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INNOVATION AND PROFITABILITY FOLLOWING ANTITRUST
INTERVENTION AGAINST A DOMINANT PLATFORM: THE WILD, WILD
WEST?
Sruthi Thatchenkery
Owen Graduate School of Management
Vanderbilt University
sruthi.thatchenkery@vanderbilt.edu
Riitta Katila
Department of Management Science and Engineering
Stanford University
rkatila@stanford.edu
Strategic Management Journal 2023, in press.
Keywords: Innovation, competition, technology ecosystems, platforms, antitrust
The dissertation from which this paper draws was the Winner of the Strategic Management
(STR) Division Outstanding Dissertation Award, and this paper was selected as Strategic
Management Society’s Annual Conference Research Methods Award Finalist. The support
and feedback of our editor Rahul Kapoor and two anonymous reviewers was extremely
helpful. We also thank Gautam Ahuja, Erik Brynjolfsson, Kathy Eisenhardt, Caroline
Flammer, Connie Helfat, Michael Jacobides, Samina Karim, Wesley Koo, Alex Oettl, Joe
Porac, Juan Santalo, Andrew Shipilov and Tim Simcoe for discussions, feedback, and
comments. We appreciate the thoughtful feedback from seminar audiences at the Academy of
Management Meetings, Bocconi, Dartmouth, IIB-Bangalore, Johns Hopkins, London
Business School, Ohio State, Rice, Tilburg, Vanderbilt, Wharton, Stanford Digital Economy
Seminar, Ghoshal Conference, Industry Studies Association Conference, Organizational
Design Conference, Strategic Management Society Annual Meetings, Stanford Technology
Ventures Program Alumni Conference, SUFE conference, and University College London
strategy reading group. We deeply appreciate the assistance of executives and ecosystem
participants in software whom we interviewed for this study. Mengjie Chen provided
research assistance. The generous research support of the Stanford Technology Ventures
Program, the National Science Foundation Graduate Research Fellowship for the first author
and the National Science Foundation grant (# 1305078) for the second author is gratefully
acknowledged. Finally, we wanted to extend our sincerest thanks to our incredible reference
librarian from the Jackson library who went above and beyond duty to help us collect the
private firm data during the pandemic.
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INNOVATION AND PROFITABILITY FOLLOWING ANTITRUST
INTERVENTION AGAINST A DOMINANT PLATFORM:
THE WILD, WILD WEST?
Research Summary
This study examines whether “unblocking” competition through antitrust intervention against
a dominant platform can spur complementor innovation in platform ecosystems. Using a
novel dataset on enterprise infrastructure software and a difference-in-differences design, we
examine the relation between the U.S. antitrust intervention against Microsoft (dominant
enterprise platform) and subsequent innovation and profitability of infrastructure applications
firms (complementors). The data show that innovation among complementors—particularly
ones with low market share—soared when the competitive pressure on the dominant platform
amplified. However, the profitability of these complementors dropped. Our results contribute
to understanding links between competition and innovation in platform ecosystems, as well
as the opportunities and threats related to dominant platforms in those ecosystems.
Managerial Summary
Complementors (apps, services) that are owned by their platforms often have an unfair
advantage. Antitrust action challenges the power of such dual platform-complementors,
reasoning that unfair advantage blocks fair competition, and, in turn, reduces firms’
incentives to innovate and thus limits consumer choice. We examine whether reducing
anticompetitive barriers and platform-complementors’ power revitalizes the platform
ecosystem. Using a landmark antitrust case, we find mixed results: while complementors do
innovate more, their profits go down. In particular, the low-share complementors that bring in
the most innovation are also the ones that lose the most financially, suggesting that they may
have over-relied on the platform for key assets. To develop a healthy ecosystem in the long
run, platform owners may want to resist the temptation to keep complementors weak and
instead help support their development to stand on their own.
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Microsoft created a weak, copycat product [Teams] and tied it to their dominant Office
[platform], force installing it and blocking its removal. A carbon copy of their illegal behavior
during the browser wars. – Workplace communications app Slack (complementor) announcing a
complaint against Microsoft (platform-complementor) before the European Commission, 2020.
“Google has used Android [platform] as a vehicle to cement the dominance of its search engine...
These practices have denied rivals [complementors] the chance to innovate.” – European Commission,
2018.
Research argues that competition and innovation go hand-in-hand (Arrow, 1962; Katila &
Chen, 2008; Thatchenkery & Katila, 2021). In the context of antitrust, dominant firms are
argued to “block” competition by, for example, building barriers to entry or expansion, such
as unequal access to distribution channels (Porter, 1979), or making it difficult or costly for
rivals to compete, leading to innovation losses in their industries. Public policy interventions,
including antitrust, aim to “unblock” competition to overcome anti-competitive barriers for
the benefit of users and innovation (Khan, 2017).
Recent research extends arguments about competition and innovation into dominant
platforms. Platforms are an interesting context because, in contrast to vertical industries,
platform power extends beyond the platform market to affect innovation in complementor
markets (Eisenmann, Parker, & Van Alstyne, 2011; Kapoor, 2018; Katila, Piezunka, Reineke
& Eisenhardt, 2022).
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In particular, a dominant technology platform that offers products in its
own complementor markets may discourage investment by rival complementors (Seamans &
Zhu, 2017; Zhu, 2019) or may exploit its market power to block complementors from
growing enough to become a threat (Adner & Lieberman, 2021; Katila, Rosenberger, &
Eisenhardt, 2008). In response, antitrust authorities worldwide have opened inquiries against
Google, Amazon, Apple, Alibaba, and other technology platforms (Kendall & Copeland,
2020).
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Yet despite substantial interest from policymakers (Crémer et al., 2019) and experts
1
Complementors are actors in digital ecosystems that innovate on top of a platform’s core resources with the
intent to create products and services for the platform’s end users. Collectively, the platform, complementors,
and end users constitute an ecosystem (Teece, 2018).
2
“Platform antitrust” differs from traditional antitrust because platforms are incentivized to share
complementary assets with complementors in order to build the multi-sided ecosystem. In traditional vertical
foreclosure, a vertically integrated downstream firm has no incentives to share assets with a rival upstream firm.
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in innovation, law, and economics (Butts, 2010; Jacobides & Lianos, 2021; Teece &
Kahwaty, 2020), research in this area remains sparse, particularly from the complementor
strategy perspective (Greene & Yao, 2014; Oberholzer-Gee & Yao, 2010).
A certain tension makes antitrust intervention in platform ecosystems particularly
intriguing. Although dual platform-complementors may block rival complementors’
opportunities to innovate (Kamepalli et al., 2020), platforms often provide critical
“infrastructure” for complementors (Ceccagnoli et al., 2012; Zhu, 2019; Katila et al., 2022)
and can help “maintain order” in the ecosystem (Gavetti, Helfat, & Marengo, 2017; Rietveld,
Seamans, & Meggiorin, 2021). Wen and Zhu (2019), for example, found that Google’s entry
threat to Android reduced wasteful duplication such as redundant apps, and Zhang, Li, and
Tong (2020) noted that Apple’s iOS gatekeeping policies encouraged knowledge sharing by
complementors. Diluting a platform’s market power may thus backfire for complementors.
The tension is an interesting one. In this paper we ask, How does increased competitive
pressure against a dominant platform through antitrust intervention relate to innovation and
profitability of complementors?
We focus on a landmark antitrust intervention against a dominant platform owner,
Microsoft, in which the platform was accused of, and subsequently prevented from, blocking
“innovation competition” in complementor markets.
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Microsoft blocked competition through
(among other tactics) bundling its own infrastructure software with its enterprise platform and
by creating efficient interoperability. Antitrust intervention reversed these effects. Using a
difference-in-differences design that takes advantage of variation in Microsoft’s market share
across complementor markets, we examine how innovation and profit of U.S. enterprise
infrastructure software firms changed after the intervention. A unique strength of our study is
3
Our focus is enterprise infrastructure software. In contrast, user-facing applications such as word processing
and supply chain logistics are outside our scope. Prominent enterprise firms like SAP and Salesforce
(Ceccagnoli et al., 2012) were not developing infrastructure software during our study period.
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our detailed coverage of the population of complementors, as well as a battery of sensitivity
and falsification tests, including matching, event studies, “honest” pre-trends tests, and 10-K
data on perceptions of competition, to show that the observed effects are robust to a variety of
empirical approaches. We supplement the quantitative analysis with interviews with industry
participants and with a review of public documents regarding the case.
The key finding is that unblocking competition creates a “wild west” where many
complementors race to innovate but fail to profit. Following the intervention, innovation in
Microsoft’s former complementor strongholds increased, consistent with the theoretical
arguments that newly opened space would incentivize rival complementors to innovate. The
boost was particularly pronounced among low-share complementors. Notably, firm entry did
not increase, underscoring that innovation originated from incumbents’ revitalized efforts, not
firm turnover. However, complementors were not able to financially capitalize on their
innovations: profits dropped after the intervention, suggesting that innovation increases did
not turn into profitable sales increases. The tendency to boost innovation at the expense of
profit was particularly pronounced for low-market-share firms, while high-market-share firms
instead pursued internal efficiency.
Altogether, our findings emphasize the unique features of platform-based ecosystems.
While much strategy research has focused on digital platforms’ growing ecosystem footprint
(Seamans & Zhu, 2017), and on the support that dominant platforms can provide to
complementors (Ceccagnoli et al., 2012; Zhu, 2019; Katila et al. 2022), our findings
contribute to an emerging stream that analyzes the decreasing influence of platforms and its
implications for complementors, particularly regarding the complementary assets they now
need to build on their own. More broadly, we add insight on how firms in technology markets
interpret and respond to their competitive environment (Thatchenkery et al., 2012;
Thatchenkery & Katila, 2021), noting that who complementors perceive as main competitors
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changes after antitrust. Antitrust cases and competition regulation across the world
(Hatmaker, 2022; Schechner & Mackrael, 2022) heighten the importance for the strategy
field to understand these issues.
RESEARCH BACKGROUND
Two streams of research are relevant for our research question. First, research on
competition and innovation explains why complementors invest (or do not) in response to
changing levels of competition from a dominant platform. Second, research on antitrust
covers interventions that seek to make industries more competitive and more innovative.
Competition and Innovation
There is a long-standing debate about the relationship between competition and
innovation (Katila & Chen, 2008; Chen et al., 2010; Thatchenkery and Katila, 2021). One
side argues that the two go hand in hand; that is, markets with less competition have low
incentives while markets with more competition have high incentives to innovate (Arrow,
1962). The logic here is that firms are pushed to pursue differentiation strategies when
competition pressure increases while the absence of competitive threat makes firms
complacent. The other side argues that innovation incentives are higher the more insulated
the firms are from competition. Here, insulation is thought to provide firms with the resources
and predictability to make innovation worthwhile (Schumpeter, 1942). We propose a more
granular approach to unpack the relationship (which has attracted much scholarly interest e.g.
Aghion et al., 2005) that incorporates the idea that how firms perceive the competitive
environment matters (Thatchenkery & Katila, 2021).
Our theoretical framework focuses on the contestability at the heart of this discussion
(Shapiro, 2012), arguing that an opportunity for profitable market-share grab (i.e.,
contestability) is the lever that spurs innovation: Firms will be more motivated to innovate the
more opportunity they perceive to achieve profitable sales. Contestability is key in platform
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settings, we argue, because the behaviors of platform owners strongly influence perceived
opportunities for market share gain across the ecosystem.
New and resource-constrained competitors are particularly likely to be incentivized if
they perceive contestability. Innovation often originates when a firm that does not currently
have a dominant position perceives that it can profit by differentiating from the dominant
players (Baker, 2007; Shapiro, 2012). These low-share firms eventually have a chance to be
market disruptors (Schumpeter, 1934; Aghion et al., 2013). In contrast, as Shapiro (2012)
notes, a high-share firm that perceives that it is not able to grow much even if it successfully
innovates has lower incentives to invest.
Because complementors in a platform setting innovate on top of the platform’s
technical infrastructure, dominant platforms strongly influence contestability and resulting
innovation incentives. For instance, if dominant platforms and their in-house complementors
control a large bulk of the customer base, rival complementors would lack prospects to gain
market share (Eisenmann et al., 2011). Once antitrust intervention limits the platform’s
ability to block competition, however, these incentives would likely change.
Prior literature provides further insight regarding how firms profit from innovation in
platform ecosystems. Because platforms must incentivize complementors to join, they often
share complementary assets that facilitate product development (Teece, 1986, 2018; Rietveld
et al., 2021).
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Restraining a dominant platform may reduce its motivation or ability to share
assets in this way. Thus, profit implications of antitrust may not be straightforward,
particularly for resource-constrained complementors.
Antitrust
Strategy research on antitrust is particularly relevant background for our research
question, which takes a firm-focused lens on policy interventions that aim to promote vigorous
4
Note that in a non-platform market, firms have an incentive to take ownership of complementary assets needed
to commercialize an innovation, not share them across the value chain.
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competition. Strategy work to-date has studied mostly low-tech industries and anti-competitive
practices that block “price competition,” including research on M&As where merging firms
would wield too much combined market power (e.g. Li & Agarwal, 2017), or collusion where
a group of participants use practices that eliminate competition (e.g. Mezias & Boyle, 2005).
Our focus is on another type of anti-competitive practice, in which a single actor—such
as a dominant platform—is accused of blocking (i.e. weakening or eliminating) competition. In
contrast to traditional antitrust, work in this stream—particularly on platforms—emphasizes
technology-based industries and “innovation competition” (Parker et al., 2020; Salop, 2021:
567). The intent of such antitrust intervention is to unblock competition and level the playing
field, thus expanding opportunities for innovation (Pitofsky, 2001). Pricing concerns are less
relevant than innovation and consumer choice (Coyle, 2019). Another key difference is the
reach of anti-competitive practices: it is ecosystem-wide, as platform dominance can pull
innovation incentives down not only in the platform market but also in adjacent complementor
markets. The concern, as Shapiro (2012: 370) explains it, is that blocking by a dominant
platform will “harm by retarding innovation” in the entire ecosystem.
Strategy research in this area has emerged relatively recently. Conceptual research on
antitrust remedies against dominant platforms (e.g. Jacobides & Lianos, 2021; Kühn & Van
Reenen, 2007) often focuses on rival platform owners. Another stream asks what happens to
complementor entries and exits when platform dominance increases (Zhu & Liu, 2018; Wen
& Zhu, 2019). Altogether, prior work shows that platform dominance tends to limit
competition and change the ecosystem. Research on the reverse scenario—what happens to
ecosystems when dominant platforms can no longer block competition—remains sparse,
particularly regarding complementors. It is an open question whether weakening a dominant
platform would bring back innovation and level the playing field for profits among
complementors. The hypotheses that follow examine this question.
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HYPOTHESES
Building on a theoretical framework of competition and innovation, we examine how
innovation incentives and profit of complementors change when a dominant platform’s
ability to block competition is reduced via antitrust intervention.
In H1a we propose that the prospect of profitable sales motivates complementors to
innovate and that the higher the prospect, the more incentivized the complementor will be.
Before intervention, complementors often perceive that profitable sales are blocked by the
dominant platform’s anticompetitive practices that grant it cost and visibility advantages.
With those practices in place, any innovation by complementors is at high risk of being
sidelined, even if their product is superior (Wang & Shaver, 2016; Wen & Zhu, 2019).
Complementors’ incentives to innovate are thus muted. Antitrust intervenes by unblocking
competition. After the intervention, the more the complementors perceive that innovation
investments are viable again, the more likely they are to invest in R&D.
We argue that the increase in complementors’ incentives will be more pronounced in
markets where the platform-complementor has high market share. The higher its market
share, the higher the perceived contestability of the market after the antitrust intervention.
H1a. Increases in competitive pressure against a dominant platform through antitrust
drive increases in complementor innovation: In particular, the higher the platform-
complementor’s share in a market, the greater the antitrust intervention’s positive impact
on complementor innovation in the market.
While complementors are in general more incentivized to innovate post intervention, in H1b
we propose that there are likely differences across complementors that also depend on their
own pre-intervention market share. High-market-share complementors, we propose, have
lower incentives because they likely have less room to grow, whereas low-market-share
complementors have more room to grow and thus higher incentives. The latter may also
believe that, due to their smaller size, they are likelier to go unnoticed and avoid strong
9
pushback from other complementors. High-share complementors are more noticeable to
competitors and may even fear being next on the radar of antitrust authorities, decreasing
their incentives to compete aggressively (including through innovation). We propose,
H1b. Increases in competitive pressure against a dominant platform have a more positive
impact on a low-market-share (vs high-market-share) complementor’s innovation.
Even though complementors may perceive a prospect for profitable sales (H1), in H2 we ask
whether they will actually realize the profits that motivated them to invest in the first place.
Access to complementary assets (e.g., development assets) likely influences whether
complementors can create value from their innovations (Teece, 2018). The answer is
complicated by the fact that pre-intervention practices may have indirectly benefited
resource-constrained complementors. For instance, if the platform-complementor had
significant market share, it was likely seen as a reliable alternative that built visibility for the
entire market, including for the rival complementors. It is also likely that pre-antitrust,
platform-complementors with high market share were able to prevent “excess” competition
by steering complementors towards opportunities not already covered by others, leaving
enough market space for each (see Wen & Zhu, 2019). The platform’s gatekeeping policies
can also have acted as a useful disciplining force, selectively weeding out or promoting
offerings based on quality to the benefit of the ecosystem as a whole (Zhang et al., 2020;
Rietveld et al., 2021). If the platform-complementor had higher market share it was also
likely to have developed more of these specialized assets in the first place (from which it
directly benefitted in its own complementor role). Other pre-intervention benefits may have
included increasing compatibility and faster and more reliable access to end-users (Gavetti et
al., 2017; Wareham et al., 2014), which platforms may have provided to complementors to
improve ecosystem viability (Kapoor, 2018; Helfat & Raubitschek, 2018), thus lowering cost.
In H2a we propose that the higher the platform-complementor’s market share, the
more the antitrust intervention pulls down complementors’ profit in the market.
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Complementors likely underestimate the assets the platform has provided while also
overestimating their own ability to develop such assets themselves. Once the competitive
pressure intensifies, the platform will often be limited in its ability and incentive to provide
such benefits. The platform may now shift from developing shared assets to improving the
quality of its own complementor products. This effect may be more pronounced in markets
where the platform has higher market share and thus more to lose. As a result, rival
complementors may need to build many assets from scratch that they were previously
provided by the platform. The costly activities of building visibility and increasing sales will
also fall on them. All these costs, and the possibility that sales may also stagnate, risk hurting
the profitability of complementors post intervention, and these effects are larger the larger the
hole that the platform-complementor leaves in the market.
H2a. Increases in competitive pressure against a dominant platform through antitrust
drive decreases in complementor profit: In particular, the higher the platform-
complementor’s share in a market, the greater the antitrust intervention’s negative
impact on complementor profit in the market.
In H2b we again propose differences across complementors depending on their pre-
intervention market share. We expect high-market share complementors to weather change
better because they likely already have many of the complementary assets needed for
innovation in-house or are better positioned to develop them quickly and efficiently. Relative
to low-market-share complementors, these firms also have high market presence, so their
visibility is less likely to suffer as the platform weakens. Low-market-share complementors,
in contrast, have more likely relied on platform-provided assets and have yet to develop their
own replacement assets. Overall, we propose that the negative profit impact of the antitrust
intervention is likely amplified by the focal complementor’s market share: high-market-share
complementors are less negatively impacted, and low-share ones more negatively impacted.
We propose,
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H2b. Increases in competitive pressure against a dominant platform have a more
negative impact on a low-market share (vs high-market-share) complementor’s profit.
METHOD
Empirical Context: Enterprise Infrastructure Software
We tested the hypotheses in the enterprise infrastructure software ecosystem between 1998
and 2004, the three years before and after the Microsoft antitrust intervention. The dominant
enterprise platform
5
was Microsoft’s Windows Server Operating System. In this ecosystem,
Windows Server provided the hub and the essential technical foundation on which
complementors developed infrastructure applications that covered critical core backend IT
functions (Thatchenkery & Katila, 2021), as visualized in Figure 1. Microsoft is a dual
platform-complementor, offering both the platform and complementor products.
----Insert Figure 1 about here---
Enterprise infrastructure software is a particularly relevant context for several reasons.
Infrastructure was a large and growing industry with total U.S. sales of roughly $20 billion in
2000. While many user-facing markets were saturated, infrastructure markets featured room
for growth, and were often described as a “strategically important growth opportunity”
(Gartner, 2001). This ensured that competition and innovation decisions were important for
ecosystem firms and profitable market-share gain was possible. Second, complementor
markets were neither too concentrated nor too fragmented (Campbell-Kelly 2003), providing
rich but tractable variation across complementors in each market. Third, infrastructure
applications required compatibility with a platform (e.g., Windows Server, Linux, etc.), but
complementors sold and distributed directly to enterprise customers. As a result, sales and
5
In enterprise software, there are two distinct platforms: the user operating system (which runs user-facing
apps) and the enterprise server operating system (which runs infrastructure apps). The user platform was
dominated by Microsoft’s Windows operating system, which held 93% market share in 2001. The enterprise
platform was dominated by Windows Server, with 51% market share. In addition to Windows Server, the other
enterprise platforms were Linux (multiple vendors combining for 23%) and UNIX (multiple vendors combining
for 11%) (IDC, 2002). Altogether, Microsoft held a dominant position in both user and enterprise platforms.
12
profits were tied more directly to each complementor.
6
A core strength of our data is its comprehensive coverage of the entire population of
public U.S. firms in complementor markets, namely, the five infrastructure applications
markets as defined by the standard industry source Gartner Research: application integration
and developer tools that help different applications work together, database management that
helps store and manage data, network & system management used to manage the overall IT
system, and security that protects from attacks and manages access to the system within the
organization. Notably, Microsoft did not have high market share in every complementor
market, a fact which creates useful variation for our research design.
Competition Shock: Microsoft Antitrust Intervention
Microsoft’s alleged blocking of competition as a dominant enterprise platform—and
the antitrust remedies detailed below—provide an opportune setting to examine our research
question on how changes in competition change innovation and profit. The government’s
antitrust case focused on the “threat to future innovation” (Shapiro, 2012: 400; see also
Rubinfeld, 2020) as is typical of antitrust interventions against dominant technology
platforms. As the first major antitrust intervention against a U.S. software firm, U.S. v.
Microsoft was a shock to the ecosystem with participants finding it difficult to anticipate its
effects. Enterprise software did not receive nearly as much mainstream media attention or
scrutiny as user-facing software (i.e., the “browser war” against Netscape), which further
made antitrust effects harder to anticipate. As Microsoft’s “home” regulator, U.S. authorities
also had a wider and stronger array of remedies at their disposal than regulators elsewhere
(Fox, 2019), making the case a particularly strong intervention.
7
6
In contrast, in settings like Apple’s App Store or Google Play where the platform controls distribution, profit
impact may be harder to assess.
7
Legal scholars evaluated the consequences of specific clauses within the settlement (e.g., Page & Childers,
2007), but empirically grounded work on broader implications is scarce. Exceptions are Lerner (2001) on
allegations that Microsoft blocked innovation prior to the intervention and Genakos et al. (2018) on inter-
platform (consumer, enterprise) evidence of Microsoft’s incentives to restrict interoperability across platforms.
13
In the antitrust case, the U.S. Department of Justice alleged that Microsoft repeatedly
used its monopoly power in central platforms to block competition in complementor markets.
Two ways of blocking were central in enterprise infrastructure: alleged practices that
increased sales for Microsoft’s own complementors at the expense of rivals, and practices
that increased costs for rival complementors—together influencing complementors’
perceived prospects of profitable sales. Microsoft was accused of restricting access to
distribution channels (via bundling and exclusionary hardware ties) and of making it difficult
and costly for rivals to compete (via closed interfaces and switching costs),
8
as detailed in the
Online Appendix.
Sample Construction
We built a dataset of public U.S. firms in enterprise infrastructure software between 1998 and
2004, starting 3 years before and ending 3 years after the Microsoft antitrust settlement. We
selected 2001, the year of the settlement, as the year of intervention because, although there
was an initial ruling in 2000,
9
firms facing antitrust action in the U.S. do not have to comply
with a ruling while it is being appealed; thus there was no expected change in Microsoft’s
behavior in response to the 2000 ruling. The fact that this was the first major antitrust case in
software added further uncertainty regarding whether the ruling would be upheld. The 2001
settlement, in contrast, was binding on both parties and not subject to appeal or reversals. By
agreeing to the settlement, Microsoft publicly agreed to abide by its terms and change its
behavior.
We focused on public firms because enterprise customers require long-term support—
particularly for the core backend functions managed by infrastructure applications—and are
thus reluctant to take a chance on unproven young firms (Eisenmann et al., 2014). Partly as a
8
U.S. Department of Justice, US v. Microsoft: Plaintiff’s Findings of Fact, 1999.
9
The ruling was issued in 2000, but Microsoft immediately appealed, casting uncertainty over whether the
proposed penalties would actually be imposed.
14
consequence, enterprise software complementors tended to go public relatively early
compared to firms in other industries, which allowed us to capture the bulk of the industry
through public firms (Campbell-Kelly, 2003). As noted below, we also added private firm
data collected from Corptech, and report additional details below. Our analyses focused on
U.S. firms because the U.S. was the biggest market for infrastructure applications at the time
(Gartner, 2001) and because the antitrust intervention was focused on the U.S. market.
Because infrastructure software is not distinguished from other types of software in
standard industrial classifications, we took several steps to identify firms, triangulating
between multiple sources to improve coverage and create a comprehensive dataset. We
started by compiling a list of all public software firms in the United States. Consistent with
prior work (Thatchenkery & Katila, 2021), we began with firms classified under the SIC code
of “prepackaged software” 7372. Between 1998 and 2004, there were 886 public software
firms in the U.S. After excluding the 322 firms that developed products only for consumers
(to focus on enterprise), we compared the remaining firms’ product portfolios with Gartner
Research’s IT Glossary. We classified a firm as an infrastructure software company if most
of its product portfolio matched the Gartner keywords for infrastructure software
(Thatchenkery, 2017).
10
We triangulated this information with The Software Catalog (annual
listing of software products) and asked two industry experts to review the list.
Of the resulting 102 enterprise infrastructure software firms, we excluded 18 firms
that were not public for both the pre- and post-treatment periods. Because going public is a
milestone event that encourages focus on immediate profit rather than innovation (Bernstein,
2015), limiting the sample to firms that were public before and after treatment helps control
for alternative mechanisms that might change innovation and profit (results are consistent
when including the excluded firms). We also excluded 4 firms that were platform owners
10
We primarily relied on the 2001 version of the glossary, but also cross-referenced against categories found in
Gartner reports from earlier and later years in our sample time frame and found them to be consistent.
15
themselves to focus on the implications for purely complementor firms.
11
It is noteworthy that firm entry was rare (only four public firms entered the industry
between 2002 and 2004), and that there was little movement across the 5 markets, affecting
only 1.2% of observations. Our pre-match sample was 78 infrastructure applications firms.
Firms exhibited typical regional patterns for software, with 32% headquartered in the San
Francisco Bay, 10% in the Los Angeles area, and 9% in the Boston area.
Data Sources
Firms were classified into complementor markets using firm press releases (Thatchenkery,
2017) and categories from Gartner Research and Gartner Research’s IT Glossary (Pontikes,
2012). We consulted Gartner Research for market share data. Patent data were collected
using the NBER database (Hall, Jaffe, & Trajtenberg, 2001) and we added citations from the
USPTO. We collected firm data including R&D expenditures, firm size, IPO year, location,
and profits from Compustat, supplemented by SEC filings and CapitalIQ.
For sensitivity analyses, product data were collected through press releases
(Thatchenkery & Katila, 2021) in Factiva and LexisNexis and private firm data through
CorpTech and Crunchbase.
12
Press coverage and court documents, retrieved from Factiva,
LexisNexis, Westlaw, and U.S. government archives, provided qualitative data on the
antitrust case.
Research design
Using a difference-in-differences design, we exploited variation in Microsoft’s market
share across complementor markets to separate the treated from the control group. While
11
Results are robust to randomly assigning the dual platform-complementor firms to be either platform
(excluded from the sample) or complementor (included in the sample).
12
CorpTech directory—published from 1986 until 2004—provides detailed, yearly lists of private firms in our
market segments pre and post intervention. We triangulate CorpTech data with Crunchbase. Crunchbase
provides recent data and lists firm founding dates, allowing us to track new entries in detail, but it is limited for
a few reasons: (1) It was founded in 2007 and so data on firms in our time period is retrospective (in contrast,
CorpTech is a time capsule snapshot); (2) Crunchbase is a single snapshot of each firm’s activities, so we cannot
be sure that the markets listed for each firm are the same markets the firm was in during our study period; (3)
because it is crowdsourced, Crunchbase’s accuracy—particularly for inactive firms—may be limited.
16
Microsoft is a dual platform-complementor in all five complementor markets, its market
share varied. As the “treated group”, we used firms in markets where Microsoft had a strong
market presence as defined by Gartner (detailed below), where the antitrust intervention
could foster a significant market share transfer to rival complementors (Shapiro, 2012). In
contrast, the “control group” comprised firms in markets where Microsoft had only a
marginal market presence. While we used a binary treatment for our main analysis, we also
ran a “continuous treatment” (variable with differing treatment intensity) design for
robustness (Angrist & Pischke, 2009: 234), with consistent results (Table A1).
At the time of the case, all five infrastructure applications markets had 2-4 of what
Gartner called “leader” firms with at least 10% market share each (Gartner, 2001). Microsoft
was one such firm in two markets, with 16% market share in database management (#3
vendor) and 15% market share in developer tools (#2 vendor). Firms in these two markets—
where platform-complementor had a high market share—are the treated group (labeled as
rival complementors). In contrast, Microsoft held a substantially weaker or even insignificant
position in application integration (0.3% market share), network & system management
(1.6% market share), and security (<1% market share). Firms in those markets are the control
group (labeled as non-rival complementors).
Measures
Dependent variables. We measured complementor innovation by yearly counts of
patents each firm had applied for (and later received). Patents are a particularly appropriate
measure of innovation because each patent is novel, non-obvious and useful, describing both
a problem and its solution (Katila, 2002; Ziedonis, 2008). Each patent thus identifies new
problem-solving efforts that are added into the industry to capture market share. Patenting is
also standard in software during our study period from the mid-1990s to mid-2010s
(Cockburn & MacGarvie, 2011). The USPTO released official guidelines for software
17
patenting in 1996, and software patents’ validity was confirmed by the 1998 US Court of
Appeals State Street decision. The U.S. Supreme Court’s Alice Corp decision in 2014
reversed this trend, introducing stricter criteria. Patents were thus a highly relevant measure
of software innovation during our period. The fact that innovation in infrastructure software
centered on performance and functionality—rather than the more ambiguous features
(aesthetics, fads) often privileged in user-facing apps—also made tracking innovation by
patents feasible. We also used yearly R&D expenditures and citation-weighted patents as
alternative dependent variables, with consistent results (Table A2). We collected ten years of
citation data from the USPTO.
Consistent with prior work on competition in the software industry, we measured
complementor profit as return on sales annually for each firm (Suarez, Cusumano, & Kahl,
2013; Young, Smith, & Grimm, 1996). ROS is more appropriate than alternatives such as
return on assets because software firms rely primarily on intangible assets (e.g., human
capital) and because software firms tend to reinvest their profits to continuously grow the
business. We also measured profit as net income (logged) and superior profits (ROS at least
double the industry average), with consistent results (Table A2), and split profit into value
creation and asset utilization components in mechanism tests.
Independent variables. Because we ran difference-in-differences, the explanatory
variable of interest is an interaction between treated group and post-treatment period. We
measured rival complementor (treated group) as a binary indicator set to 1 if the firm
competed in a complementor market in which Microsoft’s in-house complementor had high
market share (developer tools, database management) and 0 otherwise.
13
We measured post-
intervention (post-treatment period) as a binary indicator set to 1 if the year was 2002-2004.
13
Multimarket competition is not common in infrastructure software. If the firm operated in both treated and
control markets (only a handful of firms), we assigned it to (a) treated only because the firm faced strong
competition with Microsoft complementors at least in some markets, (b) in robustness tests randomly assigned
the firm to either treated or control, and (c) dropped these firms altogether. Results were robust to alternatives.
18
We measured low-market-share complementor as a binary indicator set to 1 if the firm had
less than 10% market share prior to the intervention and 0 otherwise.
Control variables. Because scale matters in software innovation (Campbell-Kelly,
2003), with product visibility and bargaining power accruing to firms with higher market
footprint, we controlled for size by annual revenue in millions of U.S. dollars, adjusted for
inflation and logged to correct for skew. We also measured size as number of employees, with
consistent results (Table A3). Because greater investment in R&D is likely to influence
patents and possibly profit, we controlled for R&D intensity, measured by dividing R&D
expenditure by total revenue annually. Results using R&D expenditures adjusted for inflation
and logged to correct for skew were consistent (Table A3).
Because firms that have been public for longer may face increased pressure to
prioritize short-term financial returns at the expense of innovation (Bernstein, 2015), and may
also be more sensitive to the potential exercise of market power (Zhang & Gimeno, 2010),
we controlled for years public as the logged number of years since the firm’s IPO. We
controlled for acquisitions, measured as a yearly count, because acquisitions by the focal firm
may give the firm more “raw material” for innovation (Ahuja & Katila, 2001) but also
increase costs related to integration (Kim & Finkelstein, 2009).
We controlled for any unobserved market effects with fixed effects for each of the five
complementor markets. We controlled for three geographical regions with high numbers of
enterprise software firms—San Francisco, Boston, and Los Angeles—because rivalry and
knowledge spillovers within a region can impact innovation and profits (Owen-Smith &
Powell, 2004). Region effects dropped out from fixed effects regressions but were included in
random effects regressions. Macroeconomic variation was controlled with year effects.
Matching variables. To improve comparability of treated and control firms, as
19
detailed below, we used propensity score matching. We matched on geographic region,
14
size, IPO year, R&D intensity, and pre-sample patents (when predicting innovation) or pre-
sample ROS (when predicting profit).
15
Except for pre-sample variables, which were
averaged from 1995 to 1997, we used three-year averages of pre-treatment values (i.e., 1998-
2000) to ensure that the matching was not influenced by the treatment itself (Flammer, 2015).
The matched sample was 374 firm-years (66 firms).
Statistical Method: Difference-in-Differences
Ideally, we would randomly assign complementors to markets where a platform
“blocked” competition versus not, observing differences in innovation and profits after the
block is lifted. Using observational data, however, we need to account for selection bias that
could arise from unobserved factors associated with complementor firms competing in
specific markets and with firm performance. Complementors may have, for example, avoided
markets where Microsoft was a substantial threat because they did not have the resources to
compete. Complementors may also have selected into Microsoft’s strongholds because they
were following the lead of the platform firm. Our results would thus be driven by differences
in firm characteristics, not competition. We address this possible bias with difference-in-
differences, as well as matching, fixed effects, and firm heterogeneity controls.
We use a difference-in-differences research design (Abadie, 2005), which allows us to
correct for selection bias when the treated and control groups are not a perfect match in the
outcome variables but the unobserved differences between the two groups remain the same
over time (parallel trends assumption). We first calculate the differences in outcomes for
treated firms and the untreated comparison group of control firms before versus after
14
We matched for whether the firm was headquartered in regions with high numbers of enterprise software
firms, using three separate dummy variables for San Francisco, Boston, and Los Angeles. Results are robust to
exact hand matching of treated firms to control firms located in the same or adjacent state (Table A4).
15
Pre-sample patents and pre-sample profit were highly correlated with firm size and R&D intensity, so we used
them as alternative matching criteria in a robustness check, with consistent results.
20
treatment and then the difference in those two numbers. Formally,
𝐷𝑉
!" = $𝛽#+ 𝛽$𝑅𝑖𝑣𝑎𝑙𝐶𝑜𝑚𝑝𝑙𝑒𝑚𝑒𝑛𝑡𝑜𝑟!+ 𝛽%𝑃𝑜𝑠𝑡𝐼𝑛𝑡𝑒𝑟𝑣𝑒𝑛𝑡𝑖𝑜𝑛"+ 𝛽&𝑃𝑜𝑠𝑡𝐼𝑛𝑡𝑒𝑟𝑣𝑒𝑛𝑡𝑖𝑜𝑛"$× $ 𝑅𝑖𝑣𝑎𝑙𝐶𝑜𝑚𝑝𝑙𝑒𝑚𝑒𝑛𝑡𝑜𝑟!+𝛾𝐶!" +$ 𝜖!"
where
𝐶!"
represents control variables and
𝜖!"
is the error term.
𝛽#
is the coefficient on the
difference-in-differences estimator, which captures the effect of the antitrust intervention on
the treated group of complementors (see Bertrand, Duflo, & Mullainathan, 2004).
We ran a difference-in-differences analysis using panel regressions with firm fixed
effects and standard errors clustered at the firm level.
16
Fixed effects models help control for
any baseline (i.e., time-invariant) heterogeneity between firms, and were preferred over
random effects by a Hausman test for both dependent variables (Hausman, 1978).
For the models predicting innovation, a count variable, we used fixed effects Poisson
regressions. A Poisson estimator is preferred to a log-OLS estimator, for two reasons. First,
applying a log-OLS specification to count data can produce biased estimates, especially in the
presence of heteroskedasticity (O’Hara & Kotze, 2010). Second, Poisson outperforms log-
OLS when the data contain a substantial number of zeroes (Silva & Tenreyro, 2011; Burtch et
al., 2018), as is the case with a number of non-patenting firms in our sample.
For the models predicting profit, we used a fixed effects panel OLS regression. To
avoid collinearity with firm and year fixed effects (Friebel et al., 2017), we included only the
Post-Intervention x Rival Complementor interaction in fixed effects regressions. Consistent
with prior work, our estimation period is three years before and after the 2001 intervention
(Flammer, 2015). Results are robust to five years before and after, and to other temporal
dynamics including short vs long term effects. Robustness checks are summarized in table 4.
We drew from Angrist and Pischke (2009) and Cunningham (2021), as well as recent
work by Roth (2022) to validate the difference-in-differences design. Specifically, we
verified treatment relevance and validity (parallel trends).
16
Results are consistent when we cluster at the market level in a single-market complementor sample (Cameron
& Miller, 2015, see Table A3)
21
Validation of the research design: Relevance of treatment
Treatment in a difference-in-differences design must be relevant, that is, trigger actual
changes in the treated group. If the treatment is not relevant, then any observed difference
between the treated and control group would be a statistical artifact and not a genuine
response to the intervention.
In our study, a relevant antitrust intervention should constrain the platform’s behavior
and change treated firms’ perceptions about sales prospects. Notably, not all antitrust
interventions achieve this outcome, as in the case of a 1956 intervention affecting telecom
monopolist AT&T (Bell Labs) (Watzinger et al., 2020).
To examine the relevance of the Microsoft case, we first obtained evidence regarding
changes in platform behavior. Anecdotal evidence suggests that there indeed was a noticeable
change in Microsoft’s behavior in treated markets, for instance, that it “made Microsoft’s
leaders skittish about bundling” (Rivkin & Van Den Steen, 2009). Data on complementor
markets suggests a similar conclusion: Microsoft’s growth slowed particularly in treated
markets (average post-intervention growth rate of 5.4% in treated versus 19.3% in control
markets), indicating that Microsoft was newly constrained in exploiting its market power
against the treated group (Gartner, 2005). In server operating systems (the platform market),
Microsoft’s growth also stalled after the intervention, and Linux became an increasingly
popular alternative, suggesting the intervention may have helped preclude a winner-take-all
outcome (Schilling, 2002). Yearly market research estimates put Microsoft at 45-60% market
share in the enterprise server platform post-intervention, a sharp contrast to its 85-95% share
in the user platform (IDC, 2019). Bill Gates, Microsoft’s CEO at the time, repeatedly stated
that “there’s no doubt the antitrust lawsuit was bad for Microsoft” (Novet, 2019).
A related point is whether complementors paid attention to changes in the platform’s
behavior. To obtain systematic evidence on perceptions of competition (Thatchenkery &
22
Katila, 2021), we studied the lists of competitors in complementors’ 10-Ks. In the three years
leading up to the intervention, 91% of the treated firms listed Microsoft as a competitive threat
while only 66% of the controls did so. In the three years after the intervention, the proportion
of treated firms listing Microsoft dropped to 66%, compared to 60% among the control firms.
The way treated firms described Microsoft also changed. In its 1998 10-K, treated firm
Borland Software (developer tools) identified Microsoft as a threat because, in addition to
directly competing in developer tools, it also made “operating environments.” In 2003,
however, Microsoft is simply noted as a direct competitor, with no mention of its platform
ownership. Thus, there is significant evidence that (1) Microsoft was perceived as more of a
competitive threat by treated firms compared to control firms and (2) that perceptions
substantially changed following the antitrust intervention.
To corroborate the logic that low-share complementors drive the results (H1b, H2b), we
examined how perceptions of competitive pressure by low vs high market-share firms differed.
As expected, the number of treated low market-share complementors listing Microsoft as a
competitor decreased from 94% prior to the intervention to 61% after. In contrast, this number
among treated high-market-share complementors did not change after the intervention
(remaining at 80%). Thus, while high-share complementors did not change their perceptions of
the competitive threat posed by Microsoft, low-share firms did, consistent with our theoretical
predictions.
As a final check on relevance, following Mahmood and colleagues (2017) and Burtch
and colleagues (2019), we tested random implementation of treatment, in which we
randomized assignment to treatment for each firm in our sample. There is no effect of random
implementation (Table A1), providing further confidence in our results.
Validation of the research design: Parallel trends
A key assumption of the difference-in-differences design is that the treated and control
23
groups would have experienced parallel trends absent the treatment (Abadie, 2005). This
assumption holds when (1) the treatment is exogenous, (2) the dynamics of the treated vs
control group are comparable pre-treatment (i.e., the control group “approximates the traveling
path of the treated group”), and (3) the differences between the control and the counterfactual
treated group remain stable post treatment (Cunningham, 2021: 422).
Exogeneity of treatment. The intuition behind the exogeneity assumption is that if
treatment is endogenous, the treated group would have diverged in the absence of
(independent of) treatment, violating the parallel trends assumption (Cunningham, 2021). In
our case, if another variable influences both a firm’s presence in treated markets and its
innovation (or profit), then the observed difference between the treated and control groups
could be driven by something other than the treatment. While we cannot conclusively prove
that treatment is exogenous, we can rule out sources of endogeneity.
We first examined whether some markets were given special attention by Microsoft
(and in turn more likely to be treated) based on expected gains. If this were the case, the
treated vs control groups would respond differently not because of treatment but because of
selection bias (Callaway, Goodman-Bacon, & Sant’Anna, 2021). For example, if Microsoft
invested more in treated markets because these markets were seen as technically more
promising, that could conflate treatment with outcomes. However, on average, pre-
intervention patenting was in fact moderately higher in control markets (where complementor
firms averaged 4.9 patents/year) compared to treated markets (3.4 patents/year), which
suggests that control markets were possibly seen as more promising. The matching algorithm
also ensures that the control group is very similar to the treated group in patents and R&D
intensity (Table A5), which alleviates the concern. Second, if the treated markets were in
general just better markets (independent of innovation), we would not expect results to differ
for (and originate from) low vs high market share firms (H1b, H2b).
24
We also ruled out influences of changes in the competitive environment of each
market (i.e., market concentration) that may have coincided with the intervention and created
endogeneity. Although our extensive search of case evidence and industry material did not
suggest this, highly concentrated market segments could have been targeted by regulators, or
innovation incentives of complementors could have changed with shifts in market
concentration. This seems unlikely for several reasons, however. First, market concentration
did not systematically differ nor change differently in treated versus control markets.
17
Second, models where we control for market concentration (HHI) and the number of
competitors in the firm’s markets are consistent with our original findings (Table A3).
Comparable dynamics in the pre-treatment period. Unlike RCT studies (in which
covariate balancing is often visualized), the difference-in-differences method does not require
the assumption that the treated and control groups are similar in covariates. Rather, what
matters for validity is that the covariate dynamics of the two groups are comparable in the pre-
treatment period (parallel trends), and that how the groups differ from each other (except for
the treatment) remains stable over time. While it is not possible to prove conclusively that
parallel trends exist pre-treatment, we follow the best practice of evaluating whether the
parallel trends assumption is likely to hold for our study. We provide evidence through
visualizing raw data, through an event study, and an “honest” pre-trends test.
We first simply “show the raw data” (Cunningham, 2021: 426) as a precursor to more
formal analysis of parallel trends (Wing et al., 2018). We plotted yearly means of treated vs
control firms’ innovation in Figure 2 and profits in Figure 3. Both provide supportive
evidence of parallel trends. Prior to treatment, the treated and control group trends were
similar (i.e., roughly parallel). Post-treatment, they diverge.
We then probed the parallel trends assumption with an event study (Cunningham,
17
At the time of the intervention, two markets (one treated, one control) met the typical FTC benchmark for
“high concentration” (HHI > 2500); the other three markets were mildly concentrated (HHIs of 950-1200).
25
2021: 452; Binder, 1998). Event studies track whether the treated vs control groups’
dynamics are comparable in the pre-treatment period by including anticipatory effects (leads)
and post-treatment effects (lags) in a regression (see Table A1 Models 4 and 8), visualized in
Figures 4-5. As expected, placebo pre-treatment leads are not statistically different from zero
prior to treatment, suggesting that the treated and control groups were on parallel trends prior
to treatment, only differing from zero after the intervention. A test of whether the pre-
treatment coefficients jointly differ from zero (dqd in Stata; Mora & Reggio, 2015) provides
further support: the p-value for innovation is 0.52 and for profit is 0.81, indicating that
violation of parallel trends was not detected. Taken together, the event study analyses
increase our confidence in the parallel trends assumption.
--- Insert figures 2-3 and figures 4-5 about here ---
Third, we implemented the “honest” pre-trends test by Roth (2022), which probes
whether the event study may lack statistical power to detect a violation of the parallel trends
assumption. To implement the test, we impute event study estimation results (coefficients and
variance-covariance matrix) into the pretrends package in R (Roth, 2022) and calculate the
likelihood of observing the event study coefficients if parallel trends were violated vs. not.
The resulting small likelihood ratios (0.088 for innovation and 0.065 for profit) indicate that
lack of statistical power is not likely to be an issue, providing further confidence that the
parallel trends assumption likely holds for our data.
Stable groups. Another significant assumption of the difference-in-differences design
is that the parallel trends assumption holds post treatment for the counterfactual treated group
and for the control group. We first confirmed that there was no significant migration between
treated and control groups (Abadie, 2005). At the end of our period (in 2003 and 2004,
respectively), two firms that had previously been in control markets entered a treated market.
We included and excluded these firms with no change in results. As noted below, entry and
26
exit of public firms was also remarkably nonexistent, further validating the research design.
It is also possible to apply matching (as described above), which allows us to restrict to
a set of observations in the control group for which the parallel trends assumption is more
likely to hold (Wing et al., 2018, p. 458). The intuition is that this assumption “may hold in a
restricted sample… even if it does not hold across all groups and times” (Wing et al., 2018).
Consistency of results with and without matching, as described below, provides further
confidence in our study design.
Finally, anticipation effects, or repeat or reversed treatments, could contaminate
treatment and the stable groups assumption, but neither seem present during our study period.
If firms anticipate the intervention then they may start to change their behavior beforehand,
which would make our results spurious (Wing et al., 2018). However, the intervention was
unprecedented within the software industry (Rubinfeld, 2020), making its effects difficult to
anticipate. Event study analyses with non-significant lead year coefficients (Table A1)
provide systematic confirmation. We also found that no other antitrust interventions took
place in the market during the study period, so repeat treatments are an unlikely concern.
Finally, settlement is particularly attractive as a treatment because it was binding for both
parties and rules out reversals through appeal.
RESULTS
Descriptive statistics are reported in Table 1. Complementor firms in infrastructure
software produced roughly 5-6 patents per year on average. Average return on sales during
the study time period (1998-2004) is -0.27, though the standard deviation is quite large
(2.19).
18
Correlations among independent variables are mostly low, and variance inflation
factors (VIFs) are under the recommended cutoff of 5 (years public is the only exception with
VIF of 9.24). Because VIFs are a sufficient but not a necessary indicator for multicollinearity,
18
The unexpectedly low profitability of enterprise software is consistent with observations of the volatility of
the software industry in general during the sample time frame.
27
we also randomly estimated subsets of the study sample by dropping one year at a time
(Echambadi, Campbell, & Agarwal, 2006), as well as by both including and excluding years
public and size variables. Results were consistent (Table A3), indicating that coefficients are
stable.
Regression Analysis: Main Results
Hypothesis testing. Table 2 and Table 3 report difference-in-differences results for
innovation and profit, respectively. The tables first report results using the full, unmatched
sample (Models 1-2) and then add matching (Models 3-4). Unmatched results are highly
consistent with those using the matched sample, providing further confidence in our research
design.
19
---Insert tables 2 and 3 about here---
Hypothesis 1a predicted that the treated group of rival complementors (i.e.,
complementors that operated in Microsoft’s pre-intervention strongholds) would be more
strongly impacted by the intervention and thus innovate more than the control group of non-
rival complementors. The difference-in-differences estimator is positive (β=0.53, p=.000) in
table 3. The treated firms introduced an average of 4.2 more patents yearly relative to
controls, supporting H1a.
Hypothesis 2a predicted that the profit of treated rival complementors would sink
after the intervention. The difference-in-differences estimator is negative (β=-0.58, p=.01).
Treated complementors experienced an average drop of 9.1 percentage points in ROS
compared to control firms.
In H1b and H2b we argued that results would be particularly driven by low-share
rivals that were most aggressively in pursuit of new sales that were previously blocked. To
19
As Angrist and Pischke (2009) note, because matching and control variables are alternatives in a regression
setting, we expect regressions with and without matching to produce highly consistent results; however, the
exact magnitude of the estimated treatment effect may differ. Our results are consistent with the expectation.
28
contrast low vs high share firms, we followed best practice from Kapoor and Furr (2015) to
compare split samples (Kapoor & Furr, 2015: 429; Lee, Hoetker & Qualls, 2015),
distinguishing low-market-share (<10%) complementors from the high-share ones (tables 2-
3, Models 5-6). For innovation, the difference-in-differences estimator is positive for the low
market share sample (β=0.45, p=.01) but indistinguishable from zero for high-market-share
firms (β= -0.02 p=.90), supporting H1b. We observe a similar, albeit less dramatic, pattern
for profit (H2b) (β= -0.39, p=.08 for low share; β=-0.56, p=.35 for high share).
To test the moderating hypotheses more directly, we tested for differences across the
split sample regressions. Ideally we would run a Wald test, but the pre-requisite of equal
unobserved heterogeneity (Lee et al., 2015) was not fulfilled. We thus followed standard
practice and ran a three-way interaction (Table A6) and event study, similar to a triple-
differences design (fig. A2; see Wing et al., 2018).
20
These additional tests provide
confirmation for innovation but do not display as clear a pattern for profit. Overall, we find
strong support for H1a and H1b (antitrust pushes up innovation incentives, particularly of
low-share firms) and for H2a (antitrust pulls down profit). We find tentative but not as strong
support for H2b’s claim that low-share firm profit was particularly affected.
Omitted variable bias. To investigate the sensitivity of our results to omitted
variable bias, we followed Frank (2000) and calculated how much bias needs to be present to
invalidate our results, in two ways. First, we calculated the impact threshold of a confounding
variable (ITCV), which tells us how strongly correlated a hypothetical omitted confounding
variable would need to be to invalidate our results (Frank, 2000). ITCV is 0.04 for
innovation and -0.11 for profit. In other words, to overturn the results, partial correlations
between the difference-in-difference estimator, the dependent variable, and the omitted
20
We plot event study charts following the template of Dranove, Garthwaite, & Hermosilla (2021) in figure A2.
The pattern for low-share firms mirrors that seen in the full sample: coefficients are statistically insignificant
prior to treatment and only diverge from 0 after treatment, as expected. High-share firms do not have this clear
pattern, further providing confidence that the low-share firms are the ones driving the results.
29
confounding variable would have to be above 0.20 (=√|0.04|) for innovation and above 0.33
(=√|-0.11|) for profit. Using current control variables as a yardstick (Larcker & Rusticus,
2010; Busenbark et al., 2022), any hypothetical omitted variable would thus need to have a
larger impact than any of our (highly influential, “standard”) controls to overturn the results.
It seems unlikely that an omitted variable would cross these thresholds.
Second, we calculated robustness of inference to replacement (RIR) (Frank, 2000)
defined as the percentage of observations for which the observed treatment effect would need
to be driven entirely by an omitted variable, not by the treatment, to invalidate the findings.
Interpretation of the RIRs is “grounded in logical intuition, such that scholars typically
determine whether the number of requisite overturned treatment cases appears reasonable”
(Busenbark et al., 2022: 44). In our data, 23% of the treatment cases for innovation and 35%
of cases for profit would need to be entirely overturned. These numbers are much higher than
thresholds accepted in prior work (e.g. Busenbark et al., 2017). Overall, our ITCV and RIR
analyses indicate that it is unlikely that an omitted variable is driving the results.
We ran a battery of additional tests for statistical robustness and to rule out alternative
explanations. Tests are summarized in Table 4 and reported in detail in the online appendix.
--- Insert Table 4 about here --
Regression Analysis: Mechanism Tests
We ran several tests to probe the proposed theoretical mechanisms underlying our
hypothesized effects on innovation and profits to further rule out that our results could be
spurious.
Innovation: Variety increases. In our theoretical framework, we argued that treated
(as opposed to control) complementors were more motivated to innovate because they saw
opportunities to pursue profitable sales increases in the recently opened space. We probed
this underlying mechanism in several ways. First, we parsed shifts in patenting within the
30
very limited number of complementors operating in both treated and control markets. Prior to
the intervention (1998-2000), among firms that were simultaneously in treated and control
markets, about 45% of patents were in treated and 55% were in control markets. After the
intervention (2002-2004), for the same firms, 68% of patents were in treated and 32% of
patents were in control markets, pointing to a shift in innovative effort towards the treated
markets, with more opportunity, as expected.
Next, we examined number of hits and flops, defined as patents with citations in the
top (or bottom) quartile of the industry (Ahuja & Lampert, 2001). If our arguments held, we
would expect treated firms’ variability in patents—mixture of hits and flops—to increase
after antitrust as they engaged in a variety of search approaches to pursue market share. This
is indeed what we saw (Table A7), driven by low-market-share complementors. Results using
superior (measured as patent output above the 95th percentile) and citation-weighted patents
were consistent (Table A2).
Third, we examined whether antitrust intervention merely prompted treated firms to
quickly file relatively low-quality patent applications, given reduced IP threat from the
platform firm. However, results were consistent to using both citation-weighted and
unweighted patent counts (Table A2), supporting that patents truly reflected innovation.
Profit: Complementary assets. We theorized that changes in profit were related to
treated firms’ (in)ability to capture value through complementary assets (e.g., in development
assets), rather than changes in internal efficiency. We collected both quantitative and
qualitative data in support.
We first gathered anecdotal evidence from the antitrust case documents and
contemporary news articles. If changes in access to complementary assets explained the
profit declines, as we have argued, we would expect Microsoft’s inclination to provide these
assets to have dropped following the intervention. Qualitative evidence provides support.
31
While Microsoft continued to provide essential assets such as software development kits and
was forced by the intervention to open its APIs, there is evidence that it was less inclined to
go “above and beyond” following the intervention. The most prominent example was
Microsoft’s introduction of a proprietary implementation of Java in 1997. Microsoft Java
provided several benefits to complementors and won awards for reliability and customer
support (Neffenger, 1998), with PC Magazine calling it “the fastest and most reliable Java
implementation available” (PC Magazine, 1998). But the antitrust investigation suggested
that the implementation had involved a conscious effort to “kill cross-platform Java.”
21
In the
wake of the investigation, Microsoft decided to phase out its proprietary version of Java,
despite the benefits it provided complementors and their disappointment at its loss. Gartner
Research noted: “For those who had any remaining hope that Microsoft would reverse
strategy and support Java, this announcement reinforces Gartner’s prediction that Microsoft
would completely abandon support” (Gartner, 2002). Microsoft did not make a second
attempt to introduce its own Java implementation until mid-2021. Thus, while Microsoft
continued to offer essential complementary assets, it was more cautious and reluctant
following the antitrust intervention.
To corroborate the mechanism that treated firms lost access to complementary assets
after antitrust, we followed Grullon and colleagues (2019) and decomposed profit into
external vs internal components. The firm’s external ability to capture value was measured
by price-cost margin (operating profits net of depreciation, divided by sales) and the firm’s
internal efficiency by asset utilization (total sales divided by total assets). If complementary
assets were the mechanism, we should see a drop in external value capture post intervention.
This is indeed what we saw (Table A8b).
22
21
U.S. Department of Justice, US v. Microsoft: Plaintiff’s Findings of Fact, 1999.
22
These findings were consistent with the other data patterns that we gathered, including that the treated firms
experienced lower sales growth but higher R&D expenditures compared to control firms post antitrust. Non-
32
To further probe the role of complementary assets, we examined changes in
commercialization of innovation, measured by product introductions (Katila et al., 2017;
Thatchenkery & Katila, 2021). Through an additional, painstaking effort we collected data on
3,684 new products by complementors. Positive results on patents but not commercial
(product) innovation (Table A8a) again pointed to external value capture, rather than internal
efficiency, as a likely explanation and indicated that the treated group did not proceed to
profit from their newly patented ideas, most likely because they lacked complementary assets
to commercialize. Split sample regressions (Kapoor & Furr, 2015) also revealed no difference
between low- versus high-market-share complementors (Table A8a), further supporting the
notion that even though low-share complementors increased technical innovation (patents),
they lacked the complementary assets to commercialize the innovation (products).
Third, we split firms by their pre-sample product introductions, expecting that product
leaders (firms in the upper quartiles) likely had relatively more complementary assets to
introduce products relative to product laggards (lower quartiles). Consistent with this
expectation, we found that product leaders in the treated group did not suffer a profit penalty
after the intervention, but that product laggards, who were less likely to have complementary
assets, did (Table A9).
Fourth, we expected negative profit effects to be transient rather than persistent as
treated firms likely eventually adapted to the new competitive environment by building
complementary assets (Sidak & Teece, 2009). Data provide support. The negative effect on
profit wanes over time. With a ten-year post-treatment window, profit for the treated group is
statistically indistinguishable from that of the control group (Table 5b). Results which
excluded short-term observations (i.e., 2002-2004) to focus on the medium and long term are
consistent. In contrast, the positive effect on innovation is robust over time (Table 5a).
R&D expenditures (e.g., operational, administrative costs) remained roughly equivalent. Controlling for firm’s
downstream capabilities (Ceccagnoli et al., 2012) (pre-sample products) did not change the results.
33
--- Insert Tables 5a, 5b about here --
Finally, entry by new firms could explain our results. Perhaps it was the entrant (not
the incumbent) complementors that generated innovation that customers valued (e.g.
Agarwal, Audretsch, & Sarkar, 2010). In fact, antitrust often encourages entry and innovation
by an entirely new set of firms (Parker et al., 2020). Although public-firm turnover was
almost non-existent during our study period, as noted above, private firm entries may have
increased. The data we compiled from CorpTech and Crunchbase, however, indicated that
entry rates dropped rather than increased in treated markets post intervention.
23
This pattern
is consistent with our argument that increased challenges to develop assets in the treated
markets were a more likely explanation, and entry a less likely explanation. Lack of access to
complementary assets may have pushed away rather than attracted entry in the short term.
These and other alternative explanations are summarized in Table 4. Overall, while our
results should be interpreted with caution (as is the case with any archival study), we present
a broad range of evidence consistent with the idea that antitrust intervention against a
dominant platform spurs innovation while dampening profits, particularly among low-
market-share complementors.
DISCUSSION
Most harmful of all is the message that Microsoft’s actions have conveyed to every enterprise with the
potential to innovate in the computer industry…[Microsoft] will use its prodigious market power and
immense profits to harm any firm that…could intensify competition against one of Microsoft’s core
products. –Thomas Penfield Jackson, U.S. District Judge, 1999 Findings of fact.
This study started with the question of what happens to ecosystems when antitrust
limits a dominant platform’s ability to block competition. We introduced a seeming tension:
Antitrust intervention against the platform may incentivize rival complementors to innovate
when they see potential for market share gain, but it can also harm complementors if they
23
Triangulation of CorpTech and Crunchbase records indicates that the population of private firms decreased in
infrastructure software between 1998 and 2004 and the decrease is higher in treated markets (-29.9%) compared
to control markets (- 20.3%). Overall, the population of firms in the treated group shrank relative to controls.
34
depend on the platform for complementary assets to innovate. We focused on a landmark
antitrust intervention in which dual platform-complementor Microsoft was accused of, and
subsequently prevented from, blocking competition in complementor markets. Using a novel
dataset on infrastructure software from 1998 to 2004, we showed how placing competitive
pressure on Microsoft resulted in a tension between innovation and profitability for
complementors. Following the intervention, innovation went up but profits went down—
particularly among low-market-share complementors. Implications, especially for the long-
standing debate about the relationship between competition and innovation (Katila & Chen,
2008; Thatchenkery & Katila, 2021), are discussed below.
Implications for Complementors
Innovative complementors are critical for platform ecosystem success. In fact, many
platforms enter complementor markets with homegrown products to jumpstart creativity and
to ensure availability of high-quality complementor products (Gawer & Henderson, 2007).
Yet our findings indicate that platform involvement in complementor markets can be a mixed
bag from a complementor perspective.
Our data and our interviews with industry informants suggest that complementors are
highly sensitive to the threat posed by a dominant platform. With the platform no longer in a
position to privilege its own offerings, complementor firms often rush to capture newly viable
opportunities, sparking an increase in innovation. At the same time, the ensuing “free-for-all”
makes it difficult to commercialize and profit from those innovations, as complementors—
especially low-market-share ones—may lack the discipline and guidance to select the right
opportunities and find themselves in a race to develop assets that were previously facilitated
by the dominant platform. Overall, intensifying the competitive pressures placed on the
platform can create a “wild west” with both benefits and drawbacks for complementors.
Our evidence suggested that the underlying reasons for the drift between innovation
35
and profit could be embedded in strategic capabilities. Complementors possibly received
more free assets from the platform than they might have realized. They seemed slower to
develop the assets themselves and thus profit from innovation, at least in the short term. The
answer to whether inducing competition through antitrust unblocks innovation opportunities
is thus ambiguous: antitrust intervention against a dominant platform does seem to spark
patenting but this does not automatically result in products that customers value. These
findings are particularly significant for regulatory changes that aim to re-invigorate
ecosystems by increasing the competitive pressure on dominant platforms.
Implications for Platform Ecosystems
Our findings also have broader implications for platform ecosystems (Kapoor &
Agarwal, 2017). Prior work has presented a tradeoff between ecosystem stability and
evolvability (Katila & Ahuja, 2002; Wareham et al, 2014; Parker & Van Alstyne, 2018;
Cennamo & Santaló, 2019). We find such a trade-off in the wake of a weakened platform:
innovation surges—particularly among low-market share complementors—but few firms
manage to profit. And while financial performance may not be a concern from the
policymaker’s perspective, it is important to individual firms and may affect the viability and
attractiveness of the ecosystem in the long run. Boosting competition by weakening a
dominant platform may have unexpectedly far-reaching and complex consequences. To
develop a healthy ecosystem in the long run, platform owners may want to resist the
temptation to keep complementors weak and instead help support their development to stand
on their own.
Does a platform need to be dominant for these effects to emerge? The answer may
depend on the industry sector. In enterprise infrastructure software—a non-faddish industry
focused on technical performance and functionality—platform dominance is likely more
sustaining. In consumer-facing industries, in contrast, consumer preferences are highly varied
36
and change rapidly, creating opportunities for smaller platforms to target a niche before
broadening to a mainstream audience (Rietveld & Eggers, 2018; Katila et al., 2022). If such a
pattern is typical in the industry, then platform dominance may be less relevant. Exploration
of how varying degrees of dominance, including changes in which platform is currently
dominant, influence complementor behavior is an interesting path for future work.
There are also implications for strategy research at the interface of public and private
sectors (see Rathje & Katila, 2021). Our unique contribution is to public-sector interventions
in private platform ecosystems. Prior strategy work on antitrust focused on less technology-
intensive industries with a vertical structure and cast doubt on whether antitrust can actually
stimulate competition and in turn innovation (Delmas et al., 2007; Madsen & Walker, 2017;
Kang, 2020). In contrast, our findings support the idea that public-sector interventions can
stimulate innovation. A key difference in our work is interdependence: complementors and
the platform need each other. The platform in particular has an incentive to support
complementors in ways that possibly initiate the effects we observed. But while the impact
on innovation may be positive, we also documented reductions in profit, which suggests that
public sector involvement may inhibit value capture in platform ecosystems.
Finally, our findings speak to digital platform antitrust by demonstrating a robust
positive relationship between an antitrust intervention against a dominant technology
platform and complementor innovation. This is highly relevant to the ongoing global debate
over big tech platforms and whether regulators should attempt to limit their influence. We
show that an antitrust remedy that is behavioral—rather than breaking up the dominant firm
into smaller pieces—can spark innovation by complementors. However, antitrust intervention
is not an automatic lever for more innovation. The intervention needs to actually change how
firms perceive their competitive environment (Cattani, Sands, Porac, & Greenberg, 2018;
Thatchenkery & Katila, 2021) and create incentives to reconsider a market that was
37
previously closed to them. Even then, building needed assets is likely to be costly and take
more time than anticipated. Furthermore, antitrust intervention did not enable entrepreneurial
entry. Rather, innovation increases were driven by incumbent complementors (particularly
low-market-share ones). The payoff for most complementors – particularly for
complementors that did not have high market share themselves - thus appears limited.
Overall, while policymakers may be satisfied with a boost in ecosystem innovation, the
observed reduction in profit suggests that, from the strategy perspective, antitrust intervention
may not have delivered for complementors.
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Journal of Economics & Management Strategy, 28, 23-28.
Zhu, F., & Liu, Q. (2018). Competing with complementors: An empirical look at Amazon.com.
Strategic Management Journal 39(10), 2618–2642.
Ziedonis R. 2008. Intellectual property and innovation. In Shane S. (Ed.), Handbook of technology
and innovation management: 295-333. Chichester, UK: Wiley.
42
Table 1. Descriptive statistics and correlations
Variable
Mean
SD
1
2
3
4
5
6
7
1
Complementor innovation (patents)
5.43
19.27
2
Complementor profit (ROS)
-0.27
2.19
0.04
3
Rival complementor
0.56
0.50
-0.11
-0.03
4
Post-intervention
0.43
0.50
0.09
0.001
0.01
5
Size (logged)
0.56
0.66
0.56
0.07
0.06
0.14
6
R&D intensity
0.38
0.99
-0.05
0.25
-0.03
-0.08
-0.17
7
Years public
6.44
4.15
0.25
0.002
0.02
0.30
0.41
-0.11
8
Acquisitions
0.06
0.24
0.14
0.02
0.004
0.02
0.31
-0.04
0.20
374 firm-years
Correlations above .10 are significant at p<.05
43
Table 2. Difference-in-differences: Fixed effects Poisson predicting complementor innovation (patents)
All complementors
Split samples
Unmatched Sample
Matched Sample
Low market share
High market share
1
2
3
4
5
6
Rival complementor x Post-intervention
0.51
0.53
0.45
-0.02
(0.000)
(0.000)
(0.01)
(0.90)
Controls
Size (logged)
1.21
1.33
2.60
2.63
-0.21
4.37
(0.000)
(0.000)
(0.000)
(0.000)
(0.25)
(0.000)
R&D intensity
0.17
-0.30
3.47
3.15
-0.30
10.34
(0.70)
(0.50)
(0.000)
(0.000)
(0.50)
(0.000)
Years public
-0.80
-0.96
-0.44
-0.70
-0.86
-0.42
(0.000)
(0.000)
(0.003)
(0.000)
(0.000)
(0.41)
Acquisitions
-0.48
-0.43
-0.59
-0.57
-0.72
-0.57
(0.000)
(0.000)
(0.000)
(0.000)
(0.000)
(0.000)
Firm fixed effects
Y
Y
Y
Y
Y
Y
Market fixed effects
Y
Y
Y
Y
Y
Y
Year fixed effects
Y
Y
Y
Y
Y
Y
Log likelihood
-612.80
-599.20
-797.40
-784.90
-529.78
-303.94
374 firm-years. P-values in parentheses (two-tailed tests). Split sample analyses are reported on the matched sample.
44
Table 3. Difference-in-differences: Fixed effects panel OLS predicting complementor profit (return on sales)
All complementors
Split samples
Unmatched Sample
Matched Sample
Low market share
High market share
1
2
3
4
5
6
Rival complementor x Post-intervention
-0.44
-0.58
-0.39
-0.56
(0.01)
(0.01)
(0.08)
(0.35)
Controls
Size (logged)
-0.06
-0.15
-0.04
-0.16
0.12
-0.44
(0.74)
(0.42)
(0.87)
(0.58)
(0.73)
(0.58)
R&D intensity
-0.03
-0.02
-0.02
-0.02
-0.02
0.69
(0.003)
(0.01)
(0.000)
(0.000)
(0.000)
(0.67)
Years public
0.19
0.21
0.23
0.29
0.25
-0.64
(0.28)
(0.23)
(0.33)
(0.24)
(0.27)
(0.26)
Acquisitions
0.13
0.11
0.39
0.38
0.24
0.41
(0.45)
(0.52)
(0.22)
(0.18)
(0.33)
(0.26)
Firm fixed effects
Y
Y
Y
Y
Y
Y
Market fixed effects
Y
Y
Y
Y
Y
Y
Year fixed effects
Y
Y
Y
Y
Y
Y
R-squared
0.19
0.21
0.27
0.30
0.26
0.19
374 firm-years. P-values in parentheses (two-tailed tests). Split sample analyses are reported on the matched sample.
45
Table 4. Summary of robustness checks
Concern
Test
Location
Statistical Robustness
Results are confounded by violation of parallel trends
Examine raw data and event studies, honest pre-trends
Figures 2-5, Table A1
Results are sensitive to omitted variable bias
Run ITCV and RIR analyses
Results: Omitted Variable Bias
Results are sensitive to length of pre- or post-treatment windows
Run results on alternate pre- and post-treatment windows
Table 5
Results are sensitive to serial correlation
Collapse pre- versus post-treatment, random implementation
Table A1
Results are sensitive to market share cutoff for treated versus control
Run continuous treatment variable
Table A1
Results are sensitive to non-patenting firms
Run zero-inflated Poisson and log-OLS
Table A2
Results are sensitive to operationalization of DV
Run alternate dependent variables
Table A2
Results are sensitive to choice of controls
Run alternate controls
Table A3
Results are sensitive to matching
Run results without matching and alternative matching schemes
Tables 2 and A4-A5
Alternative Explanations
Results are driven by dot-com crash
Run event study, examine diff-in-diff figures
Figures 2-3, Table A1
Results do not capture changes in variation in dependent variable
Run results predicting extreme outcomes
Table A2
Results are driven by multimarket contact
Run analyses only on single market firms
Table A3
Results are driven by statistical artifacts
Run mechanism tests for innovation and profit
Tables A7-A9
Results are driven by “baseline” rate of innovation
Control for pre-sample patenting
Table A10
46
Table 5a. Temporal dynamics: Fixed effects Poisson predicting complementor innovation (patents)
1996-2006
(Five years
pre- and post)
1998-2011
(Ten years post)
1998-2011
(Long term,
2002-2004
excluded)
1
2
3
Rival complementor x Post-intervention
0.91
0.85
1.08
(0.000)
(0.000)
(0.000)
Controls
Size (logged)
0.94
1.01
1.38
(0.000)
(0.000)
(0.000)
R&D intensity
-1.24
-2.89
3.10
(0.000)
(0.000)
(0.000)
Years public
-0.62
-0.06
-0.10
(0.000)
(0.53)
(0.31)
Acquisitions
-0.26
-0.25
-0.54
(0.000)
(0.000)
(0.000)
Firm fixed effects
Y
Y
Y
Market fixed effects
Y
Y
Y
Year fixed effects
Y
Y
Y
Log likelihood
-1236.47
-1757.58
-923.53
P-values in parentheses (two-tailed tests)
47
Table 5b. Temporal dynamics: Fixed effects panel OLS predicting complementor profit (return on sales)
1996-2006
(Five years
pre- and post)
1998-2011
(Ten years post)
1998-2011
(Long term,
2002-2004 excluded)
1
2
3
Rival complementor x Post-intervention
-0.68
-0.37
-0.05
(0.06)
(0.16)
(0.82)
Controls
Size (logged)
0.11
-0.37
-0.16
(0.76)
(0.37)
(0.48)
R&D intensity
-0.35
-0.36
-0.36
(0.000)
(0.000)
(0.000)
Years public
-0.07
-0.13
-0.23
(0.87)
(0.76)
(0.28)
Acquisitions
-0.02
0.10
-0.26
(0.91)
(0.35)
(0.22)
Firm fixed effects
Y
Y
Y
Market fixed effects
Y
Y
Y
Year fixed effects
Y
Y
Y
R-squared
0.48
0.47
0.47
P-values in parentheses (two-tailed tests)
Figure 1. Structure of Enterprise Infrastructure Software
Complementors
Micros oft Windows Server Oper ating System
Database
Manag ement
Network &
System
Management
Security
Developer Tools Application
Integration
Rival Complementors (Treated Group)
Non-Rival C omplementors (Control Gr oup)
Dominant platform
48
Figure 2. Visualization of trends using count measure of complementor Figure 3. Visualization of trends using ROS measure of complementor
innovation profit
Yearly means of the dependent variable in treated versus control groups
Figure 4. Event study: Estimates of antitrust intervention’s effects Figure 5. Event study: Estimates of antitrust intervention’s effects
on complementor innovation using leads and lags on complementor profit using leads and lags
90% confidence intervals
0
2
4
6
8
10
12
-3 -2 -1 0123
Patents
Year relative to treatment
Treated group Control Group
-1
-0.8
-0.6
-0.4
-0.2
0
-3 -2 -1 0 1 2 3
Return on Sales
Year relative to treatment
Treated group Control Group
-0.5
0
0.5
1
-3 -2 -1 0 1 2 3
Coefficient
Event time
-3
-2
-1
0
1
-3 -2 -1 0 1 2 3
Coefficient
Event time
ONLINE APPENDIX
49
ONLINE APPENDIX:
Innovation and Profitability Following Antitrust Intervention Against a Dominant Platform: The Wild, Wild West?
Sruthi Thatchenkery (Vanderbilt University) & Riitta Katila (Stanford University)
24
Strategic Management Journal, 2023
Antitrust
Competition interventions. While we focus on blocking competition in this paper, two other streams of research on competition interventions are
also relevant to understand. A stream on M&As argues that, by eliminating competition, mergers can cut incentives for firms to invest in R&D (Cunningham
et al., 2021).
25
“Vertical deals” for example can eliminate potential rivals and thus reshape ecosystems and value chains (Stefanadis, 1997). Altogether, this
stream is consistent with the argument that competition and innovation decreases go hand in hand, but it rarely examines increases in competition.
A stream on collusion–i.e. business practices that eliminate competition among a small group of firms in an industry–reaches similar conclusions on
“innovation competition.” A study by Mezias and Boyle (2005), for instance, examined a collusive trust among film producers in the United States in the
early 20th century. The authors found that colluding firms were slow to adopt key innovations such as feature-length films, a result broadly consistent with the
argument that competition and innovation decreases go hand in hand.
26
Vertical foreclosure. Conceptually, we can also draw a direct parallel between the vertical foreclosure literature - where a firm uses one line of
business to disadvantage rivals in another line - and antitrust in platform ecosystems. In a classic example, “a flourmill that also owned a bakery
could…degrade quality when selling to rival bakers—or refuse to do business with them entirely” (Khan, 2017: 731), much in the same way as a dual
platform-complementor could ration platform services to rival complementors and thereby undermine innovation. In platform ecosystems, the dual platform-
complementor’s ability to favor its own complementor products (such as a refusal to open up an interface) could similarly give it an unfair advantage in
visibility, costs and convenience, thus potentially blocking a range of viable opportunities from rivals in complementor markets.
While vertical foreclosure is an important analogy, it also differs in important ways. First, complementors are highly dependent on platforms for
market access, creating potential for abuse by the platform. Platform dependence is further exacerbated by network effects that often “tip” platform markets to
one or two dominant platforms, meaning that complementors need to release products on the dominant platform in order to access the bulk of their potential
24
Contact information for authors: sruthi.thatchenkery@vanderbilt.edu (Sruthi), rkatila@stanford.edu (Riitta)
25
Although some M&A scholars suggest that synergies provided by mergers could support rather than eliminate innovation (e.g. in rapidly moving technology industries
where temporary monopolies are common), others reason that in settings where network effects promote more permanent consolidation of market share (platform
ecosystems), there is a need for M&A antitrust to ensure long-term innovation (Federico et al., 2019).
26
One recent exception is Kang (2020) who showed that manufacturing firms spent more on R&D and product development while colluding. That is, cartels that aim to
eliminate competition and to raise prices caused firms to invest more in R&D. Because Kang’s sample was restricted to manufacturing firms (R&D investments typically
target process innovations), implications for other types of settings are likely different.
ONLINE APPENDIX
50
customers. In contrast, a vertically-integrated firm (e.g. flour mill-bakery), unless they achieve an outright monopoly, cannot completely block access to
customers. Second, platforms are dependent on complementors: because complementor innovation is crucial to growing the platform ecosystem, platforms
are incentivized to share complementary assets. In contrast, a flour mill that owns a bakery has no incentive to share assets with competing bakeries as it gains
no benefit from an increased variety of competitors in the value chain. These characteristics of platforms (interdependencies that create potential for abuse,
but also potential support to grow the ecosystem) differentiate platforms from vertical foreclosure and make them interesting to study.
Microsoft case details. Regarding sales, interoperability and bundling were the main issues. Prior to the intervention, Microsoft was shown to inhibit
the functionality of competing applications (e.g., purposefully making non-Microsoft applications run more slowly or less reliably) and alleged to have
created technical ‘backchannels’ that would improve integration between its own applications and the platform while sabotaging rival applications–actions
that potentially increased sales of Microsoft’s own complementor products. Microsoft was also accused of bundling its own complementor applications with
the platform and allegedly making it difficult to remove them, or outright integrating rival complementor functionality in Windows Server (aka platform
envelopment). Microsoft also engaged in exclusionary contracting where it would penalize a hardware manufacturer for pre-installing
competing complementor apps by threatening to revoke their platform license or charging them a higher licensing fee. The intervention barred these tactics.
Microsoft could no longer prevent customers from uninstalling a Microsoft application and replacing it with a competing product, or setting a competing
application as the system default. Microsoft was specifically instructed to offer customers a “separate and unbiased choice” of applications they could use on
a Microsoft platform.
27
Microsoft was also barred from exclusionary contracting and had to allow hardware manufacturers to pre-install any complementor
apps they wished. Altogether, the pre-intervention practices inflated Microsoft’s own complementor applications’ market share and deflated that of
complementors, and the intervention barred such attempts.
Regarding costs, prior to the intervention, Microsoft slowed down complementors’ development by keeping APIs (application programming
interfaces) closed. These practices created friction in development and elevated other complementors’ development costs while giving a cost advantage to
Microsoft’s own offerings. Microsoft further sold “access licenses” that helped with integration by granting complementors full access, but added cost
(Gartner, 2000). The antitrust intervention forced Microsoft to reverse these practices and open many of its APIs in order to facilitate smoother application
development. Microsoft was also forbidden from “retaliating” (via penalties such as higher platform licensing fees or cutting off access to technical resources
such as APIs and SDKs) against competing software firms that developed or bundled competing applications.
28
Altogether, the antitrust intervention focused
on reducing Microsoft’s ability to exploit its dominance through bundling, interoperability and cost advantages for its own complementor applications.
Matching: Main Analysis and Robustness
Matching on region, firm size and IPO year addresses the possibility that differences in these characteristics (e.g. through resource availability) across
treated and controls could influence innovation or profit. Matching on R&D, patents, and ROS aims to lessen concerns that treated firms may be more
profitable or more technology intensive than controls.
27
U.S. Department of Justice, US v. Microsoft: Plaintiff’s Findings of Fact, 1999.
28
U.S. Department of Justice, US v. Microsoft: Revised Proposed Final Judgment, 2001.
ONLINE APPENDIX
51
We employed propensity score matching (PSM) in our main analysis. As de Figueiredo, Feldman, and Rawley (2019) note, in samples with multiple
confounders, PSM remains stable even as the number of potential confounders increases, reducing researcher’s subjective assessments about “similarity,” and
increasing the number of treated firms that can be matched (reducing the data that need to be thrown away). To reduce the likelihood of poor matches, we
eliminated extreme values of the propensity score by trimming the top and bottom 5% from the sample. Treated firms were matched without replacement
(i.e., control firms are not re-used).
Table A4 reports results for alternative matching schemes, including different trims for PSM (top 1%, no trim). For coarsened exact matching (CEM), we
used the same matching criteria as our main PSM analysis, resulting in a CEM matched sample of 310 firm-years (54 firms). For exact hand matching, we
followed prior work (Hsu, 2006) by first identifying an exact match for each treated firm (looking for a match in the same decile for continuous variables). If
an exact match was not found, we relaxed the non-treated firm’s IPO year to the year before or after that of the treated firm. If there was still no match, we
relaxed the geographic region to include neighboring states. If there was still no match, we relaxed the firm size and R&D expenditure criteria to firms in the
same quintile. If there was still no match, we dropped the treated firm from the analysis and proceeded to match the next treated firm. Our exact matching
sample is 298 firm-years (50 firms). To illustrate the similarity of the treated and the matched control firms, Table A5 reports descriptive statistics. The
control group is very similar to the treated along the matching criteria, and thus likely provides a reliable counterfactual. Note that our estimates are doubly
robust as we also add controls for firm heterogeneity and firm fixed effects in all models.
Regression Analysis: Statistical Robustness
Alternate specifications. We tested alternatives to fixed effects Poisson when predicting innovation. Because a number of our firms did not patent,
we ran zero-inflated Poisson. For robustness, we also ran panel OLS. Results are consistent (Table A3a).
Serial correlation. Because firm fixed effects were included, we probed the sensitivity of the models to serial correlation per Bertrand et al. (2004).
We collapsed our multi-year panel into a panel of two, with one observation containing the three-year-average of variables prior and another observation after
the treatment. Results are consistent indicating that serial correlation is not a significant concern (Table A1).
Continuous treatment. Our treatment vs control design used a variable with differing treatment intensity (Microsoft’s market share in each
complementor market). In main analyses, we discretized the treatment because interpreting difference-in-differences coefficients with a continuous (rather
than binary) treatment variable can be challenging due to treatment effect heterogeneity (Callaway et al., 2021). For robustness, we followed Card (1992) and
estimated the effect of a continuous treatment (Microsoft’s market share in the focal complementor’s markets). Results in Table A1 are highly consistent.
Alternative Explanations and Auxiliary Analyses
We also test alternative explanations for our results. First, could our results be influenced by multimarket contact (MMC)? Multimarket theory
argues that greater overlap between firms reduces competitive intensity and could lift profits (Gimeno, 1999). So if control firms were also multimarket firms
that were more “friendly” with Microsoft, it could explain why they were not influenced. We do not find a major difference in treated vs controls in this
regard (average number of market segments is 1.64 among treated firms and 1.46 for control firms). Although most complementors compete in 1-2 markets,
ONLINE APPENDIX
52
making MMC less of a concern, we also test its potential influence by limiting the sample to complementors that compete in only one market (and who
therefore cannot have multimarket contact with Microsoft or any other firm). Results for single-market complementors (Table A3) are consistent, reducing the
concern about multimarket forbearance as an explanation.
Second, could our results be driven by the dot-com crash in the year 2000 rather than the antitrust intervention? Again, this does not seem likely. As
shown in figure 3, both the treated and control groups were impacted by the crash in 2000, and their divergence begins after the intervention (year 0), not after
the crash (year -1). Tests with placebo years, noted above, suggest a similar conclusion. If the crash were an explanation, we would also expect to see similar
trends for both treated and control firms, but this is not the case. In particular, we would not expect the control firms’ profit to recover faster than treated
firms’.
Third, is it possible that the prospect of profitable sales that motivated innovators could be about “big paydays” rather than average profits, and this
variability could be more significant than averages? If this were a likely explanation, we would expect treated firms to experience more extreme (positive and
negative) profit outcomes given their investments in innovation. Our data do not support this explanation, however. Models predicting whether the firm
achieves “superior profits” in a year (i.e. 2x the industry average or >95th percentile) were consistent with our main results (Table A2). In fact, treated firms
were less likely to experience extreme positive outcomes after the intervention.
Finally, baseline innovation capabilities could be an alternative explanation. Is it possible that high market share firms were already inventing at a
high rate and so had less room to grow (making it hard to empirically observe an effect)? Again, this explanation seems unlikely. When we included pre-
sample patents as a control for baseline innovation capabilities (Table A10), low market share firms still remained the ones driving the effect, supporting our
original findings.
REFERENCES (for online appendix)
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Cunningham, C., Ederer, F., & Ma, S. (2021). Killer acquisitions. Journal of Political Econony, 129(3), 649–702.
Federico, G., Morton, F. S., & Shapiro, C. (2019). Antitrust and innovation: Welcoming and protecting disruption. SSRN Working Papers.
de Figueiredo, R., Feldman, E., & Rawley, E. (2019). The costs of refocusing: Evidence from hedge fund closures during the financial crisis. Strategic
Management Journal, 40(8), 1268–1290.
Gartner Research. (2000). Win2000 Licensing: Raising prices, squeezing competitors.
Gimeno, J. (1999). Reciprocal threats in multimarket rivalry: staking out ‘spheres of influence’ in the U.S. airline industry. Strategic Management Journal,
20(2), 101–128.
Harrison, J. S., Boivie, S., Sharp, N. Y., & Gentry, R. J. (2018). Saving face: How exit in response to negative press and star analyst downgrades reflects
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Stefanadis, C. (1997). Downstream vertical foreclosure and upstream innovation. Journal of Industrial Economics, 45(4), 445–456.
ONLINE APPENDIX
53
APPENDIX Table A1. Difference-in-differences validity tests
Complementor Innovation (Patents) Complementor Profit (ROS)
Collapse pre-
and post
Continuous
Treatment
Random
Implementation
of Treatment
Event
Study
Collapse pre-
and post
Continuous
Treatment
Random
Implementation
of Treatment
Event
Study
1 2 3 4 5 6 7 8
Rival complementor x Post-intervention 1.43 -0.37
(0.000) (0.05)
Microsoft complementor market share x Post-intervention 3.13 -4.10
(0.000) (0.03)
Randomized treatment x Post-intervention -0.06 0.04
(0.56) (0.72)
Event study
Rival complementor x Three years pre-intervention -0.07 -0.15
(0.74) (0.79)
Rival complementor x Two years pre-intervention -0.06 -0.14
(0.56) (0.72)
Rival complementor x One year pre-intervention -0.02 -0.43
(0.90) (0.77)
Rival complementor x One year post-intervention 0.37 -0.14
(0.004) (0.26)
Rival complementor x Two years post-intervention 0.33 -1.14
(0.02) (0.03)
Rival complementor x Three years post-intervention 0.61 -1.47
(0.000) (0.02)
Controls
Size (logged) 0.04 1.72 1.65 1.43 0.15 -0.05 -0.12 -0.13
(0.65) (0.000) (0.000) (0.000) (0.000) (0.88) (0.71) (0.72)
R&D intensity -1.12 1.11 0.59 -0.22 0.66 -0.02 -0.02 -0.02
(0.000) (0.01) (0.70) (0.63) (0.003) (0.000) (0.000) (0.002)
Years public -2.72 -0.95 -0.52 -1.05 -0.75 0.38 0.22 0.41
(0.11) (0.000) (0.40) (0.000) (0.53) (0.22) (0.34) (0.16)
Acquisitions -0.36 -0.31 -0.35 -0.40 -1.13 0.19 0.09 0.11
(0.73) (0.000) (0.01) (0.000) (0.27) (0.37) (0.57) (0.59)
Firm fixed effects Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y
Log likelihood -81.47 -923.70 -632.00 -934.72
R-squared 0.37 0.30 0.19 0.89
P-values in parentheses (two-tailed tests). Innovation results are reported using fixed effects Poisson and profit using fixed effects panel OLS.
ONLINE APPENDIX
54
APPENDIX Table A2. Robustness tests: Alternate dependent variables
Complementor Innovation Complementor Profit
Main measure:
Patents
(Poisson)
Citation-
weighted patents
(Poisson)
R&D
expenditures
(logged, OLS)
Superior patent
output (>95
percentile, logit)
Main measure:
ROS (OLS)
Net income
(logged, OLS)
Superior profits
(>2X average,
logit)
Superior profits
(>95 percentile,
logit)
1 2 3 4 6 7 8 9
Rival complementor x Post-intervention 0.42 0.33 0.05 0.11 -0.70 -0.02 -2.88 -1.37
(0.000) (0.000) (0.08) (0.08) (0.02) (0.10) (0.09) (0.09)
Controls
Size (logged) 1.75 2.43 0.32 0.16 -0.09 0.02 -0.03 0.25
(0.000) (0.000) (0.000) (0.11) (0.79) (0.13) (0.93) (0.40)
R&D intensity 1.19 2.78 -0.001 -0.02 0.000 -0.47 -1.50
(0.01) (0.000) (0.06) (0.000) (0.41) (0.59) (0.37)
Years public -0.94 -1.45 -0.10 -0.07 0.44 -0.02 0.11 0.27
(0.000) (0.000) (0.001) (0.33) (0.13) (0.02) (0.80) (0.48)
Acquisitions -0.32 -0.41 -0.01 -0.14 0.21 0.001 0.97 -0.22
(0.000) (0.000) (0.70) (0.03) (0.27) (0.94) (0.24) (0.76)
Firm fixed effects Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y
Log likelihood -941.01 -1701.48 -1032.23 -79.94 -107.83
R-squared 0.65 0.32 0.27
P-values in parentheses (two-tailed tests)
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APPENDIX Table A3a. Robustness tests: Alternate specifications predicting complementor innovation
Zero-Inflated
Poisson
Panel OLS1
Single Market
Firms
Drop Firm
Size
Drop R&D
Size:
Employees
R&D:
Expenditures
Size (Emp) &
R&D
Expenditures
Drop Years
Public
HHI
Number of
Competitors
1 2 3 4 5 6 7 8 9 10 11
Rival complementor x Post-intervention 0.34 0.33 0.61 0.47 0.63 0.40 0.75 0.68 0.38 0.37 0.61
(0.001) (0.03) (0.02) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.002) (0.000)
Controls
Size (revenue) 1.03 1.17 0.82 2.29 0.87 2.76 2.67 2.68
(0.000) (0.000) (0.04) (0.000) (0.000) (0.000) (0.000) (0.000)
Size (employees) 4.36 1.38
(0.000) (0.000)
R&D (intensity) 0.93 0.01 0.11 -0.02 1.57 3.86 3.34 3.14
(0.03) (0.001) (0.81) (0.96) (0.000) (0.000) (0.000) (0.000)
R&D (expenditures) 4.62 4.78
(0.000) (0.000)
Years public -0.32 -0.56 -1.95 -1.28 -1.03 -0.74 -0.77 -0.71 -0.74 -0.78
(0.03) (0.002) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)
Acquisitions -0.43 0.06 -0.93 -0.14 -0.62 -0.68 -0.64 -0.64 -0.61 -0.53 -0.57
(0.000) (0.65) (0.002) (0.02) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)
Market HHI -0.0003
(0.001)
Number of competitors in market 0.02
(0.08)
Firm fixed effects Y Y Y Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y Y Y Y
Log likelihood -1045.00 -294.67 -294.67 -1027.36 -813.69 -808.65 -742.10 -745.51 -797.62 -779.60 -783.38
P-values in parentheses (two-tailed tests). Results are reported using fixed effects Poisson unless otherwise noted.
1 For OLS model predicting patents, dependent variable is log(patents+1)
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APPENDIX Table A3b. Robustness tests: Alternate specifications predicting complementor profit
Single Market
Firms
Drop Firm
Size
Drop R&D
Size:
Employees
R&D:
Expenditures
Size (Emp) &
R&D
Expenditures
Drop Years
Public
HHI
Number of
Competitors
123456789
Rival complementor x Post-intervention -0.57 -0.67 -1.28 -0.68 -1.26 -1.24 -0.67 -0.63 -0.63
(0.08) (0.01) (0.10) (0.01) (0.11) (0.08) (0.02) (0.01) (0.04)
Controls
Size (revenue) -0.06 -0.64 -0.26 -0.04 -0.11 -0.06
(0.69) (0.45) (0.83) (0.90) (0.75) (0.87)
Size (employees) -0.23 0.12
(0.68) (0.87)
R&D (intensity) -0.02 -0.33 -0.33 -0.33 -0.32 -0.33
(0.001) (0.000) (0.000) (0.000) (0.000) (0.000)
R&D (expenditures) -0.97 -1.62
(0.52) (0.29)
Years public 0.16 0.14 1.46 0.18 1.41 1.36 0.17 0.16
(0.46) (0.61) (0.30) (0.56) (0.34) (0.30) (0.56) (0.61)
Acquisitions 0.44 0.27 0.20 0.29 0.23 0.23 0.28 0.28 0.28
(0.53) (0.38) (0.43) (0.36) (0.37) (0.36) (0.39) (0.39) (0.37)
Market HHI 0.0002
(0.39)
Number of competitors in market 0.01
(0.65)
Firm fixed effects Y Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y Y
R-squared 0.36 0.44 0.08 0.46 0.08 0.08 0.46 0.46 0.46
P-values in parentheses (two-tailed tests). Results are reported using fixed effects panel OLS.
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APPENDIX Table A4. Robustness tests: Alternate matching methods
APPENDIX Table A5. Summary statistics for treated vs. control firms
Complementor Innovation (Patents) Complementor Profit (ROS)
No Matching PSM, No Trim PSM, Trim 1% CEM Exact Match No Matching PSM, No Trim PSM, Trim 1% CEM Exact Match
1 2 3 4 5 6 7 8 9 10
Rival complementor x Post-intervention 0.51 0.59 0.57 0.59 0.55 -0.44 -0.88 -0.8 9 -0.74 -0.49
(0.000) (0.000) (0.000) (0.003) (0.000) (0.01) (0.06) (0.06) (0.03) (0.02)
Controls
Size (logged) 1.33 1.51 1.52 1.47 1.59 -0.15 -0.83 -0.83 -1.10 -0.42
(0.000) (0.000) (0.000) (0.000) (0.000) (0.42) (0.26) (0.26) (0.10) (0.11)
R&D intensity -0.30 -0.12 -0.20 -0.41 0.26 -0.02 -0.02 -0.02 -0.02 -0.02
(0.50) (0.71) (0.56) (0.39) (0.63) (0.01) (0.002) (0.002) (0.000) (0.03)
Years public -0.96 -1.09 -1.11 -1.79 -0.82 0.21 0.46 0.45 0.47 0.35
(0.000) (0.000) (0.000) (0.000) (0.000) (0.23) (0.09) (0.10) (0.13) (0.15)
Acquisitions -0.43 -0.41 -0.42 -0. 18 -0.34 0.11 0.11 0.11 0.16 0.04
(0.000) (0.000) (0.000) (0.13) (0.000) (0.52) (0.29) (0.30) (0.16) (0.89)
Firm fixed effects Y Y Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y Y Y
Log likelihood -599.22 -1045.46 -1031.87 -349.92 -461.63
R-squared 0.21 0.30 0.30 0.32 0.24
P-values in parentheses (two-tailed tests). Innovation results are reported using fixed effects Poisson and profit using fixed effects panel OLS.
Full sample (no matching) is 78 firms, CEM matched sample is 54 firms, exact (hand) matched sample is 50 firms.
Before Matching After Matching
Variables (Matching Criteria)
Treated
Mean
Control
Mean
p-value
(t-test)
p-value
(KS-test)
Treated
Mean
Control
Mean
p-value
(t-test)
p-value
(KS-test)
Size (logged) 0.65 0.47 0.08 0.00 0.58 0.50 0.78 0.38
R&D intensity 0.36 0.41 0.59 0.41 0.37 0.40 0.73 0.87
Years public 7.01 6.27 0.01 0.67 6.45 6.42 0.42 0.93
Region: Silicon Valley 0.26 0.36 0.11 0.27 0.32 0.34 0.47 0.64
Region: Boston 0.09 0.12 0.31 0.83 0.10 0.08 0.46 0.92
Region: Los Angeles 0.11 0.10 0.72 0.98 0.09 0.10 0.87 0.99
Pre-sample patents11.83 1.62 0.55 0.13 1.70 1.69 0.97 0.44
Pre-sample profits1-0.20 -0.08 0.09 0.01 -0.16 -0.12 0.37 0.19
1 "Pre-sample" variables are averaged from 1995-1997
KS-test: Kolmogorov-Smirnov test for equality of distribution
Two-tailed tests. N=416 before matching, N=374 after propensity score matching
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Appendix Table A6. Three-way interaction (triple difference) comparing low versus high market share complementors
Complementor Innovation (Patents) Complementor Profit (ROS)
Main controls
No R&D
intensity
Pre-sample
patents
Main controls
1 2 1 4
Low-market-share complementor x Rival complementor x Post-intervention 0.14 0.47 0.36 -0.78
(0.002) (0.001) (0.007) (0.02)
Controls
Size (logged) 0.12 1.74 1.67 -0.05
(0.000) (0.000) (0.000) (0.89)
R&D intensity 0.42 -0.32
(0.002) (0.000)
Pre-sample patents 0.16
(0.001)
Years public 0.15 -0.93 -0.82 0.35
(0.000) (0.000) (0.000) (0.27)
Acquisitions 0.06 -0.38 -0.38 0.18
(0.000) (0.000) (0.000) (0.40)
Firm fixed effects Y Y Y Y
Market fixed effects Y Y Y Y
Year fixed effects Y Y Y Y
Log likelihood -945.23 -945.23 -945.23
R-squared 0.46
P-values in parentheses (two-tailed tests). Innovation results are reported using fixed effects Poisson and profit using fixed effects panel OLS.
Models 2-3 serve as extra robustness checks regarding differences in baseline innovation rates among high versus low market share complementors.
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APPENDIX Table A7. Mechanism tests: Patent variability (hits and flops)
All complementors Low market share complementors High market share complementors
Hits and Flops
Hits Flops
Hits and Flops
Hits Flops
Hits and Flops
Hits Flops
1 2 3 4 5 6 7 8 9
Rival complementor x Post-intervention 0.94 0.61 1.26 1.65 1.62 0.17 -0.17 -0.76 0.17
(0.000) (0.03) (0.000) (0.000) (0.000) (0.01) (0.51) (0.06) (0.79)
Controls
Size (logged) 3.29 3.13 3.61 1.99 1.78 2.11 6.16 6.10 7.03
(0.000) (0.000) (0.000) (0.000) (0.000) (0.004) (0.000) (0.000) (0.000)
R&D intensity 5.36 5.16 6.10 3.23 3.01 3.82 15.27 16.11 17.35
(0.000) (0.000) (0.000) (0.001) (0.02) (0.01) (0.000) (0.000) (0.000)
Years public -1.28 -2.12 -0.87 -0.83 -0.89 -0.97 1.25 -0.55 3.40
(0.000) (0.000) (0.09) (0.01) (0.05) (0.05) (0.29) (0.72) (0.06)
Acquisitions -0.46 -0.19 -0.81 -0.66 -0.50 -1.17 -0.57 -0.26 -0.92
(0.000) (0.25) (0.000) (0.01) (0.07) (0.03) (0.002) (0.31) (0.001)
Firm fixed effects Y Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y Y
Log likelihood -293.80 -217.20 -159.70 -160.40 -112.80 -83.82 -157.90 -133.70 -83.99
P-values in parentheses (two-tailed tests)
Only includes firms with at least one patent (50 firms, 294 firm-years)
Following Ahuja & Lampert (2001), hits (flops) are defined as number of patents with citations in the top (bottom) quartile relative to other firms in the industry.
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APPENDIX Table A8a. Mechanism tests: New product introductions
APPENDIX Table A8b. Mechanism tests: Profit decomposition
All complementors
Low market share
complementors
High market share
complementors
1 2 3
Rival complementor x Post-intervention 0.06 0.14 -0.25
(0.68) (0.14) (0.17)
Controls
Size (logged) -0.27 -0.01 0.16
(0.03) (0.90) (0.29)
R&D intensity 0.02 0.02 1.55
(0.14) (0.005) (0.01)
Years public -0.20 -0.08 -0.40
(0.15) (0.40) (0.08)
Acquisitions 0.16 0.18 -0.14
(0.10) (0.02) (0.27)
Firm fixed effects Y Y Y
Market fixed effects Y Y Y
Year fixed effects Y Y Y
Log likelihood -999.77 -863.01 -179.80
P-values in parentheses (two-tailed tests). Results are reported using fixed effects Poisson. Robust to alternate dependent variables (new product lines, new product versions, etc).
All complementors Low market share complementors High market share complementors
Price-cost margin Asset utilization Price-cost margin Asset utilization Price-cost margin Asset utilization
1 2 5 6 3 4
Rival complementor x Post-intervention -0.30 -0 .26 -0.27 -0.33 -0 .07 0.10
(0.02) (0.27) (0.07) (0.28) (0.16) (0.06)
Controls
Size (logged) -0.27 0.38 -0.21 0.23 -0.20 0.16
(0.10) (0.33) (0.31) (0.63) (0.27) (0.15)
R&D intensity -0.03 -0.01 -0.03 -0.004 -0.86 -0.41
(0.000) (0.09) (0.000) (0.19) (0.07) (0.41)
Years public 0.11 0.03 0.10 0.04 -0.13 -0.2 3
(0.39) (0.88) (0.49) (0.88) (0.31) (0.22)
Acquisitions 0.07 -0.12 0.08 -0.07 0.06 0.10
(0.39) (0.33) (0.53) (0.33) (0.46) (0.04)
Firm fixed effects Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y
R-squared 0.32 0.02 0.24 0.03 0.20 0.32
P-values in parentheses (two-tailed tests). Results are reported using fixed effects panel OLS.
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APPENDIX Table A9. Mechanism tests: Product leaders versus laggards
Product Leaders Product Laggards
Complementor
Innovation
Complementor Profit
Complementor
Innovation
Complementor Profit
Patents
(Poisson)
ROS (OLS)
Lerner index
(OLS)
Asset
utilization
(OLS)
Patents
(Poisson)
ROS (OLS)
Lerner index
(OLS)
Asset
utilization
(OLS)
1 2 3 4 5 6 7 8
Rival complementor x Post-intervention 2.46 0.01 -0.20 -0.14 0.31 -0.96 -0.26 -1.06
(0.000) (0.93) (0.77) (0.11) (0.02) (0.02) (0.07) (0.17)
Controls
Size (logged) 4.31 0.39 -0.05 0.11 2.65 -1.61 -0.13 0.15
(0.000) (0.25) (0.72) (0.14) (0.000) (0.05) (0.49) (0.75)
R&D intensity 10.92 -0.38 0.15 1.13 0.17 -2.46 -0.71 -3.04
(0.000) (0.66) (0.78) (0.12) (0.79) (0.08) (0.27) (0.34)
Years public -17.34 0.54 -2.52 3.42 -1.06 0.83 -0.18 -1.31
(0.000) (0.91) (0.30) (0.05) (0.01) (0.24) (0.41) (0.28)
Acquisitions -0.80 -0.11 -0.04 -0.04 -1.27 1.18 0.24 -0.16
(0.000) (0.06) (0.56) (0.31) (0.24) (0.26) (0.27) (0.66)
Firm fixed effects Y Y Y Y Y Y Y Y
Market fixed effects Y Y Y Y Y Y Y Y
Year fixed effects Y Y Y Y Y Y Y Y
Log likelihood -131.60 -185.40
R-squared 0.71 0.63 0.82 0.39 0.25 0.11
P-values in parentheses (two-tailed tests).
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Appendix Table A10. Robustness checks: Control for pre-sample patenting when predicting complementor innovation
j
All complementors
Low market share
complementors
High market share
complementors
1 2 3
Rival complementor x Post-intervention 0.59 0.39 0.09
(0.000) (0.02) (0.56)
Controls
Size (logged) 2.21 0.58 4.17
(0.000) (0.000) (0.000)
R&D intensity -0.03 -0.30 9.51
(0.40) (0.34) (0.000)
Years public -1.05 -0.72 -0.88
(0.000) (0.000) (0.07)
Acquisitions -0.63 -0.95 -0.54
(0.000) (0.000) (0.000)
Pre-sample number of patents 0.14 0.27 0.06
(0.000) (0.000) (0.46)
Market fixed effects Y Y Y
Year fixed effects Y Y Y
Chi-squared 1066.00 231.82 573.77
P-values in parentheses (two-tailed tests). Results are reported using random effects Poisson to avoid collinearity with pre-sample patent control.
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APPENDIX Figure A1a. Visualization of trends using relative change measure of APPENDIX Figure A1b. Visualization of trends using relative change
measure of complementor innovation complementor profit
Yearly change (relative to treatment year) in the mean of dependent variable in treatment versus control groups
APPENDIX Figure A2a. Event study: triple-diff estimates of intervention’s effects APPENDIX Figure A2b. Event study: triple-diff estimates of intervention’s
on low market share complementor innovation using leads and lags (H1b) effects on low market share complementor profit using leads and lags (H2b)
-1
-0.5
0
0.5
1
1.5
2
-3 -2 -1 0 1 2 3
Change in patents relative to
treatment year
Year relative to treatment
Treated group Control Group
0
0.2
0.4
0.6
0.8
1
-3 -2 -1 0 1 2 3
Change in return on sales
relative to treatment year
Year relative to treatment
Treated group Control Group
-1
-0.5
0
0.5
1
-3 -2 -1 0 1 2 3
Coefficient
Event time
-2
-1.5
-1
-0.5
0
0.5
1
-3 -2 -1 0 1 2 3
Coefficient
Event time
