Post-MiFID II: Dark Pool Bans and
Regulatory Effects on Lit Market Quality
Hugo Hammar∗ Isak Djudja†
June 15, 2021
Thesis for the degree of Master of Science in Finance
Supervisor: Marcin Zamojski
∗gushammahu@student.gu.se
†gusdjudis@student.gu.se
Abstract
Over recent years, increasing popularity of non-transparent trading venues known as
dark pools have spurred widespread controversy and debate; in particular regarding
their impact on lit market conditions. Following voiced concerns over dark pools’
potentially adverse effects on lit market quality, legislative actions have been taken
to restrict the amount of trading allowed to be conducted in the dark. Yet, previous
empirical and theoretical literature on the subject is divided at large; with no clear
consensus on the ultimate effects of dark pool trading on lit markets—rendering
regulatory scrutiny a priority. We leverage the cut-off in dark pool trading activ-
ity following suspension of 35 securities in Nordic equity markets invoked by the
Double Volume Cap rule trough the European MiFID II regulatory framework. We
present evidence suggesting detrimental implementation effects of the ban on lit mar-
ket liquidity—putting to question the justifiability of recent regulatory intervention.
Conversely, other measures of liquidity and volatility appear unaffected by the ban.
The lack of clarity surrounding the fundamental implementation effects calls for fur-
ther research in the field of dark pool trading and its ultimate effect on lit market
quality.
ii
Acknowledgements
First and foremost, we would like to express our deep gratitude to our supervisor
Marcin Zamojski, for his invaluable advice and comments during the entirety of our
research process. It is without hesitation we acknowledge that our quality of work
would not have been the same without his kind contributions. We also appreciate
the institutions and people who have made this thesis possible and provided us with
the foundations necessary to perform our research.
iii
Table of Contents
1 Introduction 1
2 Background 4
2.1 Dark Pools . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4
2.2 Regulatory framework . . . . . . . . . . . . . . . . . . . . . . . . . . 6
3 Literature Review 8
3.1 Price Discovery . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 8
3.2 Volatility . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11
3.3 Liquidity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 14
4 Methodology 18
4.1 Model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18
4.2 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19
4.2.1 Variables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 22
4.2.2 Descriptive statistics . . . . . . . . . . . . . . . . . . . . . . . 25
5 Results 28
6 Conclusion 44
7 References 45
8 Appendix 48
iv
1 Introduction
Over the past decades, financial markets around the world have witnessed a rapid rise
in the popularity of dark pools. The trading venues, characterized mainly by their
lack of pre-trade transparency, have grown to absorb a substantial share of market
liquidity in Europe and across the world.1 Notwithstanding the increasing popularity
of these types of venues—regularly used by institutional investors to exploit benefits
arising from this lack of transparency—their very existence is controversial. Most
notably, concerns have been raised about the inaccessibility to non-institutional in-
vestors, inflicting an unlevel playing field between dark venues and public markets,
and the potentially negative impact on market quality dark pools may entail. In
these debates, the European Commission has expressed concerns that increased lev-
els of dark pool trading may impede price discovery (European Commission, 2010).
In particular, concerns were exacerbated following MiFID I’s elimination of the con-
centration rule in 2007,2 which was applied in many European countries. As a
consequence, competition among trading venues increased—as did the proportion
of trading conducted in dark pools (Petrescu and Wedow, 2017). For the purpose
of improving pre-trade transparency on equity markets and to ensure high market
quality, the revised MiFID II/MiFIR framework was implemented by the European
Commission on January 3rd, 2018—under which single securities can be banned from
being traded in dark pools for a predetermined period of time.
Both theoretical and empirical research present conflicting results regarding
dark pools’ ultimate impact on ‘lit’ market characteristics—and by extension whether
1In Europe, by 2016, dark pools constituted over 8% of total volume traded, compared to less
than 1% in 2009 (Petrescu and Wedow, 2017).
2Under the concentration rule, all equity trading had to take place on domestic stock exchanges.
1
a dark pool ban would entail redeeming effects or impediments in the pursuit of
enhanced market quality. Common across this strand of literature, however, are
discussions on a segmenting effect of dark pools; specifically a distinction between
informed traders and liquidity traders, and on which venues these categories tend
to concentrate. Early studies by Ye (2011), and Zhu (2014), which present conflict-
ing theoretical implications based on this notion, have been highly influential in the
discussion. Much of the empirical literature springs from this theoretical founda-
tion, but is divided at large—with conflicting results indicating enhancing, adverse,
dynamic, or no effects from dark pool trading on different market quality measures
(e.g., Foley and Putniņš, 2016; Comerton-Forde and Putniņš, 2015; Johann et al.,
2019). The ambiguity surrounding dark pools’ ultimate effects on market quality
increases the need for regulatory scrutiny—especially in light of recent regulations
in Europe, where literature on dark pools is still particularly scarce.
This paper sheds additional light on dark pools’ fundamental impact on lit
market characteristics by investigating the first market-wide implementation of a
dark pool ban on European securities, taking place in March, 2018. The event
considered qualifies as a quasi-natural experiment, where we leverage the cut-off
in dark pool trading on a large number of suspended securities introduced by the
implementation of the ban. The paper focuses in particular on lit volatility and
liquidity through a selection of measures largely inspired by the work of Johann
et al. (2019). We examine the implementation effects of the ban by computing
realized volatilities and several measures of quoted and trading liquidity based on
high-frequency intraday data. The study considers a time period of a total of 23
trading days, spanning 13 days before, and ten days after, the implementation of the
ban.
We conduct the analysis above by employing a Difference-in-Differences (DID)
2
model approach, assigning our sample of suspended and non-suspended securities to
treatment and control groups, respectively. To ensure adherence to underlying model
assumptions—in particular to the strong assumption of parallel trends between the
control and treatment group in the DID framework—we follow a sample selection
procedure in which a total of 70 securities are matched based on company-specific
characteristics along dimensions of geography, industry, and size. The scope of our
analysis is limited to Nordic securities, for which high-frequency data is collected
from the Swedish House of Finance. The choice of region contributes further to the
strand of literature by entailing an interesting, and to our knowledge unresearched,
geographical setting in the context of dark pools.
Our results reveal that the impact of the dark pool ban on measures of lit
market quality is, to a large extent, ambiguous. Subsequent analysis further under-
pins the complexity involved in the market dynamics at play, and how dark pool
activity and lit market characteristics may be indivisibly intertwined. While we find
some evidence of spreads having increased as a result of the ban—robust to several
changes in both sample composition and time frame—other measures of liquidity
and volatility exhibit no statistically significant changes after the ban. Our results of
increasing spreads are supported in research by, e.g., Foley and Putniņš (2016) and
Buti, Rindi, and Werner (2011), but are contradictory to the work of Comerton-Forde
and Putniņš (2015). Our statistically insignificant results in many of the variables
of interest are largely aligned with results of Johann et al. (2019) who are unable
to present any significant relationships between the European dark pool ban and
measures of lit market quality.
This paper contributes to the literature on dark pools at large, and particularly
in the context of regulatory intervention. The results presented provide insight into
how lit market characteristics are affected by suspension of securities from dark pool
3
trading, and have implications for both practitioners and regulators. Most notably,
the paper underpins the need for scrutinizing dark pool regulations in Europe, as
our results imply that the dark pool ban may have proven unsuccessful in its quest
to improve lit market conditions for investors. We conclude that additional research
is required to disentangle the complete dynamics of dark pools and the true impact
of dark pool bans on lit market quality.
The remainder of the paper is structured as follows. Section 2 provides back-
ground and an overview of dark pool trading and presents the regulatory framework
relevant for the implementation of the ban in Europe. Section 3 provides an in-depth
review of previous theoretical and empirical literature on the relationship between
dark pools and lit markets. Section 4 establishes the methodological framework and
the sampling procedure, and presents descriptive statistics of the data. Section 5
provides the results and a discussion on their implications in relation to previous
literature. Section 6 concludes.
2 Background
2.1 Dark Pools
Operated by private institutions—most commonly banks, brokers, or exchange opera-
tors—dark pools share several similarities with public markets; most notably the fun-
damental service of offering market participants a venue to exchange securities. The
distinction between dark pools and conventional, lit, markets, lies in transparency.
In contrast to public exchanges, dark pools are characterized by a lack of pre-trade
transparency, providing investors with the possibility to place market orders without
order details being disclosed in a public order book. Accordingly, dark pools provide
4
a solution for limiting transaction costs, particularly in relation to large institutional
trades, by making self-inflicted price pressure3 avoidable for traders.
In recent years, improvements in computing power has increased the need for
protection from predatory behaviour exerted by new types of market participants,
referred to as high-frequency traders (HFT). The ability among these actors to rec-
ognize both block trades and iceberg orders4 in fractions of a second constitutes a
significant risk for institutional investors. Practicing ‘frontrunning’, HFT traders
acquire or sell shares across exchanges, depending on the direction of the institu-
tional trade—entailing significantly higher transaction costs for those institutional
investors. The phenomena of HFT and frontrunning has in later years driven an in-
creasing share of institutional investors to dark pools, largely explaining the increase
in liquidity on such venues (Petrescu and Wedow, 2017).
While all dark pools share the characteristic of no pre-trade transparency, there
are several different subsets of these venues available to traders—each with certain
characteristics targeted towards specific investor groups. One of the most distinc-
tive features in the classification of such trading venues concerns how transaction
prices are determined. As a public order book does not exist, dark pools rely on
other means of determining the reference price of a transaction; most commonly de-
rived from lit exchanges. Among the more common practices is ‘midpoint pricing’,
where—as the term implies—the price is determined based on the midpoint between
bid and ask prices, specifically on the market the security in question is primarily
3Price pressure refers to when buy or sell orders impact the price of the security in an un-
favourable direction for the investor.
4Block trades refer to single, large orders, while iceberg orders are split into lots, where orders
in the bottom of the order book are hidden until visible trades are executed.
5
listed on. Among these midpoint dark pools, there are multiple venue types with
different mechanisms for the matching of orders—commonly based on either order
volume or timeliness. For dark pools in which matching of order timing is prioritized,
the transactions occur instantaneously, which may be associated with only partially
filled orders (Petrescu and Wedow, 2017). In contrast, for dark pools prioritizing
orders based on volume, execution requires that an order of equal size exists on the
opposite side of the order book. On such venues, investors are subjected to the risk
of passively having to wait for a match to occur, and for the trade to be executed. A
plethora of other types of dark pools exist, albeit all share the common denominator
of exogenously determined prices, commonly derived from lit markets (Petrescu and
Wedow, 2017).
2.2 Regulatory framework
Since MiFID I came into force in 2007 and eliminated the widely applied concen-
tration rule in Europe, competition among trading venues has increased (Petrescu
and Wedow, 2017). Following a rise in the proportion of trading conducted in dark
pools—partly due to the protection it provides against predatory HFT practices (Pe-
trescu and Wedow, 2017)—concerns about dark pools’ impact on market efficiency
and price discovery on lit markets has increased among regulators. In 2010, the Eu-
ropean Commission expressed specific concerns that increases in dark pool activity
“[. . . ] may ultimately affect the quality of the price discovery mechanism on the lit
markets.” (European Commission, 2010).
For the purpose of improving pre-trade transparency and ensure high quality
on lit equity markets, the revised MiFID II/MiFIR framework was implemented on
January 3rd, 2018. The regulations, inter alia, impose a requirement for all market
6
operators to make public current bid and ask prices as well as the depth of trading
interests. Competent authorities can grant Alternative Trading Systems (ATSs) pre-
trade transparency waivers under certain prerequisites. Trading systems that derive
their reference prices from an external liquid market, or the venue on which the
security was first listed for trading, fall under the reference price waiver ; and include
midpoint dark markets. Under these waivers, however, MiFID II/MiFIR stipulate
further the extent to which securities can be traded in the dark. In particular, the
Double Volume Cap (DVC) mechanism limits the volume that can be traded both in
individual dark pools and across all dark trading venues. More specifically, the DVC
rule sets out two volume percentage caps, which entail the following (Regulation EU
No 600/2014):
1. Given that a trading venue is granted a waiver, trading on that venue shall
not exceed 4% of the total volume of trading in that financial instrument on
all venues across the Union over the previous 12 months.
2. Total trading under waivers is restricted to 8% of the total volume of trading
in that financial instrument on all venues across the Union over the previous
12 months.
That is, when the 4% limit is breached for a given security, the very same security
becomes suspended; such that trading in that security cannot be carried out on
the relevant trading venue for six months. Furthermore, a security also becomes
suspended if the total trading volume under waivers breaches the 8% cap; which
results in the security being suspended from all trading under waivers for a six-month
period. The DVC mechanism’s main raison d’être is to ensure that trading under
waivers does not harm price formation on lit markets, and to broaden the access to
7
liquidity. Trade data that has been gathered across venues since the implementation
of MiFID II does, however, indicate that volumes previously traded in dark pools have
partly moved to ATSs, rather than returning to lit markets. Systematic Internalizers
(SIs) function as one such substitute to dark pools, where investment firms deal
on their own account when executing client orders. The market share of SIs for
Nordic listed shares rose by approximately 20 percentage points, to above 25%, the
six months following the implementation of MiFID II (Nasdaq, 2018). These facts
alone imply potential inadequacies in the scope of recent regulations in Europe, and
accordingly that MiFID II may fail to realize any significant improvements in overall
quality of lit markets.
3 Literature Review
3.1 Price Discovery
Regulatory debates on dark pools tend to focus on their impact on price discovery.5
The European Commission has raised specific concerns that the quality of price dis-
covery may suffer from increased levels of dark pool trading (European Commission,
2010). However, neither theoretical nor empirical literature support such an effect
unanimously. The question of dark pools’ ultimate effects on price discovery, thus,
remains unsolved. This increases the need for regulatory scrutiny—especially in light
of recent regulations in Europe, where literature on dark pools is particularly scarce.
A review of the theoretical and empirical findings regarding dark pools and price
5Price discovery refers to the extent implicit information in investor trading is incorporated into
market prices in an efficient and timely manner (Lehmann, 2002).
8
discovery follows.
Two widely cited papers on this issue are those of Ye (2011) and Zhu (2014),
who approach dark pools through separate theoretical models and ultimately come to
contradicting conclusions. Ye (2011) constructs a theoretical model in a two-period
universe which distinguishes between three types of agents—informed traders, liq-
uidity traders, and market makers—and ultimately predicts that dark pool activity
should be detrimental to price discovery. On the contrary, Zhu (2014) predicts the
opposite; dark pools should effectively improve price discovery on lit markets. These
two distinctive and conflicting conclusions stem from different theoretical founda-
tions. Ye (2011) specifically finds that trading in the dark harms price discovery
under the assumption that only informed traders are allowed to submit orders in
dark pools. As informed investors, by assumption, know the true value of an asset,
they will trade more on dark venues than on lit markets to avoid self-inflicted price
pressure. While the study acknowledges the existence of lower execution probabili-
ties for informed traders on dark venues, it is deemed secondary to the benefits of
preventing information leakage. Therefore, a larger volume of informed trades will
go through dark venues without pre-trade transparency, and price discovery on lit
markets will be harmed (Ye, 2011).
On the other hand, Zhu (2014) finds that execution risk is the decisive factor
driving informed investors to lit markets and liquidity traders to dark pools, which by
extension explains the positive impact of dark pools on price discovery. Zhu (2014)
distinguishes between informed traders, who act on the basis of detailed knowledge
of a stock, and liquidity investors, whose trade decisions are exogenous to the mar-
ket. Zhu (2014) notes that, as informed orders are positively correlated with asset
value, they have a tendency to cluster on either the sell- or buy-side of the market,
resulting in lower execution probabilities on dark venues. Moreover, since liquidity
9
orders conversely tend to be uncorrelated with the asset value—these trades are trig-
gered by exogenous reasons rather than information—such clustering is less likely,
leading to lower execution risk. This enforces the segmenting effect of dark pools
and, thus, increases the concentration of informed traders on lit markets vis-à-vis its
dark counterpart—so that information is retained on lit markets and price discovery
is improved.
A crucial difference in model assumptions between Ye (2011) and Zhu (2014)
calls for attention. Ye (2011) assumes that only informed investors can migrate
to dark pools—leading to the conclusion that price discovery may be harmed due
to a higher proportion of informed traders on dark venues. On the other hand,
Zhu’s (2014) reverse assumption of self-selection is part and parcel to the study’s
subsequent findings. When both informed traders and liquidity traders can choose
venue type freely, informed traders will prefer lit venues due to execution risk, and
liquidity traders will concentrate on dark venues. Most empirical findings tend to
support the predictions made by Zhu (2014), which may suggest that the assumption
of self-selection is an important component of reality.
Comerton-Forde and Putniņš (2015) substantiate Zhu’s (2014) findings through
an empirical study using Australian data. The paper shows that the introduction of
a dark pool does lead to a partial separation of informed and uninformed investors,
where orders executed in the dark are indeed conducted by less informed investors.
The rationale is also consistent with that of Zhu (2014); namely that the risk of
non-execution drives informed investors to lit markets. As the proportion of unin-
formed investors in lit markets decreases, spreads tend to widen, and, accordingly,
the aggregated information about fundamental values is reduced (Comerton-Forde
and Putniņš, 2015). Comerton-Forde and Putniņš (2015) also find that dark pool
trading has effects on informational efficiency. Up to a certain threshold (around 10%
10
of total volume), dark pool trading is either benign or beneficial, while larger levels
of dark pool trading in a stock can harm informational efficiency (Comerton-Forde
and Putniņš, 2015). In addition, they find no evidence that block trades without
pre-trade transparency harm price discovery. These findings relate to the MiFID II
regulation; the implementation of the DVC rule entails an 8% volume cap on total
dark pool trading for a given security; and a ‘Large-in-Scale’–waiver which permits
larger block trades. If there is a discrepancy between MiFID II’s threshold at 8%
and the true threshold at which dark pool trading stops being benign or beneficial,
the DVC rule may contribute to considerable welfare inefficiencies.
Ye (2016) discusses similarly to Comerton-Forde and Putniņš (2015) a sorting
effect where, in equilibrium, traders with strong information trade on exchanges;
traders with moderate signals about fundamental values trade in dark pools; and
traders without information opt out of trading. Ye (2016) defines the result of this
sorting as an amplification effect on price discovery; when information precision is
high, dark pools enhance price discovery; and when information precision is mod-
erate, dark pools impair price discovery. Adding a dark pool when information
precision is high, Ye (2016) explains, shifts only a relatively small proportion of
informed investors to dark pools, and combined with a relatively high number of liq-
uidity traders on the dark markets, the informed-uninformed ratio on the lit market
is improved. The opposite holds for when information precision is low or moderate,
as a large proportion of informed investors shift over to dark pools.
3.2 Volatility
The scant literature surrounding dark pools presents contrasting views on a number
of connected issues. One such issue concerns the relationship between asset volatility
11
and dark pool trading. Volatility per se tends to play a small part of a broader
context in much of the previous literature—for example as a determinant of dark pool
trading (e.g., Ready, 2010, and Buti, Rindi, and Werner, 2010), a control variable
(e.g., Comerton-Forde and Putniņš, 2015), or one of several metrics for market quality
(e.g., Foley and Putniņš, 2016 and Johann et al., 2019). Empirical in-depth studies of
the relationship between dark pool trading and volatility are, however, limited. This
section gathers and reviews previous research on the specific relationship between lit
market volatility and dark pool activity.
Many of the empirical studies addressing volatility and dark pool activity sup-
port a negative relationship between the two. Foley, Malinova, and Park (2013) find
evidence that increased dark trading leads to reduced volatility and price impact
based on data from the Toronto Stock Exchange. Foley and Putniņš (2016), who
investigate dark trading’s impact on informational efficiency, conclude similarly that
dark trading has positive effects on a range of informational efficiency metrics, includ-
ing high-frequency volatility. Furthermore, Petrescu, Wedow, and Lari (2017) focus
on market instability and empirically deduce the impact of dark trading on volatility
in times of stress, using data on FTSE100 stocks. The paper finds that dark pool
trading can help predict current volatility, and concludes that dark pool trading
activity effectively lowers volatility in times of stress. In a more recent study, Anag-
nostidis, Papachristou, and Varsakelis (2019) investigate changes in market quality
by observing data on suspended European securities following the implementation
of MiFID II’s DVC rule. The study finds that the regulation has led to lit price in-
efficiencies for non-suspended securities, and increased daily volatility on lit markets
for suspended securities. This conclusion largely aligns with the view of previously
cited research, and points towards a non-detrimental impact of dark pool activity on
volatility on lit markets.
12
The theoretical support for dark pool activity being associated with lower
volatility tends to revolve around a segmentation of traders. The notion is simi-
lar to what is proposed by Zhu (2014) and Ye (2011)—with informed traders and
liquidity traders concentrating on different types of venues. Research suggests that
the availability of dark pools can result in liquidity traders migrating from lit to
dark venues (predicted by Zhu, 2014, and substantiated by, e.g., Comerton-Forde
and Putniņš, 2015). Theoretical models hold, as Petrescu and Wedow (2017) point
out, that such migration removes noise from lit markets; and the subsequent concen-
tration of informed traders on those lit markets, where price formation occurs, may
make prices less volatile.
Conversely, if dark orders would otherwise have been publicly displayed, it
has been argued that the development of dark pools and use of dark orders could
inhibit price discovery (International Organization of Securities Commission, 2010).
In that case, migration of order flow to dark venues could reduce overall information
in lit markets, and subsequently result in more volatile prices (Petrescu and Wedow,
2017). Comerton-Forde and Putniņš (2015) elaborate on this line of thought, and
highlights that clustering may lead to lower execution probabilities in the dark,
which keeps informed traders on lit markets. They also note that this segmentation
entails higher adverse selection risk and subsequently yields wider bid-ask spreads
on the lit market. The authors further claim that segmentation and wider spreads
“[. . . ] reduce incentives for costly information acquisition”, with lower aggregate
information production as a consequence. While volatility per se is no focal point
of their study, Comerton-Forde and Putniņš (2015) note that wider spreads tend to
be associated with higher intraday volatility. The relationship between dark pool
activity and price discovery is found to be concave, with a ‘tipping point’ for dark
trade volume at which the impact on market quality goes from being benign or
13
beneficial, to harming. Petrescu and Wedow (2017) find supporting evidence of a
non-linear relationship between dark pool activity and volatility, concluding it to be
quadratic.
Another strand of literature investigates volatility and its role as an explanatory
determinant of dark pool trading levels. Buti, Rindi, and Werner (2011) argue
that low (high) intraday volatility leads to increased dark pool (lit) activity. The
rationale relates to execution probabilities: when volatility is uncommonly high on
the market, “[. . . ] traders are, all else equal, more likely to forego the uncertain
executions associated with dark pools, and instead rely on marketable orders to gain
immediacy” (Buti, Rindi, and Werner, 2011). The authors recognize, however, the
issue of joint determination between market quality and dark trading, which has
been highlighted as one reason for conflicting empirical results in the context of dark
pools (Johann et al., 2019). Buti, Rindi, and Werner (2011) use a simultaneous
equation system to account for bi-causality6 and ultimately find additional evidence
supporting the fact that more dark pool activity leads to lower short-term volatility.
3.3 Liquidity
The segmentation of uninformed and informed traders between venues has an empir-
ically documented effect on liquidity, which, together with related effects on spreads,
may have a non-negligible impact on trading costs. While there are strong theoretical
foundations for the impact of dark trading on liquidity hinged on this segmentation,
conclusions differ depending on the specific type of opaque market referred to, and
6The issue of bi-causality relates here to the joint determination between market quality and
dark pool trading activity; and how increased dark pool activity may concurrently be a result and
a driver of poor lit market quality.
14
when accounting for quasi-dark alternatives.
Zhu (2014) theorizes on midpoint dark pools and concludes that, while higher
dark trading activity is associated with price discovery improvements, it concur-
rently has a detrimental impact on lit liquidity. Due to the migration of unin-
formed investors to dark markets, informed traders are concentrated on lit markets—
effectively reducing exchange liquidity due to higher adverse selection on lit markets.
Glosten and Milgrom (1985) formulate the same argument; specifically that liquidity
providers on the market tend to offset losses from trading against informed investors,
with gains from trades against uninformed investors. This induces an increased ad-
verse selection risk for liquidity providers in lit markets, and discourages liquidity
provision—ultimately harming liquidity and increasing transaction costs (Zhu, 2014).
Contrary to Zhu (2014), Foley and Putniņš (2016) evaluate effects of two-sided, or
limit order, dark markets as opposed to midpoint dark pools. The paper conducts a
natural experiment following restrictions on dark trading in Canada and Australia,
and concludes that dark trading is beneficial to liquidity. Two-sided dark trading,
as Foley and Putniņš (2016) explain, “[. . . ] lower[s] quoted, effective, and realized
spreads, [and] reduces price impact measures of illiquidity”. The study does not find
any significant and consistent evidence of such an effect from midpoint dark trading.
These conclusions are theoretically substantiated by Boulatov and George (2013),
who find that in dark limit order markets—where informational rents cannot be
expropriated by other investors through displayed orders—informed investors trade
more aggressively. The authors subsequently argue that the rise in competition can
enhance market quality. Foley and Putniņš (2016) find that this competition yields
positive spill-over effects on lit markets; to compete with dark liquidity, liquidity
providers narrow down spreads. The same notion is further supported by Buti,
Rindi, and Werner (2011), who find that higher dark pool trading is associated with
15
positive effects on market quality through, for example, lower quoted and effective
spreads. From a European perspective, MiFID II’s reference price waiver of pre-trade
transparency stipulates that when possible, the reference price shall be established by
obtaining the midpoint price within the current bid and offer prices (Regulation EU
No 600/2014). For the purpose of investigating dark pool bans in Europe following
the new regulations, emphasis should most heavily be put on literature concerning
midpoint dark pool in the context of this paper.
The segmentation arising between different types of investors is supported fur-
ther by Hatheway, Kwan, and Zheng (2017), who investigate dark pool trading in
the U.S. In line with the reasoning of Zhu (2014), the authors find that dark trading
enforces an informed-uninformed investor segmentation, which leads to a flight of liq-
uidity from lit markets when uninformed investors migrate. Furthermore, the study
finds that the majority of higher spreads accompanying dark trading act as com-
pensation to liquidity providers for trading against informed investors. Hatheway,
Kwan, and Zheng (2017) elaborate on this notion and argue that informed investors
are discouraged to place limit orders when, in the absence of a national time priority,
dark traders can trade ahead of liquidity providers in lit markets. Recent European
regulations, however, state that outside the continuous trading phase of a trading
session, the reference price shall be obtained from the opening or closing price of
the relevant trading section (Regulation EU No 600/2014)—which limits this ability.
Hatheway, Kwan, and Zheng (2017) ultimately conclude that dark trading activity is
associated with both increased transaction costs, and reduced price discovery. This
conclusion contradicts the results presented by Zhu (2014), which predicts opposite
effects on price discovery and liquidity from dark pool activity.
Degryse, De Jong, and Van Kervel (2014) conduct an empirical study on frag-
mentation in lit order books and dark trading. The authors argue, in line with much
16
previous literature, that the migration of uninformed investors to dark venues—
referred to as a “cream-skimming effect”—brings along higher adverse selection on
lit markets and a detrimental effect on lit liquidity. However, the study’s dark trade
data convey no information on the identity of the executing venue, nor does it con-
tain information on the order book—leading up to the more general conclusion that
costs and benefits of trading venue competition are determined by the type of trading
venue (Degryse, De Jong, and Van Kervel, 2014). Moreover, the study uses data on
trades executed on other venues than dark pools, including both internalized trades
and OTC trades. This fact limits the extent to which the empirical results can be dis-
cussed in light of MiFID II’s DVC rule, which concerns dark pool trading specifically.
In a more recent study, Johann et al. (2019) evaluate the MiFID II regulations, and
in particular investigate the impact of dark pool bans when quasi-dark alternatives—
such as internalization systems and periodic auctions—exist. The study brings recent
regulations to question, as the results indicate that implemented bans on stocks lead
to unexpected consequences. The authors find that only a small part of liquidity
returns to lit markets when dark pool bans on stocks are imposed, while volume
spill-overs into quasi-dark alternatives are significant. The substitutability of these
alternative trading systems may, thus, prevent MiFID II from fulfilling its purpose
of maintaining a higher proportion of trading on lit markets. The study finds that
the dark pool bans’ subsequent impact on market liquidity and short-term price
efficiency are overall insignificant and negligible.
17
4 Methodology
4.1 Model
The main objective set forth in this paper is to investigate effects on lit market
quality following the implementation of MiFID II in Europe, and in particular the
suspensions from dark pool trading invoked by the DVC rule. To this end, we employ
a Difference-in-Differences (DID) model approach, exploiting the first market-wide
regulatory intervention in dark pool trading in European equity markets. We focus
our analysis on measures of volatility and liquidity to deduce the implications of
the DVC rule in regards to market quality. The paper leverages the fact that the
strict cut-off in dark pool trading imposed by the European Securities and Markets
Authority (ESMA) in March, 2018, created a quasi-natural experiment with a clearly
defined event and treatment groups. The contextual circumstances therefore allow
us to infer any effects of the ban on our volatility and liquidity measures through the
DID model approach elaborated on below.
Perhaps the most crucial issue in the context of the DID estimator lies in the
assumption of parallel trends in the treatment and control group. Previous research
suggests that dark pool trading is related to, for example, both firm-specific char-
acteristics and liquidity conditions (Kwan, Masulis, and McInish, 2015 and Gomber
et al., 2016), rendering a need for caution in context of the DID framework and its
assumptions. This fact is directly noted and addressed by Johann et al. (2019), who
attempt to circumvent the issue of parallel trends by conducting a semi-parametric
DID model along with a robust regression discontinuity design, focusing on compa-
nies being close to the volume threshold, rather than on stocks on which suspensions
are de facto imposed. Unlike Johann et al. (2019), we address this issue by employing
18
a sample selection procedure in which securities in the treatment and control groups
are matched based on similarities in firm characteristics. As such, the peer selection
methodology is designed to ensure similar trends pre- and post-treatment for the two
groups. We elaborate on this sample selection procedure further in Subsection 4.2.
The point of departure for subsequent analyses is the following DID regression
model:
Yi,τ = β0 + β1Treatedi + β2Windowi,τ + β3Interactioni,τ + i,τ ,
where Yi,τ is a measure of liquidity or volatility, depending on the analysis. Window
is an indicator variable taking the value (0) before the implementation of dark pool
trading suspensions, and (1) during the suspension window. Similarly, the indicator
variable Treated specifies if a security was suspended from trading in dark pools
by ESMA starting on March 12, 2018 by taking the value (1), and (0) if no such
suspension was imposed on the given stock. Furthermore, Interaction, is the DID
estimate of the effect of the ban. The variable is defined as the interaction term
between Treated and Window, such that it captures effects from being suspended
from dark pool trading during the event window. Thus, in subsequent analyses,
Interaction will be the main focus of investigation.
4.2 Data
To conduct our analysis, we gather intraday data from the Swedish House of Finance,
including bid and ask quotes, market depth, and transaction prices, with correspond-
ing time stamps. The collected data is sampled at a one second time frequency and
is subsequently resampled to appropriate frequencies depending on the application,
to avoid, for example, issues of ‘microstructure noise’. We address missing values in
the data by consistently replacing them with the last available data point.
19
The list of securities which were to be subjected to the first dark pool ban was
released by ESMA on March 7, 2018—with the implementation of the ban following
on March 12, 2018. As this was the first implementation of the dark pool ban, a
large number of stocks were suspended on the same date. As such, the period is
particularly beneficial for statistical analysis, as it provides a solid basis for sample
selection.7 We use data covering the time period ranging from February 21, 2018, to
March 23, 2018, translating to a total sample of 23 trading days. The time period
therefore involves a pre-treatment window size of 13 trading days—including the
period between announcement and implementation—and a treatment window of ten
trading days. Figure 1 illustrates the timeline. Owing to to time limitations and
data constraints, the event window is comparably short. However, as we suspect the
majority of the implementation effects of the ban to be instantaneous, our sample
should be sufficient in capturing the dark pool ban’s fundamental impact on lit
market quality. Meanwhile, our sample is concurrently limited by the use of one
single event. While this fact may hamper our ability to present results that are
representative for all dark pool bans implemented by ESMA, our results should give
a strong indication of the underlying effects on lit market quality.
In line with the Difference-in-Differences model approach, our sample selection
procedure involves the construction of two separate groups of suspended and non-
suspended securities; denoted treatment and control group, respectively. For the
selection of securities in the treatment group, we use ESMA’s list of suspended
securities released on March 7, 2018. First, we limit our sample to focus on the effect
7Even though a substantial number of securities were suspended on this date, downtime in the
Swedish House of Finance database limited our ability to gather a more comprehensive set of data
comprising a larger number of securities.
20
Figure I: Timeline illustration
The figure illustrates the full sample period with dates relevant to the analysis. On March
7, 2018, ESMA announced the securities to be suspended from dark pool trading as of
March 12, 2018. The sample period ranges ten trading days prior to the annoncement, to
ten trading days post-implementation.
Post
Suspension
announcement
period
period
February 21 March 7 March 12 March 23
of the dark pool ban on Nordic equity markets by filtering the list of suspended
companies on geography. To limit issues in regard to liquidity and available data
points, we subsequently rank these securities on size based on market capitalizations
as per March 7, 2018. From this list, we select the 35 largest securities, for which
data is available, to constitute the treatment group in our analysis.
The control group is constructed to mimic the treatment group along dimen-
sions of firm size, industry, and geographical location; aiming at aligning pre- and
post-treatment trends between the two groups. Matching on these factors concur-
rently serves the purpose of eliminating, for example, industry-specific effects in the
underlying sample. In line with this notion and our geographical scope, we select
securities from the Nasdaq OMX Nordic 120 index. We derive our control group by
initially matching each security in the treatment group to the largest company in the
index which belongs to the same industry. The matching on industry is conducted
by ensuring that each pair of securities share the same Bloomberg Industry Classifi-
cation (BIC) code. To ensure that all securities in our sample can be matched, we
use macro sector BIC codes for the industry classification.
21
Accordingly and in summation, the full sample consists of 70 securities divided
into two equally-sized subgroups, with data gathered over a total of 23 trading days.
The full list of securities in our sample is presented in the Appendix, Table VIII.
4.2.1 Variables
The main focus of this paper is to assess the effect of the dark pool ban on measures of
liquidity and volatility on lit markets. The liquidity analysis largely follows the work
of Johann et al. (2019), who apply six measures relating to both quoted and trading
liquidity. For quoted liquidity, we compute conventional bid-ask spreads as well as
top-of-book depths—denoting, at time τ , the midpoint price as Mτ , and the best
bid and ask quotes as BidPτ and Ask
P . BidQτ τ and Ask
Q
τ denote the corresponding
first-level book depth quantities. Accordingly, we define:
AskP −BidP
QuotedSpreadτ =
τ τ ,
Mτ
QuotedDepthBidτ = Bid
P
τ ×BidQτ ,
QuotedDepthAskτ = Ask
P
τ × AskQτ
where best bid and ask prices are converted to euros, to ensure consistency across
the sample securities. For trading liquidity, we follow Johann et al. (2019) and
compute effective spreads, realized spreads, and a measure of price impact. The
inclusion of the effective spreads allows us to address and capture transaction costs
on the market by comparing the midpoint price to the actual transaction price.
Relatedly, realized spreads, as concisely described by Johann et al. (2019), capture
limit order traders’ earned compensation, adjusted for any losses associated with
adverse selection. Price impact is a measure of the information content in trades,
and is computed by comparing the current midpoint price with the corresponding
22
price at a future point in time. The trading liquidity measures are defined as follows:
2×Dτ × (Pτ −Mτ )
EffectiveSpreadτ = ,Mτ
∆ 2×Dτ × (Pτ −Mτ+∆)RealizedSpreadτ = ,Mτ
∆ 2×Dτ × (Mτ+∆ −Mτ )PriceImpactτ = ,Mτ
where Dτ denotes the direction of the trade, assigned value (1) for trades initiated
through a buy order, and (-1) for a sell. The trade direction is asserted through the
employment of a conventional ‘tick test’, which in most applications has been shown
to perform well (Lee and Ready, 1991). The algorithm behind the signing of each
trade involves asserting the direction of the price movement following the previously
conducted trade. If the transaction price is higher (lower) than than the previous
trade, the trade is considered an ‘uptick’ (‘downtick’), and classified as a buy (sell).
If no movement in prices occurred between trades, we look at whether the previous
trade was an uptick or downtick, and classify the trade accordingly. For realized
spreads and price impact, we use midpoint prices ∆ = {5, 10, 15} minutes ahead
in time, to limit issues which may arise due to potential illiquidity of stocks in our
sample. Given that a forward-fill approach is employed for missing data points, a too
short time span in the construction of realized spreads for securities with few trades,
would cause the variable to converge to the effective spread. Similarly, our measure
of price impact would tend to zero. For the same reasons, we perform additional
robustness checks in subsequent analysis; elaborated on in Section 5.
To investigate the impact of dark pool bans on volatility, we compute daily
realized volatilities. The measure qualifies as an apt proxy for true volatility and is
particularly accepted as such in academia for high-frequency, intraday data (Ander-
23
sen et al., 2001). The measure is conventi√onally computed and defined as:√√∑n
RVol √ 2i,t = ri,τ ,
i=1
where ri,τ corresponds to intraday returns, excluding overnight returns, for company
i between time τ − 1 and τ . The measure is based on midpoint prices resampled
at five minute frequencies in order to mitigate, to the extent possible, effects of
microstructure noise.
To add to the robustness of our models, a number of control variables are
included to account for their potentially non-negligible impact on our measures dur-
ing the time frame. For company-specific press releases—exhibiting the potential
to significantly impact both liquidity and volatility of a given stock—we include an
indicator variable, PRi,t, assigned value (1) for company i on day t if a press release
occurs, and (0) otherwise. Notwithstanding the potential issue of post-announcement
drift, the majority of the impact of such press releases on market prices is argued to
occur instantaneously. Furthermore, we address potential macroeconomic factors by
including a variable, 10yGovBi,t, relating to the price on day t of the ten-year gov-
ernment bond issued by the country in which company i is primarily listed. Finally,
we include market volatility in our models in an attempt to capture market-wide
factors impacting individual securities’ volatility and liquidity characteristics. We
model market volatilities by running a GARCH(1,1) model based on returns of the
Swedish index Nasdaq OMXS30, with data corresponding to the one-year period
between March 23, 2017 and March 23, 2018.
24
4.2.2 Descriptive statistics
An initial review of the descriptive statistics for our two groups—presented below
in Table I—reveals a number of noteworthy facts for the purpose of subsequent dis-
cussions. The securities included in the treatment group—and thus suspended from
dark pool trading within the event window—exhibit higher liquidity as measured
solely by the quantity of trades conducted each day. While this number averages
around 1,500 in this group, the corresponding figure for the control group is roughly
half. The companies included in the treatment group also tend to be larger than their
control group equivalents, as measured by market capitalization. Adjacently, we ob-
serve lower average quoted spreads in all percentiles for our suspended securities.
The same applies to realized volatilities, which similarly tend to be lower among the
suspended securities in our sample. The facts presented above are largely consistent
with what has been shown in previous literature, supported by, for example, Buti,
Rindi, and Werner (2010), who observe that more dark pools are active for larger
stocks with lower spreads and lower volatilities. While a further analysis of these
facts in isolation lies outside the scope of this paper, a few potential implications for
subsequent analyses need to be addressed.
While the level differences in our measures presented do not imply violation of
model assumptions per se, the low number of trades in the control group, particu-
larly those falling in the lower percentiles, may have implications in the robustness
of subsequent results. Even though the sample selection procedure involves sorting
securities based on market capitalization, as described in Subsection 4.2, the discrep-
ancy of the number of trades between the two groups is non-negligible. Given the
employment of a forward-fill approach for missing values, securities with few trades
per day may, therefore, also suffer from high degrees of invariability in the intraday
25
data. As a result, realized spreads could correlate strongly with effective spreads,
while values for price impact may take values very close to zero. We attempt to
control for this fact in our robustness analysis by adjusting the sample composition
using two different approaches involving replacement and exclusion of securities with
particularly low liquidity. As established, the descriptive statistics presented here do
not imply that the parallel trend assumption under DID estimations is violated. A
visual overview of the variables during the time period does not either contest this
assumption definitively (see Appendix, Figure II to XV).
26
Table I: Descriptive statistics
This table provides some descriptive statistics of the treatment and control group, each
including a total of 35 securities. Market capitalization (MCap) values are in million euros
and are collected only for March 7, 2018. All remaining variables are based on the full
sample period of 23 trading days and all 35 securities in the respective group. Realized
volatilities and quoted spreads are quoted in percentages, and Trades relates to the number
of trades per day.
Treatment group
Measure 5th prct. 25th prct. Median 75th prct. 95th prct. Average
Trades 518.0 973.8 1357.0 1880.5 3189.3 1536.5
MCap 6,405.1 9,140.9 14,970.4 22,011.7 32,552.3 18,531.3
RVol (%) 0.6803 0.8674 1.0100 1.2121 1.6292 1.0749
QuotedSpread (%) 0.0266 0.0379 0.0453 0.0531 0.0832 0.0486
Control group
Measure 5th prct. 25th prct. Median 75th prct. 95th prct. Average
Trades 30.0 104.8 456.0 976.3 2335.0 724.2
MCap 1,025.1 1,800.7 3,849.6 7,929.2 26,872.8 7,605.2
RVol (%) 0.6795 0.9706 1.2137 1.5630 2.2305 1.3086
QuotedSpread (%) 0.0364 0.0629 0.1251 0.3197 0.7750 0.2424
27
5 Results
The question surrounding dark pool bans’ effect on lit market characteristics ulti-
mately concerns which types of traders concentrate in dark pools, and where order
flows on those venues move following a dark pool ban. As previously established,
research concerning this issue is largely divided in both theoretical and empirical
literature. In particular, research diverges concerning where traders with different
amounts of information concentrate, and the rationale for such concentration. The
novelty of dark pool trading bans, especially in Europe, concurrently limits the extent
to which our results can be put in relation to previous research. Still, Johann et al.
(2019), who investigate the same DVC suspension, offer such a contextualization—
while other studies focusing on dark pool trading activity in general form a founda-
tion for the analysis of our results (e.g., Comerton-Forde and Putniņš, 2015; Foley
and Putniņš, 2016; Buti, Rindi, and Werner, 2011). Table II summarizes the results
of our main models based on the full sample of a total of 70 securities.8
8For brevity, Table II only presents realized spreads and the measure of price impact for ∆ = 5
minutes. Results for other choices of ∆ are qualitatively similar and are available in the Appendix,
Table IX.
28
29
Table II: Results: Difference-in-Differences estimations – Full sample
This table presents the ban implementation effects on our variables of interest based on random-effects Difference-in-
Differences estimations. All marginal effects have been scaled by 104 (i.e., presented in basis points), with exceptions
for quoted depths. The table presents variable significance by (*) 10%, (**) 5%, and (***) 1%.
Model Treated Window Interaction 10yGovB PM log(MCap) MVol
RVol -5.146 -5.215 -0.541 -42.259** 2.098 -16.086*** 1730.689***
QuotedSpread -14.010*** -2.938* 2.682* -0.644 -0.032 -5.310*** 446.304
log(QuotedDepthBid) 0.573*** 0.036 -0.016 0.011 0.014 0.311*** -16.419***
log(QuotedDepthAsk) 0.622*** 0.073 -0.069 0.459* 0.006 0.252*** -16.203***
EffectiveSpread -8.454** -2.015*** 1.538** -4.350 0.908 -3.633** 137.951
RealizedSpread5min -7.384** -1.878** 1.872** -1.398 0.685** -3.304* 146.644
PriceImpact5min -0.504* -0.319 -0.064 -2.753*** -0.252** -0.745*** 19.030
An initial overview of the results suggests that the impact of the ban on volatil-
ity and liquidity is not completely clear, with limited supporting evidence for either
detrimental or beneficial effects on lit market quality. We note that the DID esti-
mates of the effect of the ban are insignificant across the board, except for measures of
spreads. The significance of these measures of transaction costs, however, indicate a
potential link between lit market quality, as measured by trading and quoted spreads,
and the dark pool ban. Interestingly, the marginal effects of all three measures are
positive, implying increasing spreads following suspension from dark pools. These
results, therefore, partially contrast those of Johann et al. (2019) who, albeit with
a somewhat different methodological approach, find no evidence of any significance
in either liquidity or volatility measures. The results also differ from the conclusions
on dark pool activity made by Comerton-Forde and Putniņš (2015), who find that
higher dark pool trading activity is associated with higher spreads on lit markets.
On the other hand, our results support the findings in empirical research by
Buti, Rindi, and Werner (2011), and Foley and Putniņš (2016). The former docu-
ments an inverse relationship between dark pool activity and spreads, analogously
implying that a dark pool ban should lead to higher spreads. Foley and Putniņš
(2016) find similar evidence that higher dark pool activity is associated with lower
quoted, effective, and realized spreads, albeit the significance in their results is lim-
ited to contexts of two-sided dark trading.
In relation to theoretical research on dark pools, increased spreads are implied
neither by Ye (2011), nor Zhu (2014). Ye’s (2011) reasoning concerning higher pro-
portions of informed investors in dark pools implies that dark pool bans should lead to
increased information content and lower spreads on lit markets—as this would cause
those informed investors to migrate to lit venues. Zhu (2014) concludes conversely
that informed traders concentrate on lit markets, mainly due to execution risk, and
30
that increased dark pool trading is associated with price discovery improvements—in
isolation supporting higher spreads following a dark pool ban. However, Zhu (2014)
concurrently argues that increased dark pool trading has a detrimental effect on lit
liquidity. The argument relates to adverse selection, and is based on the notion
that liquidity providers are unable to offset losses from trading against informed in-
vestors when the proportion of liquidity traders (or uninformed traders, as argued
by Glosten and Milgrom, 1985) on lit markets is low. As such, neither of these the-
oretical frameworks appear sufficient to explain our results of increasing spreads on
lit markets. Instead, our results may be more aptly explained by arguments pre-
sented by Foley and Putniņš (2016). As competition for liquidity arises, e.g., when
dark pools are available to traders, liquidity providers are forced to narrow down
spreads on lit markets to compete with dark liquidity. In line with this argument,
the implementation of a dark pool ban should, by extension of the same reasoning,
eliminate such competition. Without the same need among liquidity providers on lit
markets to actively take action to attract order flow from dark pools, it is plausible
that spreads would increase as a result.
A more nuanced perspective of the forces at work can be introduced by con-
templating the dynamics between the theoretical notions presented above. While
our results suggest increased spreads as a result of the ban, it is still likely to hold
true that the segmentation of traders, with different information and trading ratio-
nales, plays a substantial role in the effect of the ban. Following the reasoning of
Zhu (2014) concerning this segmenting effect, the dark pool ban introduced to our
sample may effectively have led to a migration of liquidity traders from dark to lit
venues. As liquidity traders act on reasons exogenous to the efficient price—i.e.,
irrespective of the proximity between market price and the efficient price of a given
security—increased spreads may be a result of increased noise in the market. In this
31
dynamic setting, it is also possible, and perhaps even plausible, that Zhu (2014) is
correct in his notion that liquidity providers’ inability to offset losses when dark pool
activity is high should be associated with increasing spreads. What our results do
indicate, however, is that this force may be weaker compared to the competition for
liquidity that arises among lit and dark venues, in combination with the additional
noise contributed to lit markets by liquidity traders migrating from the dark.
Put in relation to the stated purpose of the DVC rule, the results of increasing
effective and realized spreads indicate that recent regulations may be unsuccessful
in improving market quality for traders on lit markets. On the other hand, we are
unable to present evidence substantiating such a statement in any other measures
of market quality. Indeed, realized volatility, quoted depths, and our measure of
price impact do not change significantly following the ban, as suggested by our
results. The lack of change in, for example, realized volatility, may be perceived
as contradictory to the notion of liquidity traders migrating to lit markets, as this
would theoretically also imply increased volatility as a result of the dark pool ban—
a relationship substantiated by, e.g., Buti, Rindi, and Werner (2011). Although we
are unable to provide evidence for significant relationships between the dark pool
ban, volatility, and other measures presented herein, there are a number of potential
underlying reasons for why such relationships would not be accurately captured.
The lack of significance in realized volatility, as in other measures in our analy-
sis, may be a matter of insufficient data. As we only investigate the implementation
of the dark pool ban during one event window, sample period bias cannot be ruled
out. A more complete set of data spanning several events could therefore have the
potential to confirm significance in several of our measures, which we are unable to
substantiate in this analysis. As previously established, it is also possible that the
occurrence of highly illiquid stocks, primarily in the control group, introduces issues
32
of data insufficiency. This is of particular interest to address in relation to realized
spreads and price impact. If trades are few, our forward-fill approach in addressing
missing data points results in realized spreads converging to our effective spreads.
Similarly, our measure of price impact would tend to zero. Indeed, by investigating
the extent of this issue, we document a correlation between effective spreads and
realized spreads of roughly 0.98. To add robustness to these results, we run corre-
sponding DID estimations on our variables of interest based on a limited sample of
securities. In this application, the most illiquid securities—and the stocks matched
with those securities—are excluded. We define illiquid stocks as securities with less
than 300 trades executed on any given day during our time period. Table III presents
the model results based on the sample with these illiquid stocks excluded.
33
34
Table III:
Results: Difference-in-Differences estimations – Sample with illiquid stocks excluded
This table presents the ban implementation effects on our variables of interest based on random-effects Difference-in-
Differences estimations, excluding the most illiquid stocks in the sample. Illiquid stocks are in this setting defined as
securities with less than 300 trades on any given day during the time period. The limited sample includes a total of
32 securities. All marginal effects have been scaled by 104 (i.e., presented in basis points), with exceptions for quoted
depths. The table presents variable significance by (*) 10%, (**) 5%, and (***) 1%.
Model Treated Window Interaction 10yGovB PM log(MCap) MVol
RVol -6.014 -6.333* 4.142 -76.691*** -0.254 -16.526*** 1854.064***
QuotedSpread -0.564 -0.078 -0.098 -1.284*** 0.004 -1.449*** 19.642
log(QuotedDepthBid) 0.247* 0.030 0.028 0.287*** 0.015 0.598*** -7.580*
log(QuotedDepthAsk) 0.221 0.039 -0.027 0.367** -0.008 0.634*** -13.446***
EffectiveSpread -0.483 -0.300*** 0.287*** 0.089 -0.062 -1.195*** -17.355
RealizedSpread5min -0.352** -0.151 0.393** 1.186 0.275** -0.420 -29.050
PriceImpact5min -0.119 -0.181 -0.112 -1.707* -0.339** -0.816*** 7.927
The results presented in Table III are similar to our previous results with sig-
nificance in effective and realized spreads, while quoted spreads no longer appear to
be significantly impacted by the ban. Supporting the robustness of these results,
the correlation between effective and realized spreads drops to 0.44 in this limited
sample with liquid stocks. The remaining variables of interest, however, still lack
significance at all confidence levels considered.
We add further robustness to these results by running regressions on an ad-
ditional sample, in which data on the most illiquid stocks are replaced. In this
reconstructed sample, data on a given illiquid security in the control group is re-
placed with data on a different, non-suspended security, that is considered liquid.
This procedure involves replacing the illiquid security with the closest match among
the non-suspended securities in regards to market capitalization, and is hinged on
the condition that the securities share the same industry. This effectively entails
that data on 14 securities are duplicated in the underlying sample. Maintaining the
definition of illiquid stocks exhibiting less than 300 executed trades on any given day,
one industry, containing five securities in each group, is eliminated completely. These
securities are excluded from the sample, resulting in a sample size of 60 securities.
Table IV presents the results based on this sample.
35
36
Table IV:
Results: Difference-in-Differences estimations – Sample with illiquid securities replaced
This table presents the ban implementation effects on our variables of interest based on random-effects Difference-
in-Differences estimations, replacing the most illiquid stocks in the control group. Illiquid stocks are in this setting
defined as securities with less than 300 trades on any of the days during the time period. Illiquid stocks in the control
group are replaced with a corresponding, non-suspended security matched on market capitalization and industry.
The sample contains a total of 60 securities. All marginal effects have been scaled by 104 (i.e., presented in basis
points), with exceptions for quoted depths. The table presents variable significance by (*) 10%, (**) 5%, and (***)
1%.
Model Treated Window Interaction 10yGovB PM log(MCap) MVol
RVol -12.604** -3.877 1.655 -58.605*** -1.288 -13.444*** 2134.793***
QuotedSpread -3.304** 0.154 -0.316 -1.419*** 0.001 -0.175 58.288**
log(QuotedDepthBid) 0.500*** 0.031 0.001 0.270*** 0.019 0.352** -7.010*
log(QuotedDepthAsk) 0.497** 0.054** -0.058 0.267** -0.017 0.368** -16.812***
EffectiveSpread -1.913** -0.250*** 0.239*** 0.069 0.067 -0.595** 24.937
RealizedSpread5min -1.436* -0.159 0.338*** 0.842 0.379*** 0.155 3.823
PriceImpact5min -0.317 -0.139 -0.105 -1.747*** -0.318*** -0.942*** 14.600
As evident from Table IV, the model results are qualitatively similar to what has
been presented above, implying that the results are robust to different manipulations
of the data set.
A plausible explanation to the overall absence of significance across our mea-
sures concerns the existence of quasi-dark trading venues—as emphasized, and elab-
orated on, by Johann et al. (2019). These venues offer, albeit not complete, but
degrees of transparency, and fall outside the scope of ESMA’s DVC legislation. As
such, they continue to offer the benefits associated with such transparency, including
offering traders protection from potential predatory behaviour from HFT traders on
lit markets. As Johann et al. (2019) find quasi-dark venues, such as periodic auc-
tions, to absorb a vast majority of the liquidity from dark venues following the ban,
effects on volatility and liquidity on lit markets may in fact be limited—in which
case our mere focus on lit markets is insufficient to understand the true underlying
dynamics of the ban and its effects. In line with the sole focus on the duality of lit
market characteristics and dark pool bans presented here, such an analysis lies out-
side of the scope of this study. Still, the inconclusiveness surrounding several of the
volatility and liquidity measures does put to question whether the implementation
of dark pool bans has indeed fulfilled its purpose of improving lit market conditions
for traders. In this regard, our results share several similarities with those of Johann
et al. (2019), where the lack of change in market quality may be aptly explained by
quasi-dark alternatives, and an inadequate scope of the MiFID II framework.
An alternative reason as to why several market quality measures are seem-
ingly unaffected by the ban concerns the potential for dissipating effects. There is
a possibility that the effects on lit market quality in the short term are partially
driven by a behavioral overreaction on the market following suspension of a security.
In this setting, this fact could also entail that these temporary effects on trading
37
behaviour return to previous patterns during the time period considered. To inves-
tigate whether any of our measures are subjected to effects which dissipate during
the event window, we run additional DID estimations while varying the number of
days in the event window.
Table V presents the model results based on the full sample of securities. Re-
alized and effective spreads show significance consistently even under window sizes
of four and five days, respectively, or more. Quoted spreads, however, only appear
affected by the ban when considering window sizes of seven days and more. As such,
the results indicate that the effect on trading spreads is near instantaneous, while
quoted spreads appear affected by the ban only when considering larger window sizes.
The theoretical reasoning concerning the impact on spreads still applies. Looking
at Table V, we also notice that the marginal effects of realized and effective spreads
decrease as the number of days in the event window increases—suggesting that the
magnitude of the impact of the ban decreases with time.
38
39
Table V:
Results: Difference-in-Differences estimations – Full sample – Varying window size
This table presents results of the main model with varying window sizes, where the size is changed by altering the
final date of the event window. The results are based on the full sample. The marginal effect of the main variable
of interest, Interaction, is presented. All values have been scaled by 104 (i.e., presented in basis points). Variable
significance is indicated by (*) 10%, (**) 5%, and (***) 1%.
Interaction
Model 3 days 4 days 5 days 6 days 7 days 8 days 9 days
RVol -0.351 1.786 1.477 0.035 1.525 1.433 0.059
QuotedSpread 3.233 3.786 3.577 3.035 2.981* 2.798* 2.752*
log(QuotedDepthBid) -0.074 -0.070 -0.034 -0.028 -0.029 -0.005 -0.015
log(QuotedDepthAsk) -0.107* -0.113** -0.083 -0.085 -0.078 -0.068 -0.062
EffectiveSpread 1.477 2.389 2.474* 2.640* 2.516* 2.307** 1.841**
RealizedSpread 1.263 2.256* 2.283* 2.540* 2.360* 2.137** 2.118**
PriceImpact 0.148 0.040 0.114 0.038 0.091 0.109 0.040
While our results show no clear signs of dissipating effects over our limited
time period, it could conversely be the case that substantially larger window sizes
are required to capture the true effect on certain of our variables. A potential reason
for this is that the market may require additional time to adapt to the ban—in
particular in the context of our analysis, given the uncertainty associated with the
implementation of the very first market-wide ban in Europe. The lack of significance
in several of the variables can also reflect potential issues of sample size, which may
limit the extent to which the true impact is captured in the applications involving
shorter event windows.
In contrast to previous results, quoted depths on the sell-side of the order book
are reportedly significantly related to the implementation of the dark pool ban. The
theoretical implications of these results would hypothetically entail either less share
volume in the top-level order book depth, or lower ask quotes, as a result of the
ban. However, it may, perhaps, more plausibly be a sole consequence of the market
conditions during this relatively short time span, with a particularly low buying
pressure among investors.9
9During the time period considered, the Nasdaq OMX Nordic 120 dropped from 997.49 to 957.52,
corresponding to a negative return of 4.0%
40
41
Table VI:
Results: Difference-in-Differences estimations – Sample with illiquid stocks excluded –
Varying window size
This table presents results of the main model with varying window sizes, where the size is changed by altering the
final date of the event window. The results are based on the sample with illiquid stocks excluded. The marginal
effect of the main variable of interest, Interaction, is presented. All values have been scaled by 104 (i.e., presented in
basis points) except for quoted depths. Variable significance is indicated by (*) 10%, (**) 5%, and (***) 1%.
Interaction
Model 3 days 4 days 5 days 6 days 7 days 8 days 9 days
RVol 2.086 5.361 4.537 3.466 5.498 5.864 4.206
QuotedSpread 0.078 0.074 0.086 0.044 0.003 -0.035 -0.080
log(QuotedDepthBid) 0.043 0.032 0.039 0.035 0.039 0.048 0.034
log(QuotedDepthAsk) -0.047 -0.064 -0.040 -0.041 -0.033 -0.023 -0.031
EffectiveSpread 0.306*** 0.304*** 0.335*** 0.321*** 0.314*** 0.304*** 0.286***
RealizedSpread 0.703*** 0.564** 0.651*** 0.581*** 0.423** 0.399** 0.364**
PriceImpact -0.395 -0.261 -0.317 -0.262 -0.110 -0.098 -0.082
When investigating the corresponding results based on the limited sample of
liquid stocks, presented in Table VI, we note that effective and realized spreads still
appear to increase as a result of the dark pool ban. In contrast to the full sample,
these measures are significantly impacted by the ban even under a window size of
three days. In contrast, quoted spreads and quoted depths consistently appear unaf-
fected, indicating that previous results may be influenced by characteristics specific
to the securities excluded in the limited sample.
We perform complementary robustness analysis to determine whether there is
an impact on our measures of market quality at announcement of the ban, rather
than at implementation. This could be the case in a setting in which investors adopt
new trading behaviors in advance, and in anticipation, of the actual implementation
of the ban and its effects. We perform this analysis this by altering the event window
to begin at announcement on March 7, 2018, and cover the days up until the im-
plementation of the ban; making out a window size of a total of three trading days.
Table VII presents these results based on the sample with illiquid stocks excluded.
Overall, the results show no material impact of ESMA’s suspension announcement—
which suggests that investors do not act in anticipation of the dark pool ban. From
a theoretical perspective this is sound, as there is no clear rationale for investors to
divert order flow from dark pools prior to the implementation of the dark pool ban.
42
43
Table VII:
Results: Difference-in-Differences estimations – Sample with illiquid stocks excluded –
Window beginning at announcement
This table presents the effects on our variables of interest based on random-effects Difference-in-Differences estima-
tions, where the event window is defined as the three trading days between announcement and implementation. The
results are based on the limited data sample excluding the most illiquid stocks. Illiquid stocks are in this setting
defined as securities with less than 300 trades on any given day during the time period. All marginal effects have
been scaled by 104 (i.e., presented in basis points), with exceptions for quoted depths. The table presents variable
significance by (*) 10%, (**) 5%, and (***) 1%.
Model Treated Window Interaction 10yGovB PM MCap MVol
RVol -7.338 -4.507 4.149 -66.414* -0.174 -15.768*** 769.765
QuotedSpread -0.407 -0.424*** 0.267*** -1.475 -0.033 -1.699*** 10.799
log(QuotedDepthBid) 0.315** -0.009 0.046 0.568*** 0.018 0.520*** -5.644
log(QuotedDepthAsk) 0.305** 0.021 -0.000 0.513** -0.018 0.546*** -8.002*
EffectiveSpread -0.380 -0.221** 0.141 0.302 -0.026 -1.340*** -25.727*
RealizedSpread -0.279 -0.026 -0.282 1.090 0.118 -0.431 -3.754
PriceImpact -0.155 -0.196 0.407 -2.191 -0.174 -0.900*** -24.452
6 Conclusion
This paper scrutinizes recent regulatory intervention in dark pool trading by investi-
gating the implementation effects of MiFID II’s DVC rule on measures of lit market
quality. By leveraging the cut-off in dark pool trading activity following suspension
of 35 securities in Nordic equity markets, we reveal that the dark pool ban has un-
clear effects on lit markets. We find evidence for increasing measures of spreads as
a result of the ban, indicating a detrimental effect on lit liquidity conditions—which
is supported by, e.g., Buti, Rindi, and Werner (2011) and Foley and Putniņš (2016).
Conversely, other measures of market quality appear unaffected by the ban, where
similar results have been presented in previous research by Johann et al. (2019).
The lack of evidence justifying regulatory intervention in dark pool trading to im-
prove market quality for investors render additional research on the subject crucial.
The strand of literature would benefit from thorough analysis of the implementa-
tion effects of the ban particularly by investigating multiple events using a more
comprehensive set of data.
44
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8 Appendix
Table VIII: Sample securities
Full sample Sample with illiquid stocks replaced
Suspended Non-suspended Suspended Non-suspended Industry
ALFA SS HUSQ A ALFA SS SAAB B Industrials
ASSA B SAAB B ASSA B SAAB B Industrials
ATCO A NIBE B ATCO A NIBE B Industrials
DSV KBHL B DSV NIBE B Industrials
HEXA B SWEC B HEXA B NCC B Industrials
KNEBV FSKRS KNEBV NCC B Industrials
MAERSK A NCC B MAERSK A NCC B Industrials
MAERSK B AF B MAERSK B NCC B Industrials
SAND BEIJ B SAND NCC B Industrials
SKA B ADDT B SKA B NCC B Industrials
SKF B NELES SKF B NELES Industrials
VOLV B SKF A VOLV B NELES Industrials
WRT1V VOLV A WRT1V NELES Industrials
DANSKE INVE B DANSKE INVE B Financials
SAMPO SHB B SAMPO INVE B Financials
SEB A SEB C SEB A INVE B Financials
SHB A INDU C SHB A INDU C Financials
SWED A KINV SWED A KINV BB Financials
TRYG INTRUM TRYG INDU C Financials
CARL B ESSITY CARL B ESSITY Consumer Staples
SWMA ICA SWMA ICA Consumer Staples
ELUX B THULE ELUX B KIND SDB Consumer Discretionary
HM B KIND SDB HM B KIND SBD Consumer Discretionary
PNDORA EVO PNDORA EVO Consumer Discretionary
CHR BOL CHR BOL Materials
NZYM B SCA A NZYM B SSAB B Materials
UPM SSAB B UPM SSAB B Materials
VWS LUNE VWS LUNE Energy
FORTUM ORSTED FORTUM ORSTED Utilities
ERIC B NOKIA ERIC B NOKIA Technology
COLO B MCOV B Health Care
DEMANT VITR Health Care
GMAB TTALO Health Care
NOVO B ARJO B Health Care
LUN ORNAV Health Care
48
49
Table IX:
Results: Difference-in-Differences estimations for different ∆ – Full sample
This table presents the effects on realized spreads and price impact for ∆ = {10, 15}, based on random-effects
Difference-in-Differences estimations. The results are based on the full sample with all stocks. All marginal effects
have been scaled by 104 (i.e., presented in basis points). The table presents variable significance by (*) 10%, (**)
5%, and (***) 1%.
Model Treated Window Interaction 10yGovB PM MCap MVol
RealizedSpread10min -6.830** -1.664* 1.892** -1.047 1.001*** -3.117* 80.755
RealizedSpread15min -7.274* -2.084 2.395* 0.352 1.100*** -2.865* 65.234
PriceImpact10min -1.002** -0.594* -0.082 -4.134*** -0.586*** -1.023*** 79.684
PriceImpact15min -1.036 -0.535 -0.209 -5.255** -0.750** -1.197*** 121.112*
50
Table X:
Results: Difference-in-Differences estimations – Full sample – Window beginning at
announcement
This table presents the effects on our variables of interest based on random-effects Difference-in-Differences estima-
tions. The event window is here defined as the three trading days between the announcement of suspended securities,
and the implementation of the ban. The results are based on the full sample with all stocks. All marginal effects have
been scaled by 104 (i.e., presented in basis points), with exceptions for market capitalization (MCap) and market
volatility (MVol). The table presents variable significance by (*) 10%, (**) 5%, and (***) 1%.
Model Treated Window Interaction 10yGovB PM MCap MVol
RVol -6.676 -4.436 -1.406 -70.492*** 3.512 -15.472*** 569.568
QuotedSpread -12.921** -0.783 -0.261 -11.417 -0.524 -6.431** 587.240
log(QuotedDepthBid) 0.629*** -0.064 0.079* -0.249 0.012 0.243** -13.599**
log(QuotedDepthAsk) 0.682*** 0.024 -0.025 0.395 0.031 0.205** -14.875***
EffectiveSpread -7.519** 0.511 -0.979 -4.584 0.726 -4.210** 88.883
RealizedSpread -6.808* 0.524 -0.840 -7.048 0.734* -3.786* 123.237
PriceImpact -0.485 -0.198 0.059 -2.917** -0.150 -0.782*** -26.682
Figure II: RVol – Figure III: RVol –
Full sample Sample with illiquid stocks excluded
Figure IV: QuotedSpread – Figure V: QuotedSpread –
Full sample Sample with illiquid stocks excluded
51
Figure VI: QuotedDepthAsk – Figure VII: QuotedDepthAsk –
Full sample Sample with illiquid stocks excluded
Figure VIII: QuotedDepthBid – Figure IX: QuotedDepthBid –
Full sample Sample with illiquid stocks excluded
52
Figure X: EffectiveSpread – Figure XI: EffectiveSpread –
Full sample Sample with illiquid stocks excluded
Figure XII: RealizedSpread5min – Figure XIII: RealizedSpread5min –
Full sample Sample with illiquid stocks excluded
53
Figure XIV: PriceImpact5min – Figure XV: PriceImpact5min –
Full sample Sample with illiquid stocks excluded
54