the dark side of analyst coverage

7/28/2019 The dark side of analyst coverage

1/53Electronic copy available at: http://ssrn.com/abstract=1959125

The dark side of analyst coverage: The case of innovation

Jie (Jack) He

Terry College of BusinessUniversity of Georgia

[email protected]

(706) 542-9076

Xuan Tian

Kelley School of BusinessIndiana [email protected]

(812) 855-3420

This version: February, 2013

* We are grateful for helpful comments from an anonymous referee, Shai Bernstein, Utpal Bhattacharya, MattBillett, Daniel Bradley, Yingying Dong, Alex Edmans, Stuart Gillan, Jean Helwege, Harrison Hong, David Hsu,Paul Irvine, Pab Jotikasthira, Sreeni Kamma, Robert Kieschnick, Josh Lerner, Jim Linck, Harold Mulherin, JeffNetter, Bradley Paye, Avri Ravid, Bill Schwert (the editor), Pian Shu, Tao Shu, Krishnamurthy Subramanian, YanXu, Scott Yonker, Xiaoyun Yu, and conference participants at the 2012 Kauffman-RCFS Entrepreneurial Financeand Innovation conference, the 2012 Northwestern University Conference on Entrepreneurship and Innovation, the2012 China International Conference in Finance, the 2012 Financial Management Association Meetings, andseminar participants at Indiana University, the University of Georgia, and the University of South Carolina. Wethank Mike Flores, Yifei Mao, and Zhong Zhang for their competent research assistance. We remain responsible forany remaining errors or omissions.



The dark side of analyst coverage: The case of innovation

ABSTRACT

We examine the effects of financial analysts on the real economy in the case ofinnovation. Our baseline results show that firms covered by a larger number of analysts generatefewer patents and patents with lower impact. To establish causality, we use a difference-in-differences approach that relies on the variation generated by multiple exogenous shocks toanalyst coverage, as well as an instrumental variable approach. Our identification strategiessuggest a negative causal effect of analyst coverage on firm innovation. The evidence is

consistent with the hypothesis that analysts exert too much pressure on managers to meet short-term goals, impeding firms investment in long-term innovative projects. We further discusspossible underlying mechanisms through which analysts impede innovation and show that thereis a residual effect of analysts on innovation even after controlling for these mechanisms. Ourpaper offers novel evidence on a previously under-explored adverse consequence of analystcoverage its hindrance to firm innovation.

Keywords: innovation, analyst coverage, patents, citations, managerial myopia

JEL classification: G24, O31, G34



1

1. Introduction

How does a nations financial sector affect the real economy? While a highly developed

financial market improves the efficiency of capital allocation and thus fosters the growth of

innovation, it also gives rise to various adverse externalities such as short-termism, opportunistic

behavior, and rent-seeking, which impair firms incentives to invest and innovate. Understanding

the role of stock market in motivating firm innovation is an important research question, both

because innovation is a crucial driver of economic growth (Solow, 1957) and because publicly

traded equity represents one of the most important sources of external capital to facilitate firm

investment. A thorough investigation into this issue entails a comprehensive analysis of how

various unique ingredients of the stock market affect firms incentives to engage in innovative

activities.

In this paper, we focus on one key ingredient of the public equity market, namely,financial analysts. Specifically, we study whether financial analysts, an active market

intermediary and gatekeeper, encourage or impede firm innovation. Although there has been a

growing literature linking various market and firm characteristics to innovation, little is known

about the roles played by financial analysts, who not only produce information for the firms they

cover but also set external performance benchmarks such as earnings forecasts or stock

recommendations. This topic is of particular interest to policy makers as analyst behavior in the

U.S. is heavily regulated and altered by securities laws and regulations over time.1 The objective

of this paper is to provide the first empirical study that examines how financial analysts causally

affect firm innovation, using a rich set of identification strategies.

Motivating innovation is a challenge for most firms. Unlike routine tasks, such as mass

production and marketing, innovation involves a long process that is full of uncertainty and with

a high probability of failure (Holmstrom, 1989). Firms investing more heavily in innovative

projects might be forced to make only partial disclosure and subject to a larger degree of

information asymmetry (Bhattacharya and Ritter, 1983), are more likely to be undervalued by

equity holders, and have a greater exposure to hostile takeovers (Stein, 1988). To protect firms

against such expropriation, managers tend to invest less in innovation (in many cases sub-

optimally) and put more effort in routine tasks that offer quicker and more certain returns,

leading up to a typical managerial myopia problem. A potential solution to the distortion of

1 Recent regulatory changes include the 2000 Regulation Fair Disclosure (Reg FD), the 2002 National Associationof Securities Dealers (NASD) Rule 2711, and the 2003 Global Research Analyst Settlement, among others.


4/53

2

investments in innovation due to information asymmetry is financial analysts. Financial analysts

collect information from various sources, evaluate the current performance of firms that they

follow, make forecasts about their future prospects, and make buy/hold/sell recommendations to

current and potential investors. Existing literature suggests that analysts help to reduce

information asymmetry along a variety of dimensions (see a detailed discussion of this literature

in Section 2). If analysts accurately convey the information of a firms innovative activities to

other financial market participants (especially its investors) and help them understand the real

value of these long-term investments, then the management of the firm would not refrain from

engaging in value-enhancing innovation activities. Therefore, our first hypothesis, the

information hypothesis, argues that financial analysts, by reducing information asymmetry of

innovative firms, mitigate managerial myopia and encourage firm innovation.2

An alternative hypothesis makes an opposite empirical prediction. Financial analysts areoften accused of creating excessive pressure on managers and exacerbating managerial myopia.

Manso (2011) shows that tolerance for failure is necessary for effectively motivating and

nurturing innovation.3

However, the least thing financial analysts can offer to innovative firms is

to tolerate short-term failures, as their job is to forecast near-term earnings and make

corresponding stock recommendations.4

Whenever they expect the firms to experience a drop in

near-term earnings, they would revise their forecasts downward and make unfavorable

recommendations, leading to negative market reactions and potential disciplinary actions against

the managers (see, e.g., Brennan, Jegadeesh, and Swaminathan, 1993; Hong, Lim, and Stein,

2000). More importantly, just as Jensen and Fuller (2002) argued, firm managers often conform

to excessively aggressive analysts earnings forecasts and accept external expectations as targets

2 Note that moral hazard models such as Grossman and Hart (1988) and Harris and Raviv (1988) may generate thesame prediction as the information hypothesis but through a different channel. These models suggest that managerswho are not properly monitored will shirk or tend to invest sub-optimally in routine tasks to enjoy private benefits. Ifmanagers derive private benefits from shirking on long-term innovation projects (as suggested by the abovetheories) and financial analysts serve as an external governance mechanism (Yu, 2008), the above moral hazardargument also implies that financial analysts encourage corporate innovation.3

Recent empirical research providing supporting evidence for the implications of the failure tolerance theoryincludes Ederer and Manso (2011), who conduct a controlled laboratory experiment, Azoulay, Graff Zivin, andManso (2011), who exploit key differences among funding streams within the academic life science, and Tian andWang (2011), who examine the effect of venture capital investors attitude towards failure on firm innovation.4 Consistent with the notion that analysts tend to focus more on shorter-term firm performance (as opposed tolonger-term performance) when issuing stock recommendations, previous literature has found that stockrecommendations depend heavily on analysts expectations of firms future earnings but do not account fully for theinformation contained in firms long-term implied cost of equity (see, e.g., Aggarwal, Mishra, and Wilson, 2010),and that the informativeness of stock recommendations mainly derives from their revisions (changes) but not theirlevels (see, e.g., Francis and Soffer, 1997).


5/53

3

to achieve. In a survey of 401 U.S. Chief Financial Officers (CFOs), Graham, Harvey, and

Rajgopal (2005) show that the majority of CFOs in the survey declared that they are willing to

sacrifice long-term firm value to meet the desired short-term earnings targets due to their own

wealth, career, and external reputation concerns.5

Innovation ranks high on the list that managers

consider sacrificing due to its nature of being a type of high-risk, long-term, and unpredictable

investment that may not generate immediate financial returns. Taken together, the alternative

hypothesis we propose, the pressure hypothesis, argues that financial analysts, by imposing

short-term pressure on managers, exacerbate managerial myopia and impede firm innovation.

We test the above two competing hypotheses by examining whether financial analysts

encourage or impede firm innovation. We make use of observable innovation outputs (i.e., the

number of patents granted to a firm and the number of future citations received by each patent)

to assess the success of long-term investment in innovation and intangible assets that havetraditionally been difficult to observe. Our use of patenting to capture firms innovativeness has

now become standard in the innovation literature (e.g., Aghion et al., 2005; Nanda and Rhodes-

Kropf, 2012; Seru, 2011).

Our baseline tests show a negative relation between analyst coverage (measured by the

number of analysts following the firm) and innovation outputs. The results are robust to using

alternative subsamples, alternative measures of analyst coverage and innovation, alternative

econometric models, and alternative empirical specifications.

While the baseline results are consistent with the pressure hypothesis, an important

concern is that analyst coverage is likely to be endogenous. Unobservable firm heterogeneity

correlated with both analyst coverage and innovation could bias the results (i.e., the omitted

variable concern), and firms with low innovation potential may attract more analyst coverage

(i.e., the reverse causality concern). To establish causality, we use two different identification

strategies and perform a rich set of robustness tests.

Our first identification strategy is to rely on two plausible quasi-natural experiments,

brokerage closures (Kelly and Ljungqvist, 2011, 2012) and brokerage mergers (Hong and

Kacperczyk, 2010), which directly affect firms analyst coverage but are exogenous to their

innovation productivity. Using a difference-in-differences (DiD) approach, we show that an

5 The adverse consequences for managers to miss the consensus earnings forecasts include significant declines in thefirms stock prices (Bartov, Givoly, and Hayn, 2002), reduced CEO bonuses (Matsunaga and Park, 2001), and anincreased probability of management turnover (Mergenthaler, Rajgopal, and Srinivasan, 2011).


6/53

4

exogenous decrease in analyst coverage leads to a larger relative increase in innovation output

for the treatment group (i.e., firms whose analyst coverage goes down due to brokerage closures

or mergers) compared to that for the control group (i.e., similar firms whose analyst coverage

does not change) in subsequent years. Further, the negative effect of analyst coverage on

innovation is stronger for firms covered by fewer analysts. The DiD results continue to hold

under numerous robustness checks using alternative matching criteria, alternative thresholds for

the number of patents or analysts, alternative subsamples, and alternative matching methods. A

key advantage of this identification strategy is that there are multiple shocks that affect different

firms at exogenously different times, which avoids a common identification difficulty faced by

studies with a single shock, namely, the existence of potential omitted variables coinciding with

the shock that directly affect innovation.

Our second identification strategy is to construct an instrumental variable, expectedcoverage, which is first introduced in Yu (2008), and to use the two-stage least-squares (2SLS)

analysis. The 2SLS results confirm the negative effect of analyst coverage on innovation and,

more importantly, reveal the direction of potential bias if endogeneity in analyst coverage is not

appropriately controlled for. Overall, our identification tests suggest that analysts have a negative

causal effect on firm innovation.

In summary, our evidence is consistent with the hypothesis that analysts exert pressure on

managers to meet near-term earnings targets. In response to such pressure, managers boost

current earnings by sacrificing long-term investment in innovative projects that are highly risky

and slow in generating revenues.

In the final part of our paper, we attempt to identify possible underlying economic

mechanisms through which analysts impede innovation. First of all, we consider different types

of institutional ownership. We find that an exogenous reduction in analyst coverage leads to an

increase in equity ownership by dedicated institutional investors but a decrease in ownership by

non-dedicated institutional investors. To the extent that dedicated institutional investors

encourage firm innovation to a significantly greater degree than non-dedicated ones (Aghion,

Van Reenen, and Zingales, 2013), analyst coverage could impede innovation by attracting more

non-dedicated institutional investors than dedicated ones. Next, we find that an exogenous

decrease in analyst coverage reduces a firms exposure to takeover attempts. Since Stein (1988)

suggests that a firms reduced exposure to takeovers would encourage its innovative activities,


7/53

5

takeover exposure could be another underlying economic mechanism. We also argue that stock

illiquidity and the difficulty of implementing accrual-based earnings management techniques

could be two additional possible underlying mechanisms. We then show that there exists a

residual (i.e., direct) effect of analyst coverage on innovation even after controlling for the above

identified economic mechanisms.

The rest of the paper is organized as follows. Section 2 discusses the related literature.

Section 3 describes sample selection and reports summary statistics. Section 4 presents the

baseline results. Section 5 addresses identification issues. Section 6 discusses underlying

economic mechanisms. Section 7 provides alternative interpretations, discusses caveats of the

study, and concludes the paper.

2. Relation to the existing literature

Our paper contributes to three strands of literature. First, our paper is related to the

emerging literature on finance and innovation. Holmstrom (1989) shows that innovation

activities may mix poorly with routine activities in an organization. Robinson (2008) shows how

firms with limited internal ability to innovate can form strategic alliances to pursue innovative

projects. Manso (2011) suggests that managerial contracts that tolerate failure in the short run

and reward for success in the long run are best suited for motivating innovation. The model in

Ferreira, Manso, and Silva (2012) argues that it is optimal for firms to be private (literally having

no analyst coverage) when they want to innovate. Empirical evidence shows that various

economic environment and firm characteristics affect managerial incentives of investing in

innovation. Specifically, a larger institutional ownership (Aghion, Van Reenen, and Zingales,

2013), corporate venture capital (Chemmanur, Loutskina, and Tian, 2011), private instead of

public equity ownership (Bernstein, 2012), and investors greater tolerance for failure (Tian and

Wang 2011) alter managerial incentives and hence help motivate managers to focus more on

long-term innovation activities.6 However, existing studies have largely ignored the roles played

by financial analysts in motivating innovation. Our paper contributes to this line of research by

filling in this gap.

6 Other studies have examined the effects of product market competition, bankruptcy laws, general marketconditions, leveraged buyouts, firm boundaries, and stock liquidity on innovation (e.g., Aghion et al., 2005; Acharyaand Subramanian, 2009; Fang, Tian, and Tice, 2012; Nanda and Rhodes-Kropf, 2011, 2012; Lerner, Sorensen, andStromberg, 2011; Seru, 2011).


8/53

6

Our paper also builds on the empirical literature studying managerial myopia. This

literature has shown evidence consistent with managerial myopia in publicly traded firms.7 For

example, Asker, Farre-Mensa, and Ljungqvist (2011) find that publicly listed firms exhibit

myopia: compared to unlisted firms, they invest less and their investment levels are less sensitive

to changes in investment opportunities. Our paper complements their findings by providing a

possible reason, namely, the pressure imposed by financial analysts, for why listed firms are

more myopic than unlisted firms. Bushee (1998) shows that managers are more likely to cut

R&D expenses in response to an earnings decline when a very large proportion of institutional

ownership comes from short-term investors. Our paper instead focuses on the effect of financial

analysts on managerial myopia.

Finally, our paper adds to the large literature debating on the effects of financial analysts.

On the positive side, existing literature generally finds that analysts help reduce informationasymmetry, have superior predictive abilities, and serve as external monitors to firm managers

(e.g., Brennan and Subrahmanyam, 1995; Hong, Lim, and Stein, 2000; Yu, 2008; Ellul and

Panayides, 2009), and therefore affect firms investment and financing decisions, stock prices,

liquidity, and valuation (e.g., Bradley, Jordan, and Ritter, 2003; Irvine, 2003; Chang, Dasgupta,

and Hilary, 2006; Derrien and Kecskes, 2011; Kelly and Ljungqvist, 2011). On the negative side,

studies show that analysts give overly optimistic long-term earnings growth forecasts (e.g.,

Dechow, Hutton, and Sloan, 2000) and near-term earnings forecasts (e.g., Dugar and Nathan,

1995; Hong and Kubik 2003). Moreover, such over-optimism has adverse consequences such as

the misvaluation of a firms equity around its corporate financing activities (see, e.g., Bradshaw,

Richardson, and Sloan, 2006). Further, Graham, Harvey, and Rajgopal (2005), in a survey study,

find that analysts impose too much pressure on managers and induce myopic behavior. The

strategy literature has also provided some empirical support to the above survey finding, using

anecdotal evidence and small-sample analysis.8

By using a comprehensive and large sample of

U.S. public firms and a rich set of identification strategies, our paper contributes to the above

7 Stein (1989) shows that managerial myopia is present even in a rational capital market, and the degree of myopicbehavior will be influenced by capital market incentives that determine the extent to which managers care aboutshort-term prices relative to long-term values.8 Benner (2010) shows that analysts tend to ignore firms strategies of incorporating new technologies. Benner andRanganathan (2012) find that negative analyst recommendations are associated with reductions in firm capitalexpenditure and R&D during times of technological change. However, it is hard to draw causal inferences from theabove two papers as they fail to address the identification issue. Moreover, their sample sizes are small (fewer than200 firms) and are limited to only a couple of industries.


9/53

7

debate by studying the causal effect of analysts on innovation, a special long-term investment in

intangible assets, and thus offers novel evidence on a previously under-explored adverse effect of

analysts.

Our paper is also related to Barth, Kasznik, and McNichols (2001) who make an

important attempt to link analyst coverage to firm intangible assets. They show that analyst

coverage is positively associated with firm R&D expenditures. Our paper advances this line of

inquiry in two important dimensions. First, using both a DiD approach that relies on multiple

exogenous shocks to analyst coverage and an instrumental variable approach, our identification

strategies allow us to evaluate the causal effect of analyst coverage on firm innovation (as

opposed to a partial correlation documented by their study). Second, instead of analyzing R&D

expenditures, we focus on patenting activity. Patenting is an innovation output variable, which

encompasses the successful usage of all(both observable and unobservable) innovation inputs.In contrast, R&D expenditures only capture one particular observable quantitative input, as

argued by Aghion, Van Reenen, and Zingales (2013), and are sensitive to accounting norms such

as whether it should be capitalized or expensed, as argued by Acharya and Subramanian (2009).

In addition, information on R&D expenditures reported in Compustat is quite unreliable, which

may introduce a significant measurement error problem.9

3. Sample selection and summary statistics

3.1 Sample selection

The sample examined in this paper includes U.S. listed firms during the period of 1993-

2005. We collect firm-year patent and citation information from the latest version of the National

Bureau of Economic Research (NBER) Patent Citation database. Analyst coverage data are

obtained from the Institutional Brokers Estimate Systems (I/B/E/S) database. To calculate the

control variables, we collect financial statement items from Compustat, institutional holdings

data from Thomsons CDA/Spectrum database (form 13F), intraday trades and quotes for

constructing stock illiquidity measures from the Trade and Quotes (TAQ) database, stock price

information from CRSP, and institutional investor classification data from Brian Bushees

9 More than 50% of firms do not report R&D expenditures in their financial statements in the Compustat database.However, the fact that a firm does not report its R&D expenditures does not necessarily mean that the firm is notengaging in innovation activities. It may do so out of strategic concerns. Replacing missing values of R&Dexpenditures with zeros, a common practice in the existing literature, introduces additional noise that may bias theestimated effect of analyst coverage on innovation measured by R&D expenditures.


10/53

8

website (http://acct3.wharton.upenn.edu/faculty/bushee). Finally, we obtain brokerage house

merger information from the Securities Data Company (SDC) Mergers and Acquisitions

database. The sample selection process ends up with 25,860 firm-year observations used in our

baseline regressions.

3.2 Variable measurement

3.2.1 Measuring innovation

We extract innovation output data and construct our main innovation variables from the

latest version of the NBER Patent Citation database (see Hall, Jaffe, and Trajtenberg (2001) for

more details). This database contains patent and citation information from 1976 to 2006. It

provides annual information on patent assignee names, the number of patents, the number of

citations received by each patent, a patents application year as well as its grant year, etc.

To gauge a firms innovation productivity, we construct two measures. The first measure

is a firms total number of patent applications filed in a given year that are eventually granted.

The reason for using a patents application year rather than its grant year is that previous studies

(such as Griliches, Pakes, and Hall, 1988) have shown that the former is superior in capturing the

actual time of innovation. However, despite its straightforward intuition and easy

implementation, the above measure is unable to distinguish groundbreaking innovations from

incremental technological discoveries. Hence, to assess a patents impact more precisely, we

construct the second measure of firm innovation productivity by counting the total number of

non-self citations each patent receives in subsequent years. Given a firms size and its innovation

inputs, the number of patents captures its overall innovation productivity and the number of non-

self citations per patent captures the significance and quality of its innovation output. To account

for the long-term nature of innovation process, our empirical tests relate firm characteristics in

the current year to the above two measures of innovation productivity three years ahead.

We adjust the two measures of innovation to address the truncation problems associated

with the NBER patent database. The first truncation problem arises as the patents appear in the

database only after they are granted. We actually observe a gradual decrease in the number of

patent applications that are eventually granted as we approach the last few years in the sample

period. This is because the lag between a patents application year and its grant year is

significant (about two years on average) and many patent applications filed during these years

were still under review and had not been granted by 2006. To adjust the truncation bias in patent


11/53

9

counts, we supplement the NBER database with the Harvard Business School (HBS) patent

database, which contains patents granted through 2010. To the extent that the patent application

outcomes have been announced by 2010 for the patents filed by 2006, this approach largely

mitigates the patent truncation concern.10

The second type of truncation problem involves

citation counts. Patents tend to receive citations over a long period of time (e.g., 50 years), but

we observe at best the citations received up to 2006. Following Hall, Jaffe, and Trajtenberg

(2001, 2005), the truncation in citation counts is corrected by estimating the shape of the

citation-lag distribution.11,12

Neither the NBER nor the HBS patent database is likely to be affected by the

survivorship bias. As long as a patent application is eventually granted, it is attributed to the

applying firm at the time of application even if the firm later gets acquired or goes bankrupt.

Moreover, since patent citations are attributed to a patent rather than the applying firm, the patentgranted to a firm that later gets acquired or goes bankrupt can still keep receiving citations long

after the firm disappears.

We merge the patent data with the analyst coverage sample. Following the innovation

literature, we set the patent and citation counts to zero for firms without available patent or

citation information from the NBER or the HBS patent database. The distribution of patent

grants in our final sample is right skewed, with its median at zero. Due to the right skewness of

patent counts and citations per patent, we winsorize these variables at the 99th percentiles and

then use the natural logarithm of patent counts (LnPatent) and the natural logarithm of the

number of non-self citations per patent (LnCitePat) as the main innovation measures in our

analysis. To avoid losing firm-year observations with zero patents or zero citations per patent, we

add one to the actual values when calculating the natural logarithm.

3.2.2 Measuring analyst coverage and other control variables

We obtain analyst information from the I/B/E/S database. For each fiscal year of a firm,

10 For robustness, we follow Hall, Jaffe, and Trajtenberg (2001, 2005) to correct for the truncation bias in patentcounts using the weight factors computed from the application-grant empirical distribution. The results arequalitatively similar.11 Note that the HBS patent database does not help too much to correct for the truncation bias in citation counts,because the HBS database only contains patent information up to 2010 while patents filed in our sample period maykeep receiving citations over a long period of time that is well beyond 2010.12 In an untabulated analysis, we construct an alternative proxy for patent quality that is based on the total number ofnon-self citations a patent received in the first N (N = 0, 1, 2, 3) years after it is granted. All our results are robust tousing this alternative patent quality proxy.


12/53

10

we take the average of the 12 monthly numbers of earnings forecasts given by the summary file

and treat that as a raw measure of analyst coverage (Coverage). This measure relies on the fact

that most analysts following a firm issue at least one earnings forecast for that firm during the

year before its fiscal year ending date and that a majority of them issue at most one earnings

forecast in each month.13 We then take natural logarithm of (one plus) this raw measure to

construct our main measure of analyst coverage (LnCoverage).

Following the innovation literature, we control for a vector of firm and industry

characteristics that may affect a firms future innovation productivity. We compute all variables

for firm i over its fiscal year t. The controls include firm size (the natural logarithm of book

value assets), firm age (the number of years since IPO date), investments in intangible assets

(R&D expenditures over total assets), profitability (ROA), asset tangibility (net PPE scaled by

total assets), leverage, capital expenditures, growth opportunities (Tobins Q), financialconstraints (the Kaplan and Zingales (1997) five-variable KZ index), industry concentration (the

Herfindahl index based on sales), institutional ownership, and stock illiquidity (the natural

logarithm of relative effective spreads). To mitigate non-linear effects of product market

competition on innovation outputs (Aghion et al., 2005), we also include the squared Herfindahl

index in our regressions. We provide detailed variable definitions in Table 1 Panel A.

3.3 Summary statistics

To minimize the effect of outliers, we winsorize all independent variables at the 1st

and

99th

percentiles. Table 1 Panel B provides summary statistics. On average, a firm in our sample

has 9.8 granted patents per year and each patent receives 3.9 non-self citations, and is followed

by 7 analysts. Regarding other variables, an average firm has book value assets of $3.59 billion,

R&D-to-assets ratio of 5%, ROA of 9.5%, PPE-to-assets ratio of 29.7%, leverage of 21.8%,

capital expenditure ratio of 6.5%, Tobins Q of 2.1, and is 17.1 years old since its IPO date.

4. Baseline empirical results

To assess how analyst coverage affects innovation, we estimate various forms of the

following model using the ordinary least squares (OLS):

13 To control for the possibility that a given analyst may make multiple forecasts within one month, we alsocalculate the total number of unique analysts issuing earnings forecasts for this firm during the 12-month periodbefore its fiscal year ending date by using the historical detail file of I/B/E/S and find that the two measures ofanalyst coverage are highly correlated (with a Pearson correlation coefficient of 0.96). All our results remainunchanged if we use this alternative definition of analyst coverage.


13/53

11

tiittitititi FirmYearZLnCoverageLnCitePatLnPatent ,,,3,3, )( (1)

where i indexes firm and t indexes time. The dependent variables capture firm innovation

outcomes: the natural logarithm of one plus the number of patents filed (and eventually granted)

(LnPatent) and the natural logarithm of one plus the number of non-self citations per patent

(LnCitePat). Since the innovation process generally takes longer than one year, we examine the

effect of a firms analyst coverage on its patenting three years ahead.14 The analyst coverage

measure, LnCoverage, is measured for firm i over its fiscal year t. Z is a vector of firm and

industry characteristics that may affect a firms innovation output as we discussed in Section

3.2.2. Yearcaptures year fixed effects andFirm captures firm fixed effects. We cluster standard

errors at the firm level.

We start with a parsimonious model that regresses the number of patents filed in three

years only on the key variable of interest, LnCoverage. We find that the coefficient estimate

(untabulated) is 0.331 (p-value < 0.001), suggesting a positive raw association between analyst

coverage and the firms innovation output. We then add year fixed effects to absorb any

aggregate time effect and report the results in column (1) of Table 2 Panel A. The coefficient

estimate ofLnCoverage is still positive and significant at the 1% level. However, the coefficient

turns negative and significant at the 10% level in column (2) when we include firm fixed effects,

suggesting that a higher level of analyst coverage is associated with a lower level of three-year-

ahead innovation output. This result also suggests that certain time-invariant variables omitted

from the regression positively affect both analyst coverage and firm innovation and thus bias the

coefficient estimate ofLnCoverage upward. For example, a corporate culture that tolerates

failures could encourage innovation (Tian and Wang, 2011) while at the same time may attract

more analysts. In this case, corporate culture is unobservable but positively correlated with both

analyst coverage and innovation, biasing our coefficient estimates ofLnCoverage upward.

Including firm fixed effects removes the effects of such time-invariant omitted variables, and the

coefficient estimate ofLnCoverage decreases, i.e., becomes negative and marginally significant.

Existing literature has shown a number of time-varying firm characteristics that directly

affect firm innovation. Omitting these characteristics from the regression could lead to biases as

well. In column (3), we add a set of controls that are important determinants of firm innovation

14 For robustness, we examine the effect of a firms analyst coverage on its patenting one, two, and five years ahead,and obtain both quantitatively and qualitatively similar results.


14/53

12

documented by existing studies: firm size, age, profitability, R&D expenditures, asset tangibility,

leverage, and capital expenditures. The coefficient estimate ofLnCoverage is still statistically

significant but becomes much more negative, i.e., -0.051 (p-value < 0.001). The finding suggests

that these time-varying firm characteristics omitted from column (2) bias the coefficient estimate

upward. In column (4), we further include in the regression Tobins Q, financial constraints

(proxied by the KZ-index), and the HerfindahlHirschman Index as well as its squared term,

motivated by the existing literature showing how these firm characteristics affect innovation

(Hall, Jaffe, and Trajtenberg, 2005; Aghion et al., 2005). The coefficient estimate ofLnCoverage

continues to be negative and significant at the 1% level with a slightly larger magnitude, i.e., -

0.053. Finally, recent work by Aghion, Van Reenen, and Zingales (2013) and Fang, Tian, and

Tice (2012) show that institutional ownership and stock liquidity are important determinants of

firm innovation. Hence, we add these two control variables in column (5). The coefficientestimate ofLnCoverage remains negative, i.e., -0.052, and significant at the 1% level.

With regards to control variables, firms that are larger, older, more profitable, and those

with more tangible assets, higher Tobins Q, and lower leverage are more innovative. Larger

R&D expenditures are associated with more innovation output.15 Further, institutional ownership

and stock illiquidity are positively related to innovation, consistent with the existing literature.

Table 2 Panel B reports the regression results from estimating equation (1) with the

dependent variable replaced byLnCitePat. We observe a very similar pattern for the coefficient

estimates ofLnCoverage as we introduce controls gradually. We observe a positive coefficient

estimate ofLnCoverage in the parsimonious regression without any controls or controlling only

for year fixed effects. The coefficient becomes significantly negative after we introduce firm

fixed effects that control for time-invariant omitted variables. Finally, the coefficient remains

negative and significant as we gradually add time-varying firm-specific and industry-specific

innovation determinants in the regressions. The above finding suggests that omitted variables

bias the coefficient estimate of analyst coverage upward. The negative coefficient estimate of

15 Since we control for R&D expenditures in our baseline regression, we have actually identified the effects ofanalyst coverage on innovation mainly through its impact on R&D effectiveness (i.e., the efficiency of R&Dexpenditures in generating innovation outputs). If, however, we do not include R&D expenditures in our baselineregression, the coefficient estimate ofLnCoverage will then capture both the R&D effectiveness effect and anyadditional effect of financial analysts on firms investments in R&D. In Panel K of Table A1 in the InternetAppendix, we re-estimate equation (1) without including R&D expenditures on the right hand side and get bothquantitatively and qualitatively similar results. For example, the coefficient estimate ofLnCoverage is -0.050 (p-value = 0.004) in model (5) of Table 2 Panel A and is -0.075 (p-value < 0.001) in model (5) of Table 2 Panel B.


15/53

13

LnCoverage in column (5) suggests that firms with more analyst coverage generate patents with

a lower impact. Once again, older firms, more profitable firms, and firms with larger innovation

input, lower leverage, greater institutional ownership, and higher stock illiquidity are associated

with higher-impact patents.

We conduct a rich set of robustness tests for our baseline results and discuss the details of

these tests in the Internet Appendix. We find that our baseline results are robust to alternative

subsamples based on the number of patents or the number of analysts a firm has, alternative

proxies for analyst coverage, alternative proxies for innovation activities, alternative econometric

models that deal with the right-skewed and non-negative nature of patent and citation data, and

alternative empirical specifications. Overall, our baseline results suggest that analyst coverage is

negatively related to a firms innovation output, consistent with the pressure hypothesis.

5. Identification

In this section, we address the endogeneity concern that omitted variables correlated with

both analyst coverage and corporate innovation could bias our results. To that end, we adopt two

different identification strategies. Section 5.1 discusses our first identification strategy that uses a

DiD approach by relying on two quasi-natural experiments: brokerage closures and brokerage

mergers. Section 5.2 discusses the second identification strategy that uses the 2SLS approach

based on a plausibly exogenous instrumental variable, expected coverage.

5.1 Quasi-natural experiments

5.1.1 Experiments

Our first identification strategy is to use two quasi-natural experiments that generate

plausibly exogenous variation in analyst coverage. The first experiment, brokerage closures, first

adopted in Kelly and Ljungqvist (2011, 2012), relies on the fact that brokerage firms often

respond to adverse changes in revenue generation from trading, market-making, and investment

banking by closing their research operations. In other words, brokerage closures are motivated

largely by business strategy considerations of the brokerage houses themselves rather than by the

characteristics of the firms covered by their analysts. This event provides us a nice quasi-natural

experiment on how financial analysts affect firm innovation. Similar to their role in Kelly and

Ljungqvist (2011, 2012), brokerage closures in our setting serve as a source of exogenous

variation in analyst coverage, which should affect a firms subsequent innovation productivity


16/53

14

only through its effect on the number of analysts following the firm.

The second experiment is brokerage mergers, which is first introduced by Hong and

Kacperczyk (2010) to identify an exogenous reason for a drop in analyst coverage. When

brokerage houses merge, they typically fire analysts because of redundancy and potentially lose

additional analysts for other reasons like merger turmoil and culture clash (Wu and Zang, 2009).

Hong and Kacperczyk (2010) argue that if a stock is covered by both brokerage houses before

the merger, they will get rid of at least one of the analysts following the stock, usually the target

analyst, which will in turn reduce the covered stocks analyst coverage. Therefore, brokerage

mergers generate a plausibly exogenous variation in analyst coverage that affects a firms

innovation only through its effect on the firms analyst coverage.

5.1.2 Identifying treatment and control firms

Since innovation involves long-term projects, we require both the treatment and the

control firms to have three years of innovation data before and after the event. Thus we focus on

brokerage mergers and closures that occur between 1996 and 2002 (given that our baseline

sample is 1993-2005). To make our analysis consistent with previous studies, we extract the list

of brokerage mergers during 1996-2002 from Hong and Kacperczyk (2010) and the list of

brokerage closures during 2000-2002 from Kelly and Ljungqvist (2012).16 Both studies have

carefully verified that their brokerage closure and merger events are exogenous to the

characteristics of affected firms, which makes our analysis less prone to endogeneity concerns.

Note that the above two lists of events may overlap because Kelly and Ljungqvist (2012) classify

the closure of target brokers due to mergers and acquisitions as a type of brokerage closures (as

opposed to independent brokerage closures). Hence, we use 12 out of the 15 brokerage mergers

from Hong and Kacperczyk (2010) since the other three brokerage mergers are outside our

sample period (which took place in 1984, 1988, and 1994, respectively). Kelly and Ljungqvist

(2012) report a total of 43 brokerage closures between Q1, 2000 and Q1, 2008. Out of the 23

brokerage closures within our sample period (2000-2002), three overlap with the list of the 12

brokerage mergers extracted from Hong and Kacperczyk (2010). Thus, we retain 20 unique

brokerage closures from Kelly and Ljungqvist (2012). Among them, 9 are independent brokerage

closures and 11 are brokerage closures due to mergers and acquisitions that are different from the

16 We thank the authors of the above two articles for making the data on brokerage mergers and closures publiclyavailable.


17/53

15

ones reported in Hong and Kacperczyk (2010).

Finally, as Kelly and Ljungqvist (2012) only cover brokerage closures starting from

January 2000, we manually collect brokerage closures during 1996-1999 by adopting the

following procedure. We first find out brokers whose last appearance in the I/B/E/S database

falls between 1996 and 1999. We then search for press releases and news articles in Factiva and

manually check that the disappearance of brokers is due to brokerage closures. We read the news

articles carefully to identify the brokerage closure event dates. If the exact date of a closure is not

provided, we use the date of the first press release that covers the news of the closure as a proxy.

We are thus able to identify 6 additional brokerage closures during 1996-1999. Our final sample

of brokerage disappearances consists of 23 mergers and 15 independent closures.

Given the fact that many brokerage closures and mergers span a long time (usually

several months), it is difficult to pin down a precise disappearance date for many of the events inour sample. Therefore, following previous studies that face a similar problem, we treat the six

months symmetrically around our identified disappearance dates as the event period. We then

measure analyst coverage one year before (after) the broker disappearance as the number of

different analysts following a firm between 15 and 3 months before (after) our identified event

(closure or merger) dates. Hence, there is a six-month gap between the end of year -1 and the

beginning of year +1. For all other variables (such as innovation variables and control variables),

we construct a twelve-month disappearance period symmetrically around our identified

disappearance dates and treat that as the event year because these variables are measured on an

annual basis and we have to avoid overlapping them in year -1 and year +1.

To construct a sample of treatment firms that are covered by the closed or merged

brokerage houses prior to the events and that lose analysts due to these exogenous shocks, we

adopt similar procedures to those described in Hong and Kacperczyk (2010) and Kelly and

Ljungqvist (2012). For brokerage closures, we first identify analysts who work for these

brokerage houses but disappear from the I/B/E/S tape (by not issuing any earnings forecasts)

during the year after the brokerage closure date. Then we obtain all firms which are covered by

these analysts before the event. For brokerage mergers, we identify firms covered by both the

target and acquirer brokerage houses before the event and for which one of their analysts

disappears. This procedure ensures that the loss of analyst coverage for these firms is indeed due

to brokerage mergers. Following Kelly and Ljungqvist (2012), we drop firms that are covered by


18/53

16

one or both brokerage houses before the merger but are no longer covered by the surviving

brokerage house after the merger. The reason for imposing the last restriction is that such

coverage terminations may be endogenous since the surviving brokerage house makes a choice

to cease covering the firm.

Finally, for a firm to be classified into our treatment group, we need it to have non-

missing matching variables (to be discussed below) for year -1 and non-missing innovation

variables (patents and non-self citations) for at least three years before and after the event (years

-3 to +3). The choice of a seven-year window (from year -3 to year +3) reflects a trade-off

between relevance and accuracy. On the one hand, choosing too wide a window may incorporate

too much noise irrelevant to the events and may unnecessarily reduce the sample size (because

the treatment firms then need to have non-missing data for more years) and thus lower the power

of our test. On the other hand, there is usually a gap between the change of a firms innovationpolicy and its innovation output. Hence, unlike the case of analyzing innovation inputs such as

R&D expenditures, choosing a window that is too narrow may limit our ability to identify any

meaningful changes in innovation outputs. Given the above considerations, we use a seven-year

window, though our results are qualitatively similar (but statistically weaker) if we use a three-

year or five-year window.

We then proceed to construct a control group of firms that are matched to the treatment

group on important observable characteristics one year prior to the events but that do not lose

analyst coverage due to the exogenous shocks. We require potential control firms to have been

traded for at least three years before the broker disappearance date, and to have Compustat data

both in years -1 to -3 and years +1 to +3. Following Hong and Kacperczyk (2010), we require

that candidate control firms be in the same market capitalization tercile, book-to-market ratio

tercile, past return tercile, and analyst coverage tercile in the matching year (year -1). In addition,

since Kelly and Ljungqvist (2012) show that stocks experiencing brokerage closures are

generally more volatile and have more turnover than average stocks in the CRSP universe, we

include these two additional variables in our baseline matching process by requiring candidate

control firms to be in the same stock return volatility tercile and stock turnover tercile in the

matching year.17

We compute the difference between treatment firms and candidate control firms

17 Market capitalization is a firms stock price times its shares outstanding at the end of yeart. Book-to-market ratiois a firms book value divided by its market cap at the end of year t. Past return is the average monthly stock return


19/53

17

according to their analyst coverage in year -1 and retain, for each treatment, five control firms

with the smallest difference in analyst coverage. We then construct portfolios of these five

control firms and use them as benchmarks. We end up with 1,165 unique pairs of treatment-

control matches.

5.1.3 The DiD estimation

After obtaining a closely matched sample of control firms, we use a DiD approach to

ensure that the difference in innovation activities between the treatment and control firms are not

driven by their cross-sectional heterogeneity or common time trends that affect both groups of

firms. As long as our treatment and control firms are similarex ante except for the loss of an

analyst for our treatment, our approach ensures that the changes in innovation are caused only by

the exogenous change in analyst coverage.

The success of a DiD approach hinges on the satisfaction of the key identifying

assumption behind this strategy, the parallel trend assumption, which states that in the absence of

treatment, the observed DiD estimator is zero. To be precise, the parallel trend assumption does

not require the level of innovation variables to be identical across the treatment and control firms

over the two eras because these distinctions are differenced out in the estimation. Instead, this

assumption requires similar trends in innovation variables during the pre-shock era for both the

treatment and control groups. Therefore, before we carry out the DiD estimation, we perform

two diagnostic tests to ensure that the parallel trend assumption is satisfied.

The first piece of evidence to support the satisfaction of the identifying assumption is

reported in Figure 1. Panel A shows the difference in the number of patents between the

treatment and control groups over a 7-year event window surrounding the exogenous shock. It

shows that the difference between the treatment and control groups is stable in the 3 years

leading up to the exogenous shock, suggesting that there are no pre-trends present for patents.

Panel B reports the difference in the number of non-self citations per patent between both groups

of firms surrounding the exogenous shock.18

We observe a similar trend in patent citations.

We present the second piece of evidence indicating that the parallel trend assumption is

during year t. Stock return volatility is the standard deviation of a firms daily stock returns multiplied by 252.Stock turnover is a stocks average monthly volume divided by shares outstanding.18 Consistent with the main DiD analysis that we discuss later, we normalize each treatment or control firms patents(non-self citations per patent) by the average annual patents (non-self citations per patent) between treatments andtheir corresponding controls over the three-year pre-event period.


20/53

18

satisfied in Table 3 Panel A, which reports the univariate comparisons between the treatment and

control firms innovation growth variables as well as other important characteristics in the pre-

event year. The univariate comparisons indicate that there are no statistically significant

differences in the three-year growth rates of innovation variables between the treatment and

control firms before the event, suggesting that the parallel trend assumption is satisfied.

Moreover, all the differences in the matching variables and almost all other important firm

characteristics between the treatment and control firms are insignificant before the event,

although control firms appear to be marginally more profitable than treatment firms. Overall, the

univariate comparisons reported in Panel A suggest that the matching process has successfully

removed meaningful observable differences between the treatments and the controls before the

event, and thus ensured that the change in innovation output are caused only by the exogenous

shock to analyst coverage.Table 3 Panel B reports the results from the DiD analysis using the size, book-to-market,

past return, coverage, volatility, and turnover matched sample. We compute the DiD estimator

by first subtracting the total number of patents counted over the three-year period preceding the

event from the total number of patents over the three-year period post the event for each

treatment firm. The difference is then averaged over the treatment group and reported in column

(1). To evaluate the quality of the patents, we first compute the non-self citation ratio for each

treatment firm by counting the total number of patents it generated three years before (or after)

the event as well as the total number of non-self citations received by these patents, and dividing

the latter by the former. We then calculate the difference in non-self citation ratios before and

after the event and average it over all treatment firms. We report it in column (1). To facilitate

the interpretation of the economic significance for the DiD estimators, we need to compare all

treatment-control pairs on an equal basis.19 Hence, following the spirit of Kelly and Ljungqvist

(2012), we normalize each treatment firms difference in the total number of patents (non-self

citation ratios) by the average total number of patents (non-self citation ratios) between this

treatment and the matched control portfolio over the three-year pre-event period. We repeat the

same procedure for control portfolios and report the average changes in the total number of

patents (non-self citation ratios) surrounding the event date in column (2).

19 For instance, some firms may be more innovative (e.g., having 100 patents to begin with) than others, so anincrease in the same number of patents (say, 10 patents) due to an exogenous loss of analyst coverage may matterless for these firms than for less innovative ones (e.g., firms having 20 patents to begin with).


21/53

19

The DiD estimator is simply the difference in the differences for the treatment and the

control groups, and is reported in column (3). Following Hong and Kacperczyk (2010), we

cluster standard errors of the DiD estimators at the event (brokerage closure or merger) level.

The average change in the three-year total number of patents for treatment firms is 0.236, while

that for control firms is much smaller, 0.054. The DiD estimator for the total number of patents is

0.182 and significant at the 1% level. In terms of economic significance, our analysis suggests

that an exogenous average loss of one analyst following a firm causes it to generate 18.2% more

patents over a three-year window than a similar firm without any decrease in analyst coverage.

The average change in non-self citation ratios (the number of non-self citations per patent) for

treatment firms is -0.357, and that for control firms is -0.651. The DiD estimator for non-self

citation ratios is 0.294 and significant at the 1% level, suggesting that an exogenous average loss

of one analyst following a firm leads it to generate patents receiving 29.4% more non-selfcitations than a similar firm without any decrease in analyst coverage. Note that we observe a

generally downward trend of patent citations over the years in Panel B. This observation is

mainly due to the fact that most brokerage closures and brokerage mergers occurred in 1999-

2001, coinciding with the burst of the dot-com bubble that gave rise to a large drop in investment

in groundbreaking innovation activities during that time period.20

In untabulated analysis, we also check the DiD estimator for analyst coverage to verify

the premise of the natural experiments: exogenous shocks to analyst coverage due to brokerage

closures or mergers should lead to an average reduction of one analyst for the treatment group

relative to the controls. Consistent with this conjecture, we observe a relative drop in coverage

by around 1.06 analysts in the year before and after the event (i.e., from year -1 to +1), which is

comparable to that reported in Hong and Kacperczyk (2010), i.e., 1.02 analysts. This effect is

significant at the 1% level.

Next, we perform a subsample analysis to understand whether the negative effect of

analyst coverage on innovation depends on the number of analysts currently following the firm.

Put differently, we examine whether there is a non-linear effect of analyst coverage on

20 An alternative possibility that explains the generally downward trend of patent citations is the limitations of theempirical method that corrects for the truncation bias in citation counts. While estimating the shape of the citation-lag distribution to correct for the citation count truncation bias is the standard method used by existing innovationliterature, it has its own limitations. In contrast, by using the HBS patent database that contains patents grantedthrough 2010, we are able to effectively mitigate the truncation bias in patent counts to a much larger degree, whichmay explain why we do not observe a generally downward trend for patent counts.


22/53

20

innovation. Intuitively speaking, losing one analyst (due to the exogenous shock) should make a

bigger difference for firms that are covered by few analysts before the shock than for the firms

that are covered by many analysts before the shock. To examine this conjecture, we first classify

the treatment firms into three groups based on their analyst coverage in the pre-event year: firms

with 10 or fewer analysts, those with 11 to 25 analysts, and those with more than 25 analysts. We

then compare each group of these treatment firms to their corresponding matched controls and

report the DiD results in Panel C.

Column (1) of Panel C reports the results for patent counts. The DiD estimator is 0.253

and significant at the 5% level for the group of firms with the smallest number of analysts

following. The DiD estimator goes down to 0.159 but continues to be significant at the 5% level

for the group of firms with moderate analyst coverage. The magnitude of the DiD estimator

further goes down and becomes statistically insignificant for the group of firms followed by thelargest number of analysts. We observe a similar pattern of patent quality in column (2). Overall,

we observe a monotonically decreasing pattern for the DiD estimator as the number of analysts

following a firm goes up, which suggests that the negative effect of analyst coverage on

innovation is stronger for firms covered by fewer analysts.

5.1.4 Robustness

We conduct a rich set of robustness tests for the DiD analysis and report the results in

Table 4. First, we address the concern that the main DiD results may be driven by the specific set

of matching variables used in our baseline matching procedure. To that end, we use alternative

combinations of matching variables to select the control firms and report the results in Panel A.

We start with a nave matching procedure that only requires both treatment and control

firms to have non-zero patents over the sample period and present the DiD estimators in row (1).

The DiD estimator for patent counts is 0.271 and significant at the 1% level, and that for non-self

citations per patent is 0.477 and significant at the 1% level. Next, we add an additional matching

criterion that requires both treatment and control firms to have a similar number of patents (i.e.,

both firms are in the same patent tercile) in the matching year.21 The results are reported in row

(2). The DiD estimators for both patents and non-self citations are positive and significant at the

21 Given the nature of our patent data, we define the bottom tercile of firms as those with zero patent in a given yearand the top tercile of firms as those whose total number of patents in that year exceed the sample median amongthose firms with non-zero patents (i.e., after excluding the bottom tercile of firms).


23/53

21

1% level. Third, instead of using the six main matching variables in our baseline matching

procedure (in Section 5.1.3), we rely on the four matching variables used in Hong and

Kacperczyk (2010), namely, size, book-to-market, past return, and analyst coverage, to select

control firms and report results in row (3). The DiD estimators for patents and citations are still

positive and significant at the 1% level. Fourth, in addition to the six main matching variables

used in our baseline DiD analysis, we include patent counts and non-self citations per patent as

additional matching criteria. In row (4), the DiD estimator for patents is 0.595 and significant at

the 1% level, while the DiD estimator for citations is 0.287 and significant at the 5% level. Fifth,

we drop book-to-market and past returns from the matching criteria and only use size, analyst

coverage, stock volatility, and stock turnover as matching variables, and report results in row (5).

The DiD estimators for both patents and citations continue to be positive and significant at the

1% level. Sixth, besides the six matching variables (size, book-to-market, past return, analystcoverage, stock volatility, and stock turnover) used in the baseline DiD analysis, we require both

treatment and control firms to be in the same Fama-French 49 industries. In row (6), the DiD

estimators of patents and citations are positive and significant at the 1% and 5% level,

respectively. Finally, we use size, book-to-market, past return, analyst coverage, and Fama-

French 49 industries as matching variables and obtain similar results, which are reported in row

(7). The DiD estimators for patents and citations are positive and significant at the 10% and 5%

level, respectively. Overall, we find that our DiD results are robust to alternative matching

criteria for selecting control firms.

Second, we address the concern that the main DiD results might be driven by the right-

skewed distribution of the patent variable. We impose various thresholds for the number of

patents that the treatment and control firms need to have up to the matching year. We report the

results in Panel B of Table 4. In row (1), we start with the restriction that the treatment and

control firms need to have at least one patent up to the matching year. The DiD estimator for

patents is 0.331 and that for citations is 0.242. Both are significant at the 1% level. In terms of

economic significance, our analysis suggests that an exogenous average loss of one analyst

following a firm that has at least one patent before the event year causes it to generate 33.1%

more patents and 24.2% more non-self citations per patent than a similar firm without any

decrease in analyst coverage. The DiD estimator in this subsample has a larger economic impact

compared to the one that is obtained from the full sample in Section 5.1.3 because this subsample


24/53

22

excludes firms that generate zero patents before the event and is a more innovation-relevant

subsample. In rows (2), (3), and (4), the threshold for the minimum number of patents up to the

matching year is two, three, and five, respectively. The DiD estimators for patents and citations

continue to be positive and significant at the 1% level.

Third, we examine whether our main DiD results are robust to using firms with various

thresholds for the number of analysts and report the results in Panel C. In row (1), we require the

firms to have at least five analysts in the matching year. The DiD estimator for patents is 0.185

and that for citations is 0.290. Both are significant at the 1% level. We impose an alternative

threshold, a minimum of 15 analysts (with results reported in row (2)), and continue to observe

positive and significant DiD estimators for both patents and citations. Finally, we restrict our

sample of firms to be covered by at least 25 analysts and report the results in row (3). The DiD

estimators are still positive but lose significance. This result is consistent with our earlierfindings reported in Panel C of Table 3 that the negative effect of analyst coverage on innovation

is absent when the firm is already covered by a large number of analysts.

Fourth, one might worry that our main DiD results could be driven by certain subsamples

of firms. For example, a reasonable concern is that many of the brokerage closures and mergers

occurred after the burst of the internet bubble (e.g., 40% of our sample of brokerage closures and

mergers took place in 2001 and 2002). Therefore, high-tech firms that are generally active

innovators are more likely to experience a decrease in analyst coverage due to brokerage closures

or mergers. To address this concern, we exclude the brokerage closures and mergers that

occurred in 2001 and 2002 and redo the DiD analysis. Row (1) of Panel D reports the results.

The DiD estimator for patents is 0.299 and that for citations is 0.549. Both are significant at the

1% level.22 Another reasonable concern is that our main DiD results may be driven by firms that

experience only brokerage closures or only brokerage mergers. To address this concern, we

exclusively focus on firms that experience a decrease in analyst coverage due to the brokerage

mergers shown in Hong and Kacperczyk (2010) that overlap with our sample period (12 of them)

and report the results in row (2). The results are robust. The DiD estimator for patents is 0.159

and significant at the 1% level, and that for citations is 0.465 and significant at the 5% level.

Finally, we examine whether our baseline DiD results are robust to using an alternative

22 In an untabulated analysis, we exclude the events occurred in 2000, 2001, and 2002, and obtain similar results.The DiD estimators for patents and citations continue to be positive and significant at the 5% and 1% level,respectively.


25/53

23

matching methodology when selecting the control group, the propensity score matching method,

which matches control firms to treatment firms on all important observable characteristics prior

to the exogenous shocks. We first run a probit regression of a dummy variable that equals one if

a particular firm-year belongs to our treatment group (and zero otherwise) on a comprehensive

list of observable characteristics, including all the independent variables in our baseline

regression as well as stock volatility and turnover. We also include year and Fama-French 49

industry dummies. Further, to ensure that the parallel trends assumption is satisfied, we also

match firms on growth measures of innovation variables (patents and citations). After estimating

the probit model, we use the predicted probabilities, or propensity scores, from this probit

estimation and perform a nearest-neighbor matching with replacement to form the control

group.23 We report the DiD estimators based on this matched sample and report the results in

Panel E of Table 4. The DiD estimator for patents is 0.190 and significant at the 5% level andthat for citations is 0.449 and significant at the 1% level, suggesting that the baseline DiD results

are robust to alternative matching methods.

Overall, the DiD analysis suggests that an exogenous decrease in analyst coverage leads

to a larger relative increase in innovation output (in terms of both quantity and quality), and that

the negative effect of analyst coverage on innovation is stronger for firms followed by fewer

number of analysts. The evidence from the quasi-natural experiments suggests a negative causal

effect of analyst coverage on firm innovation and is consistent with the pressure hypothesis.

5.2 Instrumental variable approach

Our second identification strategy is to construct an instrument for analyst coverage and

use the 2SLS approach to correct for the potential bias due to endogeneity in analyst coverage.

The ideal instrument should help to capture the variation in analyst coverage that is exogenous to

firms innovation productivity. The instrument we use is expected coverage, introduced by Yu

(2008), which captures the change of brokerage house size.24 As argued by Yu (2008), the size of

a brokerage house, usually depending on the change of its own revenue or profit, is unlikely to

be related to the innovation productivity of certain firms that the brokerage house covers.

23 Since the number of potential control firm-years is considerably larger than the number of treatment firm-years,we choose to find 3 controls for each treatment. This will allow us to avoid relying on too little information orincluding vastly different observations. However, our results are robust to any number of matches between 1 and 5.24 For robustness, we construct the second instrument suggested by Yu (2008), which is a firms inclusion in theStandard & Poors 500 index, and use it in the 2SLS regressions. We find that our baseline results continue to hold.


26/53

24

Therefore, the change of coverage driven by the change of brokerage house size is a plausibly

exogenous variation that helps us to identify the direction of causality. This argument can also be

illustrated by the following three real-world examples.

On June 6, 2007, Prudential Financial Inc. announced that it would substantially wound

down its equity research group by the end of the month. During that year, the equity research

division reported only $260 million in revenue and $137 million in total assets. By comparison,

the parent company, Prudential Financial, generated $32.5 billion in revenue and owned 454

billion in assets. Mary Flowers, the company spokeswoman, commented on the decision saying

that we dont have the scale to compete and added that the parent company was focusing on

business where we can be a top-tier player. (USA Today 2007)

In August 2012, Barclays expanded its Taiwan-based equity research team that covered

non-tech companies by recruiting a senior hire as the managing director and a bunch of analystsfrom Credit Suisse Group AG. The expansion was due to Barclays considerations of increasing

its own revenue. According to Barclays statement, the expansion of its equity research team was

driven by continuous earnings growth in its brokerage, advisory and foreign-exchange

derivative businesses. (Wall Street Journal2012)

Williams Capital Group, a New York-based brokerage firm, expanded its equity research

group for the second time in less than two years in January 2011. Its goal was to get 12 to 15

analysts by the end of the year. Besides, each analyst is expected to be covering about 15

stocks in all market caps. The head of the equity research group, Mr. Matt Rochlin, made it

clear that the decision reflected competitive pressure and strategic considerations: clients are

under pressure to get as much as they can for their commission dollars. For us to add value and

to compete for those commission dollars, research is very important. (Traders Magazine, 2011)

Following Yu (2008), we use the equations below to calculate expected coverage:

n

j

jt,i,ti,

jijjtjt,i,

eExpCoverageExpCoverag

CoverageBrokersizeBrokersizeeExpCoverag

1

,0,,0, *)/(

(2)

where ExpCoveragei,t,j is the expected coverage of firm i from brokerj in year t. BrokerSize0, j

andBrokerSizet, j are the number of analysts employed by brokerj in the benchmark year0 and

year t, respectively. Coveragei,0,j is the size of the coverage for firm i from brokerj in year 0.

ExpCoveragei,tis the total expected coverage of firm i from all brokers in yeart.


27/53

25

In the spirit of Yu (2008), we use 1993, the beginning year of our sample, as the

benchmark year. To construct a meaningful measure of expected coverage, we require a firm to

be covered by at least one analyst in the benchmark year. In our 2SLS analysis, we drop all

observations in the benchmark year because the expected coverage for that year will

automatically be set to one by design. One concern of this instrument is that in reality brokers

choose which firms to stop covering and thus may introduce a potential selection problem.

However, as Yu (2008) points out, this selection issue will only affect the realized but not the

expected coverage, since the expected coverage measures the tendency to keep the coverage

before the broker actually decides which firms to keep.

Column (1) of Table 5 shows the first-stage regression results with LnCoverage as the

dependent variable to check the relevance of the instrument. The main variable of interest is the

instrument, ExpCoverage. All other control variables are the same as those in the baselineregression equation (1). To save space, we suppress the coefficient estimates of all controls. Year

and firm fixed effects are included and standard errors are clustered at the firm level. The

coefficient estimate ofExpCoverage is positive and significant at the 1% level, consistent with

that reported in Yu (2008). Since the t-statistic of the instrument is large (75.8), the instrument is

highly correlated with LnCoverage. Based on the rule-of-thumb with one instrument (for one

endogenous variable), we reject the null hypothesis that the instrument is weak. Therefore, the

coefficient estimates and their corresponding standard errors reported in the second stage are

likely to be unbiased and inferences based on them are reasonably valid.

Columns (2) and (3) of Table 5 report the results from the second-stage regressions

estimating equation (1) with the main variable of interest replaced by the fitted value of

LnCoverage from the first-stage regression. We report within-firm R2 for the second-stage

regressions. To save space, we only report the coefficient estimates of the instrumented

LnCoverage and suppress those of all other controls. Column (2) presents the results with

LnPatent as the dependent variable. Consistent with the findings from the OLS analysis, the

coefficient estimate ofLnCoverage is negative and significant at the 1%. Column (3) reports the

regression with patent quality,LnCitePat, as the dependent variable. The coefficient estimate of

LnCoverage is negative and significant at the 1% level, reinforcing our baseline findings.

To gauge the direction and the magnitude of the bias due to the endogeneity in analyst

coverage, we run OLS regressions on the same set of firms as those used in the 2SLS regressions


28/53

26

(Table 5) and compare the (untabulated) results with those obtained from the 2SLS regressions.

It is interesting to observe that the magnitudes of the 2SLS coefficient estimates (-0.115 for

LnPatentand -0.137 forLnCitePat) are considerably larger (i.e., more negative) than those of the

OLS estimates (-0.062 forLnPatent and -0.088 forLnCitePat), even though the coefficient

estimates from both approaches are negative and statistically significant, suggesting that OLS

regressions bias the coefficient estimates ofLnCoverage upward due to the endogeneity in

analyst coverage. This finding suggests that some omitted variables simultaneously make firms

more innovative and more intensively covered by analysts. Management talent, if time varying

within a firm, could be an example of such omitted variables. For instance, high quality

managers may tend to manage companies attracting more analyst coverage, while in the

meantime may also actively engage in more long-term innovative projects that result in more

patents and citations. This positive correlation between analyst coverage and firm innovationcaused by omitted variables is the main driving force that biases the coefficient estimates of

analyst coverage upward. Once we use the instrument to clean up the correlation between analyst

coverage and the residuals (the firms unobservable characteristics) in equation (1), the

endogeneity of analyst coverage is removed and the coefficient estimates decrease, i.e., become

more negative.

In summary, the identification tests based on both the DiD approach and the instrumental

variable approach reported in this section suggest that there appears to be a negative causal effect

of analyst coverage on firm innovation, consistent with the pressure hypothesis.

6. Possible mechanisms

Our evidence so far is consistent with the implication of the pressure hypothesis that

analyst coverage impedes firm innovation. In this section, we discuss possible underlying

economic mechanisms through which this occurs and examine whether there exists a residual

effect of analyst coverage on firm innovation after controlling for such mechanisms. Section 6.1

argues that different types of institutional ownership could be an underlying economic

mechanism. A reduction in analyst coverage leads to an increase in institutional ownership by

dedicated investors who serve as a shield against short-term pressure and promote innovation

(Aghion, Van Reenen, and Zingales, 2013). Meanwhile, a reduction in analyst coverage leads to

a decrease in institutional ownership by non-dedicated investors who chase short-term financial

returns and impose pressure on firm managers. In Section 6.2, we show that a firms exposure to


29/53

27

takeovers is another possible underlying mechanism. A reduction in analyst coverage reduces a

firms exposure to takeovers, which in turn lowers the managers short-term pressure and

encourages them to make long-term investments (Stein, 1988). Section 6.3 argues that stock

illiquidity and the difficulty in implementing accrual-based earnings management techniques are

two other possible underlying mechanisms.25 Both stock illiquidity and accrual-based earnings

management practices are able to partially insulate firm managers from the short-term pressure

to meet earnings targets and thereby motivate innovation. In Section 6.4, we show that there

exists a direct (residual) effect of analyst coverage on firm innovation after controlling for all the

above possible economic mechanisms.

6.1 Different types of institutional ownership

In this section, we examine whether different types of institutional ownership could help

explain the negative effect of analyst coverage on firm innovation. Kelly and Ljungqvist (2012)

find that an exogenous reduction in analyst coverage leads to a higher degree of information

asymmetry among investors, which in turn results in an increase in institutional ownership and a

decrease in retail ownership. Their rationale is that institutional investors have access to private

information that is unavailable to retail investors who mainly rely on public sources of

information such as analyst reports. Therefore, the increase in information asymmetry due to an

exogenous drop in analyst coverage crowds out the demand by retail investors. To the extent

that this argument also applies to different types of institutional investors, we expect that after an

exogenous drop in analyst coverage there will be an increase in holdings from dedicated

institutional investors, who actively collect information about firm fundamentals, concentrate

their portfolios in a few firms, and thus have access to more private information. In contrast, an

exogenous reduction in analyst coverage should lead to a decrease in holdings by non-dedicated

institutional investors, who chase short-term profits instead of collecting information about

firms fundamental values, hold highly diversified portfolios with small stakes in many

25 Note that while Kelly and Ljungqvist (2012) find a causal effect of analyst coverage on institutional versus retailinvestor ownership, we are not aware of any studies that show the causal effect of analyst coverage on differenttypes of institutional ownership (i.e., equity holdings by dedicated versus non-dedicated institutional investors).Similarly, no previous studies have directly examined the causal effect of analyst coverage on a firms takeoverexposure. Therefore, we conduct the DiD tests for these two economic mechanisms and report the results in Table 6Panels A and B. However, since existing literature has already shown the causal effect of analyst coverage on stockliquidity (Kelly and Ljungqvist, 2012) and on accrual-based earnings management (Yu, 2008), we rely on theirfindings and only discuss these two economic mechanisms in Section 6.3 without conducting the DiD analysisourselves.


30/53

28

companies, and thus have less access to private information. Meanwhile, the model of Aghion,

Van Reenen, and Zingales (2013) implies that dedicated institutional investors encourage firm

innovation to a greater extent than non-dedicated ones. Thus, the equity ownership by different

types of institutional investors could be an underlying economic mechanism through which

analyst coverage impedes firm innovation.

To test this conjecture, we first calculate the changes in equity ownership by different

types of institutional investors surrounding the exogenous shocks to analyst coverage for the

treatment and control firms. We follow the classification scheme created by Bushee (1998, 2001)

and classify institutional investors into one of three categories: dedicated investors, quasi-

indexers, and transient investors.26

We then merge Bushees institutional investor classification

file with quarterly institutional investors holdings of U.S. securities from Thomsons 13F

database. Since Porter (1992) argues that a higher presence of transient investors and quasi-indexers have weak incentives to produce information about firm fundamentals, we group these

two types of investors together as the non-dedicated institutional investors and compare their

equity ownership to that of the dedicated institutional investors.

We examine the effect of analyst coverage on equity ownership by different types of

institutional investors in the DiD framework, using the matched sample constructed in Section

5.1.2. Specifically, we compare the change in equity ownership by different types of institutional

investors in the year before (year -1) and after (year +1) the shock for the treatment firms and

their matched controls. Reported in Table 6 Panel A, the DiD estimator for the dedicated

institutional ownership (DedOwn) is 0.013 and significan

the dark side of analyst coverage

Documents