GCOE Discussion Paper Series
Global COE Program

Human Behavior and Socioeconomic Dynamics
Discussion Paper No.219

Behavioral Efficiency I:
Definition, Methodology and Demonstration

Ronald M. Harstad

October 2011

GCOE Secretariat
Graduate School of Economics

OSAKA UNIVERSITY

1-7 Machikaneyama, Toyonaka, Osaka, 560-0043, JapanBehavioral Efficiency I:
Definition, Methodology and Demonstration
Ronald M. Harstad*

Economics, University of Missouri
harstad@missouri.edu
ISER, Osaka University

September 4, 2011
Please consult before citing or circulating
Abstract
Economic experiments conducted in laboratories employing an induced-values
methodology can report on allocative efficiencies observed. This methodology is limited byrequiring the experimenter to know subjects’ motivations, an impossibility in field
experiments. Allocative efficiency implies a hypothetical costless aftermarket would beinactive. An outcome of an allocation mechanism is herein defined to be behaviorally efficient if
an appropriate aftermarket is actually appended to the allocation mechanism and at most anegligible aggregate size of mutually beneficial gains is observed on the aftermarket.
Methodological requirements for observation of behavioral efficiency or inefficiency are put
forward. A simple field demonstration indicates when an increase in public good output cancover marginal cost in a mutually beneficial decentralization, without knowing valuations.
Several empirical issues that arise with the methodology are noted.
C9; C93; D01; D61; D03; D46; Keywords: behavioral efficiency, field experiment
methodology, allocative efficiency, revelation of valuations, aftermarkets* I thank, without implicating, Marc Willinger for organizing experimental facilities and arrangements, Dimitri

Dubois for assistance in conducting experiments, Dubois and Rafaele Preget for translating instructions,
Willinger and Sophie Thoyer for organizing financial support, David Levine, Alvin Roth and Cathleen Johnson
for useful suggestions, LAMETA at Universite de Montpellier for providing experimental facilities, and CNRS
and INRA for financial support of the experiment, and ISER at Osaka University for support during thewriting.

Behavioral Efficiency I:
Definition, Methodology and Demonstration
Abstract
Economic experiments conducted in laboratories employing an induced-values
methodology can report on allocative efficiencies observed. This methodology is limited byrequiring the experimenter to know subjects’ motivations, an impossibility in field
experiments. Allocative efficiency implies a hypothetical costless aftermarket would beinactive. An outcome of an allocation mechanism is herein defined to be behaviorally efficient if
an appropriate aftermarket is actually appended to the allocation mechanism and at most anegligible aggregate size of mutually beneficial gains is observed on the aftermarket.
Methodological requirements for observation of behavioral efficiency or inefficiency are put
forward. A simple field demonstration indicates when an increase in public good output cancover marginal cost in a mutually beneficial decentralization, without knowing valuations.
Several empirical issues that arise with the methodology are noted.
C9; C93; D01; D61; D03; D46; Keywords: behavioral efficiency, field experiment
methodology, allocative efficiency, revelation of valuations, aftermarkets“My research agenda focuses on using field experiments to learn what social policies
work, what do not, and why.” 1--Dean Karlan, Yale University
1. Introduction
I begin by quoting Karlan, not as a straw horse, but as a definitive statement by a noted
economist who has already contributed within this agenda. The verb “work” in this quote
admits a broad interpretation, including possibly impacts of a policy on median income,income inequality, income security, intergenerational mobility and related opportunities,
economic growth, educational attainment, as well as narrower impacts on family size, labor
force participation, and many others. Whatever the list a particular researcher considers, toan economist an essential component of whether a policy “works” is how small or large ashortfall from allocative efficiency it attains.
Efficiency measures are commonplace in economic laboratory experimentation. 2 The
restriction to laboratory experiments is critical, as the methodology allowing observations of
the shortfall from allocative efficiency, induced values, can only be employed in a laboratory
setting, and cannot help Karlan and other scholars observe “what social policies work …
and why” in the field.
In many hundreds of laboratory experiments, financially motivated subjects transact
abstract commodities (perhaps called X or “triangle” but not “tennis lessons” or “BigMacs”) on markets observed by the experimenter. Absent any innate values, valuations of X
1 Beginning text of his homepage, http://karlan.yale.edu/, visited 4/16/11.

2 Cf. e.g., Smith [1962], [1976], Davis and Holt [1993], Kagel and Roth [1995], and original sources cited in thelatter two works.

1are induced by the experimenter, as “the first unit of X you buy can be resold to theexperimenter for $8.75, the second for $6.80, the third for $5.10” to a potential buyer, or“the first unit of X you sell can be obtained from the experimenter for $3.10, etc.” Whentransactions costs can be deemed negligible, inducing values allows the experimenter tocalculate the set of Pareto efficient allocations, and attach a cardinal measurement to any
observed shortfall from this set.
No corresponding measure is available in field experiments, where transactions might
involve (usually subsidized) provision and/or allocation of: irrigation water, adult education,
childcare, pollution permits, microfinance, insurance against background risk, or similar“naturally occurring” goods, services and contracts. In “framed” field experiments, thesetransactions occur on a market constructed and controlled by the experimenter; in “natural”
field experiments, the experimenter observes but cannot control a naturally occurring
market. 3 The experimenter can observe transacting behavior but not valuations or
motivations, and so cannot calculate the Pareto set nor measure shortfalls from it.
This paper proposes a definition and a specific but broadly usable methodology to allow
observations relevant to allocative efficiency in field experiments, which observe only
behaviors that stem from unobserved motivations and preferences (and sometimes evenincompletely observed feasibility constraints). Theoretical issues arising with thismethodology are described. Following that, I provide a first field demonstration, observing
whether an increase in output of a public good from an ad hoc starting point can beachieved as a mutually beneficial reallocation. Then several empirical issues that arise in theconsideration of this methodology are discussed. A companion paper offers a concretedemonstration of the methodology in the simplest possible environment—an economy witha single, indivisible good—and illustrates how laboratory- and field- compatible efficiency
measures might be distinct.
Among the finest examples of how far field experiments have been able to go in the
direction of inferring efficiency conclusions from observations is Bohm [1984]. Peter Bohm
convinced the Swedish federal government to let him control whether an indivisible public
good would be produced or not, an office that would collect and provide certain statistical
data to local governments. Randomly splitting the local governments into two groups, heannounced rules to one group that gave them an incentive to understate willingness-to-pay(WTP), and to the other an incentive to overstate WTP. The observed sum of stated WTPs
slightly exceeded cost, and mean WTP per capita was not markedly different between thetwo groups. Nothing Bohm could observe, however, would let him infer whether providing
the statistical office would yield an efficiency gain.
Bohm believed the binary nature of the public good decision he studied was a largeadvantage: “The case of divisible public goods, requiring the revelation of WTP functions, orat least WTP for several alternative quantities, is referred to the science fiction department
for the time being.” (pp. 138-9) Over a quarter century later, the methodology proposed
herein seeks to move beyond (or back from?) science fiction.

3 I am defining these terms slightly differently than Harrison and List [2004], as the issue of experimenter

control seems more critical than whether subjects are aware they are in an experiment.

2

1.1. Pareto Efficiency Reinterpreted
In an economy with I individuals and C commodities, let xi be the C-dimensional
allocation to individual i, ui his utility function, and x = (x1, …, xI). Then the usual definitionof a Pareto-efficient allocation is that it satisfies(P): Max x u1(x), subject to: uj(x) ≥ uj, all j = 2,…, I, and to feasibility conditions.
In the 1950’s it became commonplace among several developers of general equilibrium
theory to add imagery in a reinterpretation of this maximization problem: Suppose an
allocation were to be Pareto-efficient. Then a hypothetical costless aftermarket would beinactive, for the simple reason that, upon reaching a Pareto-efficient allocation, there would
be no remaining mutually beneficial transactions to exploit.
This reinterpretation is informationally dissimilar: the maximization in (P) is clearly tied
to knowledge of motivations and valuations (ui, after all), while the counterfactual
aftermarket is tied to hypothetical transactions (that is, to hypothetical behaviors). In
principle, as transactions can be observed in field experiments, these experiments might avail
themselves of aftermarkets.
2. A Definition
So I define behavioral efficiency: an outcome of an allocation mechanism is said to be
behaviorally efficient if an appropriate (incentive-compatible, suitably transparent, andapproximately costless) aftermarket is actually (and immediately) appended to the allocation
mechanism 4 and at most a negligible aggregate size of mutually beneficial gains is observedon the aftermarket. Natural extensions of the definition include at least the following: [a] anallocation mechanism is said to be behaviorally efficient in a particular context if it reliably
yields behaviorally efficient outcomes; [b] a social or economic policy Y is said to be
behaviorally less inefficient in a particular context than an alternative policy Z if the shortfall
from behaviorally efficient outcomes under policy Y is robustly observed in suchaftermarkets to be significantly smaller than observed under Z.
3. Aftermarket Methodology
The aftermarket referred to in this definition must be designed and implemented so as tosupport the intended normative interpretation. It likely aids first to set aside straightforward
disqualifications: [i] In general, simply repeating an allocation mechanism does not suffice todraw meaningful conclusions about efficiency of the initial application of the mechanism (anillustration is in section 4). 5 [ii] Whatever its structure, a resale market (Zheng [2002]) does
not suffice. A key terminological distinction: unlike resale markets (e.g., for US Treasurydebt), an aftermarket necessarily involves the same economic actors as the original market(original allocation mechanism), none added and none absent. 6 Imagine $100K in 5-year Tnotes is sold today, by their purchaser at a Treasury auction on the third Tuesday of themonth before last, to a regional bank that did not compete in that particular Treasury
auction. Today’s resale in no way implies an inefficiency in the allocation that resulted from4 Any method, however informal, of reaching an allocation is herein labeled an allocation mechanism.

5 Were repeating the same mechanism to suffice in some special circumstance, likely it would create needlessconfusion for subjects.
6 This definition is clearly implied in the half-century-old reinterpretation of Pareto efficiency noted in section
1.1 above.

3

that auction. [iii] Later transactions involving an informationally distinct commodity cannot
support interpretation of an earlier allocation as inefficient. For example, suppose one of agroup of competing used-car dealers obtains a particular car at an auction of cars whose
leases have ended. Some days after the auction, the consigner of this particular car agrees toallow the winning bidder to return the car and be given a full refund; that winning bidder
continues to be considered a financially reliable bidder by the auctioneer. Even if exactly thesame set of bidders are competing when the car is re-auctioned, a different bidder winning
the re-auction does not imply any inefficiency of the original auction. The knowledge thatthe car was returned, inferred from the fact of its re-auction, leads to a realization that a
quality issue unsuspected as of the original auction has since surfaced, thus to a different
commodity being allocated at re-auction.
To shed light on behavioral efficiency, the aftermarket must be constructed so as to
identify any and all remaining mutually beneficial transactions involving the same set oftraders, under the same information as occurs when the original market (or othermechanism) reaches an allocation. 7 This requires revelation: that subjects’ behavior in theaftermarket can be interpreted as revealing the border between potential transactions they
prefer to make and prefer not to make, thus as revealing all relevant willingnesses-to-pay andwillingnesses-to-accept. 8 In straightforward situations, this can be accomplished via a typicalincentive-compatibility characterization: that the price to any partner in any transaction be
independent of his or her own behavior, with the impact of the behavior limited to affecting
whether (to be precise, the probability with which) an aftermarket transaction occurs. As
formalized below, the aftermarket should be designed in such a way that a positedequilibrium behavior in the original allocation mechanism, together with truthful revelationin the aftermarket, constitute a perfect Bayesian equilibrium of the mechanism-cumaftermarket game.
If the aftermarket had to be an allocation mechanism in its own right, this revelation
requirement would typically be impossible (Myerson and Satterthwaite [1983] provide an
impossibility theorem for perhaps the simplest case). However, the aftermarket is to be
appended to a lab or field experiment, not to determine an allocation but merely tonormatively categorize the allocation reached before the aftermarket is used. The
simplification thus obtained is characterized in section 4.
This bears emphasis: for the purpose of behavioral efficiency interpretation, an
aftermarket does not have to be an allocation mechanism.
That the aftermarket be approximately free of transactions costs, and that it be suitablytransparent, necessarily have less exacting interpretations; these are arenas where
employment of aftermarkets shifts from science, narrowly construed, in the direction of art.
7 I follow a century-old tradition in welfare economics that externalities to a transaction are either explicitly

modeled or ignored. Thus, if allocations A and B differ only in that in A, a cocktail dress remains in company
C’s inventory, while in B, Ginger buys the dress from company C at a mutually beneficial price, then allocation
B is considered Pareto-superior to A. This ignores the possibility that Ginger might later attend a party where
seeing the new dress makes Rosemary less happy with her wardrobe. In contrast, where a field study is focusedon externalities, the aftermarket must observe all possible disutilities resulting from recontracting, not just thetransactors’ evaluations.
8 I know of only two antecedent reports of experiments employing aftermarkets, Grether, Isaac and Plott[1979, 1989] and Rassenti, Smith and Bulfin [1982]. Both experiments are fine laboratory studies of airport
landing rights; in neither is the aftermarket designed to identify all possible remaining gains from trade, and inboth the induced values are utilized to analyze original and post-aftermarket efficiency.

4Negligibility of transactions costs is most usefully evaluated relative to the size of potential
mutual gains from further transacting. Indeed, transactions costs yield a calibration: anappropriate aftermarket identifies all mutually beneficial transactions for which the perceived
gains from trade exceed the perceived transactions costs.
When subjects have already been congregated, either physically or via simultaneousinteraction on the Internet, an aftermarket run fairly quickly and with simple, transparent
tasks for subjects is likely to sluff off transactions-costs concerns. When congregating isonly required for the aftermarket, it may be that an appropriate aftermarket designcompensates subjects for the costs of congregating, being careful to compensate in a manner
unrelated to observed aftermarket activity. 9
Experimental psychology and laboratory experimental economic literatures yield insights
into transparency that are extensive, although often anecdotal and always subjective. 10
3.1. Required Nature of Potential Aftermarket Transactions
A useful aftermarket needs to observe behavior with respect to any potential transactionthat may be mutually beneficial; this need will vary with the topics of field studies. When
allocation of identical units of a single private good is the concern (or when identical units ofmultiple goods are at stake, but issues of complementarities or income effects can reasonably
be assumed absent), observations of behavioral valuations of bilateral trades suffice. When
goods L and R are complements for some subjects, the possibility that subject 1 might value
an additional set {L, R} by an amount sufficient to compensate both subject 2 for forgoing
one unit of L and subject 3 for forgoing one unit of R must be observable by design.
Another important example arises when the original allocation mechanism determines aquantity of a public good to be produced, and an allocation of its production cost. Now anaftermarket merely observing potential bilateral transactions is insufficient; transactions
which alter public good output and attain some adjustment of cost shares in accordance withincreased or reduced public good production cost must be considered, as seen in section 5.
Some field studies will require the aftermarket be designed so as to observe valuations ofdynamically structured contracts. Allocations of common-pool resources are examples.
The usual characterization of efficiency via (P) above determines marginal conditions andassumes the appropriate convexities to imply that a local optimum is a global optimum. A
similar limitation may be needed in many cases to keep aftermarkets sufficiently simple andstraightforward. For example, consider examining in an aftermarket both an increase and adecrease in public good output, each by some more-than-differential amount that is incontext small. Concluding a behaviorally efficient outcome from an observed inability tofind any mutually beneficial increase or decrease by that given amount assumes theunobserved motivations were consistent with marginal valuations decreasing more rapidly
than marginal production cost. Should a behavioral inefficiency be found, the study would
9 It is important that an aftermarket be constructed so that a subject engages observable behaviors whatever

degree of satisfaction they have with the original allocation, so as to avoid “active participation hypothesis”
concerns (Lei, Noussair and Plott [2001]).
10 That price-clock-based ascending-price mechanisms are notably more transparent than sealed-bid
mechanisms seems a reasonable inference to draw from the laboratory experiments reported in Harstad [2000].
For this reason, such ascending-price mechanisms are used both in section 5’s demonstration and in thecompanion paper.

5

indicate in which direction public good output could be altered so as to obtain a perceived
mutual gain, but not how far such a movement could continue. In most contexts, theimaginable alternative of checking several possible increases in public-good output ofvarying sizes, and corresponding decreases, is likely to rob an aftermarket of a required lowtransaction-costs character. 11
4. Theoretical Issues Raised
Suppose the allocation mechanism being studied is sufficiently formal to permit analysis
as a game G. 12 Let G denote the game consisting of G followed by the aftermarket G+ thatis being constructed to test behavioral efficiency of G. Then the aftermarket must be
constructed so that E = {E, E+} is a perfect Bayesian equilibrium of G, where E is theequilibrium usually focal in literature considering G, and E+ constitutes truthful revelation in
G+. Otherwise, a behavioral efficiency (or inefficiency) conclusion is unwarranted.
Aftermarket construction can thus be viewed as a particular type of mechanism design
problem. While formal constraints of mechanism design are often limiting, the mechanism
design challenge posed here should always be attainable. An aftermarket constructor has
two critical dimensions of flexibility generally unavailable in mechanism design: the field
experiment [a] does not have to balance the budget, though hopefully limiting the size of any
deficit; [b] does not have to implement any transactions observed to be mutually beneficial
with probability one, but merely with positive probability. 13
As a simple illustration, suppose a field experiment has observed a failure to reach an
agreeable transaction in a bilateral bargaining situation. As motivations are unobserved, it isunknown whether a mutually beneficial bargain was possible. Myerson and Satterthwaite[1983] demonstrate that no mechanism can insure efficient outcomes when the potential
seller’s and potential buyer’s valuations are private information. However, at least three
distinct aftermarket constructions can observe whether the outcome was behaviorally
efficient. 14 Each asks the seller to state the lowest price that he is willing to accept, and thebuyer to state the highest price that she is willing to pay. 15 The experimenter has carefully
explained in advance to the subjects what use will be made of their responses. Aftermarket
version 1 will implement the transaction whenever B, her stated willingness-to-pay, exceeds
A, his stated willingness-to-accept, with the pre-announced rule that she will pay A, and he
11 Correspondingly, suppose an aftermarket appended to a mechanism allocating a given quantity of identicalunits of a private good were to observe that the potential buyer willing to pay the most for an additional unit
could not cover the lowest price at which some potential seller was willing to provide the additional unit.
Assuming that there was no mutually beneficial trade in which this buyer would acquire two units of the good(thus, assuming unobserved motivations included diminishing marginal utility) might be preferable to runningan aftermarket that priced 2-unit (and perhaps 3-unit) trades as well as 1-unit trades, and allowed for multiunit
trades to have multiple parties on the same side of the trade.
12 This supposition is not trivial: some of the cultural incentive schemes discussed in Ostrom [1998] may bedifficult to formalize as allocation mechanisms.
13 It may be worth noting that, where the implementation is financial, this implies a positive probability that thecommitments made are financially incurred. I see no opportunity for surveys about whether subjects wished toreallocate, or about hypothetical terms under which subjects wished to reallocate, to substitute for anaftermarket.
14 If the failure to reach a transaction occurred in a natural field experiment, the aftermarket would require atransition to a framed field experiment.
15 Depending on context and the background and culture of the subjects, this may well not be the language inwhich the experimental instructions state the request.

6

will receive B. Version 1 is incentive-compatible, implements any transaction observed to be
mutually beneficial, and requires the experimenter to cover the deficit B – A. Aftermarket
version 2 draws a random variable R from a distribution exogenous to all information
provided by this pair of subjects (perhaps uniform on [0.25 W, 1.75 W], where W is a
publicly available average price from a prior survey of similar transactions in the economy),
and transacts at random price R if B ≥ R ≥ A. Aftermarket version 2 is incentivecompatible, implements any transaction observed to be mutually beneficial with positive
probability, and balances the budget. Aftermarket version 3 also draws a random variable R
from an exogenous distribution, transacts if B ≥ R ≥ A, but she pays R and he receives 1.05
R, achieving incentive compatibility, implementing transactions observed to be mutually
beneficial with positive probability, but requiring the experimenter cover a deficit of 0.05 R
when transactions occur.
Note that mechanism design requirements can still impinge on experimental desiderata.
In particular, consider an aftermarket construction which attempted to alter aftermarket 1
above by only transacting when the deficit B – A did not exceed a maximum desired
experimenter cash infusion M. This construction would no longer suffice for incentive
compatibility: it is possible that the seller would attain the outcome of no transaction and no
gain if he truthfully stated A, as B – A might exceed M, while some overstatement X ≥ A
might yield a gain of B – X > 0 should B – X be less than M. Thus, instead of an incentive
to truthfully reveal his willingness-to-accept, the seller (and the buyer) would optimally trade
off a lower gain in the event of transaction against a higher probability of a gain by somedegree of overstatement. (Even if, instead of announcing M, the experimenter merely statedthat the transaction would occur “unless the deficit were too large,” the construction would
still be insufficient to warrant conclusions as to behavioral efficiency.)
5. A Small Field Demonstration
5.1. FIELD CONTEXT: To focus the demonstration on the aftermarket, the initial
allocation mechanism is submersed via an assumption that the outcome is production of one
unit of public good, with the costs of the first unit’s production covered from theexperimenter’s budget. The aftermarket then considers whether the cost of production of asecond unit can be allocated to the perceived mutual benefit of all members of the economy.
The aftermarket’s construction does not balance the budget, allowing the experimenter tocover a deficit if it is observed that the sum of marginal benefits exceeds production cost of
the second unit.
The public good studied is a uniform distribution of small packets of Haribo candy, aproduct in international distribution and prominent on the shelves of local grocery andconvenience stores. It is natural to think of candy as a private good, but in this experiment it
was allocated under strict adherence to the definition of a pure public good. That is, [a]there was group exclusion but no individual exclusion in consumption, and [b] there was norivalry in consumption. Either all subjects received one unit of candy apiece, or all subjects
received two units of candy apiece, depending on whether stated willingnesses-to-pay
summed to at least the production cost.
All groups studied consisted of six subjects. Eighteen subjects (in one session, twelve,
due to no-shows) were in the room during a session, so that no subject knew which others
were in the same group. Subjects were students recruited by website signup from several
campuses of the University of Montpellier. Show-up fees ranged from €3-8, depending on

7

the distance from their home campus to the Experimental Economics Lab at the Richter
campus.
Subjects were seated at visually isolated computers. Instructions were passed out andread aloud, questions encouraged and answered. 16 The initial unit of Haribo candy was given
to each subject; they were allowed to consume it immediately if they were uncertain of thequality of the candy or for any other reason. They were informed that a second unit would
be provided to every member of the group if the sum of the most each group member was
willing to pay was at least €1. 17 These were elicited, the second unit provided or not, andsubjects paid to the experimenter their cost share for the additional unit (which wasnecessarily less than the show-up fee).
5.2. METHODOLOGY IMPLEMENTATION: As mentioned, the allocation of 1 unit of public
good is treated as if it arose via some allocation mechanism, with the experiment observing
an aftermarket. A “clock” ticked up on subjects’ computer screens, increasing by 2 euro
cents, initially every 4 seconds, after 8 euro cents, increasing every 2 seconds. Subjects wereasked simply to watch the clock so long as the price was one which they were willing to pay
in order to have the group increase public good output from one unit to two, and then to
click on the “Accept” button on the screen as soon as the next tick of the clock would yielda price that they were not willing to pay in return for the increase to two units. 18
Before the clock was run, the outcome function was carefully explained to subjects. If
the sum of the six “Accept” prices was at least €1, each subject in the group would be given
a second unit of candy, and each subject would pay €1 minus the sum of the other five
Accept prices (or 0, whichever was larger).
This methodology implements the incremental version of the Vickrey-Clarke-Groves
mechanism. 19 If a subject is certain of the amount of euros which he would be willing to pay
to have the public good output increased from one to two, then it is a dominant strategy toclick on the Accept button at the multiple of 2 euro cents nearest his willingness-to-pay.
Harstad [2000] has found the price-clock mechanism to be far more transparent than directstatement of willingness-to-pay in eliciting dominant strategy responses.
The incentive compatibility of this methodology warrants the conclusion that the groupexhibits a behavioral inefficiency of the allocation—of one candy each—if the sum of
Accept prices exceeds €1.
5.3. OBSERVATIONS: Thirteen of twenty-three groups exhibited a perceived mutual gain
in increasing the distribution of candy from one unit to two units apiece. (This included sixof the eleven groups that chose well before lunchtime, and seven of the twelve groups thatchose shortly after 1:30 [or three after 3:30 pm], so there is no sign that chronobiology
played a role.) The size of behaviorally revealed efficiency gains in these groups ranged from
4% to 72% of production cost (€1), averaging 33%.
16 An English-language version of the instructions is available at http://harstad.missouri.edu/Instructs/.

17 Haribo candy was of course available for purchase outside the lab, and a subject’s transactions costs of doing

so were unknown. Hence, it was important to keep the per-capita threshold for public good production below
extra-laboratory prices, so that censoring stated valuations by extra-laboratory availability could not be an issue;
cf. Harrison, Harstad and Rutstrom [2004].
18 The experiment was conducted in the Z-Tree programming environment (Fischbacher [2007]).
19 Named for Vickrey [1961], Clarke [1971] and Groves [1973].

8

The other ten groups found one unit of public good to be behaviorally efficient relative
to the sole alternative of two units. The sums of Accept prices in these groups ranged from
56% to 98% of production cost, averaging 86%.
In none of the thirteen groups accomplishing the behavioral efficiency improvement
could public good production cost have been covered by a mutually acceptable uniform tax.
Rather, only through person-specific pricing could the public good increment be mutually
beneficial. Of course, acceptable person-specific price vectors (not uniquely determined inany of the thirteen groups) could not have been known by the experimenter, but wererevealed by behavior in the aftermarket (and the Vickrey-Clarke-Groves selection among
those vectors actually used for payment).
The highest stated willingness-to-pay was €0.54; eighteen of 138 subjects chose an Accept
price of €0.04 or less, another forty-five €0.16 or less.
Though there is evidence that it was transparent, it is of course not known whether
subjects adopted the dominant strategy of revealing their willingnesses-to-pay. Instructions
made it clear that subjects were to evaluate not a second unit of Haribo candy for their own
consumption, but a second unit of public good production. Nonetheless, it is unknown
whether any subject selfishly placed the same value on second units for all group members as
on a private purchase of a second unit. Nor is it known whether any subjects were behaving
altruistically, or the extent of any altruistic behavior. It is no more necessary to know theirmotivations than it would be necessary to know why a consumer purchased a shirt in orderto evaluate the allocative efficiency of a shirt market. This aspect justifies treating alaboratory setting as a simple field experiment.
Although the setting was simple almost to the point of contrivance, and the stakes
miniscule, this demonstration finds that, at least in the case of public good allocation, theconcept can be taken to the field. Whether an adjustment in public good output can beaccomplished—via a mutually beneficial decentralization of adjustment costs—can beinferred from observations solely of behavior, provided the aftermarket used to observe
those behaviors is appropriately designed. Larger scale, more important field studies canexactly mimic the demonstration offered here, and relate behavioral efficiency observations
to the methods used to determine levels of public good output.
5.4. LABORATORY OBSERVATION ON STRATEGIC TRANSPARENCY: Following thedemonstration, since the subjects were in an experimental laboratory, a simple induced-valuelaboratory phase was added. Subjects were given instructions about the allocation of an
abstract public good. The only value of this public good was monetary utility to eachindividual subject that had been specified by the experimenter. 20
To mimic the field demonstration, an ad hoc mechanism that was suppressed set initialpublic good output to 7 units, and each group was asked whether to increase output to 8
units, at an incremental production cost of €3. Each subject was privately told theincremental value vj to her or him of the increase from 7 to 8 units; the distribution of theseincremental values was not announced, although it was announced that the incremental
values were not all the same. These six values summed to less than the incremental cost (arandom decision, as was the 7-unit starting point); one randomly chosen subject had anincremental valuation equal to €0.7, one equal to €0.06, four equal to €0.42 (that four had
20 This assumes selfish preferences, a limitation the field experiment does not share.

9the same incremental value was not known to the subjects until results were reported).
Division of subjects into groups was via a new random draw, independent of the draw in thefield experiment; this feature was announced.
In all other respects, the induced-value procedure was identical to that of the fielddemonstration: a clock ticked up on all screens (by a multiple of €0.05), subjects were asked
to click “Accept” at the highest price they were willing to pay to increase public good output
from 7 to 8 units (their incremental value was shown on the screen as the price ticked up),and were told beforehand that an individual group member’s personal cost of this increase,which would happen if and only if the sum of Accept prices were at least the production
cost, would be the €3 production cost less the sum of the Accept prices of the other fivegroup members. It was carefully explained that their payoff for this decision would be zero
if the amount of public good were not changed, and would be their incremental value lessthe excess of production cost over the sum of the other five Accept prices if public good
output were increased. 21
As before, it is a dominant strategy to set one’s Accept price equal to the multiple of€0.05 closest to one’s incremental value. Only with incremental values induced (thus in thelab, not the field), is it possible to see whether subjects did this. Most did not exactly hit thisdominant strategy, although on average the statistic Z = (Accept price – incremental value)was €0.00103, remarkably close to the €0.015 average it would have been had every subject
exactly adopted the dominant strategy. 22 The standard error of Z was nonnegligible, €0.298;
the 23 subjects for whom vj = €0.06 had to click on Accept immediately (at €0.05) wereclicking later than this, and averaged Z = €0.38. This was compensated for by the 23
subjects for whom vj = €0.7, perhaps not waiting for the price clock to reach that high; they
averaged Z = –€0.32. Still, over 80% of 138 subjects were within €0.3 of Z = 0, nearly halfof those within €0.1. For all twenty-three groups, the six Accept prices summed to less thanthe €3 production cost, so for all groups, seven units of public good was behaviorally
efficient relative to the alternative of eight units. Evidence in the induced-value setting forinexperienced subjects to be unable to understand the incentives they faced in the fielddemonstration is unpersuasive, indeed quite limited.
6. Remarks on Some of the Empirical Issues That May Arise
If there is a limit to the empirical questions that arise with behavioral efficiency, I haven’t
grasped it. Here’s a sampling of those that are clear now.
Are Pareto-efficient allocations and behaviorally efficient outcomes necessarily
distinct? Under the assumptions of the theory, the second paper in this series takes
advantage of induced values to answer in the affirmative, finding a significant minority ofobservations that are either of these, but not the other. One side arises when the subject
with the highest privately observed estimate of asset value wins the auction (as would occur
in the symmetric, risk-neutral Bayesian equilibrium), thus attaining a Pareto efficient
allocation, but nonetheless a mutual gain in the aftermarket is observed. The inverse also
21 The sessions followed these observations with pilot experiments studying public-good allocation mechanismsthat did not bear on the issues of this paper.
22 Because the Accept bid had to be a multiple of €0.05, in each group the one subject with incremental
valuation €0.06 had a dominant strategy Z = 0.01, and the four subjects with incremental valuation €0.42 had adominant strategy Z = 0.02.

10

arises when the auction winner is not the subject with the highest private information, but
the aftermarket observes behavioral efficiency.
How large are the magnitudes of shortfalls from behavioral efficiency, and how
might these be assessed? In each circumstance where I have been able to envision theoutlines of an appropriate aftermarket design, any potential transaction perceived to be
mutually beneficial that is observed provides an absolute magnitude of the perceived gain.
To put this in percentage terms, as a shortfall from efficiency, requires being able to calculate
the Pareto set. In field studies, the best hope is to observe behaviors in the original
allocation that indicate the potential size of efficiency gains. The companion paper on
auctions provides a treatment where such a comparison has a solid theoretical basis, andanother with less foundation.
Does knowing that an aftermarket will follow an allocation mechanism affectsubjects’ behavior in the mechanism? A requirement for aftermarket design is that there
is in theory no effect. This will be a potentially important question in every field context, andI expect to have to assess it de novo, at least until a large database of field aftermarkets has
been compiled. It is possible to design demonstrations and adapt data analysis to shed somelight on this. It would be possible in most field settings to surprise subjects with anaftermarket that they almost surely did not anticipate; this will not always be best practice.
Will an aftermarket observe activity just because subjects assume they aresupposed to do something? This question arose, for good reason, in reports ofexperiments observing financial bubbles in labs (Smith, Suchanek and Williams [1988]). The
particular “active participation hypothesis” raised by Lei, Noussair and Plott [2001] (thatsubjects engage in irrational activity because the experimental setup limited rational behavior
to inactivity) need not be a concern here, however. In aftermarkets, the anticipated designs
will always have subjects do something, in essence engage in valuation activities. Even if theinitial allocation might have been Pareto efficient, there will be a financial incentive toengage in the valuation activities. It should always be possible to structure them so that azero valuation behavior has nothing to do with a preference for the status quo that wasreached in the original allocation mechanism.
Are aftermarket activities mistakes if the initial allocation reached should havebeen Pareto-efficient? In ordinary cases, it will be difficult if not impossible to label
particular aftermarket behaviors mistakes. Only when conducted in induced-values
demonstrations will it be possible to determine whether the original allocation reached prior
to the aftermarket was in fact Pareto efficient, and even then usually only under assumptions
that may well be unverifiable. For example, the Pareto efficiency characterization of theoriginal allocation may be obtainable only under assumptions such as equilibrium behavior,risk neutrality, symmetric behavior, common knowledge of distributions of private
information, selfish preferences, and others. In some situations, there may be serious
questions about whether the aftermarket design was sufficiently transparent for the subject
population, as for example when the subjects are illiterate. When transparency is adequate, I
regard it as likely that aftermarket behaviors should be taken at face value.
Might behavioral efficiency determination depend on the structure of theaftermarket used for observation and identification? This will ever be an empiricalpossibility. When field budgets and subject population sizes permit, multiple aftermarket
designs can be tested.

11

Might endowment effects lead to an inactive aftermarket even though the initial
allocation was efficient? This could be imagined, although it is hard to say thatinefficiencies exist, let alone identify and quantify them, when an appropriately constructed
aftermarket observes inactivity. Plott and Zeiler [2005], [2007] demonstrate that the size ofan endowment effect might almost be calibrable. Careful instructions (avoiding the term
“winning bidder”) in the companion paper on auction aftermarkets provide data strongly
suggesting that the endowment effect is not a problem in that particular context.
Might other studied psychological biases and behavioral anomalies affectaftermarket observations? To a first approximation, an “anomaly” such as other-regarding
preferences or hyperbolic discounting may equally impact both an original allocation
mechanism and its aftermarket. For many such concerns, there is no reason to believe thatthey suddenly arise in aftermarkets following an allocation mechanism that went untouchedby them. When there is evidence that some particular bias perceived to be relevant to aparticular field study can reliably be redressed via education, it may well be best practice toeducate first, then run the allocation mechanism followed by the aftermarket. There isconsiderable evidence suggesting persistence of some biases in the presence of education.
Since it is only behaviors that can be observed in field settings, observing aftermarket activity
in the presence of such biases may well be the most appropriate way to provide advice forpolicies that will be promulgated for the population being studied.
6. Concluding Remarks on the Meaning(s) of Behavioral Efficiency
It is a luxury of a parsimonious theory that economists who might disagree about the roleof Pareto efficiency—how important is, or perhaps even whether it is desirable—
nonetheless agree on the definition of the term and its meaning. I do not see how theterminology of empirical, behavioral studies can have the same luxury. Thus, even if thedefinition of behavioral efficiency offered here becomes widely accepted, it seems naïve tohope that its meaning will achieve any universal interpretation.
A perhaps less naïve hope is the following. Suppose, starkly, that policy Y is observed ina particular context (including a particular subject population and their characteristics) torobustly yield behaviorally efficient outcomes, while alternative policy Z in the same context
robustly yields outcomes with significantly large shortfalls from behavioral efficiency. Thenit might be widely agreed that, at whatever levels of sophistication underlie their perceptions
and whatever level of transparency the aftermarket offers, subjects perceive mutual gains
from trade that policy Z does not capture while perceiving no uncaptured mutual gains fromtrade following implementation of policy Y. Indeed, it might even be widely accepted that
advice to policymakers reporting and influenced by this finding could be an improvement
over advice reporting and influenced by field experiments that obtain no observations aboutallocative efficiency. Less starkly, when the observed size of shortfalls from behaviorally
efficient outcomes are in context robustly smaller for policy Y than for policy Z, this mightalso come to be accepted to play a role in policy advice despite divergent opinions as to its
exact meaning.

12References
Peter Bohm [1984], Revealing demand for an actual public good, Journal of Public Economics
24, 135-51.
Edward Clarke [1971], Multipart pricing of public goods, Public Choice, 11, 17-33.
Douglas D. Davis and Charles Holt [1993], Experimental Economics, Princeton University
Press.
Urs Fischbacher [2007], z-Tree: Zurich toolbox for ready-made economic experiments,
Experimental Economics 10, 171-78.
David M. Grether, R. Mark Isaac and Charles R. Plott [1979], Alternative methods ofallocating airport slots: performance and evaluation, Civil Aeronautics Board Report,
Pasadena, Calif.: Polynomics Research Laboratories, Inc.
David M. Grether, R. Mark Isaac and Charles R. Plott [1989], The Allocation of Scarce Resources:
Experimental Economics and the Problem of Allocating Airport Slots, Westview Press, Boulder.
Theodore Groves [1973], Incentives in teams, Econometrica 41, 617-31.
Glenn W. Harrison, Ronald M. Harstad and E. Elisabet Rutstrom [2004], Experimental
methods and elicitation of values, Experimental Economics 7, 124-40.
Glenn W. Harrison and John A. List [2004], Field experiments, Journal of Economic Literature
42, 1009-55.
Ronald M. Harstad [2000], Dominant strategy adoption and bidders’ experience with pricing
rules, Experimental Economics, 3 (2000), 261-80.
John H. Kagel and Alvin E. Roth, eds. [1995], The Handbook of Experimental Economics,
Princeton University Press.
Vivian Lei, Charles N. Noussair, and Charles R. Plott [2001], Nonspeculative bubbles inexperimental asset markets: lack of common knowledge of rationality vs. actual
irrationality, Econometrica 69, 831-59.
Roger Myerson and Mark Satterthwaite [1983], Efficient mechanisms for bilateral trading,
Journal of Economic Theory 29, 265-81.
Charles R. Plott and Kathryn Zeiler [2005], The willingness to pay-willingness to accept gap,
the “endowment” effect," subject misconceptions, and experimental procedures for
eliciting valuations, American Economic Review 95, 530-.
Charles R. Plott and Kathryn Zeiler [2007], Asymmetries in exchange behavior incorrectlyinterpreted as evidence of endowment effect theory and prospect theory? American
Economic Review 97, 1449-.
Stephen J. Rassenti, Vernon L. Smith and Robert Bulfin [1982], A combinatorial auction
mechanism for airport time slot allocation, Bell Journal of Economics 13, 402-.
Vernon Smith [1962], An experimental study of competitive market behavior, Journal of
Political Economy, v. 52.
Vernon Smith [1976], Experimental economics: induced value theory, American Economic
Review, v. 66.

13

Vernon Smith, Gerry Suchanek and Arlington Williams [1988], Bubbles, crashes andendogenous expectations in experimental spot asset markets, Econometrica, v. 58.
William S. Vickrey [1961], Counterspeculation, auctions and competitive sealed tenders,
Journal of Finance, 16, 8–37.
Charles Z. Zheng [2002], Optimal auction with resale, Econometrica 70, 2197-2224.

14