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The effect of leniency programmes on anti–competitive behaviour:
an experimental study
Nick Feltovich∗
Department of Economics
Monash University
Clayton VIC 3800, Australia
[email protected]
Yasuyo Hamaguchi
Faculty of Economics
Nagoya City University
Nagoya 467–8501, Japan
[email protected]
December 10, 2014
Leniency programmes, under which firms engaging in anti–competitive activities can report their behaviour to a competition authority in return for reduced punishment, are a growing facet of competition
policy in many countries. We construct and analyse a simple model of duopoly pricing and competition
policy that captures the two important effects of leniency programmes: the direct effect, a reduction in the
stability of collusive arrangements, and the counterproductive indirect effect, an increase in the incentives
to form collusive arrangements in the first place by lowering the cost of exiting them. As these point in
opposite directions, the net theoretical effect is indeterminate. We then conduct a laboratory experiment
with human subjects playing the role of firms. We compare two leniency programmes – full immunity from
fines and partial immunity – against a baseline with no leniency programme in place. We find that both
leniency programmes yield the direct effect (cartels are more likely to break down) but not the indirect effect
(they are not more likely to form initially), and thus either programme reduces the extent of collusion and
supra–competitive prices and profits overall.
Journal of Economic Literature classifications: L41, K42, D43, C73, D03.
Keywords: leniency; competition policy; antitrust policy; duopoly; cartel; collusion.
Corresponding author. Some of this research took place while Feltovich was at University of Aberdeen. Financial support from
the UK Office of Fair Trading, the Japan Society for the Promotion of Science (Grants–in–Aid for Young Scientists (B), #21730231)
and the Nomura Foundation for Social Science is gratefully acknowledged, though the views expressed are solely those of the authors.
We thank Stephen King, Erika Seki and participants at the KEEL 2010 “How and why economists and philosophers do experiments:
dialogue between experimental economics and experimental philosophy” workshop for helpful suggestions and comments.
1 Background
The study of competition policies and their effects is of significant and growing importance. Recent trends in
globalisation have led many industries to be dominated at the national level by small numbers of firms, and as the
number of firms in a particular market falls, it becomes progressively more likely that the remaining firms will
attempt to behave anti–competitively. In most countries, the primary check on such attempts is a competition
authority that actively designs, implements and enforces competition policies. However, globalisation has also
meant that the ability of individual national, or even supra–national, competition authorities to enforce competition rules has been steadily deteriorating. As one example, a vertically–integrated multinational firm may have a
great deal of latitude in the unit cost it is able to report through the use of transfer pricing strategies, and without
knowing the firm’s “true” unit cost, the competition authority will have difficulty in assessing whether prices
and profits are excessive.
Since determining whether collusion has taken place based on market outcomes such as prices and profits
has become increasingly challenging, competition authorities have come to rely more and more on testimony
from the firms themselves. One of the most important tools these authorities have developed is the leniency
programme. Under a leniency programme, firms participating in cartels are able to serve as “whistle blowers”
by reporting their (and their rivals’) illegal collusive activities to the competition authority in exchange for some
consideration. This consideration can vary from a reduced fine, to complete immunity from prosecution or
administrative penalties, and even to receiving a bonus such as a portion of the fines collected from other cartel
firms. The introduction of leniency programmes has been a fairly recent phenomenon, but they are now in effect
in most developed countries (e.g., the EU, UK, US, Japan, Canada, Australia and South Korea).1
As leniency programmes become more common, it becomes increasingly important to understand what
effects they are likely to have on market outcomes, and in particular, firms’ anti–competitive behaviour. Theoretical research has shown that leniency programmes can increase the likelihood of cartel members’ cooperating
with authorities, making cartels less stable (Motta and Polo 2003). However, leniency programmes have a second, indirect effect that has received less attention from researchers: the benefits to forming a cartel in the first
place (as well as the benefits to recidivism) increase as the leniency programme makes exit easier, so that cartels
may be more likely to form (Chen and Harrington 2007). Thus, the benefit of greater cartel instability may be
off–set by the drawback of reduced deterrence, so that the overall effect of leniency programmes is intuitively
and theoretically ambiguous.2
While theory often fails to make a sharp prediction about the effects of leniency programmes, attempts to
determine the effects empirically using field data can suffer from other difficulties. Foremost among these is
that the researcher may have very good information about anti–competitive behaviour that is detected by the
competition authority, but little if any information about undetected cartels. As a result of this selection bias,
identifying the entire population of collusive episodes – and hence reaching general conclusions about how
leniency programmes affect collusion – can be nearly impossible. Additionally, many of the relevant variables
governing behaviour in this setting (such as firms’ costs and the shape of the demand curve) are to a large extent
Hamaguchi et al. (2009) provide some statistics about the growth of leniency programmes.
Along similar lines, McCutcheon (1997) provides theoretical results suggesting that competition policies which restrict communication between firms – seemingly making collusion more difficult – can actually decrease competition by reducing opportunities to
renegotiate after collusion has broken down, and hence raising the future costs of breaking a (tacit or explicit) collusive agreement.
Andersson and Wengstr¨om (2007) present experimental evidence that this indeed can happen.
unobservable to the researcher. Even when these obstacles can be surmounted, natural experiments (pairs of
policy environments that are identical except for the leniency programme) are very rare, so it is difficult to
accomplish direct tests of policy variables.
Because of these difficulties, we turn to experimental economics. Laboratory experiments with human
subjects offer several advantages for the study of leniency programmes. First, the experimenter has much greater
control over the preferences of decision makers than field researchers do. Second, relevant policy variables
can be varied in a systematic way, so that the effect of the leniency programme itself can be isolated. Third,
an important source of selection bias is eliminated in experimental data; all decisions of all relevant decision
makers are collected and available for the researcher to view. While lab experiments also have their drawbacks
(chiefly, questions of external validity arising from differences between the population of experimental subjects
and that of real firms’ decision makers), these drawbacks are arguably outweighed by the advantages.
Experimental research into the effects of leniency programmes is still in its infancy (see Section 2.4 for a
discussion of the relevant literature). The current paper contributes to this literature, with the use of a simple but
rich theoretical model designed to replicate the important features of firms’ decisions under various competition
policies, and a human–subjects experiment implementing this model. Subjects in the experiment play the role
of firms in a repeated duopoly game with communication before the first period. Each period comprises a simultaneous choice of prices, and in the event that both firms choose high prices, they run the risk of being punished
for anti–competitive behaviour by a competition authority. (That is, communication between firms per se is not
sufficient for a finding of collusion; it is also necessary for firms actually to have chosen high prices.) Subjects in
two “leniency” treatments can avoid the fine – either partly or completely – by blowing the whistle on the rival
firm. We compare the results of these treatments to results from a baseline where reporting and leniency are not
possible. While the model has a large number of equilibria (making sharp theoretical predictions impossible),
the set of equilibria varies across treatments in systematic ways. Specifically, moving from the baseline treatment to partial leniency, or from partial to full leniency, makes it easier to support equilibria involving collusion
and with reporting. Thus, both the direct and the indirect effects of leniency policies can be seen in our model.
However, since the two effects have opposite implications for prices, the extent of collusion, and firms’ profits,
understanding the net effects on these variables requires empirical testing via our experiment.
Broadly speaking, our experimental results are optimistic about the usefulness of leniency programmes. Our
data provide no evidence in favour of the indirect effect of leniency programmes, as there is no increase in cartel
formation under either partial or full leniency, compared to our baseline treatment. On the other hand, there is
plenty of evidence for the direct effect, as collusion is less stable in either of our leniency treatments than in the
baseline, and this decrease in stability is due to firms reporting to the competition authority. The overall impact
of these leniency programmes, while smaller than the incidence of whistle–blowing on its own would suggest
(due to a countervailing reduction in price under–cutting), includes lower prices, a decrease in the fraction of
time firms spend in collusion, and decreases in firms’ excess profits.
2 The duopoly game and experimental design
Our theoretical analysis begins with a symmetric 3x3 “underlying game”, shown in Figure 1. This game is not
actually used in our experiment, but all of the stage games we do use involve only fairly minor modifications
to it. Two firms simultaneously choose prices; for simplicity we limit the set of prices to High, Medium and
Low.3 The Medium price signifies (non–collusive) competition between the firms. The High price represents an
Figure 1: The underlying stage game
Firm 2
High Medium
High 10, 10 2, 11
Firm 1 Medium 11, 2
4, 4
0, 2
0, 2
2, 0
2, 0
0, 0
attempt to collude; this yields high profits if the other firm also chooses High, but low profits otherwise (note
that High and Medium on their own form a prisoners’ dilemma). The Low price is strictly dominated, but at we
will see below, its existence allows for a richer set of equilibria than would be possible with only the High and
Medium prices. In this stage game, then, (Medium, Medium) is the unique Nash equilibrium – and indeed the
unique rationalisable outcome – with resulting payoffs of 4 for each firm.
This stage game is infinitely repeated, with a constant discount factor δ ∈ (0, 1) that is identical for all firms.
Repeated–game payoffs are defined in the usual way. For Firm i, if πi (t) is the one–shot–game payoff in round
t, we have
δ t−1 πi (t).
Ui (πi (1), πi(2), πi(3), ...) =
Since (Medium, Medium) is the Nash equilibrium of the one–shot game, there always exists a subgame perfect
equilibrium of the repeated game in which both firms choose Medium in every round, irrespective of δ. However,
infinite repetition potentially leads to an enlargement of the set of equilibria. In particular, when δ is sufficiently
high, collusion – in the sense of repeated (High, High) stage–game outcomes – can be achieved. This is done
by the use of “trigger strategies”: strategies that choose a cooperative action (High, in our setting) as long as
the opponent also has behaved cooperatively, but punish the opponent with a less cooperative strategy if the
opponent has deviated from cooperation. In the game shown in Figure 1, there exist subgame perfect equilibria
in which (High, High) is the outcome in every round as long as δ ≥ 17 ; this collusion is supported by the threat of
switching to Medium after a deviation, which is credible since (Medium, Medium) is a stage–game equilibrium.
Even with lower discount factors, collusion is possible if we relax the assumption of subgame perfection and
consider other Nash equilibria. In particular, as long as δ ≥ 19 , (High, High) in each round can be enforced using
trigger strategies in which deviations are punished with play of Low forever.4
We focus on a market with two firms, as the highly competitive nature of markets with even a small additional number of sellers
is well recognised by economists. In the theoretical industrial organisation literature, for example, Selten (1973) shows that firms are
substantially more likely to behave competitively in markets with five or more firms than in markets with fewer firms. In the empirical
IO literature, Bresnahan and Reiss (1991) look at geographically separated markets in several industries, and find that three sellers in
a market are typically enough to yield essentially competitive prices. Isaac and Reynolds (2002) find a similar result in experiments:
four–firm posted–offer markets feel a strong push toward competitive price levels, while no such tendency is observed when there are
only two firms.
Bayer (2014) provides evidence from a repeated social–dilemma experiment that whether a threat is “credible” in a theoretical sense
has little bearing on whether it can support cooperation. If so, then Nash equilibrium is the appropriate solution concept for us to use,
rather than requiring subgame perfect equilibrium.
The baseline game
Our baseline game (i.e., the game we use in our baseline treatment) arises from one small modification to
the underlying game in Figure 1: we introduce competition law, in the shape of a non–strategic competition
authority. The competition authority discovers anti–competitive behaviour, which we define as a choice of High
by both firms, with exogenous probability p ∈ [0, 1]. When such behaviour is discovered, two penalties are
imposed: (i) an exogenous fine F > 0 in the current round, and (ii) a prohibition of choices of High in all future
rounds of the repeated game (reflecting an assumption that once anti–competitive behaviour has been detected
by the competition authority, the latter will continue to keep an especially close eye on that industry, making
future collusion prohibitively difficult).
This latter punishment reduces the stage game to the game shown in Figure 2, which we refer to as the game
with punishment in effect. This reduced game also has (Medium, Medium) as a unique Nash equilibrium, with
resulting payoffs of 4 for each firm. Importantly, there is no scope for cooperation between firms in this game;
Figure 2: The stage game when punishment is in effect
Firm 2
Medium Low
Firm 1 Medium
4, 4
2, 0
0, 2
0, 0
for any δ, there is no equilibrium in which any stage–game outcome besides (Medium, Medium) is observed.
Adding competition law has no effect on payoffs as long as the firms do not collude (i.e., at least one firm
chooses Medium or Low); thus there continues to be a subgame perfect equilibrium of the repeated game in
which both firms always choose Medium. However, as before, it might be that collusion can also be supported
in a subgame perfect equilibrium. To examine this possibility, we start by noting that in the first round, it is
not possible that punishment is in effect (since there was no previous round for collusion to be detected by the
competition authority), so it is possible for firms to choose High. We next compute the repeated–game payoff to
each firm in a path of play with both firms choosing High as long as punishment is not in effect; call this payoff
π ∗ . Choices of (High, High) in the first round yield a stage–game payoff of 10 to each firm. With probability
p, the firms are caught by the competition authority, fined F in the first round, and limited to payoffs of 4 in
each subsequent round. With probability 1 − p, they are not caught, incur no fine, and begin the next round in
the same state as the current one (leading to a continuation payoff of π ∗ , discounted once). π ∗ thus satisfies the
π ∗ = 10 + p(−F + 4δ + 4δ 2 + · · ·) + (1 − p)δπ ∗ ;
solving for π ∗ yields
π∗ =
4pδ + (1 − δ)(10 − pF )
(1 − δ)(1 − δ + pδ)
It follows that (High, High) is consistent with subgame perfect equilibrium if it can be supported by a credible
trigger strategy (threatening to choose Medium forever if the other firm deviates from High), which is true if
π ∗ is higher than the payoff from a (Medium, High) outcome in the first round and (Medium, Medium) in all
rounds thereafter:
4pδ + (1 − δ)(10 − pF )
≥ 11 + 4δ + 4δ 2 + · · · = 11 + 4
(1 − δ)(1 − δ + pδ)
This equilibrium condition can be rewritten as [7(1 − p)δ − (1 + pF )](1 − δ) ≥ 0, and since 1 − δ is always
positive, the condition simplifies further to δ ≥ 7(1−p)
. As was true in the underlying game, (High, High) in this
baseline game can be supported for some lower δ in Nash (but not subgame perfect) equilibrium.5
The game with leniency
From the baseline game, we make one more modification to obtain our game with leniency: following a (High,
High) pair, the competition authority allows each firm the opportunity to report their anti–competitive behaviour
(see Figure 3). If either firm does so, then the competition authority detects their anti–competitive behaviour
with probability one, and the restriction on future prices to Medium and Low is put into place for both firms as
before. The firm reporting the anti–competitive behaviour receives a reduced fine of F − R (with R > 0 the
“reward” for reporting), while the firm not reporting receives the same fine (F ) as in the baseline game. If both
firms choose to report, both receive the reduced fine.
Figure 3: Sequence of decisions in the baseline stage game
(High, High)
Firms choose
✲ Prices
Firms choose
✿ report/no report ❍
announced ❳❳
All results
✟ announced
Not (High, High)
The analysis of the associated repeated game (with the price decision and, if applicable, the reporting decision in each stage) depends on parameter values, but as long as R is no more than the amount of the fine, the set
of subgame perfect equilibrium outcomes is identical to what it was in the baseline game: there exist equilibria
in which both firms choose Medium in all rounds, as well as equilibria in which both choose High (and do not
report) in all rounds until they are caught. Notably, for these values of R, there are no subgame perfect equilibria
in which the firms report their anti–competitive behaviour.
However, reporting can happen in non–subgame–perfect Nash equilibria. Specifically, consider a strategy
according to which the firm chooses High in the first round, and if the other firm also chooses High, reports
and then chooses Medium forever, but if the other firm chose Medium or Low in the first round, punishes by
choosing Low forever. For a given value of R, both firms’ playing this strategy constitutes a Nash equilibrium
as long as δ is sufficiently high: δ ≥ 1 − 2/(3 + F − R). In this case, the observed result would be both firms
colluding in the first round, both reporting the collusion, then both choosing Medium from then on. (A numerical
example is shown in the next section.) The reporting is supported in equilibrium because of the relatively gentle
The condition for δ is −2pδ + (1 − δ)[9δ(1 − p) − (1 + pF )] ≥ 0. This quadratic in δ holds over an interval that strictly includes
the interval from 7(1−p)
(the lowest δ for which collusion can hold in subgame perfect equilibrium) to one. That is, collusion supported
by a threat of Low prices is possible for any discount factor that allows collusion with a threat of Medium prices, and for some lower
discount factors.
punishment (fine reduced by leniency, followed by Medium prices) for reporting compared to the more severe
consequences from under–cutting (high profit in the current round, but Low prices thence). The condition on δ
additionally implies that as R increases, collusion followed by reporting becomes still easier to support, either in
the sense that a lower discount factor is needed for such equilibria to exist, or because a larger set of punishments
for deviators is available to support collusion and reporting. That is, not only is the incentive to report greater as
R increases (the “direct effect” of leniency programmes mentioned in the introduction), but so is the incentive
to collude in the first place (the “indirect effect”).
Experimental design and theoretical implications
In the experiment, we set the parameters to particular values. The discount factor δ is set to 0.8, which is large
enough to support many kinds of equilibrium but small enough to allow multiple supergames in an experimental
session. The exogenous detection probability p is set to 0.08, comparable to the values used in other collusion
experiments (see Section 2.4). The fine for being caught is set at the stage–game gain from collusion over the
competitive outcome (F = 6). The reward for reporting anti–competitive behaviour R is a treatment variable,
and takes on one of two values: R = 3 or R = 6, corresponding to partial or full immunity from the fine. We
will refer to these as our “partial leniency” and “full leniency” treatments, though we note that this is a slight
abuse of terminology, since even under full leniency, firms that report are still subject to the restriction on future
prices. In our baseline treatment, as already noted, reporting is not possible, though detection by the competition
authority is.
In all three of our treatments, given these parameter values, there exist both anti–competitive subgame perfect equilibria in which both firms choose High in all rounds (unless caught by the competition authority) and
pro–competitive subgame perfect equilibria in which both firms choose Medium in all rounds. While there is
no subgame perfect equilibrium in which reporting occurs, there are Nash equilibria – along the lines of those
described in the previous sections – in which it does. In both our full–leniency and our partial–leniency treatments, δ is sufficiently high that collusion and reporting can be supported by a threat to choose Low in every
subsequent round in the event of a deviation. However, there exist punishments that will support collusion and
reporting under full leniency but not under partial leniency.6
To summarise the implications of the theory, the multiplicity of equilibria in each of our treatments makes
crisp quantitative predictions impossible, but these sets of equilibria have the following properties:
1. Collusion is possible, but not certain, in all three treatments.
2. Reporting of collusive behaviour by firms is possible, but not certain, in both leniency treatments.
3. Collusion is easier to support under full than under partial leniency, and easier under partial leniency than
in the baseline.
4. Reporting of collusive behaviour by firms is easier to support under full than under partial leniency.
The final important aspect of our experimental design is the opportunity for cheap talk (costless, non–binding
communication) between the two firms prior to the first round. We do not attempt to model cheap talk theo6
One example is the threat to punish deviations by choosing Medium in the next round, then Low in the following round, and
continuing alternating between Medium and Low forever (there are many others).
retically here, but we note that experimental studies of cheap talk have tended to find that it raises the level of
cooperation between players – even in games where cooperation is not consistent with equilibrium behaviour, as
in one–shot and finitely–repeated prisoners’ dilemma games (see Sally (1995) for a meta–analysis of communication in prisoners’ dilemma games, and see Duffy and Feltovich (2002) for an example). We restrict cheap
talk to the first round only, so that the relevant solution concept remains subgame perfect equilibrium rather than
some notion of renegotiation proofness (Farrell and Maskin, 1989).
Related literature
In this section, we discuss the previous experimental research in this area. We place particular emphasis on the
experimental designs used by these authors, so that we can contrast ours at the end of this section, though we
also summarise those results that are most relevant to our experiment.
To our knowledge, Apesteguia et al. (2007, hereafter ADS) conducted the first laboratory experiment involving a leniency programme. Subjects in their experiment played a one–shot three–firm Bertrand oligopoly game
with homogeneous products. Prior to choosing prices (which were restricted to integers between 90 and 100),
subjects could opt to communicate; non–binding communication was possible, via a computerised chat room, if
all three subjects agreed to communicate. In all of their treatments, ADS defined a cartel to have been formed
whenever the subjects so agreed – irrespective of subsequent price choices – and the competition authority could
only detect the cartel if one of the firms reported it. In their baseline treatment, firms could report their cartel
activities, but there was no benefit to doing so (no leniency programme was in effect), and there could be a
cost, since all colluding firms incurred a fine of 10% of their own revenue if caught (leading to the possibility of
negative earnings, though these were not enforced).
Hinloopen and Soetevent (2008, hereafter HS) extended ADS’s design in several ways. Their stage game
was similar, consisting of a three–firm Bertrand oligopoly game with homogeneous products and prices between
101 and 110, and a basic fine for anti–competitive behaviour (if caught) set to 10% of revenue. Unlike ADS, they
repeated this stage game, with fixed groups playing at least 20 rounds, and with a 0.8 continuation probability
thereafter. Subjects could opt for communication before each round, except in a baseline treatment where there
was no communication at all. Like ADS, non–binding communication was possible (and a cartel was judged to
have been formed) if all three subjects agreed, but HS restricted messages to a menu of statements of minimum
and maximum prices, in contrast to the free–form communication of ADS. In an “antitrust” treatment, HS
introduced a positive probability of the competition authority detecting collusion (though reporting by firms
was not possible in this treatment); this probability was set to 0.15. In a “leniency” treatment, they additionally
allowed firms to report their collusive behaviour, at a nominal cost. The first firm to report received full immunity
from the fine, and if a second firm also reported, its fine was reduced by half.7
Bigoni et al. (2012, hereafter BFLS) modified the design of HS. Subjects played a Bertrand duopoly with
differentiated products, with prices between 1 and 12. They could opt for communication before each round;
as with ADS and HS, communication took place – and a cartel was judged to have formed – if both duopolists
so opted, and similarly to HS, communication took the form of choosing amongst pre–written messages about
prices. Unlike the two previous experiments, the basic fine was a fixed amount, so it was positive even when a
Bigoni et al. (2012) note that HS use abstract framing, in contrast to the firm/cartel context used in our paper and the other papers
discussed in this section. It is possible, though far from certain, that framing would impact behaviour in settings like these.
subject earned zero revenue in a round. Reporting was possible in all treatments except for their baseline (where
communication was also impossible), and unlike the earlier experiments, could take place either before prices
were chosen or afterwards. Subjects played multiple supergames; the continuation probability was typically
0.85, though it would fall to zero in case a session lasted for more than 2 12 hours.
Hamaguchi et al. (2009, hereafter HKS) modelled a leniency programme within a degenerate two–stage
game. In the pricing stage, subjects’ choices were forced: they had to choose the collusive price if anti–
competitive behaviour had not yet been caught by the competition authority, and the competitive price if it
had. In the subsequent reporting stage (only reached if anti–competitive behaviour had not yet been caught),
payoffs were set so that firms preferred to report if and only if at least one rival firm reported, but all firms were
better off if none reported; if no firm reported, the competition authority detected collusion with probability 0.1.
The game was indefinitely repeated, with a fixed continuation probability of 0.8. Among HKS’s treatment variables were the number of firms in each market (two or seven) and the consideration given to whistle–blowing
firms (reduced fine, no fine or bonus).
A summary of the results of these experiments is presented in Table 1. Shown for each experiment are
the changes in average price, level of collusion (according to whatever definition was used by the authors)
and frequency of reporting arising from a change in treatment from no leniency to partial leniency (reduced
but positive fine), and from partial leniency to either full leniency (zero fine) or bonus.8 There is substantial
Table 1: Selected results from previous leniency–programme experiments
Change in degree Apesteguia, Dufwenberg Hinloopen and
Bigoni et Hamaguchi, Kawagoe and
of leniency
and Selten (2007)
Soetevent (2008) al. (2012) Shibata (2009) duopolists
none → partial
partial → full/bonus
+ + (bonus)
– (bonus)
none → partial
partial → full/bonus
+ (bonus)
+ (bonus)
+ (full), – – (bonus)
none → partial
frequency partial → full/bonus
+ (bonus)
+ + (bonus)
Key: + (–): positive (negative) but insignificant. + + (– –): positive (negative) and significant. N/A: not applicable
(treatment not part of design, variable not measured in a treatment, or result not reported).
agreement in the effects of enacting a partial–leniency programme (moving from no leniency to partial leniency):
both prices and the frequency of collusion behaviour decrease as a result, while the frequency of reporting
increases. Also, increasing the degree of leniency – moving from partial leniency to either full leniency or
a bonus – leads both to more collusion by firms (though the increase is typically insignificant) and to more
reporting of this collusion, though the associated effect on prices is ambiguous, with a rise in one study and a
fall in another.
Our experimental design, described in Section 2.3 and with some additional details in Section 2.5 below,
differs from the designs of these previous papers in several ways. The most important difference is in how we
define collusion, both within the game setting (e.g., when firms risk being punished by the competition authority,
or when leniency is available) and in our analysis of the data (e.g., as a statistic that might be correlated with
HKS find negligible treatment effects with seven firms, so we restrict attention here to their two–firm sessions.
our treatment variables): in both cases, it is simply choice of the high price by both firms.9 By contrast, ADS,
HS and BFLS define collusion as mutual agreement to communicate, irrespective of either the content of this
communication or the firms’ subsequent pricing.
Our “implementation–based” definition of collusion is simple and easily verifiable within the experiment.
(Imagine, by contrast, the logistical issues involved in assessing whether an agreement to collude was made
by subjects – in real time during the experimental session – and the consequences of even infrequent errors in
assessment.) Also, it aligns culpability with damage caused; firms risk punishment if and only if their behaviour
has harmed consumers.10 But is it realistic? Clearly it is at least as realistic as the definition used by ADS, HS
and BFLS, whose “agreement to communicate” definition of collusion means that mutual choice of high prices,
an agreement to charge high prices, and even both together are neither necessary nor sufficient to establish
collusion.11 However, under our definition, collusion can be established irrespective of whether any explicit
agreement was made between the firms, or indeed whether the opportunity to communicate (available to all
pairs of firms) was even taken. The former of these would be quite difficult to assess in a lab experiment
(requiring reading the content of multiple simultaneous conversations in real time), though the latter could
easily be automated.12
The question of whether such “tacit collusion” (in legal terminology, “tacit coordination” or “coordinated
effects”) constitutes collusion is far from settled. Posner (2001) argues forcefully that from an economic standpoint, it is collusion:
If the economic evidence presented in a case warrants an inference of collusive pricing, there is
neither legal nor practical justification for requiring evidence that will support the further inference
that the collusion was explicit rather than tacit. From an economic standpoint it is a detail whether
the collusive pricing scheme was organized and implemented in such a way as to generate evidence
of actual communications. It is not a detail sanctified by the language of section 1 of the Sherman
Act... (p. 94).
Posner goes on to list examples of US Supreme Court decisions in which evidence of explicit communication was
not required to prove collusion (e.g., “American Tobacco Co v. United States actually says that ‘a tacit meeting of
the minds’ satisfies the requirement of proving unlawful concerted action’...”, p. 95). He also identifies the main
Our use of a simplified price choice set – only 3 possible prices rather than 10–12 as in ADS, HS and BFLS – has the advantage of
making it possible to identify collusive pricing unambiguously, as only one price (High) is consistent with collusion. A disadvantage,
though perhaps a minor one, is that it makes our experiment unsuitable for studying differences in the severity of collusion (e.g., if prices
from 101 to 110 are possible, collusion at 110 is worse for consumers than collusion at 102). Recall that HKS had only two prices,
allowing them also an unambiguous price–based definition of collusion, though as noted above, their experiment had price choices
imposed on the firms rather than chosen.
This is a step in the direction of assigning liability based on harm to the victim (Polinsky and Shavell, 1994), as compared to
proscribing all communication amongst firms, or even verbal agreements to collude.
Despite Adam Smith’s assertion that “[p]eople of the same trade seldom meet together, even for merriment and diversion, but
the conversation ends in a conspiracy against the public, or in some contrivance to raise prices” (Smith, 1776, Book I, Chapter 10,
Paragraph 82), which taken literally would mean that all communication amongst firms leads to collusion, real competition policy does
not proscribe communication per se (as Hinloopen and Soetevent (2008) also acknowledge; see their footnote 4). Indeed Smith’s famous
quote’s less famous continuation makes clear that he does not advocate outlawing communication per se: “It is impossible indeed to
prevent such meetings, by any law which either could be executed, or would be consistent with liberty and justice” (ibid).
In Section 3.3, we analyse the communication between firms in our experiment, including factors affecting the likelihood of verbal
agreement, as well as the connection between such verbal agreements and actual collusive behaviour.
barrier to prosecuting tacit collusion: “the difficulty of proving collusive pricing by economic evidence, given
the complex, technical, and often inconclusive, or even equivocal, character of such evidence” (p. 98). That is,
it is not that there is any ambiguity about whether tacit collusion is illegal, but from a practical standpoint it will
often be difficult to know, let alone prove, that a given profile of prices or price changes reflects collusion as
opposed to more benign factors such as input costs or consumer demand.13 Evidence of a collusive agreement,
therefore, is the “smoking gun” that in practice is needed to show that illegal behaviour has occurred; it is not
the illegal behaviour itself.
Other countries’ competition authorities – in particular, the two in which this study was conducted – have
also stated explicitly that tacit collusion constitutes illegal collusive behaviour.14 Japan’s submission to the
2006 OECD Global Forum on Competition states, “The Japan Fair Trade Commission...bases its approach on
the theory that explicit agreement among the entrepreneurs is not necessary to prove a cartel agreement; i.e.,
‘liaison of intention,’ and a tacit agreement suffices. In the Toshiba Chemical case, which involved a cartel
without direct evidence, the Tokyo High Court recognised this theory” (p. 127). In the UK, the then–Office
of Fair Trading (now part of the Competition and Markets Authority) noted that “the nature of the market may
mean that undertakings might adopt the same pricing policy on the market without ever explicitly agreeing on
price” (OFT, 2004, p. 8).
Returning to the comparison between our experimental design and others’, the second difference is that
we only allow communication between subjects in the first round of a supergame – unlike HS and BFLS who
allow it in all rounds – which as noted in Section 2.3, maintains standard equilibrium concepts (rather that
alternatives such as renegotiation–proofness) as the source of theoretical predictions. Third, we only allow
reporting in a round in which anti–competitive behaviour actually occurred, in contrast to HS and BFLS, who
allow reporting in any round after communication took place. This may seem like a minor methodological
point, but it is actually very important. Our setup removes the possibility that reporting is used (or threatened)
as retribution for deviating from collusion, so that reporting serves the purpose that the competition authority
intends: breaking collusive arrangements currently in place. Fourth, unlike all of the above papers except for
HKS, our punishment for anti–competitive behaviour includes not only fines, but also a restriction on conduct
(prices) in future rounds. This is meant to reflect the possibility that when such behaviour has been caught in
the past, the competition authority pays closer attention to the industry in the future.15 We believe that this
captures some aspects of reality, though the downside is that our experiment cannot be used to study recidivism,
whereas HS and BFLS can and do. Finally, we begin all of our sessions with play of our basic game (without
leniency). Besides allowing for between–subjects, within–subjects and difference–in–difference comparisons
when analysing the data, starting with the simplest game gives the subjects an opportunity to learn about the
experimental environment, before being thrust into the more complex game with leniency.
Similarly, Mezzanotte (2009) argues that while tacit collusion is illegal under EU law under Article 82, enforcement is essentially
impossible due to this attribution problem. However, it should be clear that this problem does not arise in our theoretical and experimental
settings, given the small price choice set and the stationarity of costs and demand.
Some countries have gone the other way, however. Australia’s competition law defines collusion as explicit collusion only, making
tacit collusion legal.
Other justifications for this design feature are (1) an enforceable consent decree is put in place, under which firms must lower their
prices; or (2) after a finding of collusion, the competition authority gains understanding of firms’ cost structures, and hence can more
easily identify when prices are supra–competitive.
Experimental procedures
We implemented infinite repetition with discounting by means of a fixed termination probability (equal to δ,
the discount factor) at the end of each round. This is a standard technique in experimental economics, and
is methodologically sound as long as individuals are expected–utility maximisers with additively–separable
(supergame) utility functions, as the corresponding objective functions are identical.
The experimental sessions took place at the the University of Aberdeen’s Scottish Experimental Economics
Laboratory (SEEL) and Kyoto Sangyo University’s Kyoto Experimental Economics Laboratory (KEEL). There
were 16 sessions at SEEL, each with between 8 and 16 subjects, while the seven sessions at KEEL had 22–
28 subjects each. Subjects in both locations were primarily undergraduate students, recruited using ORSEE
(Greiner 2004) from databases of people expressing interest in participating in economics experiments. No one
took part more than once.
Each session comprised at least five supergames; a few sessions that finished the first five especially quickly
(due to the realisations of the draws for random termination) played a sixth supergame. In the first three supergames, there was never a leniency programme; we call this “Part 1” of a session – and the remainder of the
session “Part 2”. In five of the sessions, Part 2 also had no leniency programme; these make up our baseline
treatment. (Some information is displayed in Table 2 at the beginning of the results section.) In the remaining
eighteen sessions, Part 2 had a leniency programme in which both firms could receive a reduced fine by reporting to the competition authority: eight sessions with partial leniency (R = 3 < F ) and ten with full leniency
(R = 6 = F ).
At the beginning of a session, subjects were seated in a single room and given written instructions for Part
1.16 The instructions stated that the experiment would comprise two parts, but details of the second part would
not be announced until after the first part had ended. The instructions were also read aloud to the subjects, in
an attempt to make the rules of the game common knowledge. Then, the first round of play began. Because
each supergame involved indefinite repetition, the total number of rounds played varied across sessions. After
the third supergame was completed, each subject was given instructions for Part 2. This was done even in the
baseline treatment, where the game did not change. (In this case, the new instructions were quite short – stating
essentially just that the game was not changing.) These new instructions were also read aloud, before the fourth
supergame was played.
The experiment took place on networked computer terminals, using z–Tree (Fischbacher 2007). Subjects
were asked not to communicate with other subjects except via the computer program. Subjects were randomly
matched at the beginning of the first round of a supergame, but pairings were then fixed until the supergame
ended. No identifying information was given to subjects about their opponents (in an attempt to minimise
incentives for reputation building and other supergame effects). Rather than using potentially biasing terms like
“opponent” or “partner” for the other player, we used neutral though somewhat more cumbersome terms such
as “other firm”, “firm matched to you” and similar phrases.
Each round began with subjects being prompted to choose a price (High, Medium or Low). In the first round
of each supergame, the screen also contained a “chat room” so that subjects could send and receive cheap–
talk messages (see Figure 4 for the version used in the UK; a corresponding screenshot for Japan is shown in
The instructions from the partial–leniency treatments conducted in the UK and Japan are in Appendices A and B. Instructions from
the remaining treatments, as well as the raw data from the experiment, are available from the corresponding author upon request.
Appendix B). Subjects could send as many or as few messages as they wished; they were instructed not to send
Figure 4: Screen–shot from first round of a supergame
messages containing (a) personal or identifying information or (b) physical threats, but messages were otherwise
unrestricted. Messages were visible until a price was chosen or until the time available for communication (75
seconds) ran out. Subjects could not observe other pairs’ messages.
Once all subjects had chosen their prices, a feedback screen informed them of their own price and the
opponent price. In supergames with a leniency programme in effect, subjects reaching a (High, High) outcome
were prompted to choose whether to report or not to report their collusive activities to the competition authority
(see Figure 5). (If the leniency programme was not in effect, or if any other outcome was reached, subjects
were simply asked to click a button to continue.) The next screen told subjects the complete result for the
round, including (if applicable) whether either subject in the pair reported collusive behaviour, whether collusive
behaviour was discovered, and both subjects’ profits for the round. The round then ended with subjects being
notified whether the supergame would continue for another round or end with the current round.
Figure 5: Screen–shot from reporting component following (High, High) outcome
At the end of the fifth supergame, the experimental session ended. For each subject, one round from each
of the supergames was randomly chosen, and the subject was paid his/her earnings in those rounds. Each “lab
pound” was exchanged for £0.50 of real money in the UK, and for 150 yen in Japan; both were roughly equal
to US$1.60 at the time of the experiment. There was no show–up fee. Total earnings averaged about £15 in
Aberdeen and 2400 yen in Kyoto, for a session typically lasting 60–75 minutes.
The theoretical analysis of our three treatments (no leniency, partial leniency and full leniency), with implications
outlined in Section 2.3, allow us to formulate the following null hypotheses.
Hypothesis 1 The fraction of subject pairs reaching at least one (High, High) outcome is the same in all three
Hypothesis 2 The overall frequency of (High, High) outcomes is the same in all three treatments.
Hypothesis 3 The overall frequency of High price choices is the same in all three treatments.
Hypothesis 4 The frequency of reporting, conditional on a (High, High) outcome, is the same in the two treatments with reporting.
Hypothesis 5 Average profits are the same in all three treatments.
Of these five null hypotheses, two have natural directional alternatives. Hypothesis 1 relates to the incentives
to collude. As noted in the introduction and discussed in Section 2, a potential indirect effect of leniency
programmes is that by reducing the down–side risk to colluding, they lead to more cartels forming. If so, then
we would expect the fraction of pairs with at least one (High, High) outcome to increase from the baseline to the
partial–leniency treatment to the full–leniency treatment. Similarly, Hypothesis 4 refers to reporting frequency,
and the analysis of the model suggests that reporting might be more likely under full leniency than under partial
leniency (and of course more likely under partial leniency than in the baseline where reporting is impossible).
The remaining three hypotheses – Hypotheses 2, 3 and 5 (concerning the overall frequency of collusion, the
corresponding effect on prices, and firms’ profits respectively) – have no clear directional alternative, as the direct
effect of increased reporting and the indirect effect of increased incentives to collude (suggested by Hypotheses
4 and 1) pull in opposite directions.
3 Experimental results
In total, there were 23 experimental sessions with 384 subjects (see Table 2 below). Recall that there was no
leniency programme in effect in Part 1 (the first three supergames) of any session, while in Part 2 (the remaining
supergames), the leniency programme varied as shown in the table.
Table 2: Session information
Sessions Subjects
Aberdeen No leniency
(SEEL) Partial leniency
Full leniency
No leniency
(KEEL) Partial leniency
Full leniency
Throughout our analysis, unless stated otherwise, our unit of observation is a supergame–pair: an entire
supergame played between a pair of subjects. This is more useful for our purposes than the typical analysis
focussing on individual subject choices in each round, as it allows us to control for differences in supergame
length within and across sessions (and treatments), and avoids putting excessive weight on results in the longer
supergames. In Section 3.1, we present some descriptive statistics about collusive attempts, successful collusion,
and the breakdown of collusion. In Section 3.2, we use parametric regressions to test the suggestive results we
find in the descriptive statistics.
Descriptive statistics
Table 3 reports some aggregates from the experiment, along with p–values from tests of pairwise significant
differences between treatments in Part 2.17 In what follows, we will define a “collusion attempt” as a High
price choice by either subject in a supergame–pair. “Successful collusion” is a (High, High) outcome (which
we also abbreviate as HH) occurring in one or more consecutive rounds within a pair of subjects; we also call
this a “cartel”. Collusion can last until the supergame ends, or it can break down in one of three ways: reporting
by one or both of the subjects in the pair, exogenous detection by the competition authority, or by “under–
cutting”, which we define as any choice by either subject of a Medium or Low price following a previous–
round HH outcome that was not detected (exogenously or via reporting) by the competition authority. Under–
cutting, unlike reporting or exogenous detection, allows the possibility of future collusion, so it is possible for
a supergame–pair to successfully collude more than once.18 Finally, since nearly all price choices were either
Medium or High (Low prices represented fewer than 1 percent of price choices overall), the fraction of High
choices will serve as our measure of “average price”.
In Part 1 of the experiment, where there is no leniency programme, most pairs exhibit at least one attempt
to collude, with about 85 percent having at least one High price choice by a firm. Just under half of pairs
successfully collude at least once, and overall they manage to collude in almost 30 percent of rounds. In Part 2
Table 3: Descriptive statistics, (pair–supergame)–level data
Part 2
baseline partial leniency full leniency
At least one H choice (collusion attempt) .851
At least one HH outcome (cartel formed) .424
Fraction of L choices
Fraction of H choices (average price)
Fraction of HH outcomes (collusion extent) .283
Gross average payoff
6.430 7.576
Net average payoff
6.294 7.299
Conditional on at least one HH outcome
Reporting (by at least one firm)
Under–cutting (by at least one firm)
Endogenous breakdown (report, under–cut) .347
p–values from two–sided robust rank–order tests on session–level data (n.s.: p > 0.10)
p–values, pairwise signif. tests
base/part base/full part/full
p ≈ 0.047 p ≈ 0.085
p ≈ 0.047 p ≈ 0.085
p ≈ 0.040 p ≈ 0.077
p ≈ 0.006
p ≈ 0.040
p ≈ 0.008
See Siegel and Castellan (1988) for descriptions of the non–parametric tests used in this paper, and Feltovich (2006) for critical
values for the robust rank–order test. We err on the side of conservatism in computing these p–values, using only session–level data and
two–sided rejection regions (even when the alternative hypothesis is directional).
To be precise, there are 478 supergame–pairs with exactly one successful collusion, while 19 pairs (3.7 percent) collude exactly
twice, 3 (0.6 percent) collude three times and 1 pair (0.2 percent) colludes four times.
of the baseline sessions, both high prices and collusion become more frequent, with nearly 60 percent of pairs
colluding at least once and HH outcomes occurring just under half of the time. Since there is no difference in
any strategic aspect of the game between Part 1 and Part 2 of the baseline, these increases seem to be due to
increased cooperation between subjects as they become more experienced in this setting.
The table shows no evidence of the perverse conjectured “indirect effect” of leniency programmes, as neither leniency treatment shows any increase – let alone a significant increase – in either attempts to collude or
successful cartel formation. There are, however, a significant decrease in prices in both leniency treatments compared to the baseline, and a sizeable though insignificant decrease in the fraction of rounds in which collusion
occurred. These decreases are attributable to the “direct effect” of the leniency programme: just over 20 percent
of pairs in the partial–leniency treatment, and nearly half in the full–leniency treatment, end collusion by at least
one firm reporting to the competition authority, with significantly more reporting under full leniency than under
partial leniency. There is a corresponding decrease in payoffs under either leniency programme compared to the
baseline, though this decrease (like the decrease in the extent of collusion) is smaller than it should be, since the
increase in reporting is partly offset by a decrease in under–cutting. This suggests, that some – though not all –
of reporting is done as a substitute for under–cutting, though it must be emphasised that the total frequency of
endogenous cartel dissolution (reporting or under–cutting) does increase from no leniency to partial leniency to
full leniency (though only the former increase is significant). Finally, even the reduced payoffs in the leniency
treatments are well above the competitive level (4, as shown in Figure 1).
Figure 6 shows some additional descriptive statistics about collusion. Here we depart slightly from taking
the supergame–pair as the unit of observation, and instead take each episode of successful collusion as an
individual unit. The distinction matters since some supergame–pairs successfully collude more than once (see
Note 18). The left panel shows that the vast majority of cartels (over 85 percent) are formed in the first round
Figure 6: Cartel formation and persistence – all treatments and supergames
Percent of
Round 1 Round 2 or later
Round cartel formed
Duration of cartel (rounds)
of a supergame. The fraction is even higher (nearly 90 percent) in Part 2 of the experiment, and does not vary
substantially across treatments (90 percent in the baseline, 92 percent under partial leniency, 88 percent under
full leniency). The right panel shows that collusion is often successful for only a single round; one–round cartels
form a majority of all cartels overall, and nearly a majority (47 percent) in Part 2. There is some variation here
across treatments, consistent with leniency programmes’ reducing cartel stability: one–round cartels comprise
33 percent of all Part–2 cartels in the baseline, 42 percent under partial leniency, and 59 percent under full
Cartels that last for only one round not only predominate, they are different in nature from those lasting two
rounds or longer, as Figure 7 shows. This figure categorises all episodes of collusion according to whether they
Figure 7: Exogenous and endogenous cartel dissolutions – all treatments and supergames
Cartels lasting
1 round
Cartels lasting
2–4 rounds
Cartels lasting
5+ rounds
✥ Under–cutting
Percent of
End of supergame
Detected by comp. auth.
Endo– Exo–
Endo– Exo–
Endo– Exo–
genous genous genous genous genous genous
ended endogenously (due to subject decisions – either reporting or price under–cutting) or otherwise (exogenously due being detected by the competition authority without having been reported, or only by the supergame
ending, which for present purposes we classify as an exogenous ending). Over all supergames and treatments,
over half of the cartels lasting for exactly one round ended endogenously. This fraction varied across treatments.
In the supergames of Part 2 (where the treatments differed from each other), 45 percent of cartels ended endogenously in the baseline, compared to 65 percent under partial leniency and 77 percent under full leniency.
Also varying was the proportion of endogenous breakdowns due to reporting versus under–cutting: 73 percent
of endogenous breakdowns were due to reporting in the partial–leniency treatment and 83 percent under full
leniency, as compared to zero in the baseline. By contrast, once collusion survived into a second round, it was
unlikely to break down due to decisions by the firms themselves: only about one–fifth of cartels lasting 2–4
rounds ended endogenously, and none of the cartels lasting for 5 rounds or longer did.
These properties of collusion, along with the descriptive statistics reported in Table 3, suggest that introducing a leniency programme does lead to changes in firm behaviour. It does not seem to affect the likelihood of
cartels forming, but it reduces their stability. A substantial fraction of cartels break down via reporting by the
participants, though this fraction over–states the effect of the leniency programmes on collusion, since there is a
partially off–setting decrease in cartel break–down due to price under–cutting.
Parametric statistical analysis
We next present results from several regressions. We estimate eight models, each with a different left–hand–
side variable, using either the Part–2 data or, when appropriate, the subset of supergame–pairs that reached an
HH outcome (i.e., a successful collusion) at least once. The Part–1 data are used only to construct a proxy for
subjects’ intrinsic proclivity toward collusiveness, as described below.
Our first model is meant to shed light on the incentives to collude induced by the leniency programmes;
the dependent variable is “HH indicator”, equal to one if the pair achieves an HH outcome in any round. Our
second model looks at the overall prevalence of collusion; the dependent variable is “HH fraction”, the fraction
of rounds in which collusion took place. Our third model assesses the effects on prices overall; as mentioned
earlier, since Low price choices almost never occur, the fraction of High (versus Medium) price choices can be
taken as a measure of the average price. Our next three models look at the effects of the leniency programmes
on the two endogenous ways of breaking cartels individually (using indicators for reporting and under–cutting),
and for either kind of endogenous breakdown (an indicator with value 1 if either subject reported or under–cut).
Our last two models look at the leniency programmes’ effects on firm profitability; dependent variables are gross
and net profits.
We used similar right–hand–side variables in each regression. Our main explanatory variables are indicators
for the partial– and full–leniency treatments (except for the “Report” regression, which does not use the data
from the baseline treatment, and hence we dropped the partial–leniency treatment indicator). We include the
supergame number to control for changing behaviour over time, an indicator for the session taking place in
Kyoto to control for any subject–pool effects, and a constant term. Finally, we included an index of the pair’s
collusive or cooperative tendencies, called “collusiveness”; this was simply the fraction of times the two subjects
in the pair chose High in the first round of a supergame in Part 1 of the session (thus taking on values that are
whole–number multiples of one–sixth). We use Tobit models for the two profit variables, H fraction and HH
fraction, and probits for the others. All of the models were estimated using Stata (version 12) with robust
standard errors.
The results, displayed in Table 4, largely confirm what was observed in the descriptive statistics.19 The
insignificant and near–zero (and indeed negative) marginal effects of the partial– and full–leniency variables
on the HH indicator confirm that despite potentially providing incentives for firms to collude, these leniency
programmes do not make cartels more likely to form. Moreover, they lead to lower average prices, as shown by
their negative effect on the H fraction, and they make cartels less stable, as shown by their negative effect on
the HH fraction. As with the aggregate data, we can see that these effects on prices and the extent of collusion
are driven primarily by reporting, which is significantly more likely under the full–leniency programme than
under partial leniency. Under–cutting is significantly less likely under full leniency than in the baseline, while
there is no significant difference between partial leniency and the baseline (though there is also no significant
difference between partial and full leniency). Endogenous breakdowns are more likely under full leniency than
either the baseline or under partial leniency (p ≈ 0.012 for the latter comparison). Both leniency programmes
have negative effects on both gross and net profits, but these effects are smaller than they might have been due
to the decrease in under–cutting mentioned in the discussion of aggregate results.
We are primarily interested in the effects of the partial– and full–leniency treatments, but we note here the other variables’ effects.
The strong positive effects of our collusiveness variable on prices, collusion and payoffs (and weak negative effects on the breakdown
variables) suggests that there may be intrinsic subject heterogeneity in propensity to collude. The Kyoto–session variable has no significant effects, suggesting that subject–pool effects were limited. Finally, the supergame also has no significant effects, suggesting minimal
time variation.
Table 4: Regression results, Part–2 data – marginal effects at means, std. errors in parentheses
Dependent variable: HH indicator HH fraction
partial leniency
full leniency
Kyoto session
supergame #
Full sample
H fraction
Undercut Endog. break. Gross profit
At least one HH outcome
−0.275∗∗∗ 0.318∗∗∗ −0.117∗∗
Net profit
Full sample
−1.018∗∗∗ −1.238∗∗∗
* (**,***): Coefficient significantly different from zero at the 10% (5%, 1%) level. Endog. break = endogenous breakdown (report
or undercut)
Analysis of pre–play communication
We have focussed on the effects of our treatments on various measures of the implementation of anti–competitive
behaviour, relating to pecuniary gains by firms at the expense of consumers. However, recall that each supergame
in the experiment is preceded by a round of cheap talk for each matched pair of subjects. So, our experimental
data also allow us to examine the impact of these treatments on verbal agreements to collude, as well as the
relationship between any such agreements and subjects’ subsequent behaviour. To do this, we convert the qualitative data (sequences of free–form messages) from these cheap–talk stages to quantitative data, by classifying
each individual “conversation” according to what took place during it. The events we focussed on were (a)
any non–blank message; (b) both firms in a pair sending a non–blank message; (c) any message about prices
(irrespective of whether it was a suggestion, a factual statement, a question, etc.); (d) any suggestion to collude
(a proposal of a joint pricing policy that included a positive frequency of HH pairs, irrespective of whether and
how it was responded to); (e) an agreement on any pricing policy, collusive or otherwise (a proposal made by
one member of the pair, assented to by the other, without any subsequent questioning or disagreement about the
policy); and finally (f) an agreement to collude (similar to (e), but the pricing policy had to include a non–zero
frequency of HH pairs). These variables were coded as binary (e.g., either a conversation contained a mention
of prices or it did not; we were not interested in how many mentions there were after the first). In addition, we
recorded the total number of distinct messages, and the total number of characters over all messages, for each
Table 5 shows some descriptive statistics concerning the nature of subjects’ communication and its connection with behaviour in the subsequent supergame. Overall, just under half of the supergames were preceded
by a verbal agreement to collude by the two subjects, and an additional quarter of the supergames had both
of them sending messages but no verbal agreement (within our framework, this corresponds most closely to
the “mutual agreement to communicate” definition of collusion used in previous experiments by Apesteguia et
Table 5: Communication outcomes – descriptive statistics
Part 2
partial leniency
full leniency
Frequency of...
any non–blank message
both send a non–blank message
any message about prices
suggestion to collude
agreement on any pricing strategy
agreement to collude
Frequency, given (a) agreement to collude (b) both send messages but no agreement (c) neither
Collusion attempt
.971/.808/.734 1.000/.885/.821 .937/.783/.667 .981/.837/.829
Cartel formed
.770/.225/.227 .756/.423/.464 .737/.130/.140 .722/.265/.439
Fraction of H choices
.647/.355/.291 .769/.449/.482 .559/.298/.140 .537/.331/.364
Fraction of HH outcomes
.560/.128/.123 .694/.215/.323 .511/.051/.060 .470/.081/.221
Reporting (given cartel)
.000/.000/.000 .000/.000/.000 .171/1.000/.400 .372/.769/.556
Under–cutting (given cartel)
.286/.458/.514 .118/.455/.385 .129/.000/.400 .077/.154/.167
Endogenous breakdown (given cartel) .286/.458/.514 .118/.455/.385 .300/1.000/.800 .436/.923/.722
al. (2007), Hinloopen and Soetevent (2008) and Bigoni et al. (2012)).20 While reaching a verbal agreement
is neither necessary nor sufficient for a pair of firms to achieve collusive behaviour, there is a strong positive
association between the two. Collusion attempts and cartel formation are more likely, and collusion and high
prices occur a greater fraction of the time, following a verbal agreement (case (a) in the bottom half of the table)
than without one (cases (b) and (c)), according to a Wilcoxon signed–ranks test (session–level data, p < 0.001);
for example, collusion occurs in 76 percent of supergames after a verbal agreement to collude but only 26 percent of supergames with no such agreement. There is even evidence that cartels are more stable following a
verbal agreement, with endogenous breakdowns significantly less likely (p ≈ 0.034), though there is only an
insignificant decrease in under–cutting (p > 0.20) and weakly significantly less reporting (p ≈ 0.096) after a
verbal agreement. By contrast, comparison of cases (b) and (c) highlights that when there is no verbal agreement to collude, mere agreement to communicate has little systematic effect on any of the measures of collusive
behaviour or breakdown.21
Since verbal agreements to collude are correlated, but not perfectly so, with actual collusion, it is ex ante
unclear whether our leniency programmes would have the same effects on verbal agreements that they did with
actual collusion. So, we estimate four additional probit models, each with an indicator for agreement to collude
as the dependent variable. Model 11 uses the same set of right–hand–side variables and same sample (all Part–2
data) as in the probit for collusion (Table 4), for easy comparison. Model 12 is nearly the same, but includes
some additional variables that might be associated with a verbal agreement: the total number and length of
messages in the conversation, and the product of these with the Kyoto–session indicator (since sentences in
English and Japanese have different lengths, which might also affect the number of messages needed to agree
We abuse terminology slightly by referring to “verbal” agreements even though all communication took place via the computer.
The cases where the difference between cases (b) and (c) appears largest arise from small samples (e.g., the difference in reporting
under partial leniency between (b) and (c) is based on one observation and five observations in the two samples).
on collusion). Two more models (9 and 10) use the entire data–set but exclude the leniency–treatment variables
and the collusiveness variable (which was based on outcomes in Part 1). As before, these models were estimated
using Stata (version 12) with robust standard errors. The results are displayed in Table 6.
Table 6: Regression results, dependent variable = verbal agreement to collude (marginal effects at means, std.
errors in parentheses)
All supergames
Part 2 only
partial leniency
full leniency
Kyoto session
(0.032) (0.060) (0.035)
supergame #
(0.010) (0.011) (0.035)
number of messages
total length of messages
672.86 619.60
* (**,***): Coefficient significantly different from zero at the 10% (5%,
1%) level. Message variables also interacted with Kyoto–session dummy.
The most obvious difference between these results and those in Table 4 is that here, the leniency programmes
have a positive effect on the likelihood of verbal agreement to collude – and the effect is significant in the case
of partial leniency – while we saw previously that neither programme had a significant effect on actual collusion
(indeed, the sign was actually negative). Thus, if instead of using the HH indicator as our measure of a successful
collusion attempt, we had used a verbal agreement, we would have reached a different and potentially misleading
conclusion: we would have thought that our leniency programmes do in fact increase cartel formation, so that
combined with the reduced cartel stability we also observed, we might mistakenly have concluded that the net
effect of the leniency programmes was ambiguous.
4 Summary and discussion
Leniency programmes – in which firms behaving in an anti–competitive manner are rewarded for reporting this
behaviour (along with that of their rivals) to the competition authority – represent an increasingly important facet
of many governments’ competition policies. Intuitively speaking, it is reasonable to expect that introducing a
leniency programme, or increasing the consideration given for reporting, will make it more likely that firms will
come forward, thus reducing the stability of cartels. However, a perverse indirect effect is also possible: if firms
anticipate that the cost of future exit from a cartel has become lower (as a result of the leniency programme),
they may perceive the potential risks of forming a cartel in the first place as lower, and thus may be more willing
to enter into one.
In this paper, we have developed and analysed a simple theoretical model that captures much of the essence
of firms’ decision making under competition policy, with or without a leniency programme in place. While
the model has multiple equilibria and thus sharp predictions are impossible, it does provide support for both
the direct and the indirect effect we have discussed. Specifically, either introducing a leniency programme, or
increasing the reward for whistle–blowing within a current programme, makes it easier to support equilibria in
which firms collude as well as equilibria in which they report. This means that the net effects of the leniency
programme on other market variables such as prices, the overall extent of collusion, and firms’ profits are
ambiguous: they may increase, decrease or remain the same.
Because of this intuitive and theoretical indeterminacy, we conduct a laboratory experiment in order to gain
empirical evidence from a controlled setting about the relationship between leniency programmes and anti–
competitive behaviour. The experiment comprises three treatments: one in which no leniency programme is in
effect, one in which leniency involves a reduced fine and one in which leniency involves complete immunity
from the fine. The main results from the experiment are as follows.
Result 1 There is no increase (significant or otherwise) in the fraction of subject pairs successfully colluding
(i.e., reaching at least one (High, High) outcome) from the baseline treatment to either leniency treatment.
Result 2 The overall extent of collusion (i.e., frequency of (High, High) outcomes) is significantly lower under
full leniency than in the baseline. The frequency is also lower under partial leniency than in the baseline, but
the difference is not significant.
Result 3 Average prices (i.e., the frequency of High price choices) are significantly lower under either full or
partial leniency than in the baseline.
Result 4 The frequency of reporting, conditional on successful collusion, is significantly higher under full leniency than under partial leniency.
Result 5 Average profits are significantly lower under either partial or full leniency than in the baseline.
These results correspond to Hypotheses 1–5 respectively. Additional results, not anticipated by our hypotheses,
are (a) the increase in reporting observed under either leniency programme (compared to the baseline) is partly
off–set by a decrease in under–cutting; (b) when cartels form, they typically form immediately; (c) both reporting
and under–cutting tend to involve relatively new cartels (both fall off quickly after the first round of collusion,
and neither occurs after five rounds of collusion); and (d) verbal agreements to collude (in contrast to actual
collusion) are more likely under a leniency programme than otherwise, though in the case of full leniency, the
difference is not significant.
Some amount of caution should be taken in drawing sweeping conclusions about the outside world based on
the outcome of this experiment, which took place in an admittedly artificial laboratory environment, and with
many simplifying assumptions made about the available decisions, timing, parameter values, and so on.22 But
with that caveat acknowledged, our results might be interpreted as follows. The effects of introducing a leniency
programme (or increasing the generosity of the reward for reporting within the programme) are positive on
balance: the direct effect of increased break–down of collusion via greater whistle–blowing is fairly strong,
and the potential indirect effect of reduced deterrence is not observed (suggesting that this may be at worst a
second–order effect). The net impact includes less time spent under collusion, lower average prices, and firm
profits closer to competitive levels. However, several qualifications apply. First, some of the reporting under
the leniency programmes is done by firms that would have deviated from collusion anyway (that is, they report
instead of under–cutting the rival’s price), implying that the visible effects of a leniency programme on market
outcomes will be smaller than the reporting frequency on its own would indicate. Second, most of the gains
from introducing a leniency programme can be achieved with partial leniency; the additional benefits from full
leniency are smaller and typically not significantly different from zero. Third, neither leniency programme has
much ability to dissolve collusion that has become well established. Last, the way collusion is measured (actual
harm to consumers as in our setting, a verbal agreement to mutually choose high prices, or simply mutual desire
to communicate as in several previous experiments) can affect conclusions about its prevalence.
On balance, our results imply considerable optimism about the potential for leniency programmes to reduce
anti–competitive behaviour. Some of our findings – such as the decreases in prices and collusion under partial
leniency compared to no leniency, the increased reporting to the competition authority under partial leniency,
and the further increase in reporting under full leniency – are broadly in line with results seen in the literature
(see Table 1), though our study is the first to find a significant increase in reporting under full leniency compared
to partial leniency. By contrast, our findings of further decreases in prices and collusion under full leniency
(compared to partial leniency) are at odds with Hamaguchi et al. (2009), who found increases in their analogue
to our full–leniency treatment, and perhaps to some extent with Apesteguia et al. (2007) and Bigoni et al. (2012),
all of whom found increases in their bonus treatments, but not Hamaguchi et al., who found a decrease as we
did. We do not view our results as contradicting theirs, especially given that none of the increases was significant
(nor was the decrease we found). At most, they illustrate a fairly general point about how details of the leniency
programme, and other aspects of the strategic environment, can influence the implications of a lab experiment
based on that leniency programme – just as they would influence outcomes in the outside world. In both their
full–leniency and bonus treatments, Hamaguchi et al. (2009) did not give subjects a choice of price; rather, high
prices (and thus collusion) were imposed until collusion was detected, so the increased collusion they found in
their full–leniency treatment simply reflected a decrease in reporting (and conversely, the decreased collusion in
their bonus treatment reflected an increase in reporting). Apesteguia et al. (2007) used a one–shot setting, so
the effects of cartel dissolution on future prices was not factored into their calculation of average prices, which
would likely have been lower if they had. Bigoni et al. (2012) conjecture that the increased collusion in their
bonus treatment was due precisely to the bonus (in the sense that it would not have been seen under full leniency
without a bonus). In their words, subjects “may have formed cartels with the intent of fooling their competitor
Future research may examine the robustness of our results to changes in the strategic setting. Some possible variations are: changes
to the discount factor; the size of the fine, the reward for reporting, and the incentive for under–cutting; allowing communication in all
rounds instead of just the first; oligopolies with more than two firms; having rewards split amongst reporting firms instead of giving the
full reward to all; increasing the number of possible price choices beyond three; or requiring not only high prices, but also evidence of
an agreement about high prices, for a finding of collusion. There are certainly other interesting variations, but even a study of the ones
listed here is well beyond the scope of a single paper.
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385). Clearly, further research is needed to improve our understanding of how leniency programmes should be
designed in order to maximise their benefits.
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A: Sample instructions (from partial-leniency treatment, UK sessions)
Instructions: first part of experiment
You are about to participate in a study of decision making. Please read these instructions carefully, as the
amount of money you earn may depend on how well you understand them. If you have any questions, please
feel free to ask the experimenter. We ask that you not talk with the other participants during the experiment.
These instructions are for the first part of the experiment. You will receive instructions for the second part after
this part is finished. This first part is made up of several market games. You will be playing the role of a firm.
At the beginning of each market game, you will be randomly matched to another participant, who also plays the
role of a firm. You will be matched to the same firm for an entire market game, which will last for a number of
rounds. In each round, you will choose the price of your product: High, Medium or Low. At the same time, the
other firm will choose the price of its product. Your price and the other firm’s price, together, determine your
profits from the market, as shown in the table.
Your profit: £10
Other firm profit: £10
Your profit: £11
Other firm profit: £2
Your profit: £0
Other firm profit: £2
Other firm price
Your profit: £2
Other firm profit: £11
Your profit: £4
Other firm profit: £4
Your profit: £0
Other firm profit: £2
Your profit: £2
Other firm profit: £0
Your profit: £2
Other firm profit: £0
Your profit: £0
Other firm profit: £0
Chat: In the first round of each market game, whilst deciding on your price, you have the opportunity to send
and receive messages with the other firm. The chat portion of the computer screen is shown below.
To write a message, make sure your cursor is active in the narrow rectangle (where “Compose messages here”
appears), and type normally using the keyboard. To send, press the Enter key on your keyboard. You may send
as many or as few messages as you wish. However, we ask that you NOT send messages containing:
(a) personal or identifying information about yourself;
(b) physical threats.
Sent messages will appear in the box above the narrow rectangle, on your screen and on the screen of the other
firm. If the other firm sends you a message, this will also appear in the box on your screen. Other participants in
the experiment will not be able to see your messages, and you will not be able to see theirs. Once either you or
the other firm has chosen a price, it will be impossible to send additional messages, but you can still view
messages until you’ve chosen your price or the time available for messages runs out.
Competition law: The government has ruled that choice by both firms of the High price is anti-competitive
pricing. It has also established a competition authority to discover such behaviour. In any round in which both
you and the other firm choose a High price, there is an 8% chance that the competition authority will discover
this. If your anti-competitive behaviour is discovered, the punishment is:
(i) Both you and the other firm are fined £6 in the current round; this fine is subtracted from the profit
you would have earned.
(ii) Both you and the other firm will have your prices restricted in all remaining rounds of this market
game (only Medium and Low prices will be available).
If your anti-competitive behaviour is not discovered, or if either you or the other firm (or both) does not choose
the High price, there is no punishment.
Continuing or ending the market game: At the end of each round, there is a 20% chance that the market game
will end, and an 80% chance that it continues for at least another round. If the game ends, a new market game
will begin, and you will again be randomly matched to another participant. Also, punishments for anticompetitive behaviour disappear when a new market game begins. If the market game continues, you play
another round, matched to the same other firm.
Sequence of play in a round: The sequence of play in a round is as follows.
(1) Sellers choose their prices. You will be able to send and receive messages at this time, if it is the first round
of a market game.
(2) You are informed of the other firm’s price.
(3) You are informed of your profit for the round, including any fine incurred. Also, if you and the other firm
chose High prices, you are told whether your anti-competitive behaviour was discovered.
(4) The computer randomly determines whether the game will continue or end.
Payments: At the end of the experimental session, you will be paid based on your results. The computer will
randomly select one round from each market game – in this part and the next part. You will be paid the total
of your scores in those rounds, translated into real money at an exchange rate of 2 “lab-pounds” = £1.
Payments are made privately and in cash.
Instructions: second part of experiment
The procedure in this part of the experiment is very similar to that in the first part. You will play several market
games, each for a variable number of rounds. The participant matched with you will still be chosen randomly at
the beginning of a market game, and remain the same until the market game has ended.
Leniency programme: The difference from the first part of the experiment is that the competition authority has
instituted a leniency programme. In any round where both you and the other firm have chosen the High price,
you are each given the opportunity to report your anti-competitive behaviour to the competition authority. If
either you or the other firm does report, then the competition authority will (100% of the time) discover your
anti-competitive behaviour, and both firms’ prices will be restricted (to Medium or Low) in all remaining
rounds of this market game. However, a firm that reports incurs a reduced fine of £3:
- If you report, then you will incur the reduced fine for anti-competitive behaviour.
- If the other firm reports but you do not, then you will incur the same fine as in the first part of the experiment,
while the other firm incurs the reduced fine.
- If both firms report, then both incur the reduced fine.
Sequence of play in a round: The new sequence of play in a round is as follows.
(1) Sellers choose their prices. You will be able to send and receive messages at this time, if it is the first round
of a market game.
(2) You are informed of the other firm’s price. If you and the other firm chose High prices, you choose whether
to report your anti-competitive behaviour to the competition authority.
(3) You are informed of your profit for the round, including any fine incurred. Also, if you and the other firm
chose High prices, you are told whether your anti-competitive behaviour was discovered.
(4) The computer randomly determines whether the game will continue or end.
B: Sample instructions (from partial-leniency treatment, Japan sessions)
チャット: 市場ゲームの最初の回では、あなたの価格を決める一方で、あなたは、他社とメッセー
(a) あなた自身に関する個人情報、またはあなたがどこに座っているか特定できる内容
(b) 相手を肉体的に傷つけ脅すような内容
スクリーンの両方に、細い長方形の上のボックスに表れます。もし、 他社があなたにメッセージ
を送ったら、そのメッセージは、あなたのスクリーンのそのボックスに表れます。 ペアになって
競争法: 政府は、両方の会社が高価格をつけることは非競争的価格であるとしています。また、
政府は、そのような行動を発見するために、競争当局を設置したとします。 実験の各回で、両社
(i) あなたと他社は、その回において6 の罰金を科せられます。この罰金は、それまであなた
(ii) いったん見つかったら、その後の回において、あなたと他社は、選択する価格について
市場ゲームの継続と終了: 1つの市場ゲーム内の各回の終わりに、次の回が継続されるかどうか確
1回ごとのプレーの流れ: 1つのゲーム内での各回でのプレーの流れは以下のようです。
(1) 売り手(あなたと他社)がそれぞれ価格を選びます。市場ゲームの初回では、あなたは他社に、
(2) あなたは、他社が選んだ価格を知らされます。
(3) あなたは、その回の利益および罰金について知らされます。また、あなたと他社が高価格を選
(4) コンピュータが、ゲームを継続するかどうかをランダムに決定します。
謝金: 実験がすべて終わったら、あなたの実験での結果に応じて謝金をお支払いします。コン
ピュータは、第1部と第2部の実験での、各市場ゲームからランダムに 1回を選びます。それらの
減免制度: 第1部の実験との違いは、競争当局が減免制度を導入したことです。もし、ある回にお
の回からずっと選べる価格が制限されます(中価格あるいは低価格のみしか選べません)。 ただ
- あなたが報告したとします。この場合、あなたは非競争的行動について罰金を半額免除されます。
- 他社は報告しましたが、あなたは報告しなかったとします。この場合、あなたは第1部の実験と同
- 両社が報告したとします。その場合、どちらも罰金を半額免除されます。
(1) 売り手(あなたとペアの相手)がそれぞれ価格を選びます。市場ゲームの初回では、あなたは、
(2) あなたは、他社が選んだ価格を知らされます。もし、あなたと他社の両方が、高価格を選んだ
(3) あなたは、その回の利益および罰金について知らされます。 また、あなたと他社が高価格を選
(4) コンピュータが、ゲームを継続するかどうかをランダムに決定します。