, Harvard Shareholder RightsProject is Wrong, March 23, 2012, http://blogs.law.harvard.edu/corpgov/2012/03/23/
harvards-shareholder-rights-project-is-wrong/. See also Lipton and McLeod, State Law Im-plementation of The New Paradigm, September 11, 2018, https://corpgov.law.harvard.edu/2018/09/11/state-law-implementation-of-the-new-paradigm/ (calling for corporate law reforms to favor SBs).
2
can focus on creating long-run value and avoid inefficient short-termism when the value of in-
vestments is not understood by outsiders. Supporters also argue that SBs improve the firm’s
bargaining power in the event of a takeover bid; protected by a staggered board, managers
can credibly refuse a bid and bargain for more money (DeAngelo and Rice, 1983).4
The impact of SBs is an empirical question, but the intense academic and public policy
debate about staggered boards persists, in our view, because current research suffers from
four shortcomings. First, research on staggered boards is almost entirely correlational rather
than causal. It is therefore possible that the negative correlation between staggered boards
and firm value reflects selection rather than causation. Although recent research has begun
to address causation (e.g., Cremers, Litov, and Sepe, 2017; Cohen and Wang, 2013), the
credibility of the causal inference—such as the validity of the parallel-trends assumptions—
remain problematic and contested (Catan and Klausner, 2017; Amihud, Schmid, and David-
off Solomon, 2017a). Second, prior studies have largely ignored how SBs affect managerial
behavior, including investment and reporting decisions. Third, even if SBs are on average
harmful, they may be beneficial for some firms and little work has been devoted to under-
standing possible heterogeneous effects of SBs. Finally, existing work commonly fails to
clearly distinguish between SBs and other, less powerful defenses (see more detailed discus-
sion in Section 3 below).
We make four important contributions to the contentious debate on staggered boards
and managerial entrenchment. First, we provide strong causal evidence of staggered boards’
long-run impact on firm value. Our identification strategy is based on a policy shock in
Massachusetts (MA), where a state law adopted in 1990 exogenously imposed a staggered
board on MA-incorporated firms. We believe the Massachusetts law offers a natural setting to
study the long-term effects of a staggered board and therefore construct a quasi-experiment
4The insulation provided by staggered boards may also lead to greater real authority for managers, thusincreasing their initiative or incentive to acquire new information (Aghion and Tirole, 1997).
3
by comparing the value of treated firms (firms that acquired a staggered board because of the
legislation) to the value of similar control firms between 1984 and 1997. Using a difference-in-
differences (DID) design, estimates suggest that MA firms forced to adopt staggered boards
saw an average increase in Tobin’s Q of 14.3% over the next 7 years. These findings are
robust: they hold when we extend the analysis to 15 years post-legislation, when we use
the new measure of Total Q proposed by Peters and Taylor (2017), and when we control for
various time-varying firm or industry-level effects. They are also robust to the inclusion of
lagged Q or firm-fixed effects. Moreover, we provide evidence for the validity of the empirical
design, in particular the parallel-trends assumption, on which the average treatment effect
is identified. We find no evidence of differential trends in Q prior to 1990 or that our results
are driven by differential economic trends among MA firms after 1990.
Second, we contribute to the emerging literature (e.g., Johnson, Karpoff, and Yi, 2015;
Bhojraj et al., 2017) that examines the heterogeneous effects of takeover defenses on firm
value, and build on the prior work by examining staggered boards in a quasi-experimental
setting. Our evidence on Tobin’s Q suggests that SBs could be beneficial for early-life-cycle
firms that face more severe information asymmetries, because the affected firms in MA are on
average small, young, and less profitable. We find out-of-sample validation by examining the
widely used and larger database from the Investor Responsibility Research Center (IRRC).
Estimating the traditional cross-sectional Q regressions from the literature (Gompers et al.,
2003; Bebchuk and Cohen, 2005; Bebchuk, Cohen, and Ferrell, 2009; Bebchuk, Cohen, and
Wang, 2013), we find that, although the association between Tobin’s Q and staggered boards
is indeed positive and significant for early-life-cycle firms facing high levels of asymmetry,
the association is negative and significant for mature firms.
Third, we provide the first evidence of SBs’ impact on managerial behavior, including
investment decisions, earnings management, and ultimately firms’ operating performance.
Specifically, we find that managers behaved differently when protected from shareholder
4
scrutiny: after the legislation, managers invested more in capital expenditures and R&D,
secured more patents, engaged in less earnings management, and their firms improved in
profitability.
Finally, we provide an explanation for why and for whom SBs are most likely to add
value: SBs allow certain managers—at young and high-asymmetry firms—to focus on long-
run value by insulating them from market pressures. In subsample analyses, we find that the
effects of staggered boards resulting from the legislation—increased Tobin’s Q, investments,
patents, and ROA and reduced earnings management—are all concentrated at firms that
young or that invest in R&D (“innovating” firms). Moreover, these patterns are especially
pronounced at innovating firms that were covered by sell-side analysts and thus particularly
subject to Wall Street pressures.
The results documented in this paper suggest that the greater insulation afforded by
staggered boards is valuable to an important subset of firms, and are consistent with the
empirical observation that a large proportion of IPO firms—which tend to be younger and
to face greater information asymmetries—adopt staggered boards. We note, however, that
our study is unable to resolve the ongoing debate on the effect of staggered boards at the
largest and most mature public firms.
The remainder of the paper proceeds as follows. Section 2 explains why staggered boards
matter and how they regulate exposure to the market for corporate control. Section 3
examines prior research on staggered boards. Section 4 details the Massachusetts legislation
imposing staggered boards on public firms. Section 5 presents our empirical findings. Section
6 concludes.
5
2 Why Staggered Boards Are the Most Important Com-
mon Takeover Defense
A company’s board structure is either unitary (or annually elected) or staggered. Direc-
tors of unitary boards all stand for election at each annual shareholder meeting; members
of staggered boards, by contrast, belong to separate classes—typically three classes—whose
terms are staggered. Because shareholders vote on only one class of directors (one-third of
the board) each year, a change in control requires an insurgent group to win a majority of
shareholder votes in at least two consecutive annual meetings.
To understand why the staggered board is the most effective commonly-used defense
against takeovers, and why it is therefore a focus of debate, one must first understand the
nature of the poison pill. Though justifiably famous, the poison pill is a potent device only
at firms with staggered boards. Its main effect is to ensure that changes of control occur via
elections rather than via the sale of shares (Gilson and Schwartz, 2001).
A poison pill is created when a board allows certain shareholders to purchase a great deal
of newly issued stock very cheaply in the event that anyone buys a block of shares (typically
10–20%) without managers’ prior approval. If the pill is triggered, the bidder’s ownership
stake will be drastically diluted, or even rendered worthless, making an acquisition impossibly
expensive for an unapproved buyer; thus, no acquirer has ever intentionally triggered a poison
pill. As long as the pill is in place, it is an insurmountable defense against a takeover.5
All public firms either have a poison pill in place or can speedily adopt one whenever
necessary, even after an unsolicited bid is announced.6 Thus a hostile bid can succeed only
5In December 2008, Versata Enterprises triggered Selectica’s NOL poison pill. This move was not part ofa takeover contest; it was related to a commercial dispute. The Selectica pill was designed to protect a netoperating loss asset whose value depended on whether there had been a change of ownership, not to deterhostile bids.
6See, for example, the famous Unitrin case, in which the Delaware Supreme Court upheld a poison pilladopted after a tender offer was initiated.
6
if it can defeat a poison pill. Because a pill can only be canceled by the board of directors, a
bidder must either persuade incumbent directors to eliminate it or wage a proxy fight to oust
them and elect new directors who will quickly remove it and allow the takeover to proceed.
Note that a new board can also quickly eliminate any other defenses that are subject to
the board’s discretion, such as control-share, fair-price, business-combination, and super-
majority provisions (Daines and Klausner, 2001). These other discretionary defenses thus
impose no marginal cost, given that a bidder must always replace the board to eliminate a
poison pill.
In short, because directors can adopt a poison pill at any time, every hostile takeover
requires incumbents to be voted out. The pill makes elections critical: a hostile bidder must
place an attractive offer on the table and persuade shareholders to replace incumbents with a
slate of directors willing to reconsider the offer and pull the pill. A staggered board prolongs
such a change in control of the board, and this delay is risky and costly to the bidder, who
incurs up-front search and bidding costs. Incumbent managers retain control of the target
firm in the interim and may sabotage the bidder’s plans by seeking another buyer, selling
valued assets, or pursuing incompatible strategies.7
Thus, when it is easier to remove incumbent directors in a proxy fight—that is, when a
company has a unitary board—the company and its managers will be more exposed to the
market for corporate control. When it is difficult to remove incumbent directors—when the
board is staggered—managers will be insulated.
7Under a unitary board structure, incumbent directors and their defenses can be quickly removed—oftenwithin four to six weeks. If the shareholders have the power to vote by written consent, such an electioncan be held within three to four weeks. Otherwise, bidders must distribute and collect proxies, which takesroughly six weeks. An election can be held at any time during the year if shareholders can either call aspecial meeting or vote by written consent. If they can do neither, insurgents must await an annual meeting.If a board is staggered, shareholders may not call interim elections or remove incumbent directors exceptin extreme cases, such as instances of theft, fraud, or gross inefficiency and incompetence (Balotti andFinkelstein, 2008).
7
3 Prior Research on Staggered Boards
Considerable recent research has examined how managerial behavior and firm value are
affected by governance devices that protect managers from the market for corporate control
(e.g., Bertrand and Mullainathan, 2003; Gompers et al., 2003; Bebchuk et al., 2009; Cremers
et al., 2017; Bebchuk et al., 2013; Atanassov, 2013). A centerpiece of this research, and
a subject of intense ongoing debate, is the value of staggered boards. The literature on
staggered boards has developed in parallel to the literature on takeover defenses because
they are considered the most important source of variation in firms’ exposure to the market
for corporate control; thus, any theory about how insulation affects firm value or managerial
behavior must be shown through staggered boards.
Much of the empirical work on this topic appears to support the entrenchment view.
Bebchuk and Cohen (2005) documents that staggered boards are associated with lower firm
valuations, as measured by Tobin’s Q. Consistent with the entrenchment view, Masulis
et al. (2007) finds that staggered-board firms tend to make value-decreasing acquisitions;
Faleye (2007) finds that staggered boards are associated with lower CEO pay-performance
sensitivity and lower CEO performance-turnover sensitivity. Bates, Becher, and Lemmon
(2008) finds that staggered boards are associated with higher takeover premiums but lower
takeover likelihood; consistent with earlier work, it also documents a negative association
with firm valuation. Finally, the event studies of Daines (1997) and Cohen and Wang (2013)
provide evidence that investors view staggered boards as reducing shareholder value.8
Despite this evidence, debate continues to rage—in part, we believe, due to the limitations
8The evidence of Daines (1997), which studies market reactions to the passage of the Massachusetts leg-islation examined in this paper, suggests that markets were inefficient with respect to the value-implicationsof staggered boards in 1990. Consistent with this view, Bebchuk et al. (2013) shows that during the 1990smarkets learned gradually about the value-implications of insulating governance devices. The event studyof Cohen and Wang (2013) relies on two 2010 Delaware court rulings that affect the strength of staggeredboards at a subset of Delaware-incorporated firms; their effects are local to a subsample of Delaware firms,which are in general different from non-Delaware firms, e.g., larger in size and with higher Q (Daines, 2001).
8
of existing research evidence. First, nearly all empirical research on staggered boards is
correlational and lacks a clean strategy for identifying causal effects. Second, much of this
research focuses on the effect of staggered boards on Tobin’s Q, and does not examine effects
on managerial behavior, which are important for understanding the causal mechanisms of
staggered boards. Third, much of this research has focused on average effects on the firm
value of the larger and more mature firms that are covered by the Investor Responsibility
Research Center (IRRC), and relatively little is known about the heterogeneous effects of
staggered boards. Fourth, studies often lump SBs—which likely matter most—together with
takeover defenses that likely do not (see more discussion below).
Recent papers challenging the entrenchment view, for example Ge, Tanlu, and Zhang
(2016) and Cremers et al. (2017) who study the consequences of de-staggering, and the sub-
sequent challenge to their work (e.g., Catan and Klausner, 2017; Amihud et al., 2017a), have
further fueled the debate. For example, Catan and Klausner (2017) argues that the Cremers
et al. (2017) findings are spurious because of the failure of the parallel-trends identification
assumption on which their inferences rely. More generally, both Catan and Klausner (2017)
and Amihud et al. (2017a) argue that the self-selection of firms that choose to de-stagger
muddies the causal interpretation of empirical patterns associated with these events.
This ongoing debate highlights the need for an analysis of SBs in a quasi-experimental
setting that could shed light on how SBs affect firm value and managerial behavior, including
an examination of the identifying assumptions and causal mechanisms. Our study fills this
need. Our findings also contribute evidence on the the heterogeneous effects of staggered
boards, suggesting they are valuable for firms that are early in their life cycles and thus face
greater information asymmetry.
Empirical evidence on staggered boards is particularly important in the long-standing
academic inquiry about the efficacy of insulating managers from the market for corporate con-
trol, in light of the recent criticisms of the existing empirical literature. For example, a large
9
body of literature has examined these issues by exploiting state-level anti-takeover statutes
(e.g., Garvey and Hanka, 1999; Bertrand and Mullainathan, 2003; Giroud and Mueller,
2010; Atanassov, 2013). However, the findings from this work have been called into ques-
tion recently: for example, Catan and Kahan (2016) argues that the anti-takeover statutes
exploited in this literature are not economically important in the U.S. legal-institutional en-
vironment. Others have exploited the variation in specific firm-level defenses, such as poison
pills (Malatesta and Walkling, 1988; Ryngaert, 1988; Comment and Schwert, 1995; Bhojraj
et al., 2017).9 However, Coates IV (2000) and Catan and Kahan (2016) point out the diffi-
culty of interpreting empirical results based on the observed variation in poison pills, given
that all public firms are implicitly protected by a “shadow” poison pill. Finally, other schol-
ars have attempted to exploits anti-takeover indexes that sum the number of anti-takeover
provisions adopted by the firm (e.g., Gompers et al., 2003; Johnson et al., 2015). This work
too has come under question, as scholars (e.g., Klausner, 2013) noted that much of the vari-
ation in these indexes is meaningless in event of a takeover. These recent criticisms suggest
that, despite many years of empirical investigation in this area, much more work is required
to build a solid understanding of the effects of insulating managers. We do so in this paper
by exploiting the most important variation in firms’ exposure to the market for corporate
control—staggered boards.
In short, there is good reason to think that SBs are the only common important takeover
defense and source of variation in regulating a firm’s exposure to the market for corporate
control. And the Massachusetts’s legislation imposing a SB on public firms is, in our view,
the best setting for studying the effect of this important governance device.
9Bhojraj et al. (2017) study the effects on Tobin’s Q of a number of anti-takeover measures at largeDelaware firms (using the IRRC), and argue that R&D-intensive firms benefit from such protection. Inter-estingly, their main results on Q are based on exploiting the variation in poison pills and the E-Index—thussubject to the critique of Coates IV (2000), Klausner (2013), and Catan and Kahan (2016)—but not instaggered boards.
10
4 The Massachusetts Legislation
On March 16, 1990, a large British industrial firm, BTR P.L.C., made a hostile tender
offer for the shares of Norton Company, a Massachusetts manufacturer of sandpaper, indus-
trial abrasives, and ceramics. The offer was good news for Norton shareholders: BTR’s $75
all-cash offer represented a 50% premium over the company’s share price one month earlier
and was well above its 52-week high of $60. Because Norton was protected by a poison pill,
BTR also launched a proxy fight to remove Norton’s incumbent directors and install its own
nominees, who could then (if they chose) dismantle Norton’s defenses and consummate the
takeover.
Norton’s managers and employees, and Massachusetts legislators, were less enthusiastic.
Norton managers mobilized employees and local politicians with claims that a takeover could
prompt layoffs and cuts in R&D spending, or reduce the firm’s charitable giving. The op-
position even took on a nationalistic flavor. The Boston Globe denounced “a surprise dawn
attack on one of the oldest manufacturing concerns in Massachusetts” (Boston Globe, March
17, 1990). The New York Times reported that Massachusetts Governor Michael Dukakis
“compared BTR’s tender offer to the British invasion of America during the Revolutionary
War, explaining that it was ‘another attempt by a foreign power to interfere with our ability
to shape our own [destiny]’” (New York Times, May 27, 1990: 11). Other politicians decried
this “second British invasion” and joined Dukakis in vowing to protect the “good, solid Mas-
sachusetts company” from being “victimized” or “devoured” by the “the foreign acquiror”
(UPI, March 19; Boston Globe, April 9). Norton employees even burned the Union Jack at
demonstrations outside local government offices (Reuters, April 12: 46); others sang “God
Bless America.”
Massachusetts politicians expressed “mounting concern” about foreign takeovers of “criti-
cally positioned US companies” (Financial Times, April 20: 40). Because Norton also made
11
ceramic parts used in the aerospace industry, they argued, the firm’s independence was
important to U.S. national security; they petitioned the federal government, on national-
security grounds, to stop the impending takeover.
Fearing the prospect that shareholders would oust incumbent board members at the
upcoming annual meeting, Norton managers sought help from the state legislature. With
the aid of the law firm that had invented the poison pill, Wachtell, Lipton, Rosen & Katz,
Norton’s managers and their allies proposed legislation that would impose a staggered board
on all Massachusetts firms. A staggered board would prevent BTR from gaining a majority
of the board seats in the next election, and would give managers additional time to seek
alternatives. The proposed legislation, MA House Bill 5556, provided that a board, once
staggered, could opt out of that structure at its discretion. But this opt-out offered share-
holders little leeway. Once protected by a staggered board, directors would have incentives
to retain that protection. Moreover, a board’s decision to opt out would not be credible
because it was easily reversible: a board that voted to opt out of staggering was always free
to opt back in later on, even after receiving a hostile bid (as one firm in our sample did).
10 Shareholders were not allowed to vote on a board’s initial decision about whether to opt
out of the bill’s coverage. Moreover, although shareholders could eventually vote to opt out,
they were not allowed to do so for two years; even then, they would need a super-majority
vote. (We found no firms whose shareholders succeeded at opting out.)
Because the proposed law would change the balance of power between shareholders and
managers at MA firms, it was decried by institutional investors as “an unprecedented assault
on the most fundamental right of shareholders, the right to elect a board to represent their
interests” (UPI, April 17). Some commentators even questioned whether the legislation was
constitutional (Bainbridge, 1992).
10See, for example, https://dealbook.nytimes.com/2010/11/10/behind-sanofis-letter-to-genzyme/.
12
In spite of warnings from so-called “New York” investors that they would invest in firms
in other states if the law passed (Boston Globe, April 9), it was rushed through committees
with remarkable speed. On April 17, in an emergency session attended by only “a handful
of representatives,” the bill was passed by both the House and the Senate (New York Times,
May 27, 1990: 11). Norton managers had thus secured, via lobbying, a takeover defense that
shareholders would not have granted.
The next day, in the presence of cheering Norton employees, Governor Dukakis signed
the bill and praised the firm’s victory in a second “War of Independence” (Reuters, April
19). At the signing ceremony, “Norton chairman John Nelson, who was occasionally close
to tears, said he was grateful for the bill because Norton and other state companies will no
longer ‘be vulnerable to the one-two punch of a simultaneous last-minute tender offer and
proxy fight”’ (Boston Globe, April 19: 49). Less than two weeks after winning a war of
independence against a foreign power, Norton managers agreed to an acquisition at a higher
price by the French conglomerate Compagnie de Saint-Gobain; the French apparently posed
a less serious threat to national security, and thus once again helped Massachusetts repel a
British invasion.
This legislation exogenously imposed a staggered board on MA-incorporated firms with
unitary boards. The next section describes our use of these events as a quasi-experiment,
comparing the value of treated firms (MA-incorporated firms without staggered boards prior
to the legislation) to that of control firms (non-MA-incorporated firms without staggered
boards prior to the legislation) to study the impact of a staggered board.
In theory, this law may have harmed some firms and benefited other firms, even in
equilibrium. The vast majority of the affected firms went public prior to 1985, before poison
pills were invented, when staggered boards did not affect control battles (as discussed in
Section 2, the poison pill and the SB are effective only in combination). By 1990, pills had
been accepted by Delaware courts and authorized by the Massachusetts legislature, making
13
staggered boards an important defense for the first time. Given these legal changes, what was
optimal for Massachusetts firms at the IPO—whether to adopt a staggered board—may not
have been optimal in 1990. Moreover, as the law governing takeovers changed dramatically,
we might expect investors to learn the impact of SBs in the era of poison pills only over
time. For these reasons, we believe the Massachusetts law offers a natural setting to study
the long-term effects of a staggered board. The next section details our empirical design and
findings.
5 Empirical Results
5.1 Sample Selection and Research Design
To investigate the long-run impact of staggered boards, our main empirical analyses ex-
amine the average effect of the legislation on the value of affected firms, i.e., MA-incorporated
firms whose boards were staggered due to the state law (treatment firms). To estimate such
an effect, we match the affected firms with a set of similar non-MA-incorporated firms with-
out staggered boards (control firms). Our identification strategy relies on the assumption
that a firm’s decision whether to incorporate in Massachusetts (typically made years earlier)
is unrelated to the effect of a staggered board on firm value and managerial behavior.11
We first identify a broad set of potential treatment firms by hand-collecting MA-incorporated
firms with valid observations in the CRSP-Compustat Merged (CCM) database around the
date of the legislation. Specifically, we look for firms with annual filings both before and
after the legislation, and exclude firms that had already signed merger agreements or REITs
due to their unique governance structure. We require proxies to be available for 1989 or
11GICS industry groupings have been shown to explain the cross-sectional variations in stock returns,financial ratios, and valuation multiples better than traditional industry classifications, like the SIC andNAICS codes (Bhojraj, Lee, and Oler, 2003).
14
1990, obtained from either Lexis Nexis or Compact Disclosure, to determine whether a given
firm had a staggered board prior to the legislation. This initial hand collection resulted in a
potential treatment sample of 67 MA-incorporated firms that did not have staggered boards
prior to April 1990. From this sample, we eliminate 5 firms that had reincorporated by 1997
(the end of our sample period) or for which the most recent incorporation information is
unavailable; we also eliminate one firm with missing values for total assets.12 Finally, we
also eliminate 4 firms that had dual-class shares, resulting in a final sample of 57 treatment
firms, for which we obtain from CCM all available financial data for the period 19841997.
We manually verify that the firms were affected by the legislation, and find no firms in our
sample whose shareholders opted out of the legislation.13
We follow similar steps to identify a set of potential non-MA-incorporated non-staggered
control firms: we require them to have valid observations in CCM around the date of legis-
lation, to have proxies available for 1989 or 1990, and to have a valid state of incorporation.
We filter out firms with staggered boards in 1990 and firms incorporated in Delaware, whose
unique legal environment might prompt a different selection of firms to incorporate there.14
From this pool we construct a matched control sample by matching, for each treatment
firm, the two firms within a given 2-digit Global Industry Classification (GICS2) industry
that are closest (in Mahalanobis distance) in terms of the following firm characteristics: pre-
1990 mean total assets, pre-1990 mean book-to-market ratio, and firm age as of 1990.15 The
resulting control sample consists of 114 non-MA-incorporated non-staggered firms, for which
12Applying these filters to the MA non-treated firms (i.e., those with staggered boards) results in a finalsample of 32. Our results are robust to the inclusion of re-incorporation firms.
13We do find firms whose boards opted out of the legislation, but such firms are considered treated becausetheir boards can opt back in at their discretion. As explained in the prior section, MA-incorporated firmswhose shareholders did not opt out of the legislation are either explicitly or implicitly protected by a staggeredboard, much like the implicit protection afforded by a poison pill, irrespective of whether a pill is explicitlyin place. Indeed, we found at least one firm (TCC) whose board originally opted out of staggering, but lateropted back in when faced with a takeover attempt.
14In general, firms incorporate either in their home state or in Delaware. Firms that select Delaware tendto be significantly larger and more likely to engage in M&A transactions (Daines, 2001).
15Our main findings are qualitatively similar when matched to the closest GICS2 peer.
15
all available financial data are obtained from CCM for the years 1984 to 1997.
5.2 Summary Statistics
Table 1 reports summary statistics on the characteristics—size (total assets), age, book-
to-market, Tobin’s Q, return on assets (ROA), leverage, and a proxy for information asymme-
try16—and investments of treated firms and their matched controls during the pre-treatment
period, 1984–1990. Columns 1 and 2 report the mean values of control and treatment firms
respectively; the mean differences (i.e., difference between the first two columns) and t-
statistics are reported in columns 3 and 4. Overall, the treated and matched control firms
are statistically indistinguishable at the mean for each of the background characteristics ex-
amined. Most notably, the treated and matched control firms are virtually identical in their
mean Tobin’s Q (1.565 for the matched controls and 1.609 for the treated firms).17
Relative to the IRRC sample of firms in 1990, the average treated firm in our sample
is small and young, faces greater information asymmetry, and is less profitable in terms
of ROA. Column 5 reports the percentile ranks of the treated-firm means relative to the
population of firms included in the IRRC, the set of firms on which much prior work on
staggered boards and governance has been based (e.g.,Gompers et al., 2003; Bebchuk and
Cohen, 2005; Masulis et al., 2007; Bebchuk et al., 2009, 2013). The average firm has total
assets approximately equivalent to the 19th percentile of the IRRC sample, faces information
asymmetry greater than 99.8% of the IRRC sample, and is older than only 22.6% of the
IRRC firms. Thus the treatment effects estimated in this study pertain to firms earlier in
their life cycles and facing greater information asymmetry than the larger and more mature
16We use the Amihud illiquidity ratio as a measure of information asymmetry. This measure is the absolutevalue of the daily return-to-volume ratio and is computed over the first three months of 1990 for those firmswith at least 2 positive and 2 negative return dates and with at least 10 total valid return observations.
17In untabulated results, we also find that the control and treated firms’ median values for each of thesefirm characteristics are statistically indistinguishable from each other; again, Tobin’s Q is virtually identicalat the median (1.32 for treatment firms and 1.28 for their matched control firms).
16
firms covered by the IRRC.
5.3 The Effect of the Massachusetts Legislation on Tobin’s Q
Following prior literature, our first analysis focus on the impact of staggered boards on
Tobin’s Q (e.g., Gompers et al., 2003; Bebchuk and Cohen, 2005; Cremers et al., 2017).
Figure 1 compares the rolling-three-year averages of the mean Tobin’s Q of firms that were
affected by the legislation (Treat) and their matched control firms (Control). Consistent with
the comparison of pre-period background characteristics in Table 1, Figure 1 shows that our
matched control firms exhibit trends that resemble the pre-period trends of treatment firms
in Tobin’s Q: the two groups exhibit very similar evolution in Q, lending credence to the
parallel-trends assumption necessary for inference. After the imposition of staggered boards
on MA-incorporated firms in 1990, however, treatment firms have higher Tobin’s Q values
than control firms, a difference that grows and stabilizes by the mid 1990s.
Moving to multivariate regression analysis, Table 2 reports our baseline estimates of
the average treatment effects on the MA-treated firms using difference-in-differences (DID)
specifications. Our empirical tests focus on the 14-year period surrounding the 1990 Mas-
sachusetts legislation: seven years in the pre-treatment period (1984–1990) and seven years
in the post-treatment period (1991–1997).18 The dependent variable of interest is log of
Tobin’s Q (tobin’s q). As argued in Amihud, Schmid, and Davidoff Solomon (2017b), log of
Q is desirable because of the strong positive skewness in Tobin’s Q. Moreover, this choice
facilitates interpretation of our estimated effects in terms of the percent change in Q. Fi-
nally, since we are exploiting a state-level legal change, to account for arbitrary time-series
18We analyze a seven-year post-legislation period for several reasons. First, we are interested in the long-run effects of staggered boards on firm value. Second, it may have taken some time for managers to adjusttheir behavior after the passage of the legislation and for market values to respond. Third, we wanted toavoid examining a window that ends at the height of the dot-com bubble (e.g., a ten-year post-legislationperiod), which may be correlated with the relationship between firm value and governance characteristicsCore, Guay, and Rusticus (2006). Thus we chose 1997 as the end of our sample period. Our results aresimilar if we extend the sample period to 20 years (from 1984 to 2004).
17
correlation within states we cluster standard errors at the state level (Bertrand, Duflo, and
Mullainathan, 2004) and also at the year level to account for across-firm correlation.19
Column 1 reports a basic specification from pooled OLS regressions of tobin’s q on a
treatment indicator (Treat), a post-legislation indicator (Post), and an interaction of the
two variables (Treat x Post). We note that neither the Treat nor the Post variable differs
significantly from 0 at the 10% level, suggesting that the treated and control firms do not
differ significantly from one another in tobin’s q during the pre-treatment period, consistent
with Table 1, and that there is not a significant post-treatment trend in tobin’s q among the
control firms. This finding implies that any effects we capture in the DID estimator—the
coefficient on Treat x Post—must be driven by changes among the MA-treated firms in the
post period.
Columns 2, 3, and 4 incrementally include control variables in estimating more robust ver-
sions of the baseline DID specification. Column 2 includes linear controls for one-year-lagged
firm characteristics, following Catan and Klausner (2017), to account for the possibility that
our matching algorithm does not adequately capture the treatment-control sample differences
that could explain the subsequent variation in Q. Our controls include firm age (age) and
one-year-lagged values of sales (sales), assets (assets), roa (roa), leverage (leverage), R&D
expense scaled by assets (r&d-to-assets), and capital expenditure scaled by assets (capex-to-
assets). Column 3 incrementally includes time-fixed effects, thus dropping the post-period
indicator (Post). Finally, column 4 includes industry-fixed effects.
Most notably, the coefficient on Treat x Post remains similar in magnitude and statistical
significance across these specifications; by contrast, the adjusted R2s of these specification
are increasing from 0.83% in the baseline DID specification of column 1 to 21.31% in the
specification of column 4, which includes time-fixed effects, industry-fixed effects, and firm-
level controls. As Oster (2017) suggests, these patterns alleviate potential concerns about
19Our results are similar when clustered at the firm and year levels.
18
omitted variable biases in our research design, and lends credence to our natural-experiment
setting.20 The next two subsections address and show in detail the robustness of these main
findings to potential additional sources of omitted variables.
Interpreting the coefficient in column 4, our main specification, MA-treated firms, expe-
rienced an on-average 14.3% improvement in Tobin’s Q due to the imposition of staggered
boards. These results suggest that among Massachusetts treated firms—early-life-cycle firms
that face considerable information asymmetry—the imposition of staggered boards increased
firm value, and could be consistent with the argument that, among such firms, staggered
boards allow managers to focus on long-run strategy and investments, whose value may not
be clear to outsiders.
5.4 Robustness Tests
This section examines the robustness of the main results. We provide empirical assess-
ments of the internal validity of the findings reported above, as well as external validation
of the conclusions we draw from the Massachusetts quasi-experiment.
5.4.1 Varying the Model Specification
Table 3 reports the results of a number of robustness tests by varying the model spec-
ification reported in Table 2, column 4. Column 1 excludes the 1989–1991 time window,
allowing for an “adjustment period” around the legal change. The treatment effect remains
positive and statistically significant, with the magnitude of the coefficient increasing slightly
to 15.76%.
20Prior studies have also included as control variables contemporaneous values of return on assets, capitalexpenditures, and investments in research and development. However, as noted by Catan and Klausner(2017), such measures are more appropriately regarded as outcome variables; thus lagged values are moreappropriate, and are included in our standard specifications. Nevertheless, we confirm in untabulated resultsthat our main results are robust to controlling for the contemporaneous values of these variables.
19
Column 2 extends the sample period to include the 20 years from 1984 to 2004. To the
extent that our documented effects are correlated with the dot-com bubble, extending the
window to 2004 (i.e., after the burst of the bubble) might attenuate the estimated treatment
effects of staggered boards. However, compared to the results in Table 2, column 4, we find
that extending our sample period to 2004 yields a treatment effect that remains statistically
significant, with the magnitude of the coefficient slightly larger at 14.75%.
We note that this effect in tobin’s q does not appear to be driven by differential attrition
among treatment and control firms. The attrition rates are similar: by 1997, our sample-end
year, 82% of the treated MA firms and 75% of control firms remain. Moreover, in unreported
results we consider a zero-investment strategy that goes long an equal-weighted portfolio of
MA treatment firms from May 1990 and goes short an equal-weighted portfolio of matched
control firms. This strategy takes into account that any delisting returns and firms that
drop out of the sample are reinvested in the market, using the CRSP value-weighted index
returns. This strategy produces a cumulative return between May 1990 and December 1997
of 320% for the long portfolio and 281% for the short portfolio, netting a 38.67% return.
These findings are consistent with our results in tobin’s q and suggest that differential sample
attrition is unlikely to drive our findings.
We next turn to the issue of potential confounders. Although our main results include
a number of firm-level controls that could drive tobin’s q, year-fixed effects (which account
for the effects of firm-invariant cross-sectional omitted variables), and industry-fixed effects
(which account for the effects of time-invariant industry-level omitted variables), we provide
a number of tests to examine the robustness of our results to various additional potential
sources of omitted-variables bias.
We begin by examining the possibility that our findings could be attributable to biases
arising from measurement errors in Tobin’s Q. Peters and Taylor (2017) proposes an alter-
native measurement of Q that accounts for firms’ investments in intangible capital, which
20
are ignored by the standard measurements of Q but called for by the economic theory. We
obtain this alternative measure from the Wharton Research Data Services, and estimate our
main specification (from Table 2), column 4, using total q as the dependent variable. In
Table 3, column 3, we estimate a statistically significant (at the 5% level), positive, and
even larger treatment effect: an on-average 42% increase in Total Q. Although it is possible
that these magnitudes could be driven by particular measurement peculiarities proposed by
Peters and Taylor (2017), our main results do not appear to be driven by differences in
intangible capital between MA-treated firms and their matched control firms.
Next, we examine the possibility that other unobserved firm-level variables could con-
found our main findings. We account for the possibility that time-invariant firm-specific
omitted variables could confound our results by using firm-fixed effects. In column 4, we
find that the estimated treatment effect remains positive and statistically significant at the
1% level even after including firm-fixed effects.
We also examine the possibility that time-varying omitted variables could confound our
results. Such confounders are extremely difficult to capture, but we examine their potential
effects in several ways. First, we approximate their effects by including a control for the
lagged dependent variable (Wooldridge, 2010). Our estimated effects, reported in column
5, remain statistically significant at the 1% level. Second, we examine whether a particular
time-varying confounder, industry-level trends, could confound results. Column 6 reports the
results from estimating our main specification but includes industry-year-fixed effects; since
these fixed effects absorb industry-fixed effects and year-fixed effects, the latter are dropped
from the regression. The estimated treatment effect remains positive and statistically signif-
icant at the 1% level, suggesting that industry-level trends are unlikely to confound our main
findings. The next subsection provides further analyses of the possibility that differential
trends applicable to both the treated firms and the control firms could confound our findings.
21
5.4.2 Assessing the Parallel-Trends Assumption
Perhaps the most important potential confounder is the possibility that, absent treat-
ment, the treated firms in MA and their matched control firms would have followed different
trends. The assumption of parallel trends is central to the identification of the average
treatment effect (on the treated firms); its violation could lead to misleading inferences. For
example, Catan and Klausner (2017) identify violation of this crucial assumption as the main
driver of the findings of Cremers et al. (2017) about the effect of staggered boards.
The parallel-trends assumption cannot be fully tested because counterfactual outcomes
after the policy change are unobservable, but we will examine this issue in two ways. First,
to assess the validity of the quasi-experimental design (Angrist and Pischke, 2008; Lech-
ner, 2011), we test for evidence of differential trends in the pre-treatment period between
the treated MA-incorporated firms and their matched controls. Differential trends in the
pre-treatment period would be inconsistent with the assumption of parallel trends post-
treatment. Table 4, columns 1 and 2, test for differential pre-treatment trends in tobin’s q
between the treatment firms and and the control firms by including in the main specification
an additional interaction term between Treat and an indicator for the several years prior
to the 1990 legislation. Column 1 uses an indicator for 1989 and 1990; column 2 uses an
indicator for the four years from 1987 to 1990. In each case, the interaction term is not sta-
tistically significant at conventional levels, suggesting that there are no differential trends in
tobin’s q between treatment and control firms leading up to 1990. These statistical findings
are consistent with Figure 1, which shows that our matched control firms exhibit similar
average trends in Q prior to 1990.
Although the treatment and control firms were similar before the legislation, in terms of
both the means in background characteristics and the trends in Q, it is still possible that
treatment firms became more valuable because of favorable economic conditions for MA
22
firms and not because staggered boards were imposed. Thus, the second way we address
the possibility of differential trends—in particular, the possibility that MA firms could have
experienced differential trends in tobin’s q after 1990—is to utilize a holdout sample of MA
firms that were not affected by the MA law (i.e., MA firms that already had staggered boards
before the 1990 legislation or that had dual-class shares). We perform a placebo test using
these MA unaffected firms and their two most closely matched control firms (i.e., non-MA
firms staggered in 1990 from the same GICS2 industry as the treatment firm and closest to it
in terms of pre-treatment mean total assets, pre-treatment mean book-to-market ratio, and
firm age in 1990). If the unaffected MA firms also became more valuable over time relative
to their matched controls, this would suggest that the main effects we document above arise
from economic conditions (i.e., differential economic trends) for MA firms that our matching
algorithm fails to account for, rather than from the MA legislation.
Table 4, columns 3 and 4, report the results of our tests following the specifications
in Table 2, columns 3 and 4. The DID coefficients of -0.0376 and -0.0362 are not only
statistically insignificant; they are also economically insignificant relative to the Table 2
estimates of 0.1427 and 0.1430. These results suggest that the main findings of Table 2 are
driven by the imposition of staggered boards and not by differential economic trends.
As an additional check, we also estimated our baseline specifications in Table 2 using a
sample that matches the affected MA firms to the two most closely matched control firms
incorporated in California. This alternative matching algorithm addresses the possibility that
the economic expansion that began in the mid-1990s affected firms incorporated in states
like Massachusetts and California, known for their high-tech firms, more similarly than firms
incorporated in other states. In untabulated results, we find that the specifications of Table
2 produce very similar results, both economically and statistically, using this alternative
sample. For example, using this sample to estimate the specification in Table 2, column 4,
we obtain a coefficient of 0.144, which is statistically significant at the 5% level.
23
Overall, the battery of tests reported in Tables 3 and 4 provide evidence on the inter-
nal validity of our quasi-experiments. Our findings on the effect of the MA legislation do
not appear to be driven by measurement errors in tobin’s q, time-invariant or firm-specific
confounders, differential industry-level or state-level trends, or other time-varying omitted
variables that could be captured by the lagged dependent variable.
5.4.3 External Validation Using IRRC
To further validate our main findings, we examine the hypothesis that staggered boards
could be beneficial for early-life-cycle firms whose investors face greater information asym-
metry by using an alternative sample of firms from the IRRC dataset. The advantage of the
IRRC is that it offers a much broader sample of firms over time, providing an opportunity
to validate our conclusions externally and to test more directly the possible heterogeneous
effects of staggered boards.21 The disadvantage of the IRRC is that, unlike our quasi-
experimental MA setting, the variation captured in the data is unlikely to be driven by ex-
ogenous shocks. Thus we rely on the traditional pooled cross-sectional regression approaches
in the governance literature (Gompers et al., 2010) and include a battery of firm-level con-
trols that could explain both Q and the presence of staggered boards (Bebchuk et al., 2009,
2013): an index of other provisions in the G-Index (Gompers et al., 2003), log of total as-
sets, log of company age, an indicator for Delaware incorporation, percent of shares owned
by insiders, square of insider ownership, return on assets, capital-expenditure-to-total-assets
ratio, and R&D-to-sales ratio.
Table 5, column 1, replicates the main findings of Bebchuk and Cohen (2005), using
the sample of IRRC firms from 1990 to 2007 following Bebchuk et al. (2013).22 We regress
21Each volume of the IRRC dataset covers 1,400 to 2,000 firms. In addition to those that belong to theS&P1500, firms considered important by the IRRC are also covered.
22Our construction of the annual cross-sections of governance data follows Bebchuk et al. (2013) (SeeSection 2.1 of their paper.) We also follow them in using IRRC data up to 2007 and in excluding the newerRiskMetrics data because the latter data are not comparable.
24
Tobin’s Q on an indicator for staggered boards (SB), and include firm controls, time-fixed
effects, and industry-fixed effects.23 On average, we find a negative and significant association
between Tobin’s Q and staggered boards in this sample of relatively large and mature firms.
Having replicated the traditional findings, we proceed to examine whether a subsample
of firms in the IRRC dataset that are earlier in their life cycles and whose investors face a
relatively high degree of information asymmetry exhibit the same cross-sectional associations.
We define as Early-Life-Cycle/High-Asymmetry those firms less than 6 years old (the median
age of our MA-incorporated firms) whose market capitalization lies in the lowest quartile of
the cross-sectional distribution, and whose information asymmetry (proxied by the Amihud
illiquidity ratio) lies in the highest quartile of the cross-sectional distribution.
Table 5, column 2, estimates the specification of column 1, but includes an indica-
tor for Early-Life-Cycle/High-Asymmetry and an interaction between SB and Early-Life-
Cycle/High-Asymmetry. We also include in our set of firm controls an additional interac-
tion term between the index of other provisions in the G-Index and Early-Life-Cycle/High-
Asymmetry. The main coefficient on SB in this regression suggests that, among the firms
that are more mature or larger, or that exhibit a lower degree of information asymmetry, the
association between Tobin’s Q remains negative and statistically significant at the 5% level.
However, for the set of early-life-cycle firms that face a relatively high degree of information
asymmetry, we find a significant positive association between SB and Tobin’s Q. Indeed,
among such firms the association is 0.2234 (0.3226–0.0992), which is statistically significant
at the 10% level, as reported in the last row of the table. For comparability to our main
results, Table 5, column 3, repeats the estimation of column 2 but uses tobin’s q as the
dependent variable. These estimates suggest that SBs are associated with 10.69% higher Q
among the Early-Life-Cycle/High-Asymmetry firms, whereas SBs are associated with 3.09%
23We use SIC2 industry codes, following Bebchuk et al. (2009), but our findings are similar using theGICS2 industry sectors employed in prior tests.
25
lower Q among larger and more mature firms.
To summarize, these results provide external validation of results and conclusions from
the MA quasi-experiment. They further suggest that the impact of a staggered board may
be different at different times in firms’ life cycles.
5.5 Exploring Possible Mechanisms
This subsection investigates how a staggered board affects managers’ behavior.
5.5.1 Effect on Innovating Firms
Supporters of staggered boards argue that takeover defenses can encourage innovation
and investment, particularly at firms whose strategies require a long time horizon to execute
and whose outside investors are likely to be less informed about the firm’s value. At such
firms, a staggered board might allow managers to invest in projects whose value becomes
clear to outsiders only in the long run and whose eventual success may require tolerance
for early failures (Manso, 2011). We therefore examine the differential impact of the MA
legislation on a subset of innovating firms, which we define as young firms and those that
invest substantially in research and development.
Table 6, column 1, reports on an expanded version of the OLS specification in Table 2,
column 4—with time- and industry-fixed effects as well as firm controls—for the subsample
of innovating treatment firms (firms that are younger than the median firm or that have
an R&D-to-sales ratio in the top quintile of the 1990 CCM population) and their matched
controls. We find that the baseline positive effects of staggered boards on Tobin’s Q are con-
centrated in the innovating firms, which experienced a 17.7% increase in firm value following
the MA legislation. In contrast, for the subsample of non-innovating firms (column 2), we
find a DID coefficient that is close to zero in magnitude and statistically indistinguishable
26
from zero.
Column 3 further investigates the subsample of innovating firms that are covered by sell-
side analysts. The insulation that staggered boards provide may be more beneficial to firms
that are subject to the pressures and earnings expectations of Wall Street analysts, which
critics assert can lead to managerial myopia (e.g., Bhojraj, Hribar, Picconi, and McInnis,
2009; Terry, 2015). Our analysis suggests that the benefits of staggering are strongest at
innovating firms that are covered by analysts; such firms experienced a 25.32% increase
in Tobin’s Q. In contrast, we find no significant effect on the subset of non-innovating or
non-covered treatment firms (column 4).
Overall, our findings are consistent with the idea that staggered boards are particularly
valuable for innovating firms, and thus much more common among them.
5.5.2 Effect on Long-Run Investments
We next examine how firms’ total investments in capital expenditures and in research
and development (Investments) were affected by the MA legislation. Table 7 reports DID
estimates using the entire sample (column 1), the subsample of innovating firms (column
2), and the subsample of innovating-and-covered firms (column 3). Note that we replace
missing values in Capital Expenditure and R&D with zeros; in all regression specifications,
indicators for missing values in capital expenditures and R&D are included.
We find that the MA legislation led to a significant increase in total investments in
capital expenditures and R&D investments within the subset of innovating and innovating-
and-covered firms that were most susceptible to the pressures of Wall Street. For the whole
sample, we estimate an 8.7% increase in total investments; moreover, we find greater ef-
fects on total investments within the subsamples of firms that exhibit the largest effects in
Tobin’s Q and that may find staggered boards most beneficial. In columns 2 and 3, our
estimates suggest that the MA legislation led to a 10.8% increase in investments among
27
innovating firms, and a 15.6% increase in investments among innovating-and-covered firms.
Both estimates are economically significant and statistically significant at the 1% level.
In addition to examining ex-ante measures of innovation, we also analyze the effect of the
legislation on patent generation, an ex-post measure of innovation.24 Table 7, columns 4-6
report DID estimates for Patents. For the entire sample of firms (column 4), we estimate a
10.1% increase in the number of patents (significant at the 1% level). Among the subsample
of innovating firms (column 5) and innovating-and-covered firms (column 6), we estimate
increases of 13% and 23.1% respectively. In both cases the estimated effects are significant
at the 1% level.25
Overall, these results suggest that the value increase that a staggered board generates is
explained, at least in part, by firms’ greater willingness to invest in growth and innovation.
Firms that relied on innovation and faced analyst pressure experienced significant growth
in total investments in capital and R&D expenditures as well as growth in patents. These
findings are consistent with the claim that, at firms that face high information asymmetries,
Wall Street scrutiny, and short-run earnings targets, staggered boards afford valuable sta-
bility and a longer-term investment horizon (Graham, Harvey, and Rajgopal, 2005; He and
Tian, 2013).
5.5.3 Effect on Earnings Management
We supplement the preceding analyses by examining whether the imposition of a stag-
gered board changed earnings-management behavior at the affected firms. To the extent
24Our patent data are from the Thomson Innovation database, which provides international patent cov-erage. We collected information on all U.S. patent applications that our treatment firms and their matchedcontrol firms had submitted between January 1, 1984, and December 31, 1997, that were ultimately granted.The significant gap between 1997 and 2015 alleviates the “truncation problem” encountered by empiricalstudies that use patent data, namely the inclusion of fewer patent applications toward the end of the sampleperiod due to the time lag between application and approval.
25These results are robust to the use of citation-weighted patents (i.e., the number of patents weighted bythe number of citations each patent received in subsequent years until 2015) as the dependent variable.
28
that a staggered board alleviates short-term capital-market pressures, we might expect the
affected MA firms to exhibit a less intense earnings management, which could also lead to
value destruction (e.g., Stein, 1989) and thus lower Q.
We use measures of accounting-based earnings management drawn from the accounting
literature. In particular, we employ versions of the “modified Jones” model (Dechow, Sloan,
and Sweeney, 1995), computed from available quarterly data for the universe of firms in
Compustat. These earnings-management measures are computed by subtracting a model-
implied estimate of non-discretionary accruals from total accruals. Following Hribar and
Collins (2002), we compute total accruals as:
TotalAccrualsi,t =IBi,t − (CFOi,t −XIDOi,t)
ASSETSi,t−1
(1)
where IB is earnings before extraordinary items, CFO is cashflow from operating activities,
XIDO is extraordinary items and discontinued operations, and ASSETSi,t−1 is lagged total
assets.
We calculate two earnings-management measures based on two standard models of non-
discretionary accruals: Modified-Jones (Dechow et al., 1995) and Modified-Jones with ROA
(Kothari, Leone, and Wasley, 2005). In each of these models, non-discretionary accruals are
modeled as a linear function of changes in revenue (REV ) less changes in accounts receivables
(REC ); gross property, plant, and equipment (PPE ); and, in the case of the Modified-Jones
with ROA, lagged operating income before depreciation (OIBDP):
E[TotalAccrualsi,t] = (2)
β0 + β11
ASSETSi,t−1
+ β2∆REVi,t −∆RECi,t
ASSETSi,t−1
+ β3PPEi,t
ASSETSi,t−1
+ β4OIBDPi,t−1
ASSETSi,t−1
,
where the coefficients of Eq., (2) are estimated by pooling observations for each three-digit
29
SIC industry with more than 30 observations. Our earnings-management measures are
obtained as the absolute value of the residuals from these estimation regressions. We refer
to these as the absolute value of discretionary accruals (|DA|).
Table 8 reports estimates from our DID specifications with firm-level controls, using
the earnings-management measures as the main dependent variables of interest. Columns
13 examine |DA| from Modified-Jones. We find that, for the entire sample and for the
subsamples of innovating and innovating-and-covered firms, there is significantly less earnings
management at MA treated firms than at their matched control firms; the effect is larger at
innovating and innovating-and-covered firms. Columns 46 examine |DA| from Modified-Jones
with ROA, and obtain similar results from all three sample cuts.
These results complement those of Tables 6 and 7. Jointly, our findings suggest that
staggered boards can improve firm value by protecting certain managers from short-term
capital-market pressures and by facilitating long-term investments in growth and innovation.
5.5.4 Effect on Return on Assets
Finally, we examine the effect of the MA legislation on return on assets. Table 9, columns
1–3, report DID estimates on roa for the full sample, the subsample of innovating firms,
and the subsample of innovating-and-covered firms. In each case we obtain a positive and
statistically significant (at the 10% level) coefficient. The magnitude of the coefficient for the
innovating firms (0.0205) is larger than that for the full sample (0.0161). For the subsample of
innovating-and-covered firms, which exhibit the largest proportional increase in Q, increases
in investments and innovation, and declines in earnings management, we also find the greatest
increase in roa (0.0335), statistically significant at the 1% level. The results are similar when
we do not use lagged roa as a control.
Our evidence thus differs from prior studies’ findings that insulating governance mech-
anisms, such as staggered boards, are associated with worse operating performance (e.g.,
30
Gompers et al., 2003; Bebchuk et al., 2013). In contrast to predictions that staggered boards
could destroy value for shareholders by prompting managers to settle for the job security that
such mechanisms afford them, our results suggest that staggered boards can be beneficial
for early-life-cycle firms that face a relatively high degree of information asymmetry.
6 Conclusion
Staggered boards remain a topic of controversy in corporate governance, fueled in part
by the conflicting results of academic research. Prior research suffers from a lack of causal
identification and a failure to focus on how staggered boards change managers’ behavior or
on such boards’ heterogeneous effects.
This study exploits a quasi-experimental setting created by a 1990 law requiring all
Massachusetts-incorporated firms to adopt staggered boards. Our evidence suggests that
staggered boards can be valuable at early-life-cycle firms whose managers contend with a
relatively high degree of information asymmetry. At such firms, staggered boards encourage
valuable investments and innovation and reduce earnings management. We find external
validation for this hypothesis using the conventional IRRC data.
These findings contribute to the academic literature and to the corporate-governance
debate by providing plausible causal identification that also sheds light on staggered boards’
causal mechanisms and heterogeneous effects. We caution, however, that our findings do
not suggest that staggered boards unambiguously improve firm value. Specifically, our work
does not suggest that staggered boards benefit larger and more mature firms.
The idea that a staggered board may be valuable at a particular stage in a firm’s life
cycle is consistent with recent findings in the corporate-governance literature (e.g., Johnson
et al., 2015). Very young firms, and those facing severe information asymmetries, are typ-
ically funded by venture capital or other private investors (Chan, 1983) and are insulated
31
from the market for corporate control. Investors do not object to staggered boards at this
early stage (Daines and Klausner, 2001), and such firms typically go public with staggered
boards. Some IPO firms even adopt more extreme protection from takeovers (e.g., dual-class
shares), though these protections typically phase out as the firm matures and its founders
leave the business. Generally speaking, not until public firms have matured do investors
oppose staggered boards and prefer to rely instead on the market for corporate control. Our
evidence suggests that, consistent with these patterns, staggered boards (and insulation from
shareholder intervention) are useful to early-life-cycle firms that face more severe information
asymmetries, and thus suggests that they might usefully be paired with sunset provisions
that phase out these powerful insulating forces as firms mature.
32
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1
1.2
1.4
1.6
1.8
2
Q
1984 1985 1986 1987 1988 1989 1990 1991 1992 1993 1994 1995 1996 1997Year
ControlTreat
Fig. 1.
Tobin’s Q, Treatment and Control FirmsThis figure compares the rolling-three-year averages of the mean annual Tobin’s Q of firmsaffected by the legislation (Treat) and their matched control firms (Control). The verticalred line indicates the year of the Massachusetts legislation, 1990.
37
Table A1.Description of Variables
This table presents definitions of variables used in our regressions. Our financial and corporate data areobtained from the CRSP-Compustat Merged database; Compustat variable names appear in square bracketsbelow; CRSP variable names appear in parentheses. Patent data are from the Thomson Innovation database.
Variable Description Calculationage Natural Logarithm of Firm Age ln(Number of years since first ob-
served PERMNO on CRSP)assets Natural Logarithm of Total Assets ln([at])Book to Market (equity [ceq] + deferred taxes and
investment credit [txditc]) / marketcap [prcc f × csho]
capex Natural logarithm of (1+CAPEX)where CAPEX is Capital Expenditure
ln([capx])
capex-to-assets Natural logarithm of the ratio ofCAPEX to Total Assets
ln([capx]/[at])
Patents Natural Logarithm of (1+ Patents)where Patents is the number of patentsapplied for by the firm that were even-tually granted
|DA| using Modified Jones Absolute Value of Discretionary Accru-als Using the Modified Jones Model
as defined in Dechow et al. (1995)and described in Eq., (2)
|DA| using Modified Joneswith ROA
Absolute Value of Discretionary Accru-als Using the Modified Jones ModelAugmented with ROA
as defined in Kothari et al. (2005)and described in Eq., (2)
Info Asymmetry Amihud illiquidity ratio Daily average of 1000000×|(ret)| /|(prc)|×(vol) from January 1 toMarch 30, 1990
Investments Natural Logarithm of (CAPEX and R&D)
ln([capx]+[xrd])
leverage Natural logarithm of Leverage ln(liabilities [lt] / total assets [at])Post Post-legislation indicator equals 1 if the fiscal year end oc-
curred after 1990R&D Natural logarithm of (1+R&D) where
R&D is Research and Development Ex-pense
ln(1+[xrd])
r&d-to-assets Natural logarithm of the ratio of R&Dto Total Assets
ln([xrd]/[at])
roa Natural Logarithm of (1+ ROA) whereROA is the Return on Assets
ln(1+((operating income before de-preciation [oibdp] − depreciation[dp]) / total assets [at]))
sales Natural Logarithm of Sales ln(sale)Tobin’s Q (total assets [at] + price [prcc c] ×
commonshare [csho] − equity [ceq]− deferred taxes [txdb]) / assets [at]
tobin’s q Natural Logarithm of Tobin’s Qtotal q Natural Logarithm of Total Q as de-
fined in Peters and Taylor (2017)Treat Treatment indicator equals 1 if the firm was MA-
incorporated without a staggeredboard prior to 1990
38
Table 1.Summary Statistics on Matched Sample
This table compares the pre-period (1984–1990) means of the characteristics of control firms (non-MA-incorporated firms withoutstaggered boards in 1990), reported in column 1; treated firms (MA-incorporated firms without staggered boards in 1990), reportedin column 2; their differences, reported in column 3; and the t-statistics associated with the differences in means, reported incolumn 4. t-statistics are computed based on cluster-robust standard errors. Column 5 reports the percentages of firms in theInvestor Responsibility Research Center (IRRC) database in 1990 with values lower than the treated sample’s pre-period mean.
(1) (2) (3) (4) (5)
Firm Characteristics Control Treated ∆ TPctileIRRC
Total Assets 320.207 376.094 55.887 0.326 19.4%Firm Age 10.279 10.738 0.459 0.358 22.6%Book to Market 0.764 0.743 -0.021 -0.358 60.6%Tobin’s Q 1.565 1.609 0.045 0.045 73.5%Return on Assets 0.057 0.071 0.014 0.995 22.3%Leverage 0.459 0.442 -0.017 -0.587 18.1%Info Asymmetry 13.065 7.006 -6.059 -1.619 99.8%R&D Expense 6.095 9.449 3.353 1.510 30.3%Capital Expenditure 21.751 35.994 14.244 0.952 33.7%
39
Table 2.Average Treatment Effect on tobin’s q
Column 1 reports OLS results of regressing tobin’s q on a treatment indicator (Treat), a post-legislationindicator (Post), and an interaction of the two variables (Treat x Post). Columns 2–4 include firm-levelcontrols, and vary depending on whether year or industry-fixed effects are included. The Post indicatoris absorbed by time-fixed effects and is not reported in such specifications. All variables are defined inTable A1. The sample period consists of the years 1984–1997. Standard errors are two-way-cluster robust,clustering at the state and year levels; they are reported in parentheses. Significance levels are indicated by∗, ∗∗, and ∗∗∗ for 10%, 5%, and 1% respectively.
(1) (2) (3) (4)Treat x Post 0.1410∗∗∗ 0.1472∗∗∗ 0.1427∗∗∗ 0.1430∗∗∗
(0.051) (0.022) (0.055) (0.055)Treat -0.0145 -0.0214 -0.0173 -0.0181
(0.052) (0.026) (0.045) (0.047)Post -0.0344 0.0274
(0.045) (0.052)age -0.0682∗∗∗ -0.0728∗∗∗ -0.0570∗∗∗
(0.024) (0.022) (0.020)Lag sales 0.0366 0.0321 0.0257
(0.039) (0.038) (0.041)Lag assets -0.0588 -0.0579 -0.0522
(0.037) (0.036) (0.039)Lag roa -0.0039 0.0034 0.0118
(0.132) (0.132) (0.124)Lag leverage -0.0771∗∗∗ -0.0622∗∗∗ -0.0444∗∗
(0.018) (0.020) (0.022)Lag r&d-to-assets 0.7853∗ 0.7264 0.6444
(0.460) (0.478) (0.435)Lag capex-to-assets 0.5525∗∗ 0.3927 0.4152
(0.257) (0.247) (0.282)Time FE No No Yes YesIndustry FE No No No YesObservations 1,862 1,862 1,862 1,862Adj R2 0.0083 0.1430 0.1849 0.2131
40
Table 3.Robustness
This table reports variants of the specification in Table 2, column 4. Column 1 excludes the years 1989–1991;column 2 includes all the years from 1984 to 2004; column 3 uses total q of Peters and Taylor (2017) as thedependent variable; column 4 includes lag tobin’s q as an additional control; column 5 includes firm-fixedeffects; and column 6 includes industry-year-fixed effects. All variables are defined in Table A1. The sampleperiod consists of the years 1984–1997. Standard errors are two-way-cluster robust, clustering at the stateand year levels; they are reported in parentheses. Significance levels are indicated by ∗, ∗∗, and ∗∗∗ for 10%,5%, and 1% respectively.
(1) (2) (3) (4) (5) (6)Exclude
1989-19911984-2004 total q
FirmFE
LaggedDep Var
Ind-YearFE
Treat x Post 0.1576∗∗ 0.1475∗∗∗ 0.4196∗∗∗ 0.1159∗∗∗ 0.0698∗∗∗ 0.1461∗∗∗
(0.063) (0.053) (0.094) (0.039) (0.026) (0.056)Treat -0.0174 -0.0352 -0.1518 -1.6609∗∗ -0.0207 -0.0141
(0.052) (0.048) (0.110) (0.670) (0.020) (0.048)age -0.0540∗∗ -0.0679∗∗∗ -0.3250∗∗∗ -0.1440∗∗ 0.0165 -0.0542∗∗
(0.021) (0.021) (0.092) (0.062) (0.013) (0.021)Lag sales 0.0252 0.0285 -0.1606∗ -0.0310 0.0124 0.0273
(0.046) (0.032) (0.097) (0.097) (0.013) (0.041)Lag assets -0.0540 -0.0348 0.1589 -0.1734∗∗ -0.0253∗ -0.0549
(0.045) (0.033) (0.105) (0.087) (0.014) (0.040)Lag roa -0.0086 -0.0067 0.3523∗ 0.0401 -0.1670∗∗ 0.0070
(0.152) (0.108) (0.213) (0.082) (0.079) (0.128)Lag leverage -0.0434∗∗ -0.0475∗∗ -0.2351∗∗ 0.0991∗ 0.0057 -0.0413∗
(0.022) (0.023) (0.103) (0.055) (0.011) (0.024)Lag r&d-to-assets 0.7827∗ 0.9710∗∗ -0.7778 0.1478 0.1574 0.6427
(0.403) (0.447) (0.989) (0.617) (0.247) (0.443)Lag capex-to-assets 0.4148∗ 0.5415∗∗ 1.3120 0.8509∗∗∗ 0.1005 0.3756
(0.233) (0.249) (0.979) (0.270) (0.130) (0.303)Lag q 0.6984∗∗∗
(0.023)Time FE Yes Yes Yes Yes Yes NoIndustry FE Yes Yes Yes No No NoObservations 1,557 2,414 1,650 1,862 1,829 1,862Adj R2 0.2247 0.2017 0.1478 0.5652 0.6138 0.2401
41
Table 4.Pre-Treatment Trends and Contemporaneous Placebo Tests
Columns 1 and 2 report OLS results from regressing tobin’s q on a treatment indicator (Treat), an interactionwith a post-legislation indicator (Treat x Post), time- and industry-fixed effects, and firm-level controls, as inTable 2, column 4. An additional interaction term of Treat with a time indicator for the periods 1989–1990and 1987–1990 is included in columns 1 and 2 to test for differential pre-treatment trends in tobin’s q.
Columns 3 and 4 report the results of OLS regressions using tobin’s q as dependent variables. The treatmentfirms are the MA-incorporated firms that already had staggered boards prior to the MA legislation; thecontrol firms are comparable non-MA firms that already had staggered boards or had dual-class shares priorto the MA legislation. Firm-level controls are included in both columns, and time- and industry-fixed effectsare included in column 4. All variables are defined in Table A1. The sample period consists of the years1984–1997. Standard errors are two-way-cluster robust, clustering at the state and year levels; they arereported in parentheses. Significance levels are indicated by ∗, ∗∗, and ∗∗∗ for 10%, 5%, and 1% respectively.
Pre-Treatment Trends Already-Staggered Firms
(1) (2) (3) (4)
Treat x Post 0.1354** 0.1560** -0.0376 -0.0362(0.059) (0.061) (0.047) (0.042)
Treat -0.0104 -0.0310 0.0076 0.0140(0.048) (0.041) (0.038) (0.033)
Treat x I[1989− 1990] -0.0222(0.044)
Treat x I[1987− 1990] 0.0200(0.035)
age -0.0571*** -0.0569*** -0.2295*** -0.1972***(0.020) (0.020) (0.029) (0.038)
Lag sales 0.0257 0.0257 0.1241*** 0.0667(0.041) (0.041) (0.041) (0.061)
Lag assets -0.0522 -0.0522 -0.0384 0.0267(0.039) (0.039) (0.042) (0.056)
Lag roa 0.0119 0.0120 -0.2116 -0.1285(0.124) (0.124) (0.316) (0.319)
Lag leverage -0.0443** -0.0444** -0.2171*** -0.1126(0.022) (0.022) (0.051) (0.078)
Lag r&d-to-assets 0.6461 0.6434 2.6504*** 2.0098***(0.435) (0.435) (0.517) (0.415)
Lag capex-to-assets 0.4119 0.4192 0.4767 0.7053(0.280) (0.281) (0.623) (0.598)
Time FE Yes Yes No YesIndustry FE Yes Yes No YesObservations 1,862 1,862 1,380 1,380Adj R2 0.1998 0.1998 0.3788 0.4356
42
Table 5.External Validity: IRRC Sample
This table reports pooled OLS regression results of Tobin’s Q (columns 1 and 2) and tobin’sq (column 3) on an indicator for staggered board (SB), an indicator for early-life-cycle/high-information-asymmetry firms (Early-Life-Cycle/High-Asymmetry), and an interaction term (SBx Early-Life-Cycle/High-Asymmetry), firm controls, and time- and industry-fixed effects. Early-Life-Cycle/High-Asymmetry firms are those less than 6 years old, whose market capitalization isin the bottom quartile, and whose Info Asymmetry is in the top quartile of the cross-sectionaldistribution. Following Bebchuk and Cohen (2005) and Bebchuk et al. (2013), firm controlsinclude an index of other provisions in the G-Index (Gompers et al., 2003), log of total assets,log of company age, an indicator for Delaware incorporation, the percentage of shares owned byinsiders, square of inside ownership, return on assets, capital-expenditure-to-total-assets ratio,and R&D-to-sales ratio. An additional interaction term between an index of other provisions inthe G-Index and Early-Life-Cycle/High-Asymmetry is also included. The last row reports, forthe specifications in columns 2 and 3, the p-value of the F-statistic that tests the null hypothesisthat the staggered-board coefficient for Early-Life-Cycle/High-Asymmetry firms is 0. Standarderrors are two-way-cluster robust, clustering at the state and year levels; they are and reported inparentheses. Significance levels are indicated by ∗, ∗∗, ∗∗∗ for 10%, 5%, and 1% respectively.
(1) (2) (3)Tobin’s Q Tobin’s Q tobin’s q
SB -0.0933∗∗ -0.0992∗∗ -0.0309∗∗
(0.039) (0.041) (0.013)Early-Life-Cycle/High-Asymmetry -0.3401 -0.1028
(0.229) (0.097)SB x Early-Life-Cycle/High-Asymmetry 0.3226∗∗ 0.1378∗∗
(0.132) (0.059)
Time FE Yes Yes YesIndustry FE Yes Yes YesFirm Controls Yes Yes YesObservations 22,389 22,389 22,389Adj R2 0.3399 0.3412 0.4632F-Test p-value NA 0.0658 0.0607
43
Table 6.Treatment Effect on tobin’s q for Subsamples
This table reports variants of the specification in Table 2, column 4, based on subsamples. Column 1 (2)reports the result estimated using the subsample of innovating (non-innovating) treatment firms and theirmatched control firms; column 3 (4) reports the result estimated using the subsample of innovating-and-covered (non-innovating or non-covered) treatment firms and their matched control firms. Innovating firmsare defined as those that are either young or R&D intensive. Young treatment firms are those firms whoseage (in 1990) is below the median of the CRSP-Compustat Merged database universe; R&D intensive firmsare those whose R&D-to-sales ratio (in 1990) is in the top quintile of the CRSP-Compustat Merged databaseuniverse. Covered treatment firms are those with analyst coverage in at least one of the four quarters priorto the legislation. All variables are defined in Table A1. The sample period consists of the years 1984–1997.Standard errors are two-way-cluster robust, clustering at the state and year levels; they are and reported inparentheses. Significance levels are indicated by ∗, ∗∗, ∗∗∗ for 10%, 5%, and 1% respectively.
(1) (2) (3) (4)
Innovating Non-InnovatingInnovating
andCovered
Non-Innovatingor
Non-CoveredTreat x Post 0.1770∗∗ 0.0435 0.2532∗∗∗ 0.0583
(0.072) (0.050) (0.090) (0.045)Treat -0.0289 0.0292 0.0279 -0.0123
(0.058) (0.029) (0.069) (0.040)age -0.0443 -0.0229 -0.0078 -0.0529
(0.028) (0.062) (0.048) (0.040)Lag sales 0.0739 -0.0113 -0.0218 0.0159
(0.062) (0.029) (0.108) (0.038)Lag assets -0.1111∗ -0.0083 -0.0182 -0.0539
(0.063) (0.029) (0.106) (0.036)Lag roa -0.0195 0.3769 -0.1295 0.0720
(0.133) (0.236) (0.322) (0.111)Lag leverage -0.0506∗ 0.0137 -0.0580∗∗ -0.0110
(0.029) (0.046) (0.027) (0.037)Lag r&d-to-assets 0.6093 0.0950 1.3367∗∗ 0.5259
(0.464) (0.520) (0.591) (0.502)Lag capex-to-assets 0.3248 0.9969∗∗ -0.0743 1.0036∗∗∗
(0.308) (0.478) (0.374) (0.289)Time FE Yes Yes Yes YesIndustry FE Yes Yes Yes YesObservations 1,435 427 818 1,044Adj R2 0.1881 0.3382 0.2334 0.2541
44
Table 7.Investments and Innovation
This table reports the results of OLS regressions using Investments (columns 1–3) and Patents (columns4–6) as the dependent variables. Columns 1 and 4 report the results estimated using the full sample offirms and their matched control firms; columns 2 and 5 report the results estimated using the subsampleof innovating treatment firms and their matched control firms; columns 3 and 6 report the results usingthe subsample of innovating-and-covered treatment firms and their matched control firms. Innovating firmsare defined as those that are either young or R&D-intensive. Young treatment firms are those whose age(in 1990) is below the median of the CRSP-Compustat Merged database universe; R&D intensive firms arethose whose R&D-to-sales ratio (in 1990) is in the top quintile of the CRSP-Compustat Merged databaseuniverse. Covered treatment firms are those with analyst coverage in at least one of the four quarters priorto the legislation. All variables are defined in Table A1.The sample period consists of the years 1984–1997.Standard errors are two-way-cluster robust, clustering at the state and year levels; they are and reported inparentheses. Significance levels are indicated by ∗, ∗∗, and ∗∗∗ for 10%, 5%, and 1% respectively.
Investments Patents
(1) (2) (3) (4) (5) (6)
All InnovatingInnovating
andCovered
All InnovatingInnovating
andCovered
Treat x Post 0.087*** 0.108*** 0.156*** 0.101*** 0.130*** 0.231***(0.03) (0.04) (0.05) (0.03) (0.04) (0.07)
Treat 0.003 0.016 0.030 0.185** 0.257** 0.271(0.04) (0.04) (0.06) (0.08) (0.10) (0.19)
age -0.050** -0.034 0.034 -0.019 0.078* 0.010(0.02) (0.02) (0.03) (0.04) (0.04) (0.05)
Lag sales -0.006 0.024 -0.005 0.085 -0.012 0.102(0.06) (0.09) (0.11) (0.05) (0.07) (0.12)
Lag assets 0.745*** 0.695*** 0.739*** 0.157*** 0.295*** 0.247(0.05) (0.07) (0.08) (0.05) (0.08) (0.16)
Lag roa 0.311*** 0.295*** 0.477*** -0.154 -0.248** -0.384(0.10) (0.10) (0.15) (0.10) (0.10) (0.26)
Lag leverage -0.044 -0.017 0.001 -0.111*** -0.111** -0.220**(0.04) (0.03) (0.07) (0.04) (0.06) (0.11)
Lag r&d-to-assets 4.157*** 3.930*** 5.087*** 1.250** 1.207** 1.465(0.29) (0.46) (0.69) (0.53) (0.60) (1.13)
Lag capex-to-assets 5.104*** 4.793*** 4.591*** 0.764** 0.673 1.527*(0.45) (0.46) (0.44) (0.35) (0.41) (0.79)
Time FE Yes Yes Yes Yes Yes YesIndustry FE Yes Yes Yes Yes Yes YesObservations 1,799 1,400 783 1,862 1,435 818Adj R2 0.8862 0.8665 0.8998 0.3354 0.3851 0.4489
45
Table 8.Earnings Management
This table reports the results of OLS regressions using the absolute value of discretionary accruals, estimatedusing the Modified-Jones model (columns 1–3) or the Modified-Jones model augmented with ROA (columns4–6), as the dependent variables. Columns 1 and 4 report the results estimated using the full sample offirms and their matched control firms; columns 2 and 5 report the results estimated using the subsampleof innovating treatment firms and their matched control firms; columns 3 and 6 report the results usingthe subsample of innovating-and-covered treatment firms and their matched control firms. Innovating firmsare defined as those that are either young or R&D intensive. Young treatment firms are those whose age(in 1990) is below the median of the CRSP-Compustat Merged database universe; R&D-intensive firms arethose whose R&D-to-sales ratio (in 1990) is in the top quintile of the CRSP-Compustat Merged databaseuniverse. Covered treatment firms are those with analyst coverage in at least one of the four quarters priorto the legislation. All variables are defined in Table A1. The sample period consists of the years 1984–1997.Standard errors are two-way-cluster robust, clustering at the state and year levels; they are reported inparentheses. Significance levels are indicated by ∗, ∗∗, and ∗∗∗ for 10%, 5%, and 1% respectively.
|DA| using Modified Jones |DA| Modified-Jones with ROA
(1) (2) (3) (4) (5) (6)
All InnovatingInnovating
andCovered
All InnovatingInnovating
andCovered
Treat x Post -0.0393*** -0.0451*** -0.0677*** -0.0281*** -0.0326*** -0.0340**(0.011) (0.013) (0.012) (0.009) (0.009) (0.013)
Treat 0.0191** 0.0152* 0.0301*** 0.0159** 0.0087 0.0131(0.008) (0.009) (0.011) (0.008) (0.009) (0.009)
age -0.0071 -0.0050 0.0001 -0.0058 -0.0023 -0.0075(0.008) (0.007) (0.011) (0.008) (0.004) (0.012)
Lag sales 0.0341*** 0.0513** 0.0824*** 0.0222** 0.0291** 0.0496**(0.012) (0.020) (0.026) (0.010) (0.014) (0.022)
Lag assets -0.0518*** -0.0703*** -0.1022*** -0.0361*** -0.0443*** -0.0579***(0.012) (0.021) (0.030) (0.010) (0.014) (0.020)
Lag roa -0.0718 -0.0764 -0.1914*** -0.0324 -0.0316 -0.1743***(0.047) (0.050) (0.067) (0.045) (0.048) (0.065)
Lag leverage 0.0277*** 0.0236** 0.0264* 0.0248*** 0.0221*** 0.0091(0.009) (0.011) (0.015) (0.007) (0.008) (0.012)
Lag r&d-to-assets -0.0009 -0.0270 -0.0734 0.0866** 0.0861 0.1003(0.103) (0.121) (0.139) (0.042) (0.065) (0.116)
Lag capex-to-assets -0.1966** -0.2242** -0.3360** -0.1571** -0.1861** -0.1932**(0.078) (0.087) (0.138) (0.073) (0.083) (0.092)
Time FE Yes Yes Yes Yes Yes YesIndustry FE Yes Yes Yes Yes Yes YesObservations 1,841 1,428 818 1,841 1,428 818Adj R2 0.3911 0.3789 0.4470 0.3485 0.3321 0.4097
46
Table 9.Return on Assets
This table reports the results of OLS regressions of roa on Treat, an interaction of Treat and Post, firm-and industry-fixed effects, and firm-level controls. Column 1 reports the results estimated using the fullsample of firms and their matched control firms; column 2 reports the results estimated using the subsampleof innovating treatment firms and their matched control firms; column 3 reports the results using thesubsample of innovating-and-covered treatment firms and their matched control firms. Innovating firmsare defined as those that are either young or R&D-intensive. Young treatment firms are those whose age(in 1990) is below the median of the CRSP-Compustat Merged database universe; R&D-intensive firms arethose whose R&D-to-sales ratio (in 1990) is in the top quintile of the CRSP-Compustat Merged databaseuniverse. Covered treatment firms are those with analyst coverage in at least one of the four quarters priorto the legislation. All variables are defined in Table A1. The sample period consists of the years 1984–1997.Standard errors are two-way-cluster robust, clustering at the state and year levels; they are reported inparentheses. Significance levels are indicated by ∗, ∗∗, and ∗∗∗ for 10%, 5%, and 1% respectively.
(1) (2) (3)
All InnovatingInnovating
andCovered
Treat x Post 0.0161* 0.0205* 0.0335***(0.009) (0.011) (0.012)
Treat 0.0014 -0.0024 0.0070(0.002) (.) (0.006)
age 0.0071 0.0097 0.0134(0.006) (0.007) (0.009)
Lag sales 0.0477*** 0.0506*** 0.0476(0.007) (0.011) (0.030)
Lag assets -0.0385*** -0.0389*** -0.0462*(0.008) (0.013) (0.026)
Lag roa 0.3078*** 0.2964*** 0.4717***(0.054) (0.057) (0.092)
Lag leverage -0.0019 -0.0028 0.0051(0.010) (0.010) (0.012)
Lag r&d-to-assets -0.1305 -0.1010 -0.0634(0.086) (0.100) (0.161)
Lag capex-to-assets 0.1066* 0.1273** 0.0744(0.060) (0.064) (0.162)
Time FE Yes Yes YesIndustry FE Yes Yes YesObservations 1,836 1,413 805Adj R2 0.3325 0.3244 0.4393
47
