# The Value of Names: Civil Society, Information, and Governing Multinationals

#Abstract
Can markets discipline socially costly misbehavior abroad? We explore the market penalty associated with major human rights violations---specifically, the assassination of mining activists, a context where formal legal recourse is rare and events often do not involve counterparties. We show that firms featured in media coverage of these incidents experience significant, negative abnormal stock returns. Whereas reactions to related forms of corporate misconduct may be transitory or muted, we find that the market responses are both substantial and persistent, with a median 10-day loss exceeding USD 100 million. Since formal legal sanction is exceedingly rare, we consider the role of market penalties. We highlight three mechanisms that are consistent with reputational costs: (1) Media attention magnifies the market response. (2) Information-sensitive institutional investors systematically divest following assassination events. (3) Events reduce future trade, leading to a 19\% decline in new contracts with counterparties. Despite these costs, events persist. We find that assassinations increase with dependence on mining royalties, suggesting that local rents sustain conflict despite market pressure. Thus, reputational sanctions may be significant---even in weakly institutionalized settings---yet may not fully deter misbehavior when local and global incentives diverge.

# Introduction

Global corporations are increasingly operating in territories with weak
governance, engaging in conflict-prone activities such as natural
resource extraction. The mining sector has become a flashpoint between
civil society and corporations involved in large-scale resource
extraction [@Ruggie2013], especially amid the climate transition. Since
2020, attacks against human rights activists---many protesting mining
activities---have occurred at a rate of one per day
[@Butt2019; @Hearon2020; @BusinessandHumanRightsResourceCentre2021]. The
green transition is likely to intensify the social tensions around
resource extraction. Renewables and green technology are set to create
unprecedented demand for critical minerals (e.g., lithium, cobalt,
nickel) [@InternationalEnergyAgency2021] in the developing world
[@Owen2023]. These trends have heightened international scrutiny of
human rights practices in the mining sector.[^1] With few formal laws,
managing the social costs of extractive activity has become a critical
issue in the global political economy [@Ruggie2013].

Can markets discipline human rights misconduct abroad? Market penalties,
called "reputational'' penalties, can be powerful disincentives for
socially costly behavior
[@Becker1968; @Karpoff1993; @Alexander1999].[^2] Extensive research on
firm misconduct shows that market-based reputational penalties can be
substantial, yet not in all settings. Notoriously, market penalties are
weakest for controversies that do not impact direct customers or
suppliers (i.e., counterparties), as seen famously in the case of
environmental violations [@Jones2001; @Karpoff2005; @Cline2018].
Perversely, some controversies may even enhance firm value
[@Armour2021], such as revelations of foreign bribery [@Karpoff2017].
Yet, evidence on reputational deterrence is particularly sparse for the
developing world [@Karpoff2012]. Recent work suggests that the
reputational costs of firm conduct may be weaker for multinationals in
foreign markets [@Nardella2023].

We study how markets sanction corporations exposed to foreign human
rights scandals. We do so by exploring how stock prices respond to
significant human rights events, namely the assassination of
environmental activists. We draw on a rich literature in law and
economics on firm misconduct, and use these asset price responses to
assess the market penalty. The stock market loss from events reflects
both the formal costs and the market-based reputational costs borne by
firms [@Karpoff1993; @krueger2015]. Because the formal costs for human
rights abuses are exceedingly rare, stock prices provide a gauge of the
market penalty.[^3] Nevertheless, the market penalty from foreign human
rights revelations is not obvious, especially when they don't involve
counterparties.

To study the market penalty from human rights scandals, we focus on
well-publicized acts of violence against civil society. Specifically, we
examine the assassination of activists mobilized around mining activity.
These events reflect the social spillovers of large-scale extractive
activity in developing economies, where legal institutions are weak and
recourse is limited. As prominent public events, assassinations are
among the best-documented human rights violations. Importantly, they
provide an upper bound for detecting the reputational penalty from human
rights scandals. We collect and code 20 years' worth of new granular
event data on assassinations tied to global mining activity. Using the
mining operations named in human rights reporting, we assign "treatment"
to publicly traded mining companies. We utilize this rich data to assess
the market-based penalties imposed on firms embroiled in human rights
controversies and examine the various channels driving these penalties.

We employ financial event study methodology to estimate the penalty from
these human rights events. Specifically, we use two related research
designs to identify the impact of human rights events on firm value.
First, we employ a traditional event study to estimate the abnormal
returns for treated firms---that is, firms whose operations are
implicated in targeted killings. We compare their realized returns to
predicted returns over several event windows.

Second, we estimate the impact of assassinations by comparing the
abnormal returns of treated firms to those of control firms. These
control firms are firms operating in the same country and sector during
the event but not associated with the assassination. We estimate these
effects first using standard ordinary least squares (OLS) regression.
Then, we use a synthetic matching estimator, in the spirit of
@Abadie2010a and @acemoglu2016, to account for unobserved group
differences not fully captured by fixed effects and firm-level controls.
In addition, we provide an open-source implementation of our synthetic
matching estimator, the **R** package `synthReturn`.[^4] Thus, we
estimate the impact of controversies using different counterfactual
assumptions and analyses.

We find that assassinations have a large, robust negative effect on the
value of corporations caught in human rights controversy abroad. For
these firms, we estimate significant negative cumulative abnormal
returns following an event. Stock prices decline one day after an
assassination and intensify over the subsequent 10-day window. We show
that these penalties are not driven by contemporaneous events and,
importantly, not anticipated by market reactions on the days preceding
the event. Moreover, these penalties are firm-specific and are not
polluted by broader spillovers (e.g., broader sectoral penalties), and
the effects are not driven by local disruptions to operations.

Our estimates suggest that the market sanctions. The benchmark
(short-run) estimates suggest that the median 10-day cumulative loss in
market capitalization for companies named in assassination news exceeds
USD 100 million. Thus, these effects may be severe enough to incentivize
firm behavior. We demonstrate that these effects are comparable to those
observed in other studies of market penalties resulting from misconduct.

Moreover, if market penalties are temporary, they may be insufficient to
incentivize better behavior. We show that the effects are persistent by
extending our short-run analysis and employing a long-run, buy-and-hold
analysis. This contrasts with market overreactions to uninformative
negative news events (e.g., @Tetlock2014) and evidence of transitory
penalties from controversies (e.g., major environmental disasters
[@Carpentier2015]) and noisy ESG news [@cui2020]).

We highlight three mechanisms that drive the penalty. First, we
demonstrate that media attention amplifies the market penalty,
potentially increasing the salience of events to financial
decision-makers and relevant stakeholders. We employ exogenous variation
in "news pressure" [@eisensee2007] to demonstrate how media attention
impacts the size of the penalty. We find that the penalty associated
with human rights news disappears during more active news cycles but
persists during less eventful news periods. Furthermore, we find that
placebo firms operating near the event locations---and thus not named in
media coverage---do not experience significant penalties compared to
those explicitly named in coverage. Therefore, we contribute to research
on misconduct that emphasizes the interaction between media coverage and
reputational loss [@Carberry2018; @Sampath2018; @Mariuzzo2020] by
directly testing the role of media attention.

Second, we then provide evidence that information-sensitive
institutional investors respond significantly to assassination events.
We show that these investors, such as hedge funds, systematically divest
from mining companies following assassination events. These results
align with research on the role of institutional investors in promoting
social responsibility [@dyke2019], particularly in emerging markets with
weak institutional frameworks [@DYCK2008]. These effects are also
compatible with work by @Gantchev2021, who show evidence that
ESG-sensitive players impose market penalties. Nevertheless,
sophisticated investors may also expect firms to lose business, which we
turn to next.

Third, we use rich supply chain data to show that downstream buyers
respond negatively to these events. We find that being associated with
an assassination leads to a 32% reduction in new contracts and a 39%
decrease in new corporate customers from countries that emphasize human
rights protection (i.e., countries in North America and Europe). Thus,
the market penalty may partly reflect expectations of lost sales, even
though assassinations do not represent misconduct toward counterparties.
Importantly, this mechanism suggests that third-party controversies can
still have demand-side repercussions, even for commodity producers.
Thus, we highlight a novel mechanism driving reputational risk.
Additionally, we do not find evidence that our effects are driven by (a)
formal or legal sanctions, or (b) local contemporaneous costs to
operations.

Despite high market-based reputational penalties, why do abuses persist?
We conclude by exploring the political economy of this equilibrium. We
collect new international data on mining royalties and show a
significant relationship between assassinations and the importance of
mining royalties paid to domestic governments. Although correlational,
this relationship suggests that local rents may perpetuate conflict.
Thus, even though market penalties may be high, they may fail to
constrain local agents from engaging in socially deleterious behavior or
"rational wrongdoing'' [@Shapira2017]. For instance, market sanctions
may not deter misconduct perpetrated in part by those outside the firm
(e.g., paramilitaries).

This study makes the following contributions: First, we contribute to
the literature on firm misconduct in an under-explored
developing-country setting. We apply insights from law and economics, as
well as empirical finance, to estimate the market penalty resulting from
foreign scandals. These results are surprising because: (i) market
penalties are typically weak or nonexistent for scandals impacting third
parties (i.e., those not doing business with the firm)
[@Jones2001; @Karpoff2005; @Brady2019]; and (ii) the stock market loss
from third-party misconduct typically reflects legal fines. We study a
setting where legal penalties are virtually nonexistent. Such settings
are among the least studied: "\[w\]e do not know if reputational losses
help to discipline related-party misconduct in other markets around the
world'' [@Karpoff2012 p. 376]. Our results suggest they do.
Nevertheless, the bulk of evidence comes from the developed world,
specifically the U.S. Recent work demonstrates that reputational
mechanisms can vary within the developed world, even between the U.S.
and U.K. [@Armour2017; @Armour2021]. By considering the role of
reputation in a global setting, we join emerging empirical work from
[@Nardella2023], [@Sampath2018], and others.

Second, our findings contribute to the growing literature on
environmental, social, and governance (ESG) events and compliance.
Globalization has led to the increasing role of (i) non-state
actors---such as shareholders, media, and NGOs---and (ii) extra-legal
mechanisms in monitoring firm conduct [@Ruggie2013; @Carberry2018]. Our
results suggest that informal actors and actions may play a potentially
important role in deterring misconduct. While work on economic crime
shows that reputational penalties may be limited (e.g., for forms of
foreign corruption and bribery [@Karpoff2017; @Sampath2018]), they can
be substantial for other foreign scandals.

Importantly, our findings suggest that "naming and shaming"---and
similar advocacy from civil society---may confer substantial penalties,
and do so for less visible firms. Work on corporate responsibility
literature emphasizes reputational risk for prominent brands exposed to
consumer activism [@couttenier16; @Aouadi2018; @Borelli-Kjaer2021].
While existing studies show strong market reactions to misconduct by
high-profile, consumer-facing firms
[@harrison10; @dyck2010blows; @krueger2015; @capelle2019], less is known
about reputational risks for less visible firms. Work by
@klymak2020trade shows that naming campaigns may have a greater impact
on downstream activity than on upstream activity. Nonetheless, we show
that reputational risk may be substantial for upstream firms.

Third, our findings contribute to the existing literature on the role of
media and information in shaping and disciplining conduct. First, we add
to research demonstrating the role of media coverage in firm
accountability
[@fang2009media; @bushee2010role; @griffin2011important; @birz2011effect],
showing that media and news coverage can impact the severity of the
market penalty. Our findings are supported by studies indicating that
the impact of scandals on stock performance is partly driven by the
salience of media coverage [@Palomino2009; @Borelli-Kjaer2021]. Second,
our findings suggest that key---institutional investors and buyers---are
responsive to news of mining misconduct and may contribute to the market
penalty. Thus, media may impact reputation by disseminating information
to key market participants. Our work highlights the interaction between
institutional investors (hedge funds) and the media in penalizing firms
in weak institutional environments [@DYCK2008].

The remainder of the paper is organized as follows. Section
[2](#sec:assassination-events){reference-type="ref"
reference="sec:assassination-events"} introduces the context of the
study. Section [3](#sec:data){reference-type="ref" reference="sec:data"}
details our data and coding process. Section
[4](#sec:estimating-the-impact-of-activist-assassinations-and-stock-returns){reference-type="ref"
reference="sec:estimating-the-impact-of-activist-assassinations-and-stock-returns"}
outlines the empirical methodology and presents the main findings. In
Section [5](#sec:mechanisms){reference-type="ref"
reference="sec:mechanisms"}, we investigate the mechanisms underlying
the baseline results. Section
[6](#sec:principal-agent){reference-type="ref"
reference="sec:principal-agent"} explores reasons for the continued
prevalence of assassinations. We conclude with a brief discussion of our
results in Section [7](#sec:conclusion){reference-type="ref"
reference="sec:conclusion"}.

# Context: Assassinations and Civil Society {#sec:assassination-events}

To study the market penalties from global human rights violations, we
examine how assassinations in the natural resource sector---specifically
mining---affect firms. We describe the context and also the empirical
advantages of this setting.

## Definition and Setting {#sec:definition-scope}

Assassinations are defined as the intentional murder of prominent and
influential figures [@TheAssociatedPress2000]. Throughout this study, we
use the terms "targeted killing," "extrajudicial killing," and
"assassination" interchangeably. We follow journalistic conventions
(e.g., The Associated Press, British Broadcasting Corporation (BBC),
National Public Radio) and the conflict studies literature, which treats
assassinations as a unique form of political violence
[@Kalyvas2019; @Perliger2015]. Unlike spontaneous or opportunistic
violence, assassinations are instrumental: they target "public figures
for political reasons" [@Kalyvas2019 p. 23]. By eliminating influential
individuals, assassinations aim to advance a specific agenda or achieve
a particular goal.

Our study focuses on the assassinations of civil society members who are
mobilized around natural resource activities. The individuals considered
were prominent in their communities and actively involved in various
social groups, including indigenous leaders, environmental and labor
activists, clergy, educators, and other community members. Scholars have
emphasized the growing importance of targeted killings of high-profile
civil society members
[@Bob2007; @GlobalInitiativeAgainstTransnationalOrganizedCrime2020] in
reducing monitoring [@Carey2021; @Krain2023] and increasing the cost of
collective action [@Albarracin2024].

Over the last 20 years, civil society activists have increasingly become
victims of lethal violence by state and non-state actors, reflecting
rising constraints on civil society [@Davenport2014; @Chaudhry2022].
Since the 2000s, UN special rapporteurs have highlighted that targeted
killings have become an important mode of repression against civil
society and have markedly increased
[@Forst2018; @Lawlor2021; @Krain2023]. These extreme events are
emblematic of more diffuse violence and repression
[@Butt2019; @Albarracin2024] as well as broader formal crackdowns on
civil society [@Davenport2014; @Bakke2020; @Chaudhry2022]. These trends
have inspired new data collection efforts [@FrontlineDefenders2023] and
a nascent empirical literature on targeted violence against civil
society [@Butt2019; @LeBillon2020; @Carey2021; @Krain2023]. We build on
these empirical efforts by considering the role of private activity.

To study the impact of targeted violence, we focus on the mining sector.
We do so for three reasons. First, lethal repression against civil
society is predominantly observed in the natural resource sector. For
human rights scholars and legal practitioners, this sector exemplifies
how weak institutions hinder the prevention of human rights violations
by multinationals [@Ruggie2013]. Second, the mining sector is one of the
deadliest for activists
[@BusinessandHumanRightsResourceCentre2021; @Butt2019]. @Hearon2020
shows that nearly half of recent (and rare) human rights cases against
multinationals involve extractive industries. Third, extractive
industries are capital-intensive, and equity financing is common,
enabling connections between publicly traded firms and human rights
events.

## Assassinations: Empirical Advantage and Scope

Activist assassinations are not only of substantive importance. They
also offer empirical advantages in identifying the market penalty for
severe human rights controversies:

#### Severity

Assassinations are unequivocal human rights violations and universally
illegal. As clear instances of severe misconduct, they provide a means
of assessing whether markets penalize such violations. They allow market
participants to update their perceptions of a firm's reputation and
social standards [@Carpentier2015]. Studies often provide conflicting
estimates of market penalties from negative ESG events. Such evidence,
however, may simply reflect heterogeneous choices of events. These
issues may be particularly important when studies use mass ESG datasets,
which can include numerous insignificant events and uninformative
events. Given the mixed estimates of reputational effects
[@Karpoff2012], we follow [@Carpentier2015] and use a homogeneous class
of unambiguous events---assassinations---to assess the scope of market
penalty.[^5]

#### Point-in-Time

Second, assassinations are discrete, well-defined events with concrete
dates. This is especially true compared to other forms of misconduct or
social conflict. Many negative events, such as regulatory episodes,
often have complex and ambiguous timelines, which confound estimates of
market losses [@Armour2021].[^6]. Other human rights-related events,
such as complex labor violations, can suffer from the same issues of
precision.

In contrast, assassination dates are well recorded and provide a
consistent benchmark for information revelation. As noteworthy events,
assassinations correspond closely with the dates when information is
revealed to the public. Thus, unlike other events, there is a
considerable overlap between the occurrence and initial reporting of
assassinations.

#### Salience

Relatedly, assassination events are salient and public and among "the
most visible and best documented" forms of targeted violence against
social leaders [@Albarracin2024 p. 8]. They are closely monitored by
international bodies and human rights press initiatives
[@Lawlor2021; @GlobalInitiativeAgainstTransnationalOrganizedCrime2020; @FrontlineDefenders2023],
such as the Global Assassination Monitor. By focusing on these
newsworthy events, we ensure they effectively reveal information to
markets. This approach allows us to avoid empirical issues related to
event selection in financial event studies
[@krueger2015; @Carpentier2022], such as internal regulatory events that
may not be publicized to markets.

#### Granularity

Our events permit high-resolution geographic and temporal analysis.
Previous high-quality studies on targeted political killings have
focused on national political events [@olken2009], while recent research
on the repression of civil society has often examined cross-country data
[@Bakke2020; @Krain2023] and annual outcomes. In contrast, the
availability of local information (Admin1 level) and daily event data
allows for more granular analysis and greater statistical power. This
temporal granularity also limits the occurrence of confounding events.

We now turn to the specifics of the data on assassination events.

# Data {#sec:data}

## Assassination Data {#ref:data-assassination-data}

### Event Collection {#ref:data-event-collection}

Our data encompass 354 assassinations (496 victims) over a 20-year
period. Table [\[table01\]](#table01){reference-type="ref"
reference="table01"} provides an overview of these data. Our first
observation is for 1998, and the sample covers 31 countries. Peru and
the Philippines emerged as the most dangerous countries for mining
activists. The geographic distribution of events is depicted in Online
Appendix Figure C.2.

The data collection process for the events in Table
[\[table01\]](#table01){reference-type="ref" reference="table01"} can be
broadly summarized in four steps. First, we consider killings that are
*publicly* reported by the media or human rights campaigns. Second, we
examine events for which reporting connects a victim (or victims) to
local mining and mineral extraction activity. Third, we code the
location (e.g., the ADMIN1 unit) where the death occurred. Fourth, we
code the mining companies or projects (if any) named in connection with
the event. We detail this process below; further technical details are
provided in Online Appendix B.1.

We collect data on activist assassinations through algorithmic and
manual searches of international full-text media archives. These
included databases such as the International Herald Tribune, the
Associated Press wire archive, popular news APIs (e.g., The Guardian),
and, importantly, global news databases (e.g., LexisNexis). Core
databases, such as LexisNexis, offer translations of international news
coverage. Notwithstanding, we also perform multilingual searches, for
example, in Spanish.

### Event Coding {#sec:data-event-collection}

Figure [1](#figure01){reference-type="ref" reference="figure01"} depicts
our coding process using an excerpt from the Guardian newspaper for an
assassination event in our sample. Research assistants perform all
coding manually, which principal investigators then cross-validate for
certainty. The color highlights in Figure
[1](#figure01){reference-type="ref" reference="figure01"} denote the
information we extract and record in our dataset [@GuardianArticle]. The
article identifies the victim as Ecuadorian Indigenous leader José
Isidro Tendetza Antún (highlighted in green) and establishes his role as
an activist working in opposition to mining activity (highlighted in
purple). The section highlighted in yellow indicates that this incident
resulted in the death of the victim.

Figure [1](#figure01){reference-type="ref" reference="figure01"} also
demonstrates how we define event dates (highlighted in pink). In most
cases, media reports clearly state the time of death. However, some
cases are ambiguous. In this example, although the crime occurred on
November 28, 2014 (highlighted in pink), the news may have broken only
after the discovery of the body. In such cases, financial markets are
likely to react days after the actual date of death. We address this
ambiguity in our estimation discussion (Section
[4](#sec:estimating-the-impact-of-activist-assassinations-and-stock-returns){reference-type="ref"
reference="sec:estimating-the-impact-of-activist-assassinations-and-stock-returns"}).
Our event data maps assassinations to 15 of the 26 members of the
International Council on Mining and Metals (ICMM), an industry network
dedicated to corporate social responsibility (CSR) in the mining
industry. This means that over half of the firms in the network have
been associated with at least one assassination. But what exactly do we
mean by "associated"? We turn to this question next.

## Firm Coding {#sec:associated-multinationals}

### Treated Firms

Table [\[table01\]](#table01){reference-type="ref" reference="table01"}
presents a list of publicly traded firms associated with at least one
assassination event in our sample. In this study, we define an
*association* as a company or its project being named in reporting on an
assassination event. We use the terms "treatment," "connection," and
"association" interchangeably to indicate statistical treatment.

We code the association between a public firm's operations and an
assassination event, using the event material described in Section
[3.1.2](#sec:data-event-collection){reference-type="ref"
reference="sec:data-event-collection"}, including media reports and
human rights releases. We consider a firm "treated" or connected to an
event if the reporting mentions the firm or its operations. Importantly,
our coding does not imply any stance on the relationship between a firm
and an event beyond mentioning their operations in human rights
reporting. An "associated" company may have no role in organizing or
participating in violence. As we demonstrate below, it seems unlikely
that multinationals will take an active role in these events. Our coding
indicates only a firm's proximity to the event, as reported by public
media.

Figure [2](#figure02){reference-type="ref" reference="figure02"}
summarizes the global distribution of assassinations and the
headquarters of firms associated with these events. The colored panels
on the left correspond to event countries, with their height
representing the total number of event-company pairs in each country.
The gray panels on the right correspond to countries in which publicly
traded firms in our sample are headquartered, with their height
representing the total number of events connected to firms in that
country.

The figure shows that most assassinations in our dataset are linked to
firms headquartered in Canada, the United Kingdom, and the United
States. Despite these countries being advanced liberal democracies,
legal actions against multinationals for human rights abuses remain
exceedingly rare [@Schrempf-Stirling2017]. More broadly, the
assassination events central to our study occur in key mineral-producing
countries (Online Appendix Figure C.3) and involve firms based in
nations with the highest concentration of global mining companies
(Online Appendix Figure C.4).

### Coding and Matching Publicly Traded Firms

Our event study considers the closest publicly traded entity associated
with an event, which may be the direct or indirect owner of a project
where violence occurs. We hand-match the publicly traded firm associated
with each assassination using the following process.

1.  *Identifying Public Companies.* We first determine whether a company
    named in human rights reporting is publicly traded. If so, we match
    it to the corresponding event. A special case arises when another
    public mining company holds shares in the named company at the time
    of the event, such that the named company is not the ultimate owner
    of the project. As a convention, we only consider the "downstream"
    publicly treated companies, except where the global corporate owner
    is specifically named in reporting.

2.  *Tracing Parent Companies.* If a company named in human rights
    reporting is not publicly listed, we conduct a manual search for its
    parent company. We determine whether the named company is a
    subsidiary or joint venture of a publicly traded company at the time
    of the event. We verify this information using historical ownership
    links from Bureau van Dijk's Orbis and SNL Metals & Mining database,
    as well as publicly available corporate information. The latter
    includes official corporate websites, corporate reports, Securities
    and Exchange Commission filings (and those of non-U.S. companies),
    public business registers, and more. We cross-validate all
    information.

3.  *Identifying Projects.* Event reporting may refer to the colloquial
    or popular name for a mining project rather than the ultimate
    company. Mining operations are often referred to by their geographic
    or administrative unit names. For example, news reports may refer to
    the Rapu-Rapu Polymetallic Project (Philippines) rather than the
    firm that owns it, Lafayette Mining. In such cases, we attribute
    ownership of the project to the publicly traded company using the
    process described above.

As an example of our process, consider the event shown in Figure
[1](#figure01){reference-type="ref" reference="figure01"}. In this case,
the death involved the "Mirador copper and gold mine" (blue), owned by
Corriente Resources Inc. through its subsidiary, EcuaCorriente S.A. We
identified the ultimate owner using a public records search. Public data
reveal that Corriente Resources Inc. was acquired in 2010, and at the
time of the event in 2014, it was owned by two publicly traded
companies: China Railway Construction Corporation and Tongling
Nonferrous Metals Group Holdings. These two companies are coded as being
associated with the event.

In rare cases, reporting does not name companies or projects. In these
cases, we do not associate the assassination with a company. Consider
the example in Figure [1](#figure01){reference-type="ref"
reference="figure01"}. If no identifying data (blue) are available, we
do not match the assassination to a specific firm. For an illustrative
example, refer to Online Appendix Figure B.1.

## Finance and Geo-Location Data {#sec:financial-outcomes-and-geo-location}

### Data Sources and Construction

We collect daily stock return data for mining companies identified in
Section [3.2](#sec:associated-multinationals){reference-type="ref"
reference="sec:associated-multinationals"}, as well as returns for other
companies operating in the same country during the year of the event for
each event. Daily return data for 1998--2019 and additional firm-level
covariates are drawn from the Datastream global financial database. We
remove market holidays from our closing price time series and denominate
all financial variables in USD to account for currency fluctuations.

We source location and company ownership information for the mining
projects in our data from the SNL Metals & Mining database, which we
then match to assassination events (Section
[3.1.2](#sec:data-event-collection){reference-type="ref"
reference="sec:data-event-collection"}). The SNL database also allows us
to identify a robust set of control companies for each event year by
identifying other mining companies with operations in the geographic
vicinity of the event mine. For recent studies using the SNL Metals &
Mining database, refer to @berman2016 and @knutsen2017.

We use annual project ownership information to track treated and control
companies over time. For example, consider an assassination in Colombia
in 2013. In this case, the control company set comprises all publicly
traded companies that own mining projects in Colombia that year but are
not associated with the assassination; see Online Appendix Figure B.3
Panel A for an example.

Online Appendix Table C.1 reports summary statistics for key financial
variables, disaggregated by event country and treatment status. We
construct market returns using the Morgan Stanley Capital International
(MSCI) stock indices and match each mining company's security to the
corresponding MSCI index for the country in which it is listed. Our
sample includes mining companies listed in 23 markets and headquartered
in 25 countries, specifically focusing on mining corporations active in
event countries at the time of assassinations. We provide further
details on this sample data in Tables C.2 and C.3.

### Financial Factors and Methodological Considerations

We use the following daily, market-level Fama-French factors: small
minus big (market capitalization), high minus low (book-to-price ratio),
and momentum for the United States and developed markets, obtained from
Kenneth French's
[website]("https://mba.tuck.dartmouth.edu/pages/faculty/ken.french/data_library.html").
For emerging markets, we construct the daily momentum factor for all
emerging markets where at least one treated company is listed (i.e.,
Brazil, China, Mexico, Philippines, and South Africa). We follow Kenneth
French's methodology to form winner-minus-loser (WML) portfolios using
the intersection of two portfolios formed on size (market
capitalization) and three portfolios formed on prior returns (month
$t-12$ to month $t-2$).

Following the literature, we exclude thinly traded company securities
from our baseline analysis. Specifically, we require that companies are
traded for at least 200 days out of the 250 trading days in our
estimation window and 8 out of the 11 days of the event window. We
follow standard practice in dealing with events falling on non-trading
days by assigning the event date to the first trading day after the
actual event date.

# Estimation: The Impact of Assassination on Firm Value {#sec:estimating-the-impact-of-activist-assassinations-and-stock-returns}

We show the impact of assassinations in two steps. First, in Section
[4.1](#sec:classic-evstudy){reference-type="ref"
reference="sec:classic-evstudy"}, we employ a classic financial event
study to establish core empirical patterns. Assassinations have (i) a
significant negative impact on treated firms, and (ii) these events are
not anticipated by pre-event activity. Second, in Section
[4.2](#sec:OLS){reference-type="ref" reference="sec:OLS"}, we employ a
contemporary regression-based event study to further analyze these
results. The negative impact of assassinations is (a) firm-specific and
does not produce (negative or positive) spillovers to non-treated firms
and (b) not driven by contemporaneous events or disruptions. Third,
Section [4.3](#sec:longrun){reference-type="ref"
reference="sec:longrun"} uses a long-run analysis to show that negative
abnormal returns are persistent.

## Traditional Event Study: Basic Patterns {#sec:classic-evstudy}

### Estimation {#sec:classic-evstudy-estimation}

We employ the traditional event study methodology
[@Campbell1997; @mackinlay1997event] to estimate the impact of events on
treated firms. We study how assassination events influence the returns
for treated firms relative to their counterfactual returns absent the
event. We use the relationship between the treated firm's returns and
the market during the estimation window prior to the event (Figure
[3](#figure03){reference-type="ref" reference="figure03"}) to estimate
the counterfactual "normal" returns. Specifically, we estimate the
following linear market model over a standard 250-day estimation window
ending 30 days before the event \[-280,-30\]: $$\begin{align}
    R_{ie\tau} = \alpha_{ie} + \beta_{ie} R_{ie\tau}^{M} + \epsilon_{ie\tau},
    \label{eq:market-model}
\end{align}$$ where $R_{ie\tau}$ is the observed daily return for firm
*i*, for event $e$ at time $\tau$, where $\tau$ denotes days relative to
the event day ($\tau=0$); $R_{ie\tau}^{M}$ is the return for the MSCI
index for the country in which firm $i$'s stock is listed. For
robustness, we use a Fama-French four-factor model and construct factors
for each international equity market (see Section
[3.3](#sec:financial-outcomes-and-geo-location){reference-type="ref"
reference="sec:financial-outcomes-and-geo-location"}).

We investigate the impact of assassinations by studying how observed
stock returns deviate from normal returns on and around the event date
or over the *event window*. Specifically, for each firm $i$ and each day
$\tau$ of the event window, we calculate the abnormal returns
(ARs)------the difference between the observed and normal (non-event)
returns------as follows: $$\begin{align}
&\widehat{AR}_{ie\tau} =  R_{ie\tau} -\left( \hat{\alpha}_{ie} + \hat{\beta}_{ie} R_{ie\tau}^{M} \right). \label{eq:ar},
\end{align}$$ where $\hat{\alpha}_{ie}$ and $\hat{\beta}_{ie}$ are
estimates from the market model
[\[eq:market-model\]](#eq:market-model){reference-type="eqref"
reference="eq:market-model"}. Specifically, we study the cumulative
abnormal returns (CARs), or the cumulative sum of
$\widehat{AR}_{ie\tau}$ over the event window: $$\begin{align}
\widehat{CAR}_{ie}\left(\tau_{1}, \tau_{2}\right)  = \sum_{\tau=\tau_{1}}^{\tau_{2}} \widehat{AR}_{ie\tau}, \label{eq:car}
\end{align}$$ where $\tau_1$ and $\tau_2$ represent the start and end
points of each cumulative sum over the event window from $\tau = 0$ to
$\tau = 10$: $i.e., [0,0], [0,1], ... [0,10]$. Likewise, we consider the
days leading up to the event to assess threats to the study design
(contemporaneous leading events or market anticipation) and factors such
as information leakage.

Our study considers the *average* impact of assassinations across
treated firms. Thus, we compute the aggregate CARs across $N$
company-event pairs: $$\begin{align}
    \overline{CAR}\left(\tau_{1} , \tau_{2} \right) =& \frac{1}{N}\sum_{j=1}^{N}\widehat{CAR}_{ie}\left(\tau_{1} , \tau_{2} \right). \label{eq:avg-car}
\end{align}$$ We test whether the mean CAR for a given window is zero
using a robust, non-parametric test statistic from
@kolari2011grank.@kolari2011grank's generalized rank *t*-statistic, or
GRANK relaxes parametric assumptions and introduces refinements suited
to our setting. Specifically, GRANK performs well for longer event
windows and when the exact pricing day--in contrast to the event
(assassination) date--is uncertain [e.g., @Luechinger2014; @Barrot2016].
The GRANK statistic is also robust to event-induced volatility, serial
correlation, and event-day clustering.

We present our preferred test alongside three alternative parametric
tests: *(i)* a simple (benchmark) *t*-test assuming that
$\overline{CAR}\left(\tau_{1}, \tau_{2} \right)$ follows a normal
distribution with mean zero and variance
$\sigma^{2} \left[ \overline{CAR}\left(\tau_{1}, \tau_{2} \right) \right]$;
*(ii)* the BMP [@boehmer1991event], which scales abnormal returns to
prevent volatile securities from biasing estimates toward detecting
average effects; and *(iii)* the modified BMP test of @kolari2010rho,
which corrects for cross-correlation ("clustering\") of abnormal
returns.

### Results: Main Patterns {#sec:classic-evstudy-results}

#### Negative Impact of Assassination Events

Figure [4](#fig:clascestudy-baseline){reference-type="ref"
reference="fig:clascestudy-baseline"} plots the traditional event study
estimates for treated firms and the benchmark *market* model. The
estimates show a steady negative abnormal reaction over the
post-assassination period. We observe little market reaction on the day
of the assassination, followed by a borderline significant effect of
about -0.7 percentage points the next day. This initial reaction
precedes a steady decline over the next four days and a steep (and
robustly significant) decline from days 5 to 10. On average, the CAR is
-2.0 percentage points 10 days following the event for the market model,
and this result is significant at the 1% level when using our preferred
non-parametric (GRANK) test statistic.

We report the alternative test statistics in Table C.4 and show that the
results from the main market model are robust to using a Fama-French
four-factor model (Figure C.5). Likewise, in (Section
[4.2](#sec:OLS){reference-type="ref" reference="sec:OLS"}), we show
similar effects using a regression-based exercise with control groups.

In other words, assassination events are significant and relevant to
firm value---and negatively so. We can compare these effects to
short-run estimates for instances of environmental crime (e.g., EPA and
other regulatory violations) from @Brady2019 (short-run estimates -1.6
to -1.7). In contrast to the environmental crime or environmental
disasters studies in the reputation literature [@Bouzzine2020],
penalties are unlikely in our setting.

Would we expect a negative impact? Not necessarily, and at least not a
strong one. Existing studies show reputational costs matter but vary
widely depending on the type of event. Notably, the reputational
penalties of events are small if those events are unlikely to change the
value of future interactions with counterparties. The literature shows
few reputational losses in cases where negative events do not impact the
direct parties with whom the firm does business, as is the case, for
example, with pollution and environmental disasters. The negative stock
reactions to these thus tend to almost entirely reflect governmental and
legal costs rather than market-based reputational losses; see reviews by
[@Karpoff2012] and [@Armour2021].

Importantly, controversial negative news has tended to be more impactful
when it contains stronger legal and material (direct economic) language
[@krueger2015; @Capelle-Blancard2010; @Carberry2018]. Whereas most
studies focus on the United States and, to a lesser extent, the OECD
countries, the negative impact of ESG events may, in part, be a
reflection of the strength of institutions in those jurisdictions
[@Karpoff2013]. For instance, @Lundgren2010 finds significant negative
abnormal returns for European firms relative to the US. Yet, the
imposition of legal penalties for human rights abuses abroad is
notoriously rare (see discussion and analysis in Section
[5.4.1](#sec:legal-and-financial-implications-of-associations-to-assassinations){reference-type="ref"
reference="sec:legal-and-financial-implications-of-associations-to-assassinations"}).

#### Slow Diffusion and Market Under-Reaction

The short-run dynamics of Figure
[4](#fig:clascestudy-baseline){reference-type="ref"
reference="fig:clascestudy-baseline"} are also notable. The market
response in Figure [4](#fig:clascestudy-baseline){reference-type="ref"
reference="fig:clascestudy-baseline"} is not sharp and immediate;
instead, the response to information is delayed. Among other things,
this pattern suggests slower information diffusion through the market.
For example, market participants may gather additional information on an
event before pricing the expected costs for a treated company. Unlike
more common ESG events, assassinations are relatively unique and
complex. Political events of this nature may require further information
and more time for investors to process their impact. Hence, we may
observe a market underreaction to the initial event in Figure
[4](#fig:clascestudy-baseline){reference-type="ref"
reference="fig:clascestudy-baseline"}.

The dynamics of this market reaction differ from those identified in
many of the studies of corporate controversies. Several empirical event
studies document swift over-reactions (large short-run declines,
followed by reversals) to corporate controversies [@cui2020; @Chen2020],
which is consistent with work on negative media and over-reaction to
corporate news [@tetlock2007]. We explore these dynamics in our
regression analysis below (Section [4.2](#sec:OLS){reference-type="ref"
reference="sec:OLS"}) and in our long-run analysis (Section
[4.3](#sec:longrun){reference-type="ref" reference="sec:longrun"}).

#### No Pre-Event Abnormalities: Validating the pre-event window

We validate the estimation strategy above and show that stock returns
did not move significantly over the days before the assassination dates.
By doing so, we provide evidence that the market is indeed pricing new
information, rather than merely detecting pre-existing trends or
responding to other prior events. Furthermore, where (assassination)
events are planned, the "authorization" date is unknown. A reasonable
assumption is that if private information exists, it should be priced
close to the actual event date when the likelihood of execution can be
best assessed by insiders [@Dube2011].

We study the pre-event period by aggregating abnormal returns *backward*
starting on the day before the event and run a placebo exercise [see
@Dube2011; @Luechinger2014]. We find no significant market responses
before assassination events. Online Appendix Figure C.6 shows that the
average abnormal return on the day before the event is positive, while
the CAR over the 10 days before an event is close to zero or slightly
negative and insignificant across test statistics.

In other words, Online Appendix Figure C.6 indicates two things. First,
the market does not price prior knowledge of assassinations. For studies
of malfeasance and ESG controversies, it is not uncommon for ambiguity
to surround events and their timing [@krueger2015], particularly in
complex cases of firm misconduct (e.g., SEC enforcement activity
[@Karpoff2008]). Second, and importantly, our core event study results
are not *merely* picking up a downward pre-trend in the asset prices for
those companies associated with violence. Furthermore, if other
non-assassination events drive these results, they do not occur prior to
the event day. We test for pre-trends more thoroughly in Section
([4.2](#sec:OLS){reference-type="ref" reference="sec:OLS"}) and also
reject the possibility that other disruptions are confounding our
estimates (Section [4.2.3](#sec:OLS-robustness){reference-type="ref"
reference="sec:OLS-robustness"}).

#### Robustness

The negative pattern described above is robust to alternative (stricter)
estimation criteria. Online Appendix Figure C.7 shows that our results
remain unchanged when we require companies to be traded each day within
the 11-day event window and for 225 out of the 250 days in the
estimation window. This criterion drops seven company-event pairs and
reduces the magnitude of our CARs to -1.5 percentage points 10 days
after an event; the estimates remain highly significant and robust. The
difference in point estimates may be driven by trading halts for highly
affected securities. Moreover, the securities of small mining companies
may be less frequently traded than larger companies; we expect these
firms to be dependent on a single project and, therefore, more
vulnerable to disruption following an event than larger companies. Thus,
stricter requirements on trading frequency may underestimate the true
effects of assassination events.

## Regression-Based Event Study {#sec:OLS}

### Estimation {#sec:OLS-estimation}

We build on the traditional event study analysis above (Section
[4.1](#sec:classic-evstudy){reference-type="ref"
reference="sec:classic-evstudy"}) by estimating the impact of
assassination publicity using a comparison between treated and
non-treated firms. Specifically, we compare the CARs for companies with
projects named in human rights reporting against those of control
companies: firms operating in the same sector, country, and period in
which the assassination occurred. Formally, consider the following
regression equation:

$$\begin{align}
    CAR_{ie}\left( \tau_{1}, \tau_{2} \right) = \alpha + \delta D_{ie} + \boldsymbol{X}_{ie}'\phi + \gamma_{e} +\epsilon_{ie},
    \label{eq:regression}
\end{align}$$

where $CAR_{ie}\left( \tau_{1}, \tau_{2} \right)$ is the CAR for company
$i$ and event $e$ from $\tau_{1}$ to $\tau_{2}$. CARs are calculated
identically for both treatment and control firms. The indicator $D_{ie}$
denotes the treatment and equals one if a company is associated with an
event, and zero otherwise. The coefficient of interest, $\delta$,
captures the average difference in CARs between treated and control
firms. Our empirical strategy relies on the assumption that, absent a
company being linked to an assassination event in reporting, we would
not observe systematic differences in the returns of treated and control
firms during the event window.

The strength of this identifying assumption depends, in part, on our
choice of controls and the control group. Our preferred specification
includes event-fixed effects, $\gamma_{e}$, which control for common
market reactions around dramatic events. These effects capture shifts in
market sentiment toward the event country or increased excess volatility
following political events. We also present an alternative version of
Equation [\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"}, which replaces event-specific effects,
$\gamma_{e}$, with company-fixed effects ($\gamma_{i}$). In this case,
we compare the impact of an assassination event on a company when it was
merely active in the country during an event period to the impact when a
company is directly tied to an assassination. Note that a company cannot
be part of the control and treatment groups for the same event; we thus
do not have a convolution of the control and treatment groups. The
baseline specification
[\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"} also includes a set of firm-level controls,
$\boldsymbol{X}_{ie}$: total assets and leverage (total debt to
capital). Small or highly leveraged firms may be more dependent on
specific mining projects and thus differentially impacted by disruptions
in the wake of an event. Hence, baseline estimates are conditioned on
these key variables. We address issues of "bad controls" by using the
value of each firm characteristic in the year before the event.

Importantly, we compute CARs for each event and set of firm controls for
the company-specific effect of market movements on the firm's stock
price over the event window. By re-estimating the market model for each
event, we account for changes in the relationship between market and
firm returns over time.

Our set of control companies has multiple advantages and is guided by
the political economy and finance literature. First, we select control
firms with mining operations in the same country where the event
occurred. Doing so accounts for common exposure to political risk
events---especially those impacting mining---in a given locale at the
time of the event; for instance, incidents where violence against
activists changes the national sentiment against the mining industry.
Second, following @ferrara2007, we compare treated companies to those
with a similar "comparative advantage" operating in high political risk
environments (p.1987). Lastly, we control for commodity price
fluctuations that impact mining companies operating in similar commodity
markets and the same domestic market.

We estimate Equation
[\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"} using a standard linear fixed effects
regression. Because we use event $\times$ firm-specific cross-sectional
variation, Equation
[\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"} is not a two-way fixed-effects (TWFE)
estimator. We are, therefore, able to avoid issues posed by TWFE
regressions [@GoodmanBacon2021 among others]. Standard errors are robust
to heteroscedasticity and clustered at the event level.

Further, we employ an alternative synthetic control-type estimator,
where treated firms are matched with respect to their return patterns
prior to each event. Section
[4.2.4](#sec:synthReturn){reference-type="ref"
reference="sec:synthReturn"} shows our OLS results are robust to this
alternative method. We first turn to the baseline estimates from
Equation [\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"}.

### Regression Event Study: Results {#sec:OLS-results}

#### Main Patterns

Our OLS estimates of Equation
[\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"} reveal clear patterns in the impact of
assassinations on returns. Figure
[5](#fig:cross-section-main){reference-type="ref"
reference="fig:cross-section-main"} displays these results, plotting 42
*individual* regression coefficients across time. The vertical axis
shows the ($\tau$) days after (before) the event. The top panel displays
our baseline specification, Equation
[\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"}, with event-fixed effects, whereas the bottom
panel employs company-fixed effects. Both panels present 90 and 95%
confidence intervals.

Before assassination events, exposed and non-exposed firms show no
significant differences in CARs; in fact, treated firms have slightly
higher returns. This pre-event stability mirrors the lack of pre-period
movement we observe in our traditional event study (Section
[4.1.2](#sec:classic-evstudy-results){reference-type="ref"
reference="sec:classic-evstudy-results"}).

Assassinations trigger a consistent decline in abnormal returns for
treated companies relative to the control group. There is no change on
the event day, yet significant changes emerge two days later. CARs drop
by 1.0 and 1.3 percentage points for event- and company-fixed effects
specifications, respectively. This negative trend persists, and CARs
continue to decline over the next five days. By the tenth day following
the assassination, the abnormal returns of exposed mining companies fall
between 2.0 and 2.8 percentage points.

The findings from our regression and traditional event study demonstrate
that financial markets process information on assassination events
gradually. This contrasts with the response to firm scandals and other
ESG events. It is not uncommon for studies to find markets overreact
with sharp initial declines, followed by reversions
[@Karpoff2012; @Borelli-Kjaer2021] or overreactions to negative ESG news
[@Chen2020]. For example, the negative effects of corporate crises
[@Wei2017] or major chemical disasters [@Capelle-Blancard2010] are
insignificant by Day 10.

#### Impact of assassinations on treated v. control firms {#sec:impact_on_controls}

Are the effects in Figure
[5](#fig:cross-section-main){reference-type="ref"
reference="fig:cross-section-main"} driven by negative returns among
treated firms, or by benefits accruing to competitors in the control
group? *A priori*, the impact on competitors is unclear. While
competitors could benefit from firms operating in the same country and
industry being embroiled in controversy, assassination events could also
have negative industry-wide effects and spillovers
[@Bouzzine2020; @Bouzzine2021], prompting industry-wide scrutiny or
regulation, especially among similar firms [@Ouyang2020].

We assess the impact on control firms by conducting a placebo version of
the traditional event study, restricted to the sample of treated firms.
Online Appendix Figure C.8 shows that the effect of assassination events
on control companies is small and insignificant. In absolute terms,
placebo estimates are smaller than our principal event study estimates;
the average CAR does not exceed 0.4 percentage points in the 10 days
following the event.

These findings indicate that the negative market reactions in Figure
[5](#fig:cross-section-main){reference-type="ref"
reference="fig:cross-section-main"} are not driven by spillovers to
control firms (whether positive or negative). Instead, our results
reflect firm-specific negative returns rather than broader sectoral or
inter-firm effects. Practically, it is worth noting that our
regression-based estimates align with traditional event study estimates,
which do not rely on control group counterfactuals. Moreover, Figure
[5](#fig:cross-section-main){reference-type="ref"
reference="fig:cross-section-main"} row 2 shows that differences in
cumulative returns are particularly pronounced in our specification
using only within-firm variation.

#### Widening the window: testing for pre-event trends and reversals

Next, we expand the event window to 20 days before and after the event
to (a) investigate the potential of pre-trends and (b) test for
reversals after the 10-day window. Online Appendix Figure C.11 displays
the assassination coefficient estimates for our baseline specification,
Equation [\[eq:regression\]](#eq:regression){reference-type="eqref"
reference="eq:regression"}. We adjust the minimum trading data criteria:
companies must be traded on at least 15 of the 21 days after the event
and 15 of the 20 days before the event. After the event date, returns
decrease monotonically until Day 13, with this decline appearing
permanent. Before the event date, estimates are positive but
insignificant.

These findings suggest that our results are (a) not attributable to
pre-existing trends and (b) are relatively persistent. We perform a
longer-run band-and-hold analysis in Section
[4.3](#sec:longrun){reference-type="ref" reference="sec:longrun"} and
contrast these effects to reversals seen in the nascent reputation and
deterrence literature.

#### Loss from assassination events

The estimated effects are also economically meaningful. Figure
[6](#fig:loss){reference-type="ref" reference="fig:loss"} plots the
estimated loss in market capitalization on each day for the median
treated company. The dots correspond to baseline estimates; the error
bars correspond to the minimum and maximum loss across specifications
(see Online Appendix Figure C.9).

According to Figure [6](#fig:loss){reference-type="ref"
reference="fig:loss"}, the median treated company is estimated to lose
between USD 100 and 150 million in market capitalization over the 10
days following the event. The effect is also economically sizable in
relative terms: for instance, @krueger2015 [p.313] finds a median loss
of USD 76 million to news of negative ESG events in a well-known CSR
database.[^7]

### Robustness: Regression Results {#sec:OLS-robustness}

We demonstrate that our OLS event study results are robust to several
extensions. Specifically, they are not driven by individual countries or
firms, nor are they sensitive to specific events or specifications. We
also rule out that the effects are driven by general contemporaneous
conflict.

#### Sensitivity to single firms or countries

Figure [7](#fig:leave-one-out){reference-type="ref"
reference="fig:leave-one-out"} presents a "leave-one-out" analysis of
our OLS results, showing that estimates are not driven by any single
country or firm. Our baseline regression results appear in bold, with
permutations in light gray. In Panel A, we re-estimate our baseline
specification, sequentially dropping individual event countries from our
sample. The negative effects remain visually similar across sample
permutations, showing a clear and gradual decrease in abnormal returns
over the 10 days following the event. Abnormal returns in the days
leading up to the event remain slightly positive, though close to zero.
Importantly, the core pattern persists even when excluding the two
deadliest countries for mining activists: Peru and the Philippines
(dashed red line).

This exercise is repeated in Panel B of Figure
[7](#fig:leave-one-out){reference-type="ref"
reference="fig:leave-one-out"} with firms sequentially dropped. Our
baseline results remain qualitatively similar, with the homogeneity
across the light gray bands indicating that our findings are not driven
by particular "bad actors\". This suggests the broad applicability of
our results to publicly traded mining firms.

#### Event type

Our OLS results are also robust across different types of assassinations
and similar events. Online Appendix Table C.5 shows that post-event
assassination estimates remain qualitatively unchanged when we exclude
unsuccessful assassinations (Columns 1 to 5) or activist killings during
protests (Columns 6 to 10). While the point estimates follow a similar
pattern to our baseline results, excluding these events (26 events
corresponding to 47 event-company pairs in the latter case) reduces the
explanatory power and significance of the results.

#### Functional form

Online Appendix Figure C.9 demonstrates the robustness of our baseline
results when accounting for potential non-linear effects of covariates.
Including cubic polynomials in size, leverage, and profitability (return
on equity) does not significantly alter our findings (Column 2). The
core pattern remains consistent across specifications with different
fixed effects, including less conservative sets like year ($\gamma_{y}$)
and headquarter-country ($\gamma_{h}$) effects (Rows 2 and 3).

#### Outliers

Our baseline results persist when we control for outliers. Online
Appendix Table C.5 shows that excluding CARs beyond the 1st and 99th
percentiles (Columns 11 to 15) does not substantially change our
findings. The assassination coefficients remain similar in magnitude
and, in most cases, become more precise, with the exception of the
company-fixed effects specification. This suggests that, for some firms,
association with an assassination event is an extreme observation and
supports the notion that assassinations can impact individual firms.

#### Assassinations or Contemporaneous Local Conflict?

Are our estimates driven by assassination events or by contemporaneous
disruptions? We address this question by comparing the returns of
treated firms to geolocated control firms: mining companies operating
within the same subnational administrative unit but not named in
relation to the event (i.e., not treated). This approach helps
distinguish between the market pricing of an association with activist
murders and reactions to concurrent disruptions or unobserved regional
violence.

We create a new set of control companies by matching assassination
events to mining projects in the same subnational (*Admin1*) region.
Using the SNL Metals & Mining database, we map the geolocation of
assassinations to nearby properties, as illustrated in Online Appendix
Figure B.3. This approach capitalizes on the geographically specific
nature of most mining opposition, which often involves land claims,
Indigenous territory, and environmental concerns. If there is other
contemporaneous conflict, it is likely to be geospatially clustered.
Although we face data constraints, we successfully match at least one
publicly traded control company operating in the same region as an
"exposed" company for 92 firms in our sample.

Using these granular control firms---those most susceptible to localized
conflict---yields results qualitatively similar to our main findings.
Panel B of Online Appendix Figure C.10 presents estimates of Equation
[\[eq:regression\]](#eq:regression){reference-type="ref"
reference="eq:regression"} using the fine geographic controls; Panel A
presents our benchmark estimates. Despite the reduced sample size
following geomatching, Panel B shows a gradual relative decrease in CARs
for treated firms, with no discernible pre-trend. Ten days after an
event, CARs are 1.3 (2.8) percentage points lower for our baseline
specification with event effects (company fixed effects). Online
Appendix Table C.6 shows broadly negative estimates across
specifications with similar magnitude. In the unrestricted specification
(Column 1), coefficient estimates are precise and significant at the 5%
level.

These findings suggest that the negative impact we observe is not driven
by spatial disruptions from conflict. Rather, our estimates likely
capture market responses to firms' associations with violence in
reporting by the media and NGOs.

### Synthetic Matching Estimation {#sec:synthReturn}

We build on our OLS estimator and estimate the impact of events using a
modified version of the synthetic matching estimator in the spirit of
[@Abadie2010a] and @acemoglu2016. This approach accounts for potential
unobserved differences between treated and control firms not captured by
our regression Equation
[\[sec:OLS-estimation\]](#sec:OLS-estimation){reference-type="eqref"
reference="sec:OLS-estimation"}. This allows us to compare the returns
for each treated firm to a synthetic control group with similar
pre-event dynamics. Specifically, a synthetic firm's returns are a
weighted, convex combination of control-company returns, where weights
are chosen to optimally match pre-event returns for a given treated
company. We provide an open-source **R** software package
[`synthReturn`](https://github.com/davidkreitmeir/synthReturn) that we
used to implement this procedure.

Our synthetic matching estimator extends the approach in @acemoglu2016
to accommodate multiple event dates and two inference procedures. We
select a set of control firms for each event date and treatment company
combination. The estimated average treatment effect,
$\hat{\phi}\left(\tau_{1},\tau_{2}\right)$, averages the CARs for each
treatment group company, weighted by the "goodness" of its synthetic
match over the estimation window. The abnormal return equals the
difference between a treated firm's actual return and the return of its
synthetic match. To ensure a sufficient number of control firms at each
event date, we define the pool of potential control companies to include
all mining companies traded in treatment markets. We use a simple
nonparametric bootstrap and a permutation inference method, drawing
placebo treatment groups from the set of control firms, to to obtain
uncertainty estimates for the cumulative effect estimates.[^8] For more
details on the synthetic matching method, see Online Appendix Section
[\[synth-match\]](#synth-match){reference-type="ref"
reference="synth-match"}.

Table [\[tab:synth-match\]](#tab:synth-match){reference-type="ref"
reference="tab:synth-match"} reports the synthetic event study estimates
for the event day and the ten subsequent trading days. As in our OLS
estimation, the impact of being associated with an assassination event
is negative and increasing over the event window. The estimated
cumulative effect even exceeds our benchmark OLS estimates, reaching
about 6.1 percentage points ten days after the event.

## Long-Run Effects: Persistence and Testing for Reversals {#sec:longrun}

We confirm that the market penalties are long-run. If negative returns
are temporary, market sanctions may not provide sufficient incentives to
improve firm behavior [@Ambec2008; @Gantchev2021]. Although work on
reputation often establishes short-run impacts---typically $[-1,1]$ or
$[-2,2]$ day windows---these penalties may be transitory. Indeed,
numerous empirical studies find that stock market penalties for negative
events are often transitory [@Ambec2008; @Capelle-Blancard2010], such as
in the case of major environmental disasters [@Carpentier2015]. More
generally, in the short run, equities may simply overreact to news
events with negative valence and quickly mean-revert. Such reversals are
seen in low-information negative news events [@Tetlock2014] or extreme
events [@Kwon2020]. However, the benchmark penalties thus far are not
consistent with temporary market penalties or overreactions to noisy
news.

We further confirm that the effects are not transitory. We show the
long-run impact of human rights controversies by first (a) conducting
descriptive analyses and then (b) using buy-and-hold abnormal returns
(BHAR). This approach serves as an alternative to long-horizon event
studies, which face econometric challenges and are sensitive to baseline
specifications [@Mitchell2000; @kothari2007].

Panel A of Figure
[8](#fig:classic-event-study-long-run){reference-type="ref"
reference="fig:classic-event-study-long-run"} presents the average CARs
for treated companies in the 90 days following the event. Following the
significant negative initial market reaction over the first 13 days, the
long-run average of the CAR for the following 77 trading days remains at
2.4 percentage points. Given the challenges of measuring abnormal
returns and statistical inference, these results are only indicative.

We follow the literature and use buy-and-hold abnormal returns to study
the long-run effect on treated firms. The BHAR approach involves
comparing the total returns of two portfolios of firms held for a
pre-determined period and comparing the total returns of event firms to
a benchmark portfolio held over the same long-run period.[^9]

In other words, relative to a benchmark, how well would an investor
perform if they bought and held treated stocks? According to Panel B
(Figure [8](#fig:classic-event-study-long-run){reference-type="ref"
reference="fig:classic-event-study-long-run"}), quite well over the long
run. Although the difference between summing returns (CAR) and
compounding (BHAR) returns is negligible in the short run, differences
compound in the longer term. The short-run BHAR on Day 13 deviates only
marginally from the CARs, whereas the long-run average of the BHAR
surpasses the CAR by 3.2 percentage points. This pattern is robust to
the use of a Fama-French normal-return model instead of the classic
market model.

In sum, the long-run analyses above suggest a persistent impact of
assassination events on firm returns. The extent and duration of these
effects stand in contrast to the transitory shocks in studies of
reputation and firm conduct. We next turn to the forces potentially
driving the extent of the market penalties.

# Mechanisms {#sec:mechanisms}

We consider three channels driving the reputational penalties above.
First, we examine the role of *(1)* media in disseminating information
to stakeholders and show that key trading-partners (investors and
buyers) respond: specifically, *(2)* sophisticated institutional
investors, and *(3)* counterparties in the global supply chain. All
three factors are compatible with reputational penalties. Accordingly,
we do not find evidence that the decline in stock market value is driven
by *(4)* other non-market forces, such as legal fines and local
disruptions to operations.

## Mechanisms: The Media {#sec:fourth-power}

Media influences the informational environment of international
financial markets, and the extent to which stakeholders act on
revelations. We establish the role of media attention in disseminating
information to other market participants, including stakeholders.
Empirical behavioral finance demonstrates that media attention
significantly impacts stock returns and the cost of capital
[@Tetlock2014; @Tetlock2015]. Additionally, research on misconduct
penalties indicates that media coverage amplifies the market penalty
[@Carberry2018; @Mariuzzo2020]. The reputational consequences of events
for firms---distinct from formal legal costs---are likely mediated by
the media environment. We build on earlier research into misconduct and
directly test this channel using an empirical strategy from media
economics [@eisensee2007].

We show the impact of media coverage on market responses by considering
exogenous variation in media attention. A principal challenge in
isolating the role of reporting is that media attention may be
endogenous to the event. For instance, simple proxies of media attention
(e.g., counts of articles surrounding an assassination) may be driven by
stock movements or other factors. Hence, we consider exogenous variation
in media attention to our events, using the daily news pressure index of
@eisensee2007.

Our exogenous shifter of attention, *daily news pressure*, is defined as
the median number of minutes the main US news broadcasters devoted to
the top three news segments in a day @eisensee2007 (see Section II.C and
Online Appendix V.B). We expect the degree of attention to be lower if
the assassination coincides with a "high news pressure" day---that is, a
day on which an event is overshadowed by larger global events exogenous
to the assassination.

We study the impact of media by expanding our baseline regression model:
$$\begin{align}
    CAR_{ie}\left( \tau_{1}, \tau_{2} \right) = \alpha + \alpha^{N} N_{e} + \delta D_{ie} + \delta^{N} \left( D_{ie} \times N_{e} \right) + \boldsymbol{X}_{ie}'\phi+ \gamma_{e} + \epsilon_{ie},
    \label{eq:interaction-reg}
\end{align}$$

where we add an interaction term between the treatment indicator
$D_{ie}$ and a dummy variable, $N_{e}$ that is equal to one if the event
falls on a day where news pressure is high, and zero otherwise. We allow
for different intercepts of high and low news pressure days to account
for general differences in trading behavior on the days where news
pressure is high. The coefficient $\delta^{N}$ conveys the difference in
average CARs for events that fall on high versus low news pressure days.

#### Baseline Results

Figure [9](#fig:news-pressure-main){reference-type="ref"
reference="fig:news-pressure-main"} shows the differential impact of
media and reports the estimates from Equation
[\[eq:interaction-reg\]](#eq:interaction-reg){reference-type="eqref"
reference="eq:interaction-reg"}. In Panel A, high news pressure days are
defined as those where the news pressure is above the median value of
the news pressure index for the period 1998 to 2018. Estimates in Panel
B use an alternative 75th percentile cutoff. Black lines (dots)
correspond to the impact of assassination events that fall on days when
news pressure is high ($\delta + \delta^{N}$), whereas red lines (dots)
correspond to the impact of events that fall on low-pressure days
($\delta$). Blue lines (squares) depict the absolute difference between
the two ($\left|\delta^{N}\right|$) or the differential impact of
assassinations depending on whether they fall on days with high or low
news pressure. Each panel reports 95% confidence intervals.

The estimates in Panels A and B show a significant, continuous decline
in CARs for treated companies when assassinations fall on low-pressure
days. However, estimates are indistinguishable from zero when the event
coincides with a high-news-pressure day. Moreover, we observe a gradual
divergence in CARs between the two types of events. By Day 10, the
difference in CARs between above and below median days is 4.1 percentage
points and significant at the 5% level (Panel A). A qualitatively
similar pattern appears if the event falls on a day where the news
pressure is above the 75th percentile in Panel B. Quantitatively, the
divergence is less precisely estimated and slightly attenuated in this
more demanding specification.

#### Alternative News Pressure

A potential concern is that perpetrators may strategically time their
attacks to coincide with high-pressure days, thereby minimizing public
scrutiny. We address this concern by employing the empirical strategy of
[@jetter2022] and consider an alternative measure: "disaster predicted
news pressure." This measure isolates the exogenous component of news
pressure. Specifically, we regress the daily news pressure index on
*(i)* the day-to-day count of unpredictable disasters (earthquakes,
epidemics, and volcanic eruptions) in countries hosting at least 50,000
U.S. emigrants (plus Iraq and Afghanistan), *(ii)* linear and squared
time trends, and *(iii)* a set of day-of-the-week, month-, and
year-fixed effects.[^10] The disaster coefficient estimate is 0.247
(significant at the 1% level using Newey--West standard errors, with a
lag of one day). We then use these parameter estimates to predict the
news pressure on any day $t$ for the period 1998 to 2018 and create an
indicator of high levels of news pressure using only statistically
unpredictable variations in news pressure.

We rerun the analyses in Panels A and B using this alternative pressure
variable, as shown in Panel C. These estimates are quantitatively and
qualitatively similar when the event occurs on a day on which the
*predicted* news pressure is above the 75th percentile, substantiating
the baseline findings in Panel A.

#### Robustness

In Online Appendix Section C.3, we show that the findings above are
robust to additional sensitivity checks and that more transparency
surrounding the extractive industry magnifies the human rights penalty.
Additionally, we demonstrate that there is no statistically significant
correlation between the daily level of news pressure and assassination
events.

## Mechanisms: Institutional Investors {#sec:institutional-investors}

Having shown the negative impact of assassination events and the role of
the media, we now consider the role of institutional investors.
Institutional investors have the power to move markets in response to
revelations. These investors are large, sensitive to new information,
and capable of processing complex social events
[@puckett2011; @hendershott2015 e.g.,]. Importantly, large investors are
increasingly attentive to and act on reputational events [@Brady2019].
Sizeable market players, such as sovereign wealth funds, may have
explicit ESG objectives. Likewise, a growing literature documents that
sophisticated investors react to revelations of misconduct.
"Irresponsible" corporate behavior is an important trigger for
shareholder activism for 72% of institutional investors [@mccahery2016].
Importantly, large investors may actively trade on revelations and
transmit ESG preferences through stock prices, as recently shown by
@Gantchev2021.

#### Empirical Framework

We examine the role of institutional investors and analyze how they
respond to human rights controversies using a stacked
difference-in-differences estimation framework developed by @StackedDID.
This framework accounts for staggered treatment and multiple events per
company, as well as non-continuous treatment in our setting.[^11]

To employ this estimator, we use a separate dataset balanced in
event-time for each *sub-experiment*, that is, each event calendar
period. Each of these sub-experiments $a \in \Omega_\kappa$ comprises
$N_{a}^{D}$ treated and $N_{a}^{C}$ clean control units for the entire
event window from $\kappa_{pre}, ..., \kappa_{post}$. Next, we stack all
sub-experiments in event time such that at each event period, the
stacked dataset comprises
$N_{\Omega_{\kappa}}^{D} = \sum_{a \in \Omega_{\kappa}} N_{a}^{D}$
treatment-group units and
$N_{\Omega_{\kappa}}^{C} = \sum_{a \in \Omega_{\kappa}} N_{a}^{C}$
control-group units. Therefore, each observation in the stacked data
refers to a
$\text{company} \times \text{sub-experiment} \times \text{event-time}$
$(i, a, \tau)$ observation.

We then estimate the following weighted event-study regression:
$$\begin{align}
Y_{ia\tau} = \alpha_{0} + \alpha_{1}D_{ia} + \sum_{j = \kappa_{pre},...,-2}^{\kappa_{post}}\bigl( \lambda_{\tau} \boldsymbol{1} \left[\tau = j\right] + \delta_{\tau}D_{ia} \times \boldsymbol{1} \left[\tau = j\right] \bigr) + e_{ia\tau},
    \label{eq:stacked-DID}
\end{align}$$ where the bias-correcting sample weights are defined as
$$\begin{align}
    Q_{ia} = \left\{\begin{array}{cc}
        1 &  \text{if} \qquad D_{ia} = 1 \\
        \frac{N_{a}^{D}/N_{\Omega_{\kappa}}^{D}}{N_{a}^{C}/N_{\Omega_{\kappa}}^{C}} & \text{if} \qquad D_{ia} = 0,
    \end{array}
\end{align}$$ and where $D_{ia}$ equals 1 if company $i$ is treated in
sub-experiment $a$, and 0 otherwise. The dependent variable $Y_{ia\tau}$
denotes the total value of shares of company $i$ held by institutional
owners in quarter $\tau$ divided by the total market capitalization of
company $i$ in quarter $\tau$. By expressing the holding position in
*relative* rather than *absolute* terms, the outcome is unaffected by
price changes, and we can isolate the effect on the institutional
owners' trading behavior.

The parameters of interest are the event-study coefficients
$\delta{\tau}$, with $\tau = -1$ serving as the reference period.
Following [@StackedDID], we allow all observations from the same unit to
be dependent, even if they appear in multiple sub-experiments and
cluster standard errors at the unit level.

#### Data {#data}

Data on institutional ownership come from the FactSet Ownership
database, which reports institutional investors' equity holdings on a
quarterly basis from 2000 to 2017. FactSet is widely used in the
empirical finance literature [e.g. @aggarwal2011; @dyke2019] due to its
global coverage of institutional investors, with data collected from
fund reports, regulatory authorities, fund associations, and fund
management companies. We rely on "Institutional Ownership Summary
Statistics by Firm'' as developed by @ferreira2008 and provided by WRDS.
Data on annual firm characteristics are from the FactSet Fundamentals
database.

Our final stacked panel comprises 67 public mining companies associated
with assassination events and 144 event-company pairs. The set of
possible control companies includes firms active in the "extractive"
sector; we define corporations as operating in the extractive sector if
their TRBC Business Sector classification is "Energy - Fossil Fuels,"
"Uranium," or "Mineral Resources."

#### Results

Our baseline results are presented in Figure
[10](#fig:io){reference-type="ref" reference="fig:io"}. Overall, the
total share of institutional ownership decreases in the event quarter
and the following year. However, these total effects are imprecise.
Importantly, institutional investors differ in their objectives and
investment strategies (e.g., pensions versus hedge funds) and how
responsive they are to ESG events.

Thus, Figure [10](#fig:io){reference-type="ref" reference="fig:io"}
depicts separate estimates for Equation
[\[eq:stacked-DID\]](#eq:stacked-DID){reference-type="eqref"
reference="eq:stacked-DID"} by type of institutional investor. We find
that, except for banks and insurance companies, institutional investors
appear to reduce their holdings after assassination events. This is the
case for hedge funds, in particular; these investors reduce their
holdings by about 7.8% relative to their average position. This swift
liquidation relative to other institutional investors aligns with
findings that hedge funds have shorter investment horizons [@cella2013],
are more inclined to monitor corporate behavior and respond rapidly to
costly information disclosures [@gargano2017], particularly following
revelatory news [@huang2020]. In contrast, institutional investors with
a long-term, strategic view of their portfolios, such as pension funds,
do not seem to systematically change their holdings in the aftermath of
an assassination event.[^12]

This heterogeneity may be attributed to several factors. Despite their
ESG commitments, even investors who actively engage companies on human
rights issues may be reluctant to set clear divestment timelines, even
when investee companies have contributed to severe human rights abuses
over extended periods [@UNHR2021]. The cases where pension or sovereign
wealth funds have divested from companies accused of human rights
violations are the exception; divestment is often the last resort among
strategies to engage with investee companies on human rights
issues.[^13]

#### Robustness: Social Events vs. ESG Scores

In Online Appendix Section C.5, we show that assassination events have
no significant impact on the overall ESG performance scores of mining
corporations, nor on their human rights or community scores. These
findings help explain why institutional investors, who primarily rely on
external ESG indicators for portfolio decisions rather than sourcing
information from NGOs or media outlets, show no reaction---or react
slowly. Our results align with survey responses from institutional
investors in @BHRC2018, which highlight that ESG indicators often lack
sufficient coverage of large companies operating in emerging markets.

## Mechanisms: Supply Chain {#sec:supply-chain}

Does the market penalty above reflect expectations of future lost
business in the supply chain? We explore this effect by considering
whether the market penalty could stem from changes in supply chain
activity.

Why might investors have negative expectations about sales after a human
rights controversy? In classic reputation theories, the size of the
reputational loss reflects the value of lost activity from
counterparties, such as buyers. Yet, ex ante, we may not anticipate a
reputational penalty in our setting. First, assassinations target
community members, not downstream buyers, as civil society tends not to
purchase unrefined cobalt concentrate. Conceptually and empirically,
news of misconduct against consumers tends to produce significant
reputational losses [@Karpoff1993; @Alexander1999; @Murphy2009]. Second,
it may be relatively harder to boycott undifferentiated commodities.
However, downstream buyers may still change their behavior following
revelations. We contribute to the literature on reputation by examining
how third-party controversies can impact reputation when they alter the
behavior of second parties (those trading with the firm).

We use rich supply chain data to investigate whether downstream buyers
adjust their behavior following these events.

#### Supply Chain Data and Empirical Framework

Specifically, we employ data at the corporate-customer-supplier level
from FactSet Revere, matched with our event dataset and firm
fundamentals from Worldscope. Revere provides a unique database of
global supply chain relationships that extends back to 2003 and has
become the research gold standard [@Dai2021; @Darendeli2022 among
others]. This data covers both major and minor private and publicly
listed customers. The database includes approximately 23,400 companies
worldwide, including 38 mining companies linked to at least one of our
assassination events and 143 untreated control mining companies.

For each of the 181 mining firms in our sample, we construct two main
outcome variables at the calendar-year level to capture transactions
with their corporate customers: *(i)* the number of contracts signed in
year $\tau$, and *(ii)* the number of unique customers initiating those
contracts. We analyze data at the calendar-year level because the
average contract duration for mining firms in our sample is 308 days.
This duration makes it unlikely that corporate customers would respond
to a CSR shock by canceling existing contracts, which would expire
within the next year [@Darendeli2022]. Instead, we expect customers to
reduce new or follow-up contracts. Additionally, we disaggregate
contracts by customer location to test whether customers from countries
with strong human rights records are more likely to sever ties with
mining companies linked to severe human rights violations.

We estimate the effect of assassinations on supply chain contracting by
employing the stacked-DID framework introduced in Section
[5.2](#sec:institutional-investors){reference-type="ref"
reference="sec:institutional-investors"}. Our baseline specification
includes the number of contracts expiring in a given year as an
additional control. This accounts for the independent effect of
re-contracting on our outcome variables [@Darendeli2022]. We consider an
event window that extends from three years before to one year following
the event.

#### Results

Figure [11](#fig:supply-chain){reference-type="ref"
reference="fig:supply-chain"} presents our baseline estimates. We find
that, overall, assassinations have a negative effect on both the number
of new contracts (first row) and the number of new customers (second
row), although these estimates are insignificant. Column 2 shows that
these negative estimates become stronger and more significant when we
focus on customers from countries with strong human rights protections,
defined as an above-median V-Dem Civil Liberties index score
[@vdem2022]. Mining companies in the human rights spotlight experience a
19% to 21% decrease in the number of contracts signed and the number of
unique customers relative to the mean.

Likewise, the results in Column 3 underscore the importance of civil
society. For customers from countries with a strong civil society, we
find a quantitatively and qualitatively comparable effect on supply
chain contracting (Column 3).[^14] Our benchmark findings are robust to
the use of alternative country-level indicators of human rights
protection (see Online Appendix Figure C.16).

In contrast, Online Appendix Figure C.17 shows that being linked to an
assassination event attracts customers from countries with weak
institutions. That is, customers based in authoritarian regimes or
countries with weak civil societies are unlikely to be deterred by
reports of human rights violations. Instead, they may strengthen their
ties with the implicated supplier if the loss of customers from
countries with strong human rights protection results in more favorable
contract conditions.

## Mechanisms: Alternative Channels {#sec:legal-and-financial-implications-of-associations-to-assassinations}

Thus far, we have highlighted market-based penalties for human rights
controversies. In this section, we offer additional analysis and explore
whether our results are driven by non-market costs born by firms
following assassinations. First, we consider the extent to which the
decline in stock prices reflects expectations about formal penalties.
Next, we consider whether the events directly impact firm operations by
seeding unrest. In other words, we verify the extent to which our main
results reflect market-based losses born by firms.

### Direct Legal and Financial Costs {#sec:legal-and-financial-implications-of-associations-to-assassinations}

We demonstrate that our results are unlikely to be driven by investor
expectations regarding legal penalties for human rights violations
abroad. In environments where legal capacity is high, stock price
movements reflect the expected formal and legal penalties that follow
revelations of a firm's conduct. In key cases, the price response to
negative events entirely reflects the formal legal penalty for
misconduct, implying a small reputational penalty [@Brady2019]. Studies
on responses to social controversies are almost entirely based on
controversies in the United States and, to a lesser extent, Western
Europe [@Karpoff2012]. Nevertheless, weakly governed areas may lack the
legal and enforcement capacity for firms to internalize the social costs
of misconduct.

Our setting is no different. When it comes to corporate human rights
violations abroad, there are notoriously few legal tools available
[@Ruggie2013]. Across our entire sample, we were unable to find evidence
that any of the events resulted in convictions or significant legal
fines for the treated companies. A detailed qualitative discussion on
the scarcity of court cases involving human rights conduct is provided
in Online Appendix Section C.7.1.

Formally, we conduct an empirical analysis to determine if the effect of
being associated with an activist's assassination varies with the
likelihood of facing legal consequences. We combine our event-level data
with the "Law and Order" index from The International Country Risk Guide
(ICRG) by the PRS Group, which measures the quality of a country's
judicial system. Specifically, we obtain information about the judicial
system's quality for both the country in which the mining company is
headquartered and the country where the assassination occurred.

If investors expect that association with an activist's assassinations
will result in legal indictments and subsequent financial losses due to
fines, then the effect on the company's CAR should increase with the
quality of the judicial systems in both the headquarters and event
countries. Our empirical analysis follows a similar approach to
specification
[\[eq:interaction-reg\]](#eq:interaction-reg){reference-type="eqref"
reference="eq:interaction-reg"} in Section
[5.1](#sec:fourth-power){reference-type="ref"
reference="sec:fourth-power"}. We analyze whether the effect of
assassination varies by the quality of the judicial system; we include
an interaction term between the treatment indicator $D_{ie}$ and a dummy
variable equal to one if the judicial-system quality is high (defined as
the respective country's Law and Order index at the 25th, 50th, or 75th
percentile) and zero otherwise.

The results, which examine the quality of the judicial system in the
event and headquarters country, are presented in Figure C.18 of the
Online Appendix. We find no evidence that the magnitude of the
assassination effect differs by the likelihood of facing legal
challenges and fines in either the headquarters or event country, as
proxied by the quality of the country's judicial system. Given the lack
of evidence of legal indictments resulting in substantial penalties for
the associated mining companies, we suspect that investors' reactions
are not driven by expectations about future legal actions for this type
of human rights violation.

### Protest and Local Disruptions {#assassinations-and-local-opposition}

Do assassinations and the resulting media attention provoke protests and
cause costly disruptions to firm activity? A priori, the effect of
assassinations on protests is ambiguous. On the one hand, eliminating a
key opposition figure might deter future protests and hinder
coordination. On the other hand, this violence could provoke a backlash
from the local community and increase opposition to a mining project.
Protests---whether nonviolent or violent---against a company's
operations can lead to temporary disruptions in resource extraction,
interruptions in logistics, damage to physical assets, or even a
permanent shutdown of operations.

#### Data and Empirical Framework

We employ a stacked-DID estimation framework to examine how
assassinations influence local protest movements in a two-month window
surrounding the event. Since protests are expected to intensify in the
weeks leading up to an assassination, we select a reference in the
saturated event-study regression as the start of the event window. Our
sample includes all 25 countries in which at least one assassination
linked to a mining company occurred. The analysis is conducted at the
ADMIN1-calendar-week level.

We source protest data from two datasets. First, the Mass Mobilization
(MM) Data Project [@Clark2016] provides reliable, granular information
on global protests, including their type and cause, making it more
dependable than other sources. Second, we use the Global Database of
Events, Language, and Tone (GDELT), which categorizes over 300
activities using CAMEO event codes [@CAMEO] and records roughly 60
attributes for each event based on print, broadcast, and web news media
in over 100 languages.[^15]

#### Results

Online Appendix Figure C.19 displays the stacked DID event-study
estimates of the impact of assassinations on protest incidence
probabilities during the four weeks before and after the event. For
protests recorded in MM, we observe a modest, imprecisely estimated
increase in incidence probability during the event week, with no
significant effect in subsequent weeks (Panel A). The fact that several
extrajudicial killings in our dataset occur during and around protests
is consistent with these protests being tied to mining opposition and
related violence.[^16]

The GDELT data (Panel B) exhibit a noisier and less consistent pattern,
which contrasts with anecdotal evidence. In Panels C and D of Online
Appendix Figure C.19, we focus on MM protests using detailed start and
end dates to analyze whether assassinations trigger or suppress
opposition. The probability of protest onset peaks within the three
weeks surrounding the event but drops sharply after the second week. In
contrast, the probability of protest termination peaks during the event
week and remains elevated thereafter.

Overall, our findings suggest that protest activity peaks in the week
before and during the week in which the event occurs. Activity then
declines. The absence of market reaction in the weeks leading up to
assassinations, combined with the drop in protest activity after the
event, reinforces the conclusion that expectations of escalating costs
from intensified protests are unlikely to drive investor behavior.

# Persistence: Assassinations and the Political Economy of Local Rents {#sec:principal-agent}

Given the economic losses associated with these assassinations, why do
they persist? Multinationals are sprawling and complex, with blurry
organizational boundaries. Their upstream operations may be controlled
by actors whose incentives diverge from those of their owners. Local
stakeholders benefiting from mining projects may have incentives to
suppress or eliminate opposition while avoiding the financial losses
borne by shareholders. Domestic governments and state-aligned
paramilitaries exemplify such agents, as uninterrupted production
generates higher royalties and tax revenues. The relative gains from
malfeasance should, therefore, increase with an increase in the mining
company's relative importance as a revenue source. Put differently, the
larger a company's tax payments relative to its competitors, the greater
the incentive for local authorities to suppress opposition leaders who
challenge its projects.

#### Data {#data-1}

We construct new data on local public financing of mining companies to
examine the relationship between violence and government rents. We
collect this data manually from reports published by the Extractive
Industries Transparency Initiative (EITI), an international civil
society organization. Nations participating in EITI commit to disclosing
payments received from extractive companies, typically including
payments from subsidiaries and joint ventures.

We aggregate tax payments at the company level by hand coding yearly
ownership shares using historic ownership data from Bureau van Dijk's
Orbis database. When such data are unavailable, we obtain supplementary
data from annual reports. Tax revenues from subsidiaries and joint
ventures are allocated to owners according to their ownership shares.
For instance, in 2014, Anglo American owned 81.90% of the Peruvian
mining company Anglo American Quellaveco S.A., while Mitsubishi owned
the remaining 18.10%. In this case, USD $202,232$ of the USD $246,925$
in tax and royalty payments to the Peruvian government is attributed to
Anglo American, with the remainder being attributed to Mitsubishi.

For each country-year pair (i.e., report), revenues are aggregated at
the corporate-owner level and divided by the total tax revenues from the
mining industry to calculate the annual tax share of firm $i$. Summary
statistics are presented in Online Appendix Table C.11, disaggregated by
event country.[^17]

#### Empirical Framework

To analyse how government revenues influence the occurrence of
assassinations. Specifically, we estimate the following equation:

$$\begin{align}
\text{K}_{ict} = \beta_{1} \text{T}_{ict} + \gamma_{ct} + \epsilon_{ict},  
\label{eq:lpm}
\end{align}$$

where $\text{K}_{ict}$ is a dummy variable that takes the value of one
if an assassination event in country $c$ in year $y$ is associated with
company $i$ and $\text{T}_{icT}$ corresponds to the tax share of company
$i$ in country $c$ in year $t$.

In our preferred specification, we include
$\text{country} \times \text{year}$ fixed effects ($\gamma_{ct}$) to
account for country-specific economic and political developments. By
relying exclusively on within-$\text{country} \times \text{year}$ (i.e.,
EITI report) variation, we minimize concerns about potential sample
bias. Standard errors are clustered at the
$\text{company} \times \text{country}$ level.

#### Results

Table
[\[tab:royalties-table\]](#tab:royalties-table){reference-type="ref"
reference="tab:royalties-table"} reports the results. In Column 1, we
find a significant and positive unconditional correlation coefficient of
13.8 percentage points. Including country-fixed effects (Column 2) and
year-fixed effects (Column 3) increases the estimated effect to 17.4
percentage points. In our preferred specification, which includes
$\text{country} \times \text{year}$-fixed effects (Column 4), we
estimate that a hypothetical mining company (as the sole taxpayer) is
associated with an 18-percentage-point increase in the likelihood of an
assassination event occurring in connection with one of its projects.
For the average firm in our sample, this represents a 26% increase
relative to the mean.[^18] Estimates are qualitatively similar when we
employ a *probit* instead of a linear probability model (Online Appendix
Table C.12).

Reassuringly, we find no significant impact of an assassination event on
the company's relative importance as a source of government revenue
(Online Appendix Table C.13). These findings assuage concerns about
reverse causality. Nevertheless, the estimates are indicative, not
causal.

# Conclusion {#sec:conclusion}

Can markets discipline human rights misconduct abroad? We study the
significance of market or reputational penalties resulting from
significant corporate events abroad. Extensive research on firm
misconduct shows that market-based reputational penalties can be
substantial, yet not in all settings. Notoriously, market penalties are
weakest for controversies that do not impact direct customers or
suppliers (i.e., counterparties), as seen famously in the case of
environmental violations [@Jones2001; @Karpoff2005; @Cline2018]. Yet,
evidence on reputational deterrence is particularly sparse for the
developing world [@Karpoff2012]. Recent work suggests that the
reputational costs of firm conduct may be weaker for multinationals in
foreign markets [@Nardella2023].

We study how markets sanction corporations exposed to foreign human
rights scandals by examining how stock prices respond to the
assassination of environmental activists. We employ financial event
study methodology using 20 years' worth of new granular event data on
assassinations tied to global mining activity. We find that
assassinations have a large, robust negative effect on the value of
corporations caught in human rights controversy abroad. For these firms,
we estimate significant negative cumulative abnormal returns following
an event, with the median 10-day cumulative loss in market
capitalization exceeding USD 100 million. We show that the effects are
persistent by extending our short-run analysis and employing a long-run,
buy-and-hold analysis. This contrasts with market overreactions to
uninformative negative news events and evidence of transitory penalties
from controversies.

We highlight three mechanisms, all of which are compatible with
reputational channels. First, we demonstrate that media attention
amplifies the market penalty, potentially increasing the salience of
events to financial decision-makers and relevant stakeholders. We find
that the penalty associated with human rights news disappears during
more active news cycles but persists during less eventful news periods.
Second, we provide evidence that information-sensitive institutional
investors respond significantly to assassination events. Third, we use
rich supply chain data to show that downstream buyers respond negatively
to these events. We find that being associated with an assassination
leads to a 19% reduction in new contracts and a 21% decrease in new
corporate customers from countries that emphasize human rights
protection. Despite high market-based reputational penalties, we
demonstrate that assassinations increase with dependence on mining
royalties, suggesting that local rents may perpetuate conflict even when
multinationals face severe reputational costs. All three mechanisms are
compatible with prior theoretical and empirical work on market
penalties.

This work contributes to the emerging work on the political economy of
multinationals and the political economy of human rights. Human rights
advocates identify the lack of quantitative evidence on the financial
impacts of human rights violations as the primary barrier to integrating
these concerns into investment decisions [@BHRC2018]. Our study provides
a better understanding of the material consequences of human rights
violations and quantifies their effect on the valuation of associated
companies.

Thus, our findings highlight the potential of human rights reporting,
advocacy, and journalism, especially through their reputational (market)
mechanisms. Our results indicate that informational campaigns by civil
society can indeed influence multinational corporations, specifically
through reputational (market) mechanisms. However, our results
illustrate that, while significant, market mechanisms alone may be
insufficient to fully constrain misconduct abroad.

::: tablenotes
Notes: Events where a connection between the assassination (attempt) and
the victim's opposition to mining was established, but no specific
mining project or company was mentioned, are referred to as *no ties*.
*Unsuccessful attempts* are assassination attempts that resulted in
non-fatal injuries. Entries in the *distinct company entities* column
report how many unique mining firms were associated with at least one
assassination event in the country.
:::

::: tablenotes
Notes: The estimated effect of assassination events on corporate stock
returns using the synthetic matching method are reported. $P$-values for
two inference procedures are presented: (1) nonparametric bootstraps
(clustered at the unit level) of $5,000$ times; (2) drawing $5,000$
placebo treatment groups from the set of control firms (permutation
inference). For more details, please see Section A.2 in the Online
Appendix.
:::

::: tablenotes
Notes: *Assassination* equals 1 if a mining firm was associated with an
assassination event in a given year, and 0 otherwise. The *Tax Share* is
defined as the amount of taxes and royalties paid by a corporation to a
country's government divided by the total government revenue the mining
industry. Robust standard errors clustered at the company-country level
are in parentheses: \* p$<$`<!-- -->`{=html}0.1, \*\*
p$<$`<!-- -->`{=html}0.05, \*\*\* p$<$`<!-- -->`{=html}0.01.
:::

![Extracting events and company associations from NGO and media reports.
The source of the article is:
<https://www.theguardian.com/world/2014/dec/06/ecuador-indigenous-leader-found-dead-lima-climate-talks>
(Last accessed: *24 May 2025*).](figures/figure01.png){#figure01
width="90%"}

![Event country activity and company headquarter
locations.](figures/figure02.png){#figure02 width="80%"}

<figure id="figure03" data-latex-placement="!h">

<figcaption>Event Study Timeline</figcaption>
</figure>

![The effect of assassinations on stock returns. The average cumulative
abnormal return (CAR) for the baseline market model. The number of
company-event pairs, $N$, is 167. A minimum of eight trading days is
required during the event window from Days 0 to 10. The estimation
window spans from Day -280 to Day -30, with a minimum of 200 trading
days during this period. Stars depict significance levels for the GRANK
[@kolari2011grank] test-statistic: \*p$<$`<!-- -->`{=html}0.1, \*\*
p$<$`<!-- -->`{=html}0.05, \*\*\* p$<$`<!-- -->`{=html}0.01. The graphed
results and additional test statistics are presented in Online Appendix
Table C.4.](figures/figure04.png){#fig:clascestudy-baseline
width="\\linewidth"}

![The treatment effect of assassination events on mining companies. The
coefficients when regressing the respective cumulative abnormal return
(CAR) on an indicator for being tied to an assassination event are
represented by black dots. The horizontal axis represents the trading
days before and after the event on $\tau = 0$. CARs are aggregated
backward before the event date and forward starting with the event date;
for example, $-5$ refers to the CAR between $-1$ and $-5$ while $5$
refers to the CAR between $0$ and $5$. The top panel displays the point
estimates for $\hat{\delta}$ when event-fixed effects are included, and
the bottom panel displays estimates for the specification with
company-fixed effects. In total, the coefficients of 42 regressions are
displayed; 90% and 95% confidence intervals using robust standard errors
clustered on the event level are depicted in black and gray,
respectively.](figures/figure05.png){#fig:cross-section-main
width="\\linewidth"}

![The estimated economic value of assassination events. Dots correspond
to the estimated loss in market capitalization of the median company for
the baseline event fixed effects specification. Gray bars depict the
estimated minimum and maximum loss in market capitalization for the
median company across all specifications reported in Online Appendix
Figure C.9.](figures/figure06.png){#fig:loss width="\\linewidth"}

![Leave-one-out robustness check. The thick black line in Panels A and B
depicts the coefficient estimates for our baseline specification with
event fixed effects (Figure
[5](#fig:cross-section-main){reference-type="ref"
reference="fig:cross-section-main"}). Panel A presents CAR estimates
when we consecutively drop one country at a time from the sample. The
red lines depict the estimates for excluding all events in the
Philippines and Peru from the sample. Panel B displays the estimated
coefficients when treated companies are dropped from the sample one at a
time.](figures/figure07.png){#fig:leave-one-out width="\\linewidth"}

![The long-run effect of assassination events. Panel A displays CAR
estimates for the market model. Panel B presents the buy-and-hold
abnormal return (BHAR). Companies have to have been traded on 70 out of
the 91 days following the event at $\tau = 0$ to be included in the
sample.](figures/figure08.png){#fig:classic-event-study-long-run
width="\\linewidth"}

![The influence of news pressure on the event day. Estimates of equation
([\[eq:interaction-reg\]](#eq:interaction-reg){reference-type="ref"
reference="eq:interaction-reg"}) for the marginal treatment effect of
assassination events on high versus low news pressure days are depicted
by the black solid line and red dots, respectively. The estimated
(absolute) difference in treatment effects $|\hat{\delta}^{N}|$ is
represented by the dotted line and squares. In each panel, the treatment
indicator $D$ is interacted with a different binary indicator for high
news pressure [@eisensee2007] on the event day: *(a)* an above median
news pressure day; *(b)* an above the 75th percentile news pressure day;
and *(c)* an above the 75th percentile disaster-predicted news pressure
day. 95% confidence bands using robust standard errors clustered at the
event level are
displayed.](figures/figure09.png){#fig:news-pressure-main
width="\\linewidth"}

![The effect of assassination events on institutional investor holdings.
Stacked DiD estimates of equation
([\[eq:stacked-DID\]](#eq:stacked-DID){reference-type="ref"
reference="eq:stacked-DID"}) are presented. The control group comprises
mining firms that were not treated during the event period. The
dependent variable mean is presented in parentheses in the panel header;
90% and 95% confidence intervals using robust standard errors clustered
on the company level are displayed in black and gray,
respectively.](figures/figure10.png){#fig:io width="\\linewidth"}

![The impact of assassinations on supply chain contracts Stacked DiD
estimates are presented. The first row presents estimates for the log of
the number of new contracts, and the second row displays estimates for
the log of the number of new customers. The estimated effect on overall
contracting is presented in the first column, while the second and third
column displays how contracting with customers headquartered in
countries with *(2)* above median civil liberties and *(ii)* below
median civil society repression was affected, respectively. The control
group comprises mining firms that were not treated during the event
period. 90% and 95% confidence intervals using robust standard errors
clustered on the company level are displayed in black and gray,
respectively.](figures/figure11.png){#fig:supply-chain
width="\\linewidth"}

[^1]: For example, high-profile United Nations initiatives
    [@UNSGPCETM2024], European Union initiatives to govern the mineral
    supply chain (e.g., the 2024 Critical Raw Materials Act), and
    increased monitoring by NGOs (e.g., the
    @BusinessHumanRightsResourceCentre2024's (2024) Transition Mineral
    Tracker).

[^2]: Market penalties, or reputational penalties, are defined as the
    decrease in a firm's market value as the market expects
    counterparties (investors, customers, and suppliers) to change the
    terms of business when revelations of firm conduct change the firm's
    reputation [@Karpoff1993; @Sampath2018; @Armour2021].

[^3]: No firm in our study has faced legal penalty. See Section
    [5.4.1](#sec:legal-and-financial-implications-of-associations-to-assassinations){reference-type="ref"
    reference="sec:legal-and-financial-implications-of-associations-to-assassinations"}.

[^4]: See:
    [github.com/davidkreitmeir/synthReturn](https://github.com/davidkreitmeir/synthReturn)

[^5]: Given reputational penalties from environmental violations have
    been noisy and small, [@Carpentier2015] uses major environmental
    accidents to test whether reputation could be significant enough to
    deter environmental misconduct.

[^6]: There may also be a considerable gap between the event date (e.g.,
    the violation of a regulation) and the public revelation of the
    event (e.g., by the press or government bodies). In studies of
    reputation shocks and fraud, abnormal activity may occur ahead of a
    press release [@Gillet2010].

[^7]: We use @krueger2015's median $\text{CAR(-10,10)}$ estimate of
    $-1.11$% and the median market capitalization of sample firms to
    compute the median loss, that is, $0.0111 \times 6.86$B.

[^8]: The distribution of the placebo treatment effects from randomly
    drawing $5,000$ placebo treatment groups from the control group is
    presented in Online Appendix Figure C.12.

[^9]: The BHAR is defined as the geometric sum:\
    $\text{BHAR}\left(\tau_{1}, \tau_{2}\right) = \prod_{\tau = \tau_{1}}^{\tau_{2}} \left( 1 + R_{ie\tau} \right) - \prod_{\tau = \tau_{1}}^{\tau_{2}} \left( 1 + E\left(R_{ie\tau}|X_{\tau}\right) \right)$

[^10]: We require that, to be included in the analysis, disaster events
    in the EM-DAT database (CRED / UCLouvain, 2024, www.emdat.be,
    [@delforge24]) need to have information on their start and end dates
    and must meet one of the following three conditions: *(i)* 10 or
    more deaths; *(ii)* 100 or more people affected/injured/homeless;
    *(iii)* declaration by the country of a state of emergency and/or an
    appeal for international assistance. See [@jetter2022] for details.

[^11]: @StackedDID demonstrates that existing stacked DID estimators
    [e.g. @cengiz2019qje; @Deshpande2019; @Butters2022] are unable to
    recover causal effects because of implicitly assigning different
    weights for treatment and control groups across sub-experiments.

[^12]: Results are quantitatively unchanged if we include time-varying
    firm characteristics as additional controls (Online Appendix Figure
    C.15).

[^13]: For example, in December 2019, the largest Danish pension fund,
    ATP, divested from Grupo Mexico after eight months of failed
    attempts to engage with the mining company over the environmental
    and human rights risks associated with a new dam project.

[^14]: Note that V-Dem codes all indexes such that a higher score
    represents a more positive outcome. Hence, an above-median score for
    "Civil Society Repression" indicates a below-median level of civil
    society repression.

[^15]: Details on constructing our protest measures are available in
    Online Appendix Section B.4.

[^16]: In unreported results, we obtain similar estimates when protests
    are limited to those categorized as addressing "land tenure or farm
    issues."

[^17]: It is worth noting that this analysis is not limited to public
    companies; private companies are also matched to assassination
    events in our dataset. For completeness, we retain potentially
    relevant cross-country variation and do not exclude countries where
    an assassination falls outside the EITI coverage period.

[^18]: The average probability of an assassination event in the sample
    is 4.16%, and the average tax share is 5.9%.
