Statistical discrimination in labor markets: an experimental analysis.
Dickinson, David L. ; Oaxaca, Ronald L.
1. Introduction
When membership in a particular group conveys valuable information
about an individual's skills, productivity, or other
characteristics, a nonprejudiced agent may still find it rational to
statistically discriminate. Examples of statistical discrimination
include wage or hiring decisions in labor markets, racial profiling in
law enforcement, determinants of loan approval rates, voting the party
ticket in elections, or differential premiums for insurance, among
others. In some settings statistical discrimination is legal and
acceptable (for example, insurance rates); whereas, in others it is
controversial and/or illegal (for example, racial profiling and
employment discrimination). Existing research has focused on
first-moment statistical discrimination: that is, discriminatory wage
offers to females or lower loan approval rates for minority applicants
are based on average productivity and default rates, respectively.
Agents attribute average group characteristics to each individual from
that group when it is costly to gather information.
In this article we explore the possibility that statistical
discrimination extends beyond differential treatment based on average
group characteristics. Specifically, discrimination may also exist if
agents base decisions on productivity distribution risk (or default
rates, accident rates, etc.). Using labor markets as an example,
risk-averse employers may make lower wage offers to females if their
productivity variance is believed to be higher, even though average
productivity may be identical to that of males. If such variance-based
statistical discrimination is empirically documented, then existing
measures of statistical discrimination are biased, and measures of
prejudiced-based discrimination may be overstated. Some have found field
evidence of statistical discrimination based on higher-order moments of
a distribution (Ayers and Siegelman 1995; Goldberg 1996; List 2004), but
we also recognize that statistical variance may not be the only
behaviorally important measure of distributional risk. Thus, we
contribute additionally by examining the support of the productivity
distribution (Tversky and Kahneman 1973; Curley and Yates 1985; Griffin
and Tversky 1992; Babcock et al. 1995) and the possibility for loss
(Kahneman and Tversky 1979) as two other potentially important cognitive
assessments of risk. In short, some discrimination labeled as personal
prejudice or taste based may really be just a different form of
statistical discrimination than what is typically examined.
We report results from a controlled laboratory experiment in which
subjects are engaged as employers and workers in a laboratory
double-auction labor market. We choose a labor market context for our
experiments for several reasons. First, we believed that because payoffs
to employer-subjects are determined by an outcome variable minus a
contract payment to another subject, the labor market context would aid
subjects in understanding payoffs in our experiment. Second, statistical
discrimination is very relevant to labor markets, highlighted by the
many existing empirical studies of statistical discrimination that
examine labor markets. Finally, the use of labor market context in a
competitive double-auction market environment is a logical context with
precedence in the experimental economics literature (Fehr et al. 1998).
That said, the insights we gain from our data extend to other contexts,
and the implication of our results is that statistical discrimination
may be more pervasive than previously thought. Our results show that
subjectemployers make significantly lower wage offers when the
probability of loss is greater, and this measure of risk mattered more
than the statistical variance or support distribution.
Statistical theories of discrimination have been advanced by Arrow
(1972), Phelps (1972), Aigner and Cain (1977), and Lundberg and Startz
(1983). Some studies base statistical discrimination on noisier
productivity signals for certain worker groups, while others base it on
imperfect or incomplete information. (1) Most researchers advance
theories that depend on differences in average productivity
characteristics; although, others note that statistical discrimination
need not be based on differences in average productivity (e.g., Aigner
and Cain 1977; Curley and Yates 1985). For risk-averse individuals, it
seems clear that a less risky outcome distribution would be preferred to
a more risky distribution; although, "risk" may be defined in
ways other than just a statistical variance, as we note. Empirical
evidence alluding to statistical discrimination can be found in a
variety of settings; although, it is often difficult to identify
taste-based versus statistical discrimination (see discussion in Arrow
1998). Probably the only easily observable forms of statistical
discrimination are the legal forms, such as those found in the insurance
industry. In labor markets there is some direct evidence from employer
interviews that race is used as a proxy in employment decisions (Wilson
1996). Neumark (1999) uses field data to uncover discrimination not
based on productivity characteristics, but Altonji and Pierret (2001)
find little evidence for statistical discrimination based on race. (2)
Given identification and causation issues inherent in field data
examinations of discrimination, some have used controlled experiments to
study statistically based discrimination resulting from imperfect
information (Anderson and Haupert 1999), asymmetric information (Davis
1987), or ethnic stereotypes (Fershtman and Gneezy 2001). We employ a
full information environment to examine higher-order statistical
discrimination and to explore which of several risk measures is more
behaviorally important. Our design is such that causation can go in only
one direction (that is, exogenous wage distributions imply that wage
contracts cannot affect future worker productivity), and the market
institution for determining wage contracts is one that produces strong
convergence to the competitive equilibrium prediction. Nevertheless, we
find evidence for statistical discrimination based on one important
measure of worker risk.
2. Experimental Design
We implement a two-sided auction market design to simulate a labor
market. Specifically both employers (buyers) and workers (sellers)
negotiate in an open-pit fashion, with no central auctioneer. Workers
are more plentiful than employers, and so there is an equilibrium level
of "unemployment" in this design. Both supply and demand for
labor are induced upon the experimental subjects using standard
experimental techniques, discussed in Smith (1982). (3)
The baseline design we use is simple in that it generates clear
equilibrium predictions. Specifically the demand side of the
experimental market consists of five employers, each capable of hiring
one unit of labor in each experimental market round. The productivity of
a unit of labor in the baseline (treatment 1) is certain and fixed at
three units of output (each unit of output sells for SI experimental),
and so the demand for labor is perfectly elastic at $3.00 up to five
units of labor. The supply side of the market consists of 10 workers,
each with a reservation wage of S0.40, and each is able to sell at most
one unit of labor services in each experimental market round. As such,
the supply curve is perfectly elastic at SO.40 up until 10 units of
labor. The predicted market wage is S0.40, and the predicted market
quantity of labor traded is five units. We used the labels
"worker," "employer," and "wages" to
facilitate the subjects' understanding of the connection between
productivity and final payoff, but it was clear to all subjects that no
labor task would be completed in the experiment. In this way we maintain
strict control over productivity in the experiment. Figure 1 shows the
experimental design graphically.
The baseline experimental design is quite similar to that used in
Smith (1965), though Smith does not use a labor market context. That is,
at the predicted equilibrium the entire market surplus is allocated to
one side of the market (the buyers of labor). In our design the
employers are not given information on worker reservation wages, and
workers are not informed as to the value (to employers) of a unit of
output. Payoff information is therefore private to each subject, as in
Smith (1965), who shows that, even when market surplus at equilibrium is
designed to be extremely imbalanced, this trading institution produces
strong convergence of equilibrium prices to the competitive equilibrium
prediction. Any evidence of statistical discrimination in the uncertain
productivity treatments would then be significant, given the strong
competitive tendencies inherent in our baseline design.
[FIGURE 1 OMITTED]
The stochastic or uncertain productivity treatments are labeled
treatments 2, 3, and 4. The difference across these uncertain
productivity treatments lies in the particular (known) productivity
distribution for the labor pool. After hiring a unit of labor in an
uncertain productivity treatment the employer discovers the realized
productivity of that unit of labor by means of an ex post random draw.
Specifically, in treatment 2, productivity of the labor pool is either
one, two, three, four, or five units of output with probability 10%,
10%, 60%, 10%, and 10%, respectively. Productivity is determined by a
random draw from a Bingo cage, and an independent draw is conducted for
each employer who hires a unit of labor. Though wage contracts are made
with a specific experimental subject in any given trading round, it is
made clear that productivity draws are independent of the actual
worker-subject (that is, you cannot contract in the next round with John
Doe to ensure productivity of five just because it happened to turn out
that way in the current or past rounds when contracting with John Doe).
The independence of the productivity draw from the specific
worker-subject controls for differences that employers in naturally
occurring work environments would have in sorting and selecting workers
from a given labor pool. We simply assume that employers are equal on
this dimension, and so hiring any worker from a given pool of workers
with a specific productivity distribution is similar to taking a random
draw from the productivity distribution.
Treatments 3 and 4 also involve uncertain productivity
distributions of the labor pool, but they differ from treatment 2 in
terms of the specific distribution. In treatment 3 productivity of the
labor pool is either one, two, three, four, or five units of output with
probability 20% for each possible outcome. In treatment 4 productivity
of the labor pool is either two or four units of output with probability
50% for each.
The expected competitive employer profit is $2.60 experimental
dollars because the expected revenue is $3.00 and the competitive wage
is $0.40. There were a total of seven experimental sessions in which the
order of the treatments was randomized. Each of the four treatments in
an experimental session lasted four periods. There were a total of 35
employers in our experiment, and we observe wage contracts for each
employer a total of 16 times. Hence, we have a panel with 560
observations.
Table 1 describes the experimental design in terms of how each of
the treatments varies with respect to distinct measures of productivity
distribution risk. This design allows us to examine several candidate
variables for statistical discrimination: discrimination based on the
variance of labor productivity, based on the support of the productivity
distribution, or based on the probability of less-than-expected
competitive profits for the employer. A comparison of wage contracts in
treatment 1 to treatments 2, 3, and 4 allows us to test these different
hypotheses of statistical discrimination. Binary comparisons among
treatments 2, 3, and 4 allow us to look at the joint effects of varying
combinations of variance, support, and probability of lessthan-expected
competitive profits for the employer. The difference between treatment 3
and treatment 2 reflects the joint effects of a higher variance and
greater probability of less-thanexpected profits in treatment 3. The
difference between treatment 4 and treatment 2 reflects the joint
effects of a smaller support and a greater probability of
less-than-expected profits in treatment 4. Finally, the difference
between treatment 4 and treatment 3 reflects the joint effects of a
smaller variance, a smaller support, and a greater probability of
less-than-expected profits in treatment 4. For the statistical analysis
discussed next, we also create independent variables that isolate the
effects of changes in each distinct measure of distributional risk.
3. Results
We report results on a total of seven experiment sessions, using
105 unique college-aged subjects (35 employers and 70 workers). Our
sample has 53% female subjects overall: 57% female employers (N = 20 out
of 35 employers) and 51% female workers (N = 36 of 70). Six of the seven
treatments had either four, five, or six female workers (out of 10 total
worker-subjects in the session). Session 7 abnormally had eight of 10
workers that were female. Each session lasted about 1.5 hours, and
average earnings were $I8.13.
Our results are summarized in Tables 2, 3, and 4. In Table 2 we use
dummy variables to control for the uncertainty productivity treatments
2, 3, and 4 (T2, T3, T4, respectively), to control for rounds 2, 3, and
4, and to control for treatment order within a four-treatment experiment
(for example, T03 = 1 if a treatment occurs third in a particular
session). Because our data consist of repeated observations on
employers, panel data methods seem appropriate. Fixed effects and random
effects estimators account for differences in wage contracts across
employers and possible correlation in the error terms across rounds for
an individual employer's wage contracts. Given our particular
orthogonal design, the estimated parameters of the wage contract
equations are identical for fixed effects, random effects, and ordinary
least squares (OLS) with a single constant term. The estimated standard
errors are also identical for fixed effects and random effects but
differ from those obtained from OLS (see Oaxaca and Dickinson 2005 for
details). Because we are able to reject the classic OLS model in favor
of both fixed effects and random effects, we interpret this as support
for using the fixed/random effects estimated standard errors in our
analysis.
The Table 2 results show that, for the full sample, treatment 4
significantly lowers wage contracts offered to workers, but the results
from the gender-specific samples show that this is due entirely to the
behavior of the male employers. (4) The estimated wage contract effect
of treatment 4 relative to treatment 1 captures the combined effects of
all three of our risk measures. Wage contracts offered by male employers
are about 12 cents lower in treatment 4 compared to the certain worker
productivity treatment 1. This represents an average wage offer decrease
of about 20% given the average wage contract level of about 60 cents for
male employers. Female employers, on the other hand, did not offer
significantly different wages across treatments. While this is
consistent with female employers being risk neutral, the literature
suggests otherwise. We return to this point later. Across rounds, the
estimated coefficients indicate that wage contracts converge toward
equilibrium in later rounds of each treatment, and wages also converge
downward for a given treatment the later it occurs in the experiment.
Table 3 presents treatment effects comparisons (that is,
coefficient comparisons) from within the uncertain productivity
treatments. Treatment 4 compared to treatment 2 (T4-T2) reflects the
combined effect of the smaller support but higher probability of
less-than-expected profits in treatment 4. In all samples the combined
effect is negative but statistically significant only in the full sample
and female employer subsample. We note that the depressed wage contract
effects of treatment 4 relative to any of the other treatments are
larger in absolute value than any other binary treatment comparisons.
These results reflect the dominance of the loss aversion motive.
Though these results presented thus far offer some initial evidence
of statistical discrimination based on distributional risk, it is also
the case that the treatment effects specification does not directly
control for differences in the productivity distribution's
variance, support, or probability of below average profits. This follows
from the fact that certain treatments vary more than one of these
distributional characteristics (see Table 1). In formulating our
statistical design, we had not originally considered the loss aversion
factor associated with the variation in the probability of less-than
expected profits (that is, the probability of a less than average
productivity draw). We therefore also estimate a model using explicit
controls for individual changes in each of these distributional
characteristics in Table 4.
In Table 4 wage contracts are regressed on variables for variance,
support, and loss probability, where variance and loss probability are
coded as defined in Table 1 (that is, loss probability is measured
relative to expected [competitive] profits). The variable for
productivity distribution support is defined as the width of support: 0,
0.4, 0.4, and 0.2 for treatments 1, 2, 3, and 4, respectively. Given our
particular orthogonal design, the statistical model in Table 4 is the
same as that in Table 2 but offers an alternative way to view the
results pertaining to the treatment effects. Consequently, as in Table
2, the Table 4 results are from a fixed/random effects specification,
and estimates are presented for the entire employer sample as well as
the gender-based employer subsamples. (5) For comparison purposes, we
estimate two versions of the model for each sample. The first model
controls only for distributional variance as the risk measure of
interest; whereas, the second model controls for variance, distribution
support, and loss probability. Among the risk measure variables in Table
4, we can see in the overall sample that the only significant predictor
of wage contract differences is the probability of loss, due entirely to
the male employer subsample. Specifically, male employers offer
significantly lower wage contracts when faced with higher probability of
profits less than average from a worker. Interestingly, if we control
only for productivity distribution variance in the first model of the
full and employer samples, as might typically be done, this significant
effect would (incorrectly) be attributed to traditional risk aversion.
Our design is therefore able to discriminate between what looks like a
risk aversion effect to show that it is really a Joss aversion effect.
On the other hand, female employers did not significantly alter
wage contracts in response to changes in any of the distributional risk
variables. The result is consistent with females being risk or loss
neutral. It may also be the case that female employers possess similar
risk attitudes as male employers but with different subjective beliefs
regarding the productivity distributions (for example, optimism as to
the likely productivity draw from a distribution with larger support).
If beliefs as well as risk preferences are important determinants of
wage contracts, there may be systematic differences in both of these
across genders (for example, males being either less optimistic, or
having risk aversion that dominates any optimism toward the likely
productivity draw). Though we do not generate data on beliefs, we do not
consider optimism to be a likely explanation for our results. The reason
is that subjects were given very explicit details on the exact
productivity distribution.
Existing research on gender differences has shown that females are
generally less driven by competition and more averse to negotiations
than males (Niederle and Vesterlund 2007): That is, female employers
might negotiate worse outcomes (higher wage contracts) in general,
independent of the riskiness of the worker productivity distribution. In
our experiment employer payoffs are partly determined by one's
ability to compete with other employers while negotiating with workers
in the double-sided auction institution. Babcock and Laschever (2003)
document that females are generally more averse to negotiations than
males. If this aversion to competitive negotiations is most prominent
when worker productivity is uncertain, then this "negotiations
aversion" may interact with female risk attitudes toward worker
productivity. Across the seven treatments, the percentage of workers
that were female were 60%, 50%, 40%, 40%, 50%, 40%, and 80%; whereas,
the percentage of those female workers unemployed across all 80 wage
contracts (five employers times 16 rounds each) in the respective
sessions were 66%, 50%, 43%, 40%, 48%, 45%, and 76%. We do not therefore
find evidence to indicate that female workers are, on average, more
likely to be unemployed relative to male workers.
Suppose that female subjects in our sample are averse to
negotiations risk and expected payoffs are a function of the
productivity distribution risk as well as negotiations risk. If
employer-worker matching is essentially random, then we would expect
male employers and workers to have better contract outcomes than
females. Female employers would offer higher wages, on average, and this
would counteract any tendency to lower wages in response to worker
productivity distribution risk. We do not, however, find such evidence
that female employers offer higher wage contracts, ceteris paribus, or
that females do worse in mixed-gender negotiations. (6) Aversion to
negotiations may also manifest itself in gender-matching patterns, with
female employers more likely to contract with a female worker. That is,
women may be more averse to negotiating with men than with other women.
In our sample single-gender contracts--male-male or female-female
agreements--are statistically significantly more likely than
mixed-gender contracts (306 to 254 individual wage contracts: p = 0.01
for the one-sided binomial test). However, female employers contracting
with female workers (56% of the time) are not much more likely than male
employers contracting with male workers (53% of the time). Overall our
evidence with respect to female aversion to negotiations is weak. The
gender difference in those unemployed or the propensity for same sex
contracts is not great, and any such aversion is not displayed in the
wage contracts themselves.
There is thus only weak evidence that females may be more averse to
mixed-gender negotiations than males, but we do not find evidence that
women fare worse in mixed-gender pairs or that they offer generally
higher wage contracts. In short, the fact that females may be more
averse to competitive negotiations does not explain the wage results
from our gender-specific samples. Our experimental data indicate that
males react more significantly to the probability of loss than females.
Though we cannot fully explain the nature of this gender difference
result, the overall significance is that we find evidence for
statistical discrimination not based on average group differences.
Considering the labor market context, our full data sample results
indicate that this variable--a higher potential for less-than-average
payoffs--can significantly decrease the wage that an employer would pay
to workers from that more risky labor pool. (7)
The context of the statistical discrimination may be important for
this result, but it implies that individuals respond significantly to
increased distributional risk. If subjects feel somehow entitled to earn
expected profits, then, for the entire sample, we find evidence
consistent with statistical discrimination resulting from loss aversion.
We are careful to note that our experiments examine only a particular
range of variance and support of the productivity distribution. We do
not take these results to imply that distributional variance and support
are not behaviorally important measures of risk. Rather, we have shown
that a dominant influence on behavior may be loss probabilities. And,
because loss probability is not naturally independent of distribution
variance and support, it is important that our results identify this
more significant independent effect of loss probability on wage
contracts. It is indicative of the fact that the reference point of
average or expected profits is an important determinant of wage
negotiations outcomes.
4. Concluding Remarks
This article has examined a very simple framework for studying
second-moment statistical discrimination. In a general sense, this type
of statistical discrimination is really about how aversion to various
measures of risk might manifest themselves in a market setting. Despite
the strong competitive equilibrium convergence properties of the
double-auction institution, we were able to uncover indications of
statistical discrimination, mainly among male subjects. The robust
result from this study is that we find evidence of loss aversion among
employers; although, this is again only significant among male subjects.
Results from our female employer subsample indicate that females did not
alter wage contracts to workers from more risky productivity
distributions. This gender difference cannot be explained by a
hypothesis of female aversion to negotiations/competition in the
double-auction experiment environment. The only hypothesis consistent
with this result would be female risk- or loss-neutrality or a combined
effect of risk attitude and belief differences across gender. At this
point we have no explanation as to why there should be a gender
difference, though perhaps the labor market context we use may play a
role. We do not report the results here, but we also examined whether or
not the gender composition of the contract pair had any effect. The
results showed that gender composition of the contract pair had no
effect on wage contracts (these results are available on request).
There is an important message that emerges from these data.
Statistical discrimination can exist in many forms, and only the most
obvious forms of statistical discrimination--based on differences in
average productivity among worker-groups--are likely to be measured in
field studies. Even studies that examine distributional variance may not
be capturing all the statistical discrimination in the data.
Productivity risk from distinct worker-groups should be a concern, and
our results indicate that current measures of statistical discrimination
are predictably biased when this is not taken into account.
Specifically, statistical discrimination will be underestimated when one
ignores more hidden forms of this type of discrimination. (8)
Furthermore, measures of prejudice-based discrimination may be
overestimated if one fails to account for the likelihood that a certain
component of unexplained wage differentials is due to a form of
statistical discrimination not usually considered. Policy prescriptions
aimed at reducing discrimination in various markets may require
reassessment if the reason behind the discrimination has a different
motive than typically thought.
Appendix A: Instructions--EMPLOYERS
This is an experiment in economic decision making. Please read and
follow the instructions carefully. Your decisions, as well as the
decisions of others, will help determine your total cash payment for
participation in this experiment.
In this experiment, you are an Employer. Other individuals in the
experiment will be workers. As an employer, you will have the ability to
hire one unit of labor (at most) in each decision round from a pool of
workers. You may wish to do this because a unit of labor will be assumed
to produce a certain amount of output for you for that round. To keep
things simple, whatever output a unit of labor produces, we will assume
that you will sell each unit of that output for a market price of $1
(one experimental dollar). You will have the ability to hire a unit of
labor in each round for a series of decision-making rounds. In each
decision round, your experimental earnings will be determined by your
employer "profits." Profits are calculated as total revenues
minus total costs. Your employer profits in each round are then simple
to calculate--your total revenues are given by the quantity of output
that the unit of labor will produce for you (multiplied by the $1 that
you receive for each unit of output), and your total costs are just
given by whatever you agree to pay for the worker for his/her unit of
labor.
You will receive specific and more detailed instructions on labor
productivity shortly.
You are not required to purchase a unit of labor in each round.
Rather, if you do not purchase a unit of labor in a given round, your
profits for that round are zero (since total revenue and total cost are
zero). If you do hire a unit of labor in a given round, your profits for
that round will depend on both the productivity of labor (i.e., how much
output the unit of labor produces for you) and the wage that you pay for
that unit of labor. For example, if a worker produces three units of
output for you, and if you agree to pay that worker $2, then your
profits for that decision round would be $1 (remember, three units of
output are assumed to be sold by you for $1 each, and so total revenues
are $3). If, on the other hand, you agree to pay that worker S4, then
your profits for that round would be -$1. In other words, one dollar
would be subtracted from your total experimental earnings in that case.
As such, your experimental earnings would be higher if you did not hire
a unit of labor in a given round, as opposed to hiring a unit of labor
and earning negative profits. The way in which you earn money in this
experiment (through your profits) is private information to you and
should not be discussed with other employers or with the workers.
In this experiment, there are a total of 5 employers and 10
workers. Each worker in the experiment has the ability to sell one unit
of his labor to only one employer in each decision round, and each
employer can hire only one unit of labor per decision round. As an
employer, you will be allowed to freely "shop" around within
the pool of workers in your attempt to hire one unit of labor for the
round. Similarly, each worker will be allowed to freely shop among the
employers in order to sell his/her unit of labor. Each round will last
for a maximum of 2.5 minutes. The wages you and a worker mutually agree
to and your per-round experimental profits will be calculated on the
decision sheet that you have also been given. If you and a worker agree
on a wage for a given round, the decision sheet also includes a space
for you to document the identification number of the worker you
purchased your unit of labor from for that round.
FOR TODAY'S EXPERIMENT, YOUR CASH EARNINGS ARE RELATED TO YOUR
EXPERIMENTAL EARNINGS BY THE FOLLOWING EXCHANGE RATE: $1 EXPERIMENTAL =
$_J_U.S.
Specific (Treatment) Instructions for--EMPLOYER
TREATMENT 1
For the next few rounds, each of the workers in the worker pool
will be equally productive, and a unit of labor from any worker will
produce 3 units of output. As such, if you mutually agree with any
worker on hiring his/her unit of labor in a particular round, you know
that the productivity of the worker will be 3 units of output.
TREATMENT 2-4 (combined for exposition only)
For the next few rounds, different workers may have different
productivities, and you will not know the productivity of any given
worker until after you have hired a unit of labor from that worker. You
will, however, be given some general information on the entire group of
workers.
The pool of workers for the following rounds has these
characteristics (productivity refers to how many units of output a
worker's unit of labor will produce for you):
Treatment 2
10% chance that a worker has productivity of 1
10% chance that a worker has productivity of 2
60% chance that a worker has productivity of 3
10% chance that a worker has productivity of 4
10% chance that a worker has productivity of 5
Treatment 3
20% chance that a worker has productivity of 1
20% chance that a worker has productivity of 2
20% chance that a worker has productivity of 3
20% chance that a worker has productivity of 4
20% chance that a worker has productivity of 5
Treatment 4
50% chance that a worker has productivity of 2
50% chance that a worker has productivity of 4
Neither you nor the workers know exactly how productive a worker
will be until after the unit of labor is hired. You may seek to mutually
agree upon a wage with any worker, but you will not know his/her
productivity until after you have made your wage agreement with the
worker. The workers do not know how productive their labor will be for
an employer either. Workers see the same general worker characteristics
that you see above.
Once the round is over, for all employers who hired a unit of
labor, a random draw will be made from a Bingo cage to determine the
productivity of the unit of labor. A separate draw will be made for each
employer. Profits for each employer can then be calculated using the
random draw of productivity to determine the total revenue that is
generated by that unit of output. Your total costs are still just the
agreed-upon wage for the unit of labor that you hired.
Finally, it is important for you to realize that each new round
under this set of instructions will be conducted similarly. You may have
made a wage agreement with a particular individual in a previous round
which resulted in a productivity of 1,2, 3, 4, or 5. However, that does
not affect in any way the probabilities for productivity for a future
round, even if you re-hire the same person. In other words, if you make
an agreement with Jane Doe in round one, and the random productivity
draw says that the productivity for that unit of labor is 3, that does
not imply that you can make an agreement with the same Jane Doe in the
next round and be guaranteed a productivity of 3. The productivity that
Jane Doe's unit of labor provides for you or any other employer in
any round will always be determined by a new draw from the Bingo cage.
Each round should be treated as independent from any other round in
terms of determining worker productivity after agreements have been
made--even though the pool of workers is still physically composed of
the same individuals. Please raise your hand if this is confusing in any
way!
ALL TREATMENTS
Each decision round is 2.5 minutes long, and the experiment will
continue in this fashion until you are given different instructions. If
you and a worker agree on a wage for a given round, the decision sheet
also includes a space for you to document the identification number of
the worker you purchased your unit of labor from for that round.
Your decision sheet for these rounds is attached to these
instructions. Please raise your hand if at any point you have questions
about how each round will proceed and/or how to correctly fill out your
decision sheet.
[ILLUSTRATION OMITTED]
TOTAL PROFITS FOR THIS DECISION SHEET--
Appendix B: Instructions--WORKERS
This is an experiment in economic decision making. Please read and
follow the instructions carefully. Your decisions, as well as the
decisions of others, will help determine your total cash payment for
participation in this experiment.
In this experiment, you are a Worker. Other individuals in the
experiment will be employers. As a worker, you will have the ability to
sell one unit of labor (at most) in each decision round to only one
employer. You may wish to do this because selling a unit of labor will
provide you with a wage for that round. You will have the ability to
sell a unit of labor in each round for a series of decision-making
rounds. In each decision round, your experimental earnings will be
determined by the wage you can obtain from selling your unit of labor.
Employers may be interested in paying you a wage for your unit of labor
because your labor produces output for the employer, which we will
assume the employer can sell for profit.
You will receive specific and more detailed instructions on labor
productivity shortly.
You are not required to sell a unit of labor in each round. Rather,
if you do not sell a unit of labor in a given round, you will still earn
a minimal $.40 for that round. If you do sell your one unit of labor in
a given round, then your experimental earnings for that round will be
the wage you mutually agree upon with the employer. For example, if you
agree with an employer to sell your unit of labor for $1.00, then your
earnings for that round would be $1.00 (one experimental dollar). If you
agree with an employer to sell your labor for $.25, then your earnings
for that round would be $.25. If you do not sell your unit of labor to
any employer, then your earnings for that round are $.40. As such, your
experimental earnings would be higher if you did not sell your unit of
labor in a given round, as opposed to selling it for less than $.40. The
way in which you earn money in this experiment (through wages) is
private information to you and should not be discussed with other
workers or with the employers.
In this experiment, there are a total of 5 employers and 10
workers. Each worker in the experiment has the ability to sell one unit
of his labor to only one employer in each decision round, and each
employer can hire only one unit of labor per decision round. As a
worker, you will be allowed to freely "shop" around among the
employers in your attempt to sell one unit of labor for the round.
Similarly, each employer will be allowed to freely shop among the pool
of workers in order to hire his/her unit of labor. Each round will last
for a maximum of 2.5 minutes. The wages you and an employer mutually
agree to and your per-round experimental profits will be calculated on
the decision sheet that you have also been given. If you and an employer
agree upon a wage for a given round, the decision sheet also includes a
space for you to document the identification number of the employer you
sold your unit of labor to for that round.
FOR TODAY'S EXPERIMENT, YOUR CASH EARNINGS ARE RELATED TO YOUR
EXPERIMENTAL EARNINGS BY THE FOLLOWING EXCHANGE RATE: $1 EXPERIMENTAL =
$_1_U.S.
Specific (Treatment) Instructions for WORKER
TREATMENT 1
For the next few rounds, each of the workers in the worker pool
will be equally productive, and a unit of labor from any worker will
produce 3 units of output. As such, if you mutually agree with any
employer on selling your unit of labor in a particular round, the
employer will know that the productivity of your unit of labor will be 3
units of output.
TREATMENT 2-4 (combined for exposition only)
For the next few rounds, different workers may have different
productivities, and employers will not know the productivity of any
given worker until after the employer has hired (and you have sold) the
unit of labor. As a worker, you will not know either what your own
productivity will be for that employer until after your labor unit is
sold. You will, however, be given some general information on the entire
group of workers. The employers are given this general information as
well, and productivity refers to how many units of output a worker will
produce for the employer who purchases his/her unit of labor.
The pool of workers for the following rounds has these
characteristics:
Treatment 2
10% chance that a worker has productivity of 1 10% chance that a
worker has productivity of 2 60% chance that a worker has productivity
of 3 10% chance that a worker has productivity of 4 10% chance that a
worker has productivity of 5
Treatment 3
20% chance that a worker has productivity of 1 20% chance that a
worker has productivity of 2 20% chance that a worker has productivity
of 3 20% chance that a worker has productivity of 4 20% chance that a
worker has productivity of 5
Treatment 4
50% chance that a worker has productivity of 2 50% chance that a
worker has productivity of 4
Neither you nor the employers know exactly how productive a worker
will be until after the unit of labor is hired. You may seek to mutually
agree upon a wage with any employer, but the employer will not know your
productivity for that round until after you have made your wage
agreement with the employer.
Once the round is over, for all employers who hired a unit of
labor, a random draw will be made from a Bingo cage to determine the
productivity of the unit of labor (for the purposes of the
employer's calculation of profits). A separate draw will be made
for each employer. As a worker, your experimental earnings for each
round are still determined by the wage agreed upon with the employer (or
$.40 in a round when you do not sell your unit of labor to any
employer).
Finally, it is important for you to realize that each new round
under this set of instructions will be conducted similarly. An employer
may have made a wage agreement with you in a previous round which
resulted in a productivity of 1, 2, 3, 4, or 5. However, that does not
affect in any way the probabilities for your productivity for a future
round. In other words, if you make an agreement with an employer in
round one, and the random productivity draw says that the productivity
for your unit of labor is 3, that does not imply that your productivity
is guaranteed to be 3 in the next round. The productivity that your unit
of labor provides to any employer (even the same one) in any round will
always be determined by a new draw from the Bingo cage. Each round
should be treated as independent from any other round in terms of
determining worker productivity after agreements have been made---even
though the pool of workers is still physically made of the same
individuals. Please raise your hand if this is confusing in any way!
ALL TREATMENTS
Each decision round is 2.5 minutes long, and the experiment will
continue in this fashion until you are given different instructions. If
you and an employer agree upon a wage for given round, the decision
sheet also includes a space for you to document the identification
number of the employer you sold your unit of labor to for that round.
Your decision sheet for these rounds is attached to these
instructions. Please raise your hand if at any point you have questions
about how each round will proceed and/or how to correctly fill out your
decision sheet.
[ILLUSTRATION OMITTED]
TOTAL PROFITS FOR THIS DECISION SHEET--
Received April 2008; accepted September 2008.
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(1) Cornell and Welch (1996) consider that it is less costly to
assess workers with similar backgrounds; thus a "screening"
discrimination results. Lang (1986) also considers discrimination from
differential communication costs across groups.
(2) Additional evidence of statistical discrimination is found in
mortgage lending (Ladd 1998). car price negotiations (Ayers and
Siegelman 1995; Goldberg 1996; Harless and Hoffer 2002), sports card
price negotiations (List 2004), vehicle repair estimates (Gneezy and
List 2006). and law enforcement decisions (Applebaum 1996). See also the
discussion in Loury (1998).
(3) That is, workers are assigned cost values and paid the
difference between the negotiated wage and the assigned cost value.
Employer demand values depend on the productivity of the worker hired,
and employers are paid the difference between the marginal revenue
product of the worker and the negotiated wage.
(4) Average wage contracts for each of treatments 1, 2, 3, and 4
were 0.65 ([sigma] = 0.36), 0.62 ([sigma] = 0.26), 0.57 ([sigma] =
0.26), and 0.54 ([sigma] = 0.25), respectively.
(5) As before, the random effects estimates are identical to those
from fixed effects or OLS specifications due to our particular design,
though the estimated standard errors in OLS will differ from those in
fixed or random effects (see Oaxaca and Dickinson 2005).
(6) We conduct a wage regression identical to the full employer
sample in Table 4, while including a dummy variable for female employer.
The coefficient on this variable is statistically no different from zero
(p = 0.84). We also find statistically insignificant effects of
gender-composition dummy variables. These results are available from the
authors on request.
(7) This result is due to the single-period framework we utilize.
In a multiperiod framework where market participants can have repeated
interactions, this result may not hold.
(8) This assumes that groups with lower average productivity are
the same groups that have riskier distributions. Otherwise, these two
forms of statistical discrimination would have opposing effects in the
data.
David L. Dickinson, Department of Economics, Appalachian State
University, Boone, NC 28607, USA; E-mail dickinsondl@appstate.edu;
corresponding author.
Ronald L. Oaxaca, Department of Economics, University of Arizona,
Tucson. AZ 85721-0108, USA; E-mail rlo@u.arizona.edu.
The authors are grateful for research funding made possible by the
McClelland Professorship. Valuable comments were provided by Bob Slonim,
Todd Sorensen, and participants at the Economic Science Association
meetings in Tucson.
Table 1. Experiment Treatment Design
Description Productivity Productivity
Treatment (Probability) Mean
1 3 (1.00) 3
21 1,2,3,4,5 (0.1, 0.1, 0.6, 0.1, 0.1) 3
31 1,2,3,4,5 (0.2, 0.2, 0.2, 0.2, 0.2) 3
4 2,4 (0.5, 0.5) 3
Productivity Likelihood of
Productivity Distribution Productivity < Mean
Treatment Variance Support Productivity
1 0 3 0
21 1 1-5 0.20
31 2 1-5 0.40
4 1 2-4 0.50
Table 2. Wage Contracts (Random Effects)
Full Employer Sample Male Employer Sample
Variable Coeff. Std Error Coeff. Std Error
Constant 0.861 0.038 *** 0.906 0.061 ***
T2 -0.003 0.029 -0.063 0.042
T3 -0.028 0.036 -0.069 0.049
T4 -0.062 0.029 ** -0.116 0.044 ***
Round 2 -0.119 0.028 *** -0.116 0.039 ***
Round 3 -0.143 0.028 *** -0.153 0.039 ***
Round 4 -0.149 0.028 *** -0.167 0.039 ***
T02 -0.181 0.034 *** -0.154 0.048 ***
T03 -0.183 0.029 *** -0.193 0.042 ***
T04 -0.186 0.029 *** -0.177 0.044 ***
[R.sup.2] 0.137 0.168
Nobs 560 240
Female Employer Sample
Variable Coeff. Std Error
Constant 0.812 0.050 ***
T2 0.048 0.042
T3 0.012 0.052
T4 -0.027 0.039
Round 2 -0.121 0.039 ***
Round 3 -0.135 0.039 ***
Round 4 -0.135 0.039 ***
T02 -0.193 0.048 ***
T03 -0.153 0.041 ***
T04 -0.172 0.040 ***
[R.sup.2] 0.123
Nobs 320
** and *** indicate significance at the 0.05 and 0.01 levels,
respectively, for the two-tailed test.
Table 3. Binary Comparisons among the Uncertain Productivity Treatments
Full Employer Sample Male Employer Sample
Comparison Coeff. Diff. Std Error Coeff. Diff. Std Error
T3-T2 -0.025 0.031 -0.006 0.041
T4-T2 -0.059 0.030 ** -0.053 0.049
T4-T3 -0.034 0.036 -0.047 0.051
Nobs 560 240
Female Employer Sample
Comparison Coeff. Diff. Std Error
T3-T2 -0.036 0.046
T4-T2 -0.075 0.043 *
T4-T3 -0.039 0.053
Nobs 320
Coefficient comparisons from Table 2 results.
* and ** indicate significance at the 0.10 and 0.05 levels,
respectively, for the two-tailed test.
Table 4. Wage Contracts with Alternative Measures of Risk
(Random Effects)
Full Employer Sample
Variable Coeff. Std Error Coeff. Std Error
Constant 0.863 0.037 *** 0.861 0.038 ***
Variance -0.023 -0.017 0.006 0.042
Support 0.056 0.123
Loss Prob. -0.159 0.092 *
Round 2 -0.119 0.028 *** -0.119 0.028 ***
Round 3 -0.143 0.028 *** -0.143 0.028 ***
Round 4 -0.149 0.028 *** -0.149 0.028 ***
T02 -0.165 0.033 *** -0.181 0.034 ***
T03 -0.197 0.028 *** -0.183 0.029 ***
T04 -0.199 0.028 *** -0.186 0.034 ***
[R.sup.2] 0.132 0.137
Nobs 560 560
Male Employer Sample
Variable Coeff. Std Error Coeff. Std Error
Constant 0.898 0.060 *** 0.906 0.061 ***
Variance -0.042 0.024 * 0.048 0.058
Support -0.141 0.17
Loss Prob. -0.273 0.136 **
Round 2 -0.116 0.038 *** -0.116 0.039 ***
Round 3 -0.153 0.038 *** -0.153 0.039 ***
Round 4 -0.167 0.038 *** -0.167 0.039 ***
T02 -0.143 0.047 *** -0.154 0.048 ***
T03 -0.213 0.040 *** -0.193 0.042 ***
T04 -0.218 0.039 *** -0.177 0.044 ***
[R.sup.2] 0.159 0.168
Nobs 240 240
Female Employer Sample
Variable Coeff. Std Error Coeff. Std Error
Constant 0.826 0.048 *** 0.812 0.050 ***
Variance -0.001 0.025 -0.014 0.062
Support 0.209 0.176
Loss Prob. -0.108 0.129
Round 2 -0.121 0.039 *** -0.121 0.039 ***
Round 3 -0.135 0.039 *** -0.135 0.039 ***
Round 4 -0.135 0.039 *** -0.135 0.039 ***
T02 -0.185 0.045 *** -0.193 0.048 ***
T03 -0.176 0.039 *** -0.153 0.041 ***
T04 -0.177 0.039 *** -0.172 0.040 ***
[R.sup.2] 0.116 0.123
Nobs 320 320
*, **, and *** indicate significance at the 0.10, 0.05, and 0.01
levels, respectively, for the two-tailed test.
