productivity under group incentives: an experimental study

Productivity Under Group Incentives: An Experimental Study

By HAIG R. NALBANTIAN AND ANDREW SCHOTTER*

This paper pre.sents an experimental examination of a variety of group incentiveprograms. We investigate simple revenue sharing and more sophisticated, target-based systems such as profit sharing or productivity gainsharing, as well astournament-based and monitoring schemes. Our results can be characterized bythree facts: (1) history matters; how a group performs in one incentive schemedepends on its history together under the scheme that preceded it; (2) relativeperformance schemes outperform target-based schemes; and (3) monitoring canelicit high effort from workers, but the probability of monitoring must be highand. therefore, costly. iJELJ33, C92)

Despite its recent resurgence, the productiv-ity of American workers remains an issue ofcentral concern of business and public policy.Traditionally, the efforts to strengthen Amer-ican competitiveness have stressed technolog-ical advance and investment in physical andhuman capital. More recently, however, atten-tion has been turning to the behavioral dimen-sions of labor productivity, the variations inthe quantity and quality of labor inputs thatstem from the complex of financial and non-financial inducements that constitute an orga-nization's reward system. It is increasinglyrecognized in industry that by introducingcarefully crafted group incentive compensa-tion systems, it may be possible to induceAmerican workers to work both harder andsmarter and to use even existing technologiesin new and better ways that enhance their pro-ductivity. In the short run at least, and perhapseven longer term, this may be the most effec-tive instrument for raising productivity, yet in-sufficient attention has been paid to thispossibility in the economics literature.

* Nalbantian; William M. Mercer, Incorporated. 1166Avenue of the Americas, New York. NY 10036; Schotter:Department of Economics, New York University, 269Mercer Street, New York, NY 10003. The authors wouldlike to thank the C, V. Starr Center for Applied Economicsfor its financial and technical assistance in writing thispaper. We also would like to thank Ken Rogoza for hisheip, as well as Blaine Snyder, Sunando Sen, and TaoWang, who took a key role in helping us process the data.Finally, Ihc comments of three anonymous referees aregreatfully acknowledged.

The paucity of empirical research in thisarea is quite surprising given the substantialtheoretical advances that have been made inthe analysis of labor contracting. The work incontract theory has shed considerable light onthe nature of optimal contracts under alterna-tive assumptions about the level and distribu-tion of information amongst contractingparties and differences in their respective at-titudes towards risk. But until very recently,there has been little empirical testing of thepertinent theoretical results in relation to groupincentives. What has emerged in the last sev-eral years are a number of rigorous econo-metric studies of the relationship betweenprofit sharing (and/or employee stock own-ership plans) and labor productivity. (For anexcellent and thorough review of this econo-metric literature, see Martin L. Weitzman andDouglas L. Kruse, 1990; also, U.S. Depart-ment of Labor, 1993.) But to our knowledgethere has been no direct investigation of therelative performance of alternative types ofgroup incentive systems, something which isof considerable academic and practical interestgiven the huge variety of group incentive sys-tems actually employed by firms. As a result,there is little empirical basis for discriminatingamongst the various group incentive pro-grams, especially as concerns the structure ofthe sharing rules or payoff formulae that dis-tinguish them.

Perhaps the reason for this lack of attentionhas to do with the difficulty of using naturallyoccurring data to answer these questions. Nat-ural data on employee compensation and pro-

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VOL. 87 NO. 3 NALBANTIAN AND SCHOTTER: PRODUCnVITY AND GROUP INCENTIVES 315

ductivity are difficult to obtain and generallyquite suspect in terms of quality. Moreover,the data required to undertake satisfactory em-pirical tests of the underlying theory includepreference and production function parametersthat are not directly observable. Beyond thesefactors there are the inherent limitations of sta-tistical techniques with respect to endogeneityand "control" problems, limitations that areespecially severe when comparisons are to bemade of systems operating in diverse andhighly idiosyncratic environments. These lim-itations are compounded in our case, as we aretesting several mechanisms that are theoreti-cally inspired and which exist, at best, infre-quently (if at all) in actual practice. Theexperimental approach, on the other hand,readily allows for a systematic analysis of cet-eris paribus changes in discrete aspects ofgiven institutions, in our case, the different re-ward fonnulae. By so isolating the effects ofthese changes, we are better able to assess ifthe incentive properties identified in theorymaterialize in the actual behaviors of individ-uals operating in the stylized markets createdin the lab.

In this paper we take a first, experimentalstep in rectifying this omission. We report ona set of nine experiments run using 408' paidhuman volunteers, the purpose of which wasto investigate the problem of group moral haz-ard and the performance characteristics of sev-eral different classes of group incentiveschemes now in use or deduced from eco-nomic theory. Unlike previous studies, wefocus directly on the reward formulae them-selves, trying to illuminate the behavioral andoperational mechanics of the incentive struc-tures they define. The specific schemes we in-vestigate range from simple revenue sharing(egalitarian partnerships) to more sophisti-cated, target-based systems such as profit shar-ing and so-called productivity gainsharing.^These are prototypical real-world incarnationsof what economists call "forcing contracts."

We also examined the properties of team-based tournaments, denoted here as "compet-itive teams." in which intrafirm competition,for example, between profit centers, is createdso that relative performance becomes the basisof incentive awards. The performance of allthese group incentive systems then is com-pared to that of individual incentive systemscharacterized by probabilistic monitoring andefficiency wages.

The conclusions of our study are straight-forward and can be summarized by four sim-ple observations.

Observation 1; Shirking happens.—Whenexperimental subjects are placed under an in-centive plan which provides strong incentivesto shirk, their effort levels do approach theshirking equilibrium as they near the end ofthe experiment.

Observation 2: History matters.—The per-formance of an experimental group using anyparticular group incentive formula depends onthe effort norm established by this group in itsprevious experience with other incentiveschemes. In addition, when a past commongroup experience is extremely positive (i.e.,exhibits high levels of group output), currentoutput levels tend to be high as well.

Observation 3 ; A little competition goes along, long way.—Tournament-based groupincentive mechanisms that create competitionbetween subgroups in the organization for afixed set of prizes (i.e., which create internaltournaments) determine higher mean outputsthan all target-based mechanisms examinedand smaller variances in those outputs thanmany of them.

Observation 4: Monitoring works but iscostly.—When monitoring is possible but notperfect, high levels of effort can be elicited

' We actually ran 13 experiments using 588 subjects,but a number of experiments were run to answer questionswhich subsequently were edited out of the paper.

" Productivity gainsharing is a form of group incentivesin which employees share (usually 50-75 percent) in im-provements over past performance. The programs typi-

cally are applied to production units and use measures ofopeming performance rather than broader financial measuresas the basis of awards. Unlike profit sharing where targets aresimply stipulated by management, under productivity gain-sharing the historical performance of the group in someagreed upon base period becomes the benchmaik againstwhich current performance is measured.

316 THE AMERICAN ECONOMIC REVIEW JUNE 1997

from workers. However, unless the probabilityof detection is great (and, therefore, costly tomaintain), such monitoring schemes are likelyto fail.

In this paper we proceed as follows. In Sec-tion I we motivate our work by presenting aquick overview of the industrial use of groupincentive or variable pay schemes in theUnited States and the empirical research esti-mating their effectiveness. In Section II wemake our discussion more precise by present-ing the theory behind the exact group incentivemechanisms we are considering. Section IIIreviews our experimental design, while Sec-tion IV presents our results substantiating thefour observations listed above. Section V of-fers some conclusions. Finally, an Appendixcontaining the instructions for our profit-sharing experiment is presented.

I. Industrial Practice and PreviousEmpirical Research

The use of group incentive or variable payschemes has grown rapidly in the UnitedStates over the past 50 years. While in 1945there were only 2,113 qualified deferred andcombination-cash profit-sharing plans operat-ing in the United States, by 1991 this figurehad risen to 490,000, with over one-quarter ofthem including immediate cash payments.Carla O'Dell and Jerry L. McAdams (1987)found that 13 percent of firms responding totheir survey has some form of gainsharing inplace. With respect to employee stock own-ership programs (ESOPs), Joseph R. Blasiand Douglas L. Kruse (1991) project that bythe year 2000 more than one-quarter of pub-licly traded firms on the New York, American,and over-the-counter Stock Exchanges will bemore than 15 percent owned by theiremployees.

The bulk of empirical research on group in-centives is represented either by field studiesdetailing company experiences with specificgroup incentive plans (for example, see Na-tional Commission on Productivity and WorkQuality, 1975; Mitchell Fein, 1982; Brian E.Graham-Moore and Timothy L. Ross, 1983)or by simple correlational studies examiningthe relationship between the adoption of groupincentive plans and various measures of firmperformance and/or labor productivity (see

Bion B. Howard and Peter O. Dietz, 1969;Betram L. Metzger and Jerome A. Colletti,1971; Metzger, 1975). In addition, a numberof industrial surveys have been conducted thatcompare and evaluate the effectiveness ofbroad classes of group incentive plans (U.S.General Accounting Office, 1981; New YorkStock Exchange Office of Economic Research,1982; McAdams and Elizabeth J. Hawk,1994). Overwhelmingly, the assessments ofgroup incentives offered in these studies arepositive, though the variance of productivityeffects is considerable.

Some of the more recent studies have uti-lized more sophisticated statistical techniquesapplied to time-series and cross-sectional data(for example, see Felix FitzRoy and KomeliusKraft, 1986, 1987; John A. Wagner III et al.,1988; John Cable and Nicholas Wilson, 1989;Kruse, 1992). These studies show strong pos-itive effects of group incentives on variousproductivity and financial performance vari-ables even, in some cases, after addressing theproblems of endogeneity. Group incentivesalso have been considered in several recentempirical studies of the effects on productivityof alternative human resource "systems" (forexample, see Mark Huselid, 1995; CaseyIchniowski and Kathryn Shaw, 1995;Ichniowski et al., 1996). These studies showthat the more participatory work systems em-phasizing decentralized decision-making, ex-tensive information sharing, flexible jobassignments, and some form of profit sharing,among other things, tend to outperform tradi-tional hierarchial system designs. Of course,there are exceptions to these findings (Jone L.Pearce et al., 1985; Andrew Weiss, 1987;Michael Conte and Jan Svejnar, 1989), andmuch of the empirical literature cited is sus-pect due to methodological weaknesses, mostnotably, the frequent failure to control forother potential explanatory variables and forfeedback relationships. Nonetheless, it is clearthat the preponderance of evidence supportsthe claim that group incentives can, and oftendo, contribute to significant increases in laborproductivity and firm performance.'

' Detailed reviews and evaluations of the empirical ev-idence can be found in Nalbantian (1987) and Alan S.Blinder (1990).

VOL 87 NO. 3 NALBANTIAN AND SCHOTTER: PRODUCTIVfTY AND GROUP INCENTIVES 317

To our knowledge, except for the work ofSchotter and Keith Weigelt (1992a) on long-and short-term corporate bonuses, and CliveBull et al. (1987) and Schotter and Weigelt(1992b) on symmetric and asymmetric tour-naments, there has not been any experimentalwork in economics on the group incentiveproblem as posed herein. However, the prob-lem posed here shares many common charac-teristics with the public goods problem, and tothat extent a rich body of pertinent experimen-tal work does exist. We will comment on thelinks between this work and ours in Section IIbelow.

II. A Simple Model of the GroupIncentive Problem

To economize on space, we will present a setof models which underlie our experiments, usingthe exact experimental parameterization andfunctional forms. This will allow us to avoid pre-senting the theory twice—once in its general,and once in its specific, experimental form. Con-sider a firm composed of six workers indexed /= 1, 2, ... ,6. Each member of the firm canchoose an effort level e, from the closed interval[0, 100]. Effort is costly, with the cost definedby C(e,) = e;/100. The effort levels of thefirm's workers produce output using a simplestochastic linear technology specified as:

(1)

where Y is firm output, e^ is the effort of theith worker, and a is a random variable defineduniformly over the integers in the closed in-terval [ —40, -1-40]. Assume next that this firmsells its output on a competitive market for aprice of 1.5. As a result, the firm's revenue is

(2) R= l.5Y= 1.5

Given this specification, the Pare to-optimal ef-fort level for each worker can be defined bysolving the following simple maximizationproblem:

(3) maxTT = -f e -

Given R is linear in each e, and eachis strictly convex, the first-order conditionsdefine a unique profit-maximizing effortlevel as:

(4) c)7r,/ae, - 1.5 - 2e,/100 = 0,

i = 1,2, ... , 6 , or e, = 75.

The problem for principal-agent theory is howto design an incentive scheme or mechanismwhich will implement these Pareto-optimal ef-fort levels as Nash equilibria.

In the remainder of this section we will re-view a set of different incentive mechanismswhich can either be derived from principal-agent theory or actually observed in industrialpractice. Some of these mechanisms imple-ment Pareto-optimal effort levels as Nashequilibria while others do not. In general,we lump all incentive schemes into four cate-gories: partnership schemes, target-basedschemes, tournament-based schemes, and in-dividualistic monitoring schemes. We will re-view these types of mechanisms each in tumsince they are the mechanisms we eventuallytest experimentally.

A. Partnership Schemes: Revenue Sharing

Egalitarian partnership schemes, compara-ble to the voluntary contribution mechanismsof public goods theory, represent the archetyp-ical incentive mechanism for which free-ridingis a dominant strategy (see Section II,subsection E, for a comparison of public goodsand group incentive experiments). As such,they suffer from the same disincentive effects.We illustrate such schemes using a revenue-sharing mechanism in which the payoff to theith worker is defined as follows:

(5) = 1.5 e\/6-e:/lOO.

As we can see, in this scheme all revenue gen-erated by the firm is shared equally and aworker's final payoff is simply his revenueshare minus his cost of effort.

To determine the Nash equilibrium effortlevels defined by the game associated with thismechanism, we take the partial derivative of

SIB THE AMERICAN ECONOMIC REVIEW JUNE 1997

each worker's payoff function with respect tohis or her own effort level e, and set it equalto zero. This yields:

(6) dTT./de, = 1,5/6 - 2e,/100 = 0

or e, = 12,5.

Note that since the marginal benefit from ex-erting a unit's worth of effort is 1.5/6 and isindependent of the effort level, choosing 12,5is a dominant strategy under egalitarian reve-nue sharing. Hence, this scheme defines a typ-ical free-riding prisoner's dilemma situation inwhich there is a dominant strategy yieldingPare to-inferior outcomes for all,

B. Target Based SchemesForcing Contracts

Bengt R, Holmstrom (1982) has made anumber of suggestions about finding solu-tions to the shirking dilemma presented byrevenue sharing. Among his suggestions isthe forcing contract mechanism. Such amechanism is the generic form representativeof a class of target-based mechanisms inwhich revenue or other outcome targets areset exogenously for the firm or a performancegroup within the firm. If the target revenue isachieved,, the workers share in all of the rev-enue generated, while if the firm's revenuefalls short of the target, each worker is paid arelatively low penalty wage.

More formally, the payoff to workers underthis kind of forcing contract is defined asfollows:

( 7 ) TT, =

1,5 / 6 -

if

B otherwise.

Such forcing contracts have many Nash equi-libria, each characterized by a different Y* -B pair. To find these Nash equilibria, let P{ei,Sy., e-i) denote the probability that a groupmeets its target of Y* given an effort level ofe, by agent i and Ij^^ e., by the other agentsexcluding i. Note that for a fixed e, and Sy*y

e_i, the expected value of the firm's output,conditional on meeting the target, is

(8) E{Y\Y> Y*)

+ +40

where the constant 40 represents half of thesupport of the random variable E.

Consequently, each worker faces a payofffunction of

(9)j*i j*i

X B

100'

For a Nash equilibrium the following first-order condition must hold for each /:

(10)

e,

( • = 1 , 2 , , , , , 6 .

This condition sets up a relationship, given allof the other parameters, between Y* and Bsuch that in order to implement Y* = 450(e* = 75) as a Nash equilibrium, we must setB < 1.125.

VOL 87 NO. 3 NALBANTIAN AND SCHOTFER: PRODUCTIVITY AND GROUP INCENTIVES 319

Profit Sharing

It should be obvious to the reader that whatwe happen to call a profit-sharing scheme isnothing tnore than a forcing contract schemewith a lower target and a penalty wage of zero.Our original intention was to devise a profit-sharing scheme characterized by a base wageand target consistent with the shirking equilib-rium of the revenue-sharing experiment. Inshort, our aim was to set a target Y* = 75(R* = 112.5) and a base wage of 112.5/6 =18.75. This would guarantee subjects a wageequal to tlieir expected equilibrium payout of therevenue-sharing scheme and then aJlow them toshare revenue as it increased above the target of112.5. If output actually rose above this level,the increase could be attributable to the profit-sharing aspect of the scheme. Unforiunately, byguaranteeing subjects a wage of 18.75 and set-ting the tiirget at y* = 75, we also guaranteeda dominant strategy for subjects to shirk and ex-eri zero effort. Hence, we could not create a pro-totypical profit-sharing scheme enforcing therevenue-sharing Nash equilibrium without si-multaneotisly altering some other institutionalvariable as well (e.g., introducing an indi-vidualistic incentive component like monitor-ing). To maintain the condition of allowingdiscrete, ceteris paribus changes only, we insteaddevised what we consider to be a second-bestexperiment which kept the target at the revenue-sharing ec|uilibrium Y* = 75 (e* = 12.5) butlowered tlie penalty wage B to zero (B = 0).With these parameters, the Nash equilibrium in-volves each subject choosing 19.1. For these rea-sons we call this experiment a profit-sharingexperiment—yet that designation is arbitrary.

Gainsharing

A gainsharing scheme is a target-based,profit-sharing scheme in which the target isgenerated endogenously by the previous out-put of workers. Hence, gainsharing is a forc-ing contract with a target based on historicalor "base period" performance. In our ex-periments we always perform gainsharingafter an initial 25-round revenue-sharing ex-periment, taking the average output of thelast ten rounds of the revenue-sharing ex-periment as the target for the gainsharing ex-periment. (Subjects were not told that their

performance in the first revenue-sharing ex-periment would in any way influence theirpayoffs in the second experiment they wouldperform. In fact, they knew no details at allof the second gainsharing experiment theywere to perform until the revenue-sharingexperiment that preceded it was completed,,though they knew that a second experimentwould occur.) Note that since we do notknow, a priori, the output of our subjects intheir revenue-sharing experiment, we couldmake no predictions about the output forthese gainsharing experiments, or whetherthey even had equilibria.

C. Tournament-Based Schemes:Competitive Teams

In contrast to target-based schemes, tourna-ments make the payoffs of agents or groups ofagents contingent upon relative, rather than ab-solute, performance. In our experiments we testa tournament-like mechanism which we callcompetitive teams, which involves dividing thefirm into two (or more) teams and having theseteams compete for prizes. The team producingthe most output gets the big prize, while the losergets the small prize. As a result, our competitiveteams scheme relies on competition to motivatethe workers functioning under it.

To be more precise, let the firm be dividedinto two teams, T^ and T^, and let/?, = \.5(Y\)and ^2 = 1-5(1̂ 2) be the revenues and outputsgenerated by these teams. Under a competitiveteam mechanism, the payoff for any worker /on Team I is defined as:

(11)

+ TR e]

6 100

- 77? e}

100

if Kl >

if Y,<

where 77? is a transfer made from the win-ning team to the losing team. A similar pay-off function can be defined for workers onTeam 2.

Note that as formulated above and as im-plemented in the lab, the competitive teamscheme is played as a noncooperative gamewith each worker choosing its effort level in


isolation and without knowledge of the choicemade by its team members. In the experimentsonly the teams' revenues, and not any individ-ual member's effort, were announced to thesubjects after each round of the experiment.Also, note that we specified the mechanism asdefining a transfer made from the winningteam to the losing team. Clearly, we easilycould have specified the winning team as re-ceiving a bonus paid by the firm and not as anintrafirm transfer from one branch to another.Economically, but perhaps not psychologi-cally, they are equivalent.

Let £1 = 2, e r, e, for all workers on Team1 and £2 = S, E 7; ei for all workers on Team2.

To demonstrate that the competitive teammechanism is capahle of implementing Pareto-optimal outcomes as Nash equilibria, assumethat ail members of each team choose an effortlevel of 75. Given these choices, the expectedrevenue for each team is 675 and the proba-bility of each team winning the transfer is '/2.Now consider one worker, say on Team 1,who contemplates a change in his or her effortby a marginal amount. Increasing effort mar-ginally increases the probability of winning bydPrlde,. The benefit of winning is (2 X TR)I6 -f (dRldei)l6, i.e., the difference betweenwinning the transfer and losing it, TTR, andone's share in the marginal revenue generatedfor the team {dRIdet )/6. The marginal cost ofchanging one's effort is 2e,/100. Hence, inorder for each worker not to want to deviatefrom the Nash equihbrium we must have

TR)/6]

{dRlde,)l6 =

Given our experimental parameters (e G[-40, +40], p = 1.5, andC(e,) - e^/lOO),if 77? is set equal to 360, a Nash equilibriumexists in which all subjects choose 75.

D. Individualistic Schemes: Monitoring

Our final incentive scheme is not a groupincentive scheme at all, but an individ-ual wage-cum-supervision mechanism {seeGuillermo A. Calvo and Stanislaw H. Wellisz,1978; Calvo, 1987). Under this mechanismour firm offers its workers a wage W greater

than their opportunity wage w if they put outan effort of e * when on the job. The firm willcheck the effort level of the worker with aprobability of p each period; if the worker iscaught working at an effort level lower thane*, he or she will be fired. Again, effort isassumed to be costly for the worker as definedby the cost function C(eJ = e?/100. In short,the worker is offered an efficiency wage if heor she will put out an effort level of e*.

With correctly set parameters, this schemewill determine Pareto-optimal effort levels onthe part of the workers. Obviously, a workerwill shirk depending on whether the expectedpayoff from shirking is greater than that ofworking. Realizing that the optimal shirk sets,̂ = 0, while the optimal nonshirking effort

level sets e, = e*, we see that shirking willoccur if

(12) £7r,(e, = 0 )

= p X (w) + (1 - p) X Ws: IV

= £7r̂ {e, = e*)

or {W -w)^ [ ( eh /100] X - .P

Setting/? = 0.70, W= 112.5, w = 18.75, ande* = 75, we see that the worker would preferto work rather than shirk. When p = 0.30, theopposite conclusion arises. There is a directrelation between the intensity of supervisionand the size of the efficiency wage required todeter shirking.

To summarize, we present Table 1, whichalso furnishes us predictions for the experi-ments to be reported on in Section IV. Notethat for all schemes, the Pareto-optimal effortlevel is 75 for each worker, which yields anindividual payoff of 56.25, a group output of450, a group revenue of 675, and a group profit(group revenues minus group effort costs) of337.5.

E. Relationship to the PublicGoods Literature

There is an obvious analogy between publicgoods experiments and our group incentiveexperiments; in the latter, group output is, in

VOL. 87 NO. 3 NALBANTIAN AND SCHOTTER: PRODUCTIVTTY AND GROUP INCENTIVES 32!

TABLE 1—THEORETIC AI- PREDICTIONS*

Experiment Effort PayoffGroup output

(revenue)Profit ( revenue-group effort cost)

1, Revenue sharing 12,5 17.18

2, Forcing contract (75) 75 3.5

3, Forcing contract (40) 40 19,41

4, Profit sharing 19,1 25

P = 112.5

5, Gainsharing ** **B = 0Y* = ?

6, Competitive teams 75 56,2Transfer = 360

7, Monitoring 75 56.25p = 0,70W= 112.5w = 18,75

8, Monitoring 0 84,32p = 0,30W= 112.5w = 18,75

75(112.5)

450(675)

240(360)

114,6(171.9)

103.1

337.5

264

150.01

450(675)

450(675)

0(0)

337.5

337,5

-506.25

*Note thai for all mechanisms there are six subjects facing a cost of effort function ofthe form c(,e,) = (f,)VlOO. Production is of the form x = "Le, -¥ E. E will be distributeduniformly over the interval [-40, +40], and ati subjects will choose their effort from theclosed interval [0, 100]. Finally, when subjects divide team revenue they do so equally sothat each worker gets a share of l/6th.

**Since we do not know what Y* will be in the gainsharing experiment until we have thehistorical data from which to calculate it, we cannot know in advance what the Nashequilibrium of the gainsharing experiment is. This fact is indicated by the asterisks in thetable.

fact, a kind of public good which is nonex-cludable and shared equally by the workers.Despite this similarity, some differences doexist, since the environment defining somegroup incentive experiments is different fromthose typically seen in public goods experi-ments, as are some of the mechanisms orschemes we investigate. Let us review thesedifferences each in turn.

With respect to environments, while groupoutput is a public good, it is exhaustible andsubject to crowding, since as n grows any fixedamount of group output gets shared by moreand more people. Further, our group output isstochastic in the sense that for any level ofgroup effort the eventual output (and, there-

fore, the probability of surpassing a target) isstochastically determined by the addition ofthe random shock e. Both of these elementsare missing in most public goods experiments,yet could easily be incorporated. Finally, whilemost public goods environments specify a de-mand function for the public good for eachsubject (or at least a marginal willingness topay function) with a constant marginal cost,in our experiments subjects face a convex andincreasing cost function with a constant mar-ginal revenue of 1,5 for the group output.

With respect to mechanisms, although someof the group incentive mechanisms we inves-tigate have natural interpretations as publicgoods mechanisms, others could not easily be


used in public goods contexts. For example,while revenue sharing can be interpreted as astraightforward voluntary contribution mech-anism similar to that of R. Mark Isaac andJames M. Walker (1988), and forcing contractmechanisms can be considered simple thresh-old mechanisms similar to those of GeraldMarwell and Ruth E. Ames (1980) andThomas Palfrey and Howard Rosenthal( 1991 ), mechanisms such as competitiveteams and gainsharing have no easy analoguein public goods theory. More precisely, thetechnology of public goods construction doesnot readily permit communities to be split intwo and compete in their contributions to apublic good. The same is true of gainsharing,which is an inherently dynamic mechanismwith thresholds or provision points set endog-enously. Finally, while public goods thresholdmechanisms are capable of offering money-back guarantees (see Vemon L. Smith, 1977;Robyn M. Dawes et al., 1986; Jeffrey S. Bankset al., 1988), such that if the public good isnot built, all citizens get their money back andnothing is lost; in group incenfive problemssuch guarantees are not natural since effort isexpended and lost forever, whether or not thetarget is reached.

In summary, while group incentive experi-ments share many of the properties of publicgoods experiments, there are more thanenough differences to call for them to be stud-ied in their own right.

ni . The Experiments and Experimental Design

A. The Experiment

To investigate our various group incentiveformulae, we ran a set of nine different exper-iments using 408 college undergraduates re-cruited in groups of 12 from undergraduateeconomics courses at New York University.Students were requested to come to an exper-imental computer laboratory at the C.V. Stan-Center for Apphed Economics.^ They werepaid $3.00 for showing up and engaged in anexperiment lasting about I hour and 20minutes. Their average final payoffs for this

•* The instructions for the experiments are contained inthe Appendix of the paper.

amount of time was about $14.00-$15.00,which seemed more than sufficient to motivatethem. Because of the convex cost function, themarginal incentives to work or shirk are notlinear and depend on effort levels. Further-more, since different mechanisms implementdifferent group output levels as equilibria, themarginal incentives vary across these equilib-ria as well. However, we know from the def-inition of Pareto-optimality that any of ourmechanisms which implement Pareto-optimalNash equilibria provide identical marginal in-centives for our subjects at those equilibria.For the revenue-sharing equilibrium, it is adominant strategy to choose 12.5 since themarginal private revenue generated from ex-erting one more unit of effort is 1.5/6 =0.25 everywhere while, with increasing con-vex costs, the marginal cost of doing so is lessthan 0.25 for all e^ < 12.5 and greater than0.25 for all e, ^ 12.5 no matter what groupoutput is.

The experiments engaged in were a directimplementation of the incentive plans de-scribed in Section II. For instance, in allexperiments (except the monitoring experi-ments) the 12 subjects recruited were ran-domly divided into two different groups of sixsubjects who remained anonymously groupedduring the entire experiment. After reading theexperiment's instructions (and having themread aloud by an experimental administrator,who answered any questions), subjects wereasked to type a number between 0 and 1(K) intotheir computer terminals. Such a number canbe interpreted as their unobservable effort lev-els, although in the instructions only neutrallanguage was used. After these numbers wereentered by each subject, the program guidingthe experiment added up all of these numbersfor each group separately and drew a randomnumber uniformly distributed between -40and +40 independently for each group. Therandom numbers for each group were addedto the sum of their effort levels. In the instruc-tions subjects were told that the higher the de-cision number they chose the higher their costswould be, and they were given a cost tableillustrating the cost of each integer between 0and 1(K). (This table was an integer represen-tation of the cost function e^ / 1(X)).

The payoffs for each experiment then weredetermined according to the incentive plan be-

VOL 87 NO. 3 NALBANTIAN AND SCHOTTER: PRODUCTIVTTY AND GROUP INCENTIVES 323

ing used as discussed in Section II. After eachround, subjects could see only their own effortlevels and the output levels of their own group.(In the competitive team experiment, eachteam also could see the output of its opposingteam after each round.) No information aboutthe individual effort levels of other subjectsever was revealed.

When round 1 of the experiment was over,round 2 started and was identical to round 1.Each experiment lasted for 25 rounds, whichwe felt was a sufficient length of time to fos-ter learning if any was to occur. After thefirst 25 rounds were over, new instructionswere handed out for a second experiment.(Subjects were not told about the details ofthe second experiment before they engagedin the first, but were informed that some sec-ond experiment would occur. This was doneso that no interexperiment strategies couldbe engaged in while informing subjects thatthey would be held in the laboratory for an-other experiment.) In the second experiment,all subjects stayed with their same group.The payoffs at the end of the experimentwere simply the sum of the payoffs of thesubjects over the 50 rounds of their experi-ence. Payoffs in each round were made interms of points, which were converted intodollars at a rate that was known in advanceby all subjects.

B. Experimental Design—Phase I andPhase II

Since our original intent in running theseexperiments was to investigate the incrementalimpact of group incentive formulae on poorlyfunctioning work units. Phase I of our exper-imental design involved running each groupfirst in a revenue-sharing experiment with theexpectation that we would observe the low ef-fort equilibrium in which each subject chosean effort of 12.5. Using this as a baseline anda basis for comparison, we then had eachgroup perform a second experiment where oneof our four other group incentive plans (profitsharing, gainsharing, forcing contracts, andcompetitive teams) was used. Hence, in Phase1 we ran a set of experiments, all of whichstarted with 25 rounds of revenue sharing fol-lowed by 25 rounds of some other group in-centive experiment. Because we also were

interested in observing how history affectedgroup performance, in Phase II of our experi-ment we reversed the process and ran othergroups of subjects for 25 rounds of some non-revenue-sharing experiment first, followed by25 rounds of a revenue-sharing experiment.For monitoring experiments in Phase I we ran25 rounds of a monitoring experiment with adetection probability of 0.70, followed by 25rounds of the same experiment, but with amonitoring probability of 0.30. In Phase-II ex-periments the order of these experiments wasreversed. Our design is presented in Table 2below.

Note that in our experimental design all costand production parameters are held constantso that in moving from one experiment to an-other only the incQUtiwe formula changes. Thisallows us to attribute all changes in behaviorto the formula and not to differing cost or pro-duction parameter levels. We compare purelyinstitutional changes.

IV. Results

As previously stated, we will present the re-sults of our experiments by substantiating Ob-servations 1-4.

A. Observation 1: Shirking Happens

To illustrate this observation we concentrateon the behavior of our subjects in the revenuesharing-experiments. We consider these ex-periments to be classic examples of pure shirk-ing or free-riding experiments since theypresent subjects with a dominant strategy ofchoosing an effort level 12.5 which leads toPare to-inferior outcomes. These experimentsfurnish us with a baseline from which to mea-sure the effectiveness of the other plans; henceit is crucial to establish behavior here first.

Figures 1 and 2 present the mean and me-dian effort levels of our revenue-sharing ex-periments when they were performed first(Phase I). As we can see, while both the meanand median effori levels of subjects in round1 start off at 34.86 and 34.08, respectively, byround 25 they converge toward the equilib-rium effort level of 12.5. While they remainabove this level (18.63 and 17.67 for the meanand median, respectively, in round 25), thereis a clear downward tendency in the data. This


TABLE 2—EXPERIMENTAL DESIGNPHASR I

Experimentnumber

1

2

3

4

5

Experimentnumber

6

7

8

9

Contract typerounds 1-25

Revenue sharing

Revenue sharing

Revenue sharing

Revenue sharing

Monitoringp = 0.70


Forcing contracts

Competitive teams

Protit sharing

Monitoringp = 0.30


Forcing contract

Competitive teams

Profit sharing

Gainsharing

Monitoringp = 0.30

PHASE II


Revenue sharing

Revenue sharing

Revenue sharing

Monitoringp = 0.70

Number ofgroups

7

ID

6

10

2

Number ofgroups

10

10

10

2

Number ofsubjects

42

60

36

60

15

Number ofsubjects

60

60

60

15

data is consistent with the stylized facts aboutpublic goods experiments as described by JohnO. Ledyard (1995); he notes that a typicalpublic goods experiment starts out with ap-proximately a 50-percent (of Pareto-optimallevels) contribution rate and then decreases toapproximately 11 percent as the experiment isrepeated.

We take these results as supporting the hy-pothesis (as summarized in Observation 1)that subjects will take advantage of shirkingopportunities when they function under a planthat at least poses these opportunities in theform of dominant strategies.

B. Observation 2: History Matters

To illustrate this observation, we first com-pare the mean and median effort levels ofgroups engaged in our profit-sharing, forcingcontract, and competitive team experiments inPhases I and II of our experimental design(i.e.. before and after subjects have a historywith revenue-sharing schemes). Note that twoof these mechanisms (forcing contracts andcompetitive teams) implement Pareto-optimaleffort levels as Nash equilibria, while theother, profit sharing, entails a suboplimal Nash

equilibrium. Hence, we will be comparing theeffort levels of subjects in Experiments 3 and10, 1 and 7, and finally 2 and 9, and look tosee if these before-and-after experiences dif-fer. Figures 3 - 8 illustrate our conclusionshere.

As we can see, for both the median and themean, effort levels in practically all roundswere higher in those experiments run beforerevenue sharing. In other words, the experi-ences of groups in the revenue-sharing exper-iment (where effort levels tended to movetoward the low effort Nash equilibrium levelof 12.5) tended to lower the effort levels ofgroups in their second non-revenue-sharingexperiment below what they were when thosesame schemes were run first in Phase II. Con-sequently, previous history with a revenue-sharing mechanism that encourages shirkingleads to lower outputs with subsequent non-revenue-sharing mechanisms.

To investigate the impact of history moreclosely, we ran a set of dummy variable re-gressions. In the first regression (RegressionI) , run on our Phase-I data, we attempt to ex-plain the mean effort level of groups in the firstfive rounds of the second non-revenue-sharingexperiment as a function of their history (mean

VOL 87 NO. 3 NALBANTIAN AND SCHOTTER: PRODUCTIVITY AND GROUP INCENTIVES 325

60 00

50 00

40 00

30.00

10 00

0001 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

FIGURE 1. REVENUE SHARING (PHASE I )—MEAN EFFORT LEVELS

60.00

4000

30 00

10.00

0.00

10 It 12 13 14 15 16 17 18 19 20 21 22 23 24 251 2 3 4 5 6 7

FIGURE 2. REVENUE SHARING (PHASE 1)—MEDIAN EFFORT LEVELS


60.00

50,00

40,00

30,00

20,00

10,00

0,00

2 3 4 5 6 7 a 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

FIGURE 3. COMPETITIVE TEAMS—MEAN EFFORT LEVELS

60,00

50,00

40,00

30,00

20,00

10,00

0.00

2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

FIGURE 4, FORCING CONTRACT.S—MEAN EFFORT LEVEI..S

VOL 87 NO. 3 NALBANTIAN AND SCHOTTER. PRODUCTIVITY AND GROUP INCENTIVES 327

60,00

50,00

40 00

ig 30,00

20,00

10.00

0 001 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

Round

FrGDRE 5, PROFIT SHARING — MEAN EFFORT LEVELS

60,00

50.00

40 00

30,00

20.00

10,00

0.001 2 3 4 5 6 7 8 9 10 11 12 13 14 15 18 17 18 19 20 21 22 23 24 25

Round

FiGURF 6- COMPH'IITIVF, TRAMS —MEDIAN EFFORT LtVEL.S


60,00

50,00

- FC(I) -*- FC(II)

40,00

30,00

20,00

10 00

000

2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

Round

FIGURE 7. FORCING CONTRACTS—MEDIAN EFFORT LEVELS

60,00

5000

40.00

30.00

20,00

1000

0.00

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

FIGURE 8. PROFIT SHARING—MEDIAN EFFORT LEVELS


TABLE 3—DUMMY VARIABLF, REGRESSION

Variable

a (con.stant)

o,

DhD,D,

o,,

DuD p

D,]0,4

Die

O|BOigO^i,

o;,

Regression1

DroppedN.A.N.A,N.A.

J^

DroppedN.A.N.A.N.A.N.A.N.A.N.A.N.A.N.A.N.A.

Regression2

"^

1 ^

^^

Dropped(^k^

DroppedN.A.N.A.N.A.N.A.N.A.N.A.N.A.N.A.N.A.N.A.

Regression3

DroppedN.A.N.A.N.A.(^

) ^Dropped

N.A.t ^

1 ^

DroppedN.A.N.A.

individual effort level) in the last five roundsof their first revenue-sharing experiment andthe current plan being used. A second dummyvariable regression (Regression 2) was run us-ing Phase-II data in an attempt to explain themean effort level of groups in the first fiverounds of the second revenue-sharing experi-ment as a function of their history (mean in-dividual effort level) in the last five rounds ofthe first non-revenue-sharing experiment andthe plan used previously. Finally, a third re-gression (Regression 3) was run seeking toexplain the mean effort level of groups in thelast five rounds of the second non-revenue-sharing experiment as a function of the planused, the mean effort levels of the group dur-ing the last five rounds of the previous exper-iment, and the mean effort levels of the firstfive rounds of the current one.

The following dummy variables weredefined;

Di is a dummy variable taking a value of 1if the experience of the group (its meanindividual output) during the final fiverounds of the first part of the experimentwas between (i - 1)0 and iO, and 0 other-wise, / = 2, ... , 7. For example if 1 = 5,

then variable D^ takes a value of 1 if themean individual output of the group underinvestigation had a value between 40 [(5- 1 )0] and 50 during the final five roundsof the first part of the experiment, and 0otherwise.

D7,, is a dummy variable taking a value of 1if the plan used is plan j , and 0 otherwise,where) = 1 is the competitive team plan;7 = 2 is the forcing contracts plan;7 = 3 is the profit-sharing scheme;7 = 4 is the gainsharing scheme, and

D|| +i/ is a dummy variable taking a value of1 if the experience of the group (its meanindividual output) during the first fiverounds of the second part of the experimentwas between (/ - 1 )0 and (0, and 0 other-wise, / = \,2,...,l,k= 1,2 7.

The dummy variables and the regressions runare presented in Table 3, and the results of theregressions are presented in Tables 4-6 .

Regression I looks at the set of non-revenue-sharing experiments which were runin Phase I where they were run after partici-pation in a revenue-sharing experiment. Theleft-hand variable to be explained is the meaneffort level of groups in the first five rounds ofthe non-re venue-sharing experiment, and twofactors are used for this explanation: the meaneffort levels experienced by these groups inthe last five rounds of the revenue-sharing ex-periments and the current plan being used. Inessence we are trying to separate the infiuencethat experience has (as captured by mean ef-fort levels in the last five rounds in a revenue-sharing experiment) from the infiuence of theincentives incorporated in the plan.

As we can see from Table 4, with the ex-ception of the profit-sharing dummy (Z^io). allplan and experience variables were significantvariables in the regression. In addition, we cansee from the negative coefficients in front ofall experience variables that progressivelyworse experiences in the first revenue-sharingexperiment lower mean output in the first fiverounds of the subsequent non-revenue-sharingexperiments. With respect to the plan, it ap-pears that gainsharing and profit sharing arethe worst plans; but performance increaseswith the introduction of either forcing con-tracts or competitive teams. (Note that the co-efficient of the competitive team plan variableis significantly diff̂ erent from that of profit


TABLE 4—DUMMY VARIABLE REGRESSION: NON-REVENUE-SHARING EXPERIMENTS (PHASE-1 EXPERIMENTS)

Variable Coefficient Standard error P>95-percent

confidence interval

ConstantExperience

o,Dl

D,PlanD,D.0 , 0

Notes:

39.422

-19.002-14.145-12.142

14.4799.297

-4.407

Number of observations = 41F(n.29) = 6.92Adjusted R^ = 0.4703

4.488

6.5024.0534.413

3.9483.7894.595

Prob > F = 0.000R^ - 0.5498.

8.738

-2.922-3.490-2.751

3.6672.454

-0.959

0.000

0.0060.0010.009

0.0000.0190.344

30.300, 48.544

-32.216, -5.788-22.382, -5.908-21.111, -3.173

6.454. 22.5031.596, 16.998

-13,7476. 4.931

sharing and implicitly different from gain-sharing as well.) Finally, it is interesting to seethat with respect to output in the first fiverounds of the non-revenue-sharing experi-ments, forcing contracts appears to be indistin-guishable from competitive teams (at least asreflected in the confidence intervals about theestimated coefficients). This will not be thecase at the end of the non-revenue-sharing ex-periments, as we will see below.

When we look at Phase II (where non-revenue-sharing experiments were run firstfollowed by revenue sharing) and conduct Re-gression 2 (note, of course, that here plan re-fers to the plan used in the first, and not thesecond, part of the experiment where allgroups engaged in revenue sharing), we find(see Table 5) that experience in the last fiverounds of non-revenue-sharing experimentshas no significant effect on how subjects starttheir revenue-sharing experiment, nor does theactual experiment they participated in duringthat first experiment. In short, these resultssuggest that performance of groups in arevenue-sharing experiment is independent ofhistory—subjects tend to shirk no matter whatmechanism they previously participated in andno matter what their experience with that planwas.

While these results above pertain to behav-ior during the first five rounds of the secondexperiment run, we also might be interested inhow that same group ended up its experiencewith each other during the last five rounds ofthe second experiment. In Regression 3 the

mean group effort during the last five roundsof the non-re venue-sharing experiment wasexplained on the basis of three factors: the planor incentive mechanism used (plan), the ex-perience of the group (individual effort level)during the last five rounds of the first revenue-sharing experiment (Experience I), and theexperience of the group (mean individuallevel) during the first five rounds of the secondexperiment (Experience II). The results ofthese regressions are presented in Table 6.

Note that when we have two experiencevariables, the variable Experience I becomesinsignificant. In other words, behavior at theend of the second experiment appears only tobe a function of how a group started that ex-periment and the actual plan under which it isfunctioning. However, such a conclusion is de-ceiving since we already know from Table 5that the variables Experience I and ExperienceII are correlated. Hence, Experience I and Ex-perience II are colinear variables with Expe-rience I having at least an indirect effect ongroup performance at the end of the secondexperiment. Further, notice that it is particu-larly good experience in the first five roundsof the second experiment {£)jy, the droppeddummy variable) that is a critical determinantof performance at the end of the second ex-periment. In fact, all other experiences signif-icantly lower the mean effort level of groupsduring the last five rounds of the non-revenue-sharing experiment. Finally notice that theforcing contracts plan (Dy) is the only planwith a significant negative coefficient in ex-


TABLE 5—DUMMY VARIABLE REGRESSION: REVENUE-SHARING EXPERIMENTS (PHASE-II EXPERIMENTS)

Variable

ConstantExperience

o.D.D,D,D,D^Plan*

D..

Coefficient

41,512

-12.390-12.820-13,721-12.386

-5.631-8.120

-4.2622.731

Standard error

10,453

10.86810.62510.4759.9459.165

12.08

6.0193.787

3.971

-1.140-1.207-1.310-1.245-0.614-0.672

-0.7080.721

P > \t\

0.000

0.2640.2380,2010.2230,5440,507

0.4850.477

95-percentconfidence interval

20.100.62.932

-34.654. 9,8738-34.585,9.9458-35,180,7.7363-32,758,7.9858-24.406, 13.144-32.875, 16.635

-16,593, 8.068-5.026. 10.488

Notes:Number of observations = 37 Prob > F = 0.857Adjusted R- = -0.129 R- = 0.\2\.F(8,28:i = 0.480*In this regression there is no gainsharing plan since that plan never preceded a revenue-sharing plan.

plaining mean output in the last five rounds,while competitive teams is the only plan witha positive coefficient (albeit insignificant).The fact that the forcing contract coefficient isnegative indicates that the forcing contractplan is not stable in maintaining output levelsthroughout the history of the group interaction.In our experiments, the forcing contract re-gime consistently and substantially underper-forms competitive teams in maintaining highoutput levels, even when the performance tar-gels were significantly reduced and environ-mental uncertainty completely eliminated{making these plans less risky).^ Typically,after the group fails to reach the target suffi-ciently often, group output tumbles. These re-sults cast doubt on the efficacy of exogenoustargeting as a solution to the problem of groupmoral hazard.

Our results here are reminiscent of earlier re-sults by Van Huyck et al. (1990, 1991). In thosepapers the authors examine whether subjectschoose an equilibrium of a game on the basis of

'' In the set of experiments not reported here, we alteredthe parameters of the forcing contract regime, either re-ducing performance targets (to 240) for the entire group,or removing uncertainty from the group output functionentirely. In these experiments, the comparative perfor-mance of competitive teams and forcing contracts remainsqualitatively unchanged. A full discussion of these resultscan be found in Nalbantian and Schotter (1994).

the closest previous equilibrium chosen in gamesplayed immediately before. As in our work, theyinvestigate whether a Pareto-dominant, yet riskyor "vulnerable," equilibrium (see Nalbantianand Schotter [1994]; Schotter [1996]) will bechosen in a game if that group previously hashad a successful experience playing a Pareto-dominant equilibrium of a less risky game.While their results are mixed, they find evidencethat successful group-rational coordination inearly games does not carry over to a continuationgame, the Pareto-dominant equilibrium of whichis risky. The logic behind our results is identical.On the other hand, when groups of laboratoryworkers have a common history of shirking,there is a lack of trust among them which causesthem to avoid taking a chance on a risky, yetPareto-dominant, equilibrium (this is what Fig-ures 3 - 5 demonstrate). However, if theyhappen upon a very good common experiencein their earlier interaction, then they build up alevel of trust sufficient to allow them to take achance in their subsequent interactions (at leastduring the first five periods of it). When thegame they play has a dominant strategy equilib-rium, like revenue sharing, then such a deductivecharacteristic overpowers any inductive selec-tion principles inherent in the history of priorplay of the group.''

'' For a closer look at the problem of trust and risk andtheir impact on worker productivity, see Schotter (1996).


TABLK 6—DUMMY VARIABLK RKGRESSION: NoN-Rf-VENUE-SHARiNG EXPERIMENTS

LAST FIVE ROUNDS (PHASE-II EXPERIMENTS)

Variable

ConstantExperience ID,

o.Plan

Experience IIDnD,4O|5

Dn

Nates:

Coefficient

73,171

-3,852-4.930-7.524

7.798-16.740

-7.524

-52,150-46,0! 8-38.053-36,628-52.038

Number of observations = 41F(II,29) = 5Adjusted fi'

,38= 0,544

Standard error

13.338

11,4096,8376,700

7,4005.4286.700

14,53111,36811,75411,92714,461

Prob > F = 0,001fl' = 0,67154,

t

5,486

-0.338-0.721-1.123

1,054-3,084-1.123

-3.589-4.048-3.237-3.071-3,598

P> \t\

0,000

0,7380,4770,271

0.3010.0040,271

0,0010,0000,0030.0050.001

95-percentconfidence interval

45.890, 100.453

-27,187. -19,482-18.913, 9,053

-211.228, 6,180

-7.337. 22,934-27.843. -5,637-21.228. 6.180

-81,870. -22.429-69,268. -22,767-62.092, -14,013-61.024, -12,233-81.616. -22,461

Finally, the impact of history on behavior isalso pointed out by Isaac et al. {1991), wherethey survey a group of articles indicating thathistorical events may influence a person's per-ceptions of what is a fair outcome.

C. Observation 3: A Little Competition Goesa Long, Long Way

There really are two criteria one might want touse to evaluate any particular group incentivemechanism. First, one obviously would want tosee what mean effort levels this mechanism de-fines. This is the aim of most principal-agent anal-yses. However, a corporate manager also mightbe interested in how reliable any given mecha-nism is in generating these high mean outputs.For example, say that a corporation has a numberof identical plants situated across the country eachproducing identical products. At its disposal aretwo group incentive plans. Plan A and Plan B.Say that if Plan A were instituted in each of thecorporation's plants, its mean aggregate outputwould be greater than Plan B's, but Plan B hasless plant-to-plant variance attached to it. In otherwords. Plan B is a reliable producer of reasonablygood outcomes, while Plan A has a higher meanbut also a higher variance. Which plan one uses

obviously will depend on one's attitude towardrisk. However, if one plan dominates the other inthe sense of generating both higher mean outputsas well as smaller group-to-group variations, thenclearly it should be chosen.

Observation 3 states that on these criteria thecompetitive teams mechanism practically dom-inates all other mechanisms tested, except for thefact that profit sharing and revenue sharing,while having significantly lower means, also havesmaller variances around that mean than does thecompetitive team mechanism. When comparedto forcing contracts or gainsharing, however, thecompetitive teams mechanism elicits both ahigher mean effort level during the last fiverounds of any experiment and a smaller across-group variance of effort around that mean.

Our support for Observation 3 is presentedin Figures 9 and 10, which show the efficiencyfrontier for all of the mechanisms we have in-vestigated in mean-variance space. In otherwords, we look at the mean group plan foreach group during the last five rounds of eachPhase-I and Phase-II experiment and thegroup-to-group variance across these groupsin these same periods. Each point in the mean-variance space represents the mean-varianceconfiguration for a specific plan. All vectors


Mean

FIGURE 9, MEAN-VARIANCE P u n s ot GROUP OUTPUT (PHASE I)

on the boundary of this set are connected. Notealso that the competitive teams mechanismdominates all mechanisms except for profitsharing and revenue sharing. Further, since themean of the competitive team experiment is somuch higher than that of either profit sharingor revenue sharing, it is hard to conceive of adegree of risk aversion that would lead a cor-porate planner to actually prefer profit sharingover competitive teams. (Note, of course, thatany risk-neutral corporate planner would pre-fer the competitive teams mechanism over allothers. )̂ It is in this sense that we claim thata little competition goes a long way.

^ Note that white the forcing contract (75) and com-petitive teams formulae have identical Pareto-optimaiequilibria, profit sharing and revenue sharing do not,(Gainsharing has no predictable equilibrium outcome,)Hence, we should not expect profit sharing or revenuesharing to outperform these other mechanisms. However,since forcing contract (75) is. in essence, a profit-sharingmechanism with a Parelo-optimal target, comparing forc-ing contract (75) with competitive teams is equivalent tocomparing a competitive teams mechanism to a profit-

D. Observation 4: Monitoring WorksBut Is Costly

As principal-agent theory tells us, if moni-toring is possible it becomes quite easy to elicitoptimal levels of effort from workers simplyby monitoring them and firing them if they arecaught shirking. When only imperfect moni-toring is possible or monitoring is so expen-sive that workers can only be checkedsporadically, the cost-effectiveness of suchmonitoring schemes is called into question.What principal-agent theory does not tell us ishow sensitive workers will be to the detectionprobability of shirking. For instance, will evenminor detection probabilities lead to high ef-fort levels? Do workers misestimate the detec-tion probability or suffer from some type ofprobability bias as is evidenced in other.

sharing mechanism. Also, revenue sharing is added toillustrate the mean variance properties of a non-target-based scheme (remember, of course, that no revenue shar-ing, Pareto-optimal equilibrium exists).


FiGURb 10. MEAN-VARIANCB PI-()T.S OF GROUP OUTPUT (PHASK II)

decision-under-uncertainty experiments, whichleads them to consistently underestimate theprobability of being caught? (See the surveyby Colin Camerer [1995] for other instancesof probability bias.)

Clearly these are questions that must beanswered before we can suggest the relativesuperiority of monitoring schemes in corpo-rations. Our experimental design furnishesdata which give us some insight into this ques-tion. For instance, in Figures 11 and 12 we seethe median effort level of subjects in our mon-itoring (0.70) and monitoring (0.30) experi-ments run in Phase I and II [i.e., in Phase I weran our monitoring (0.70) experiment first andthen our monitoring (0.30) experiment, whilein Phase II the process was reversed I). Clearlythere is a dramatic difference between themedian effort levels of subjects when beingmonitored with a 0.70 probability and a 0.30probability. This is, of course, to be expectedsince the optimal response of subjects to a 0.70monitoring probability is to choose a Pareto-optimal effort level, while the optimal re-sponse to a 0.30 monitoring probability is toshirk. This is seen in Figures 11 and 12, whichshow that groups functioning under a 0.70

monitoring probability choose Pareto-optimaleffort levels as a median, while the 0.30 prob-ability groups choose efforts the median ofwhich involves almost complete shirking. Fur-thermore, while high detection levels (0.70)lead to consistently high effort levels whetherthe experiment was run before or after a low-detection experiment, low detection levels(0.30) lead to quite different types of behaviorin experiments run before and after high-detection experiments. This is clearly seen inFigure 12, where the median effort level forthe low-detection group is practically zero inall periods when the experiment is performedin Phase I (after the 0.70 detection experi-ment). When it is performed in Phase II (be-fore the 0.70 experiment), the results are quitedifferent. What is striking is that the predic-tions of the theory seem to fail when subjectsare not experienced and when they are subjectto the low 0.30 monitoring probability (me-dian effort levels are periodically above thezero effort levels). Obviously, when groupsare used to high-detection probabilities, a dropto low probabilities seems to lead them toreevaluate their effort choices and lower them.Again, history matters.

VOL. 87 NO. .? NALBANTIAN AND SCHOTTER: PRODUCTIVTTY AND GROUP INCENTIVES 335

100

90

80

70

60

50

40

30

20

10

70 Percent, Phase I - .— 70 Percent, Phase II

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

Rounds

FIGURE 11. MONITORING {70-PERCENT PROBABILITY )—MEDIAN EFFORT LEVELS

V. Conclusions

This paper has attempted to take a first stepon the road to adding some empirical meat tothe skeleton created by theorists working on theproblem of group incentives and productivity. Inour experiments we have uncovered a numberof factoi-s which we think are probably importantfor the proper design of group incentive mech-anisms. Most important among these findingsare the observations which follow. First, we havefound that the history of a group and its perfor-mance in the past is an important predictor ofhow that group will perform when a new incen-tive program is introduced. In addition, we havediscovered evidence that one effective way toincrease group effort is to introduce somewithin-firm competition between work units per-forming the same task—setting up an intrafirmteam tournament. Targets established endoge-nously on the basis of relative performance dobetter at stimulating group output than those thatare externally stipulated."

Finally, although we do not report theseresults here (see Nalbantian and Schotter[1994]; Schotter [1996]), our findings in-dicate that it is not sufficient to expect amechanism to implement Pareto-optimaloutcomes as Nash equilibria without takinginto account the out-of-equilibrium proper-ties of the mechanism. If those optimal out-comes actually are to be achieved, it isnecessary that those equilibria be relativelyriskless or not "vulnerable" to slight mis-takes by one's colleagues. Mechanismswhich attach considerable risk to selectingthe efficient equilibrium ultimately may leadeconomic agents to opt out of the mechanismand play it safe by shirking as was the casein our forcing contracts plan.

While these findings strike us as interesting,we are well aware of their limitations. Tobegin with, our experiments provide at besta bare-bones economist's view of the incen-tive problem. They characterize productive

** Of course, we recognize that where there is substantialinterdependence across work groups, the use ot" relative

performance evaluation can undermine incentives for co-operation and reduce organizational productivity.

THE AMERICAN ECONOMIC REVIEW JUNE 1997

2 3 4 5 6 7 9 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25

Rounds

FIGURE 12. MONITORING (30-PERCENT PROBABILITY )—MEDIAN EFFORT LHVKLS

performance as the outcome of a noncooper-ative game and are concerned solely with theincentive properties of the various reward for-mulae as the explanation of behavior. Psy-chologists, compensation practitioners, andothers certainly would protest that life is fardifferent in the workplace than in our experi-ments. The character of interactions amongworkers is considerably more complex thanthat presumed here. For one thing, work couldjust as well be modeled as a cooperative gamein which workers communicate with eachother and implicitly establish work normswhich they then enforce upon each other. Re-sults from Dawes et al. (1977) indicate thatcommunication between subjects dramaticallyaffects their performance in public goods ex-j>eriments. Similarly, while managers may notbe able to monitor workers effectively, work-ers themselves may be in a better position todo so. And they would have more incentiveto perform that function in a system wheretheir rewards depend on co-worker perfor-mance than in a system where they depend onone's own performance alone (Nalbantian,1987; David I. Levine and Laura D'Andrea

Tyson, 1990; Eugene Kandel and Edward P.Lazear, 1992). A full and proper experimentaldesign should allow this factor to come intoplay.

These are all valid points, but we do not feelthat they reduce the significance of what wehave uncovered here. Our intent in these ex-periments was to see how far the orthodox eco-nomic model of group incentives and the"corrective" reward formulae deduced there-from can take us in explaining behavior. Aspreviously noted, substantial evidence fromthe field does indeed suggest that observed be-havior under group incentives is often at vari-ance from that predicted by standard theory.Certain other factors clearly are central to theoperation of group incentives and, therefore,should be incorporated in experimental treat-ments of the problem. We intend to do so inour future research. Still, in conducting theseexperiments we have learned important les-sons about the properties of prototypical groupincentive formulae—findings that transcendthe particular context in which they were re-vealed. We have established an economicbaseline which helps determine how much


more of observed behavior under group incen-tives needs to be explained.

APPENDIX

The enclosed Appendix presents the instruc-tions for the profit-sharing experiments. Otherinstructions are identical except, of course, forthe section entitled "How Your Payment IsDetermined."

Instructions for Profit-Sharing Experiment

IntroductionYou lire about to partake in an experiment

on group decision-making. A number of re-search foundations have provided funds to runthese experiments. Depending on the decisionsyou and other participants in the experimentsmake, you may be able to earn a considerablepayoff which will be given to you as you leave.

Your Task in This Experiment

As you walked into the room you were ran-domly assigned to a group of six subjects. Youwill be in this group for the entire experiment,which will last for 25 rounds.

When you sit down at your computer ter-minal, your screen will appear as follows;

Decision Group TargetRound No. Rev. Rev. Payment Cost Earnings

(112.5 fr.) (payment—cost)

25

Do Not Touch Any Computer Key Until WeInstruct You to

In round 1 of the experiment, you and theother five subjects in your group will be askedto type in a number between 0 and 100. Thecomputer will prompt you to do so by stating:"Please enter a number between 0 and 100."

We call the number you enter your decisionnumber. You enter your decision number hytyping it on the number keys and hitting thereturn key when you are finished. Thecomputer will then confirm your choice bystating: "You have chosen . Is that whatyou wanted?"

If this is, in fact, the decision number youwant to enter, push the Y (Yes) key. Yourparticipation in this round of the experimentwill then be over. If you wish to change yourmind, or you made a mistake in your typing,type N (No), and you will be prompted tochoose another number. When you have suc-cessfully decided upon a decision number andentered it, your participation in this round ofthe experiment will be over.

Round-by-Round Payoffs

In each round of the experiment you willreceive a payment in a fictitious currencycalled "francs." (The francs you earn will beconverted into dollars at the end of the exper-iment at a rate to be described shortly.) Thepayment you receive will depend on your de-cision number and those of the other membersof your group, as well as the realization of arandom number. Precisely how the randomnumber influences your payment is describedin the next section. Your actual payoff (orearnings) in any round is the difference be-tween the payment you receive and the directcost to you of the decision number you se-lected as given by the cost schedule table inthe beginning of this Appendix. In otherwords: earnings = payment - decision cost.Let us see specifically how both these com-ponents determine your earnings.

How Your Payment Is Determined

When you and the other members of yourgroup have entered your decision numbers (in


column 2), the computer will add them up. Wewill call the resulting number the group total.The computer will then randomly choose anumber between - 4 0 and +40 and add it tothe group total. When we say "randomly," wemean that each number in the interval - 4 0 to-1-40 has an equal chance of being chosen.Hence, the chance of - 3 0 being chosen isequal to the chance of +15 being chosen,which in turn is equal to the chance of +5being chosen, and so on. Finally, the sum ofthis random number and the group total willbe multiplied by the number 1.5 (francs) toget what we call group revenue, which willappear in column 3 on your screen as "GroupRev." For example, say that the decision num-bers of the six members of your group are Z\,Z2^ z^, Za, Z5, and s^, where Z\ is the decisionnumber of subject #1, Zj is the decision numberof subject #2, and so on. Further, suppose thatthe random number generated by the computeris +5. Then the group total would be: (z, +Zi + Z} + Z4 + Z5 + Z(y + 5) and the grouprevenue wouid be \.5(_Zi + Zi + Z:^ + ZA +5̂ + Zf, + 5). As you can see, group revenue

will thus reflect both the choices of each groupmember regarding his/her decision numberand the realization of the random number,namely, pure chance.

Group revenue (group total) is the basisof your individual payment. Specifically, ineach round of the experiment your groupwill be given a target group revenue of 112.5francs. (Note: this corresponds to a grouptotal of 75, i.e., 75 X 1.5 = 112.5.) If yourgroup revenue turns out to be less than112.5, your payment for the round will bezero. If your group revenue precisely equals112.5, your payment for the round will bethe fixed amount of 18.75 francs. On theother hand, if your group revenue exceeds112.5 francs, your personal payment will bethe sum of 18.75 francs and one-sixth of thedifference between your group revenue and112.5 francs. In other words, in addition tothe fixed amount, 18.75 francs, you person-ally will be paid one-sixth of the excess ofactual group revenue over the target grouprevenue. For example, say that your grouprevenue is 172.5 francs, which exceeds thetarget of 112.5 by 60 francs. Your paymentfor this round would then be 18.75 + 1/6(172.5 - 112.5) = 28.75 francs.

Clearly, above the 112.5-franc threshold or"group target," the larger is group revenue,the greater your payment will be—though asyou will see, you will have to deduct fromyour payment the cost associated with your de-cision number. Below the group target, yourpayment is a fixed amount (0 francs) indepen-dent of group revenue.

The group target of 112.5 francs is indi-cated in column 4 on your screen. Your pay-ment for each round of the experiment will becalculated by the computer and appear in col-umn 5 on your screen.

How Your Earnings Are Determined

Your payoff or earnings in any round willequal the payment you receive, as describedabove, minus the cost of your decision num-ber. Decision costs are presented in the costschedule table. You will note that for each de-cision number you might choose over therange 0 to 100, there is an associated cost tobe incurred. You can read your cost table bylooking down the first column and finding thedecision number you are contemplating. Thesecond column will then inform you what itwill cost you to choose that decision number.For example, a decision number of 25 has anassociated cost of 6.75 francs, while the deci-sion number 50 has a cost of 25 francs. Severalimportant features of this cost schedule are ev-ident in this example and are especially note-worthy. First, the larger the decision number,the higher the cost you must incur. Second, thecost of decision numbers increases at an in-creasing rate. Hence, the cost of choosing de-cision number 50 is more than twice the costof choosing 25; The cost of choosing 100 ismore than twice the cost of choosing 50. Youcan verify this characteristic of costs of deci-sion numbers by considering other examplesfrom the cost schedule.

The cost of the decision number you choosewill be deducted from the payment you aredue in that round to determine your actualearnings for the round. Again, earnings =payment - decision cost. The cost of your de-cision numher for each round will appear incolumn 6 on your screen.

To illustrate how your earnings will be de-termined, suppose that group revenue in round1 of the experiment is calculated at 200 francs

VOL. 87 NO. 3 NALBANTIAN AND SCHOTTER: PRODUCTIVITY AND GROUP INCENTIVES 339

and that the decision number you selected inthat round was 40. Since 200 is greater than112.5 {the group target), your payment thenwould be calculated as: 18.75 + l/6[200 -112.5] - 33.33 francs. From the cost scheduletable we find that the cost of decision number40 which you chose is 16 francs. Therefore,your earnings for round 1 would be: 33.33 —16 = 17.33 francs. Suppose, on the other hand,that group revenue in a given round is 112.5francs, and that your decision number is again40. Since the group target is precisely attained,your payment will be 18.75 from which yourdecision cost must be deducted; your earningsare then calculated as 18.75 - 16 = 2.75francs. Finally, suppose your group revenue is110, while your decision number remains 40.Since the group target has not been achieved,your payment is 0 francs. Thus your earningsfor this round would be 0 — 16 francs = —16francs. (Negative earnings will be deductedfrom your accumulated earnings at the end ofthe experiment.)

Your earnings, or payoff, for the round arecalculated by the computer and appear in col-umn 7 on your screen.

Final Payoffs

Your final payoff in the experiment will beequal to the sum of the francs received overthe 25 rounds of the experiment. Each francwill be converted at the rate of 1 franc = .71cents. In addition to this payoff, you will re-ceive a fixed payoff of $3.00 just for showingup at the experiment.

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productivity under group incentives: an experimental study

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