Decomposing Desert and Tangibility Effects in a Charitable
David Reinstein and Gerhard Riener
Several papers have documented that when subjects play with standard laboratory “endow-
ments” they make less self-interested choices than when they use money they have either
earned through a laboratory task or brought from outside the lab. In the context of a chari-
table giving experiment we decompose this into two common artifacts of the laboratory: the
intangibility of money (or experimental currency units) promised on a computer screen rela-
tive to cash in hand, and the distinct treatment of random “windfall” gains relative to earned
money. While both effects are found to be signiﬁcant in non-parametric tests, the former
effect, which has been neglected in previous studies, has a stronger impact on total dona-
tions, while the latter effect has a greater impact on the probability of donating. These results
have clear implications for experimental design, and also suggest that the availability of more
abstract payment methods may increase other-regarding behavior in the ﬁeld.
Several economists have found that when subjects play with standard laboratory “endow-
ments” they make less self-interested choices than when they use money they have either
“earned” through a laboratory task or brought from outside the lab (Cherry et al. 2002; Hoff-
man and Spitzer 1985; Loomes and Burrows 1994). This effect is typically interpreted as a
result of Lockean desert effects (Rutstrom and Williams 2000; see Locke 1988, pp. 287-8.),
fairness concerns (a la Rabin 1993), or a different mental accounting over windfall gains
(Sheffrin and Thaler 1988, Thaler 1985, and Thaler and Johnson 1990). Our experiment does
not differentiate between these models (this is left for future research); we will refer to the
Preprint submitted to Elsevier July 21, 2011
net effect of these as the windfall effect.
There is ample evidence for windfall effects in the context of dictator games. Cherry et al.
(2002) ran a series of dictator game experiments where, in the baseline treatment the dictator’s
endowment was randomly determined, while in their earnings treatment the endowment was
based on performance in a cognitive task (solving GMAT questions), and this was common
knowledge. Their double blind with earnings treatment modiﬁed the earnings treatment
to increase subject-experimenter anonymity. Both their earnings and double-blind-earnings
treatments lead to signiﬁcantly less generous dictator behavior; in the latter treatment the
dictators became almost entirely hardnosed, keeping nearly all of the money.
Oxoby and Spraggon (2008) compare dictator behavior in treatments adapted from Hoff-
man et al. (1996), comparing a case where the funds to be divided are “earned” by the dicta-
tor’s quiz performance to a case where the potential recipient takes the quiz (to determine the
amount available for the dictator to divide). They ﬁnd that dictators are signiﬁcantly more
generous in the latter case. This suggests that fairness concerns are important, and that rela-
tive desert may be driving dictator decisions. Rufﬂe (1998), Mittone and Ploner (2006), and
Cherry and Shogren (2008) ﬁnd similar results on the importance of the receiver’s effort.1
In contrast to the dictator environment, there is little evidence for windfall effects in
voluntary contribution mechanism (henceforth VCM) experiments. Clark (2002) examines
contribution rates in a VCM game. He ﬁnds no signiﬁcant difference between contributions
in the “own money” treatment, in which subjects are asked to bring $8 from outside the lab
to purchase tokens, and the “house money” treatment, in which subjects are simply given the
tokens.2However, as Clark’s “own money” subjects are also given house money at the end
1In all of the experiments mentioned above the dictator subjects’ “earnings” come from answering GMAT
questions, some of which involve retailers’ and consumers’ decisions, dishonest job applicants, wealth, invest-
ments, money, and marketing. These may be triggering more self-interested behavior through a framing effect
as in Vohs et al. (2006) and Cookson (2000), rather than simply increased legitimacy of the dictators’ own en-
dowments. However, the estimated relationships between the dictators’ gifts and the recipient’s performance,
hence the observations of a fairness (or relative desert) motive is robust to this critique; the variation in the
recipient’s performance does not yield any additional framing effect of this sort.
2Still, Harrison (2007), who reanalyzed Clark’s data to deal with the potentially non-independent error
structure, suggests that a house money effect is present. However, the tangibility and earnings effects are not
of the experiment, they presumably have the same expected “windfall” earnings as the other
subjects. Furthermore, Clark’s subjects use tokens, and the earnings effect may be more
salient when the rewards are more tangible. In related VCM experiments, neither Cherry
et al. (2005) nor Kroll et al. (2007) ﬁnd that subjects who earned their endowments (through
answering GMAT questions) contribute less than those who did not.
Finally, there is some very recent evidence in the context of charitable giving itself. Carls-
son et al. (2009) ﬁnd windfall effects in a charitable giving experiment in both a laboratory
and a ﬁeld setting; subjects in both environments donate less when they have “earned” their
pay by completing a survey.
This literature has ignored a second component of the bias that may limit the external
validity of many laboratory results: people may treat money they are promised (or are given
in the form of tokens) differently then cash they physically hold – we call this the tangibility
effect We hypothesize three potential reasons why this may occur. First, psychology exper-
iments demonstrate that subjects given “reminders of money” are both less helpful and less
likely to ask for help in a variety of non-remunerated tasks (Vohs et al., 2006).In addition,
Cookson (2000) ﬁnds that subjects subtly motivated with an “I” frame contribute less in a
VCM setting than those motivated with a “we” frame, and Oberholzer-Gee and Eichenberger
(2004) ﬁnd that offering an unattractive lottery option to the choice set leads dictators to
give less to other subjects.Second, using cash may cause subjects to more carefully consider
the consumption they are sacriﬁcing. Along similar lines, Oberholzer-Gee and Eichenberger
(1999) argue that subjects do not fully consider the opportunity costs of the funds they give
away in experiments, and Mazar et al. (2008) ﬁnd that people cheat more when using ex-
changeable tokens then when they use cash. Finally, parting with cash may itself bring some
disutility, perhaps through an attachment to this money similar to the “endowment effect” of
Kahneman et al. (1991). For all of these reasons, we might therefore expect that subjects
holding cash will be less likely to contribute this to a public good or a charitable cause.
separable in this context.
To the best of our knowledge, there is no economic evidence on the effect of the medium
of exchange on generosity. However, at least one prominent experiment varies this in con-
junction with other variations in the treatment, leading to a potential confound.3In the present
paper we implement a real charitable giving experiment to provide the ﬁrst salient economic
evidence that the tangibility of the choice medium affects other-regarding decisions.
2. Experimental design
We use a charitable giving experiment with a 2⇥2 design to differentiate two distinct arti-
facts of laboratory endowments. Firstly, the treatments vary according to the extent to which
subjects should see the money as earned; we compare giving behavior after compensation
based on performance on a ﬁve minute task to behavior with a randomly assigned payment.
The second dimension of variation involves the tangibility of the payment: we either give
cash to the subjects before they decide how much to donate (and they physically place any
donations they make into envelopes) or they allocate their donation from an endowment on
the computer screen and they are paid cash at the end of the experiment. Thus, we separately
test whether earning the money and having cash in hand affect giving behavior in the lab.4
Unlike many of the experiments previously mentioned, our subjects make decisions over
donations to charitable foundations – institutions outside the laboratory. In line with Eckel
and Grossman (1996), we see this as a more obvious and typical expression of other-regarding
behavior than donations to a laboratory public good or towards another laboratory subject.
Our environment also provides a more demanding test for tangibility and windfall effects. In
the real world it is rare to be asked for a gift from a random non-needy stranger (or to re-
ceive such a gift); hence, it is not surprising that standard dictator games should be sensitive
to framing effects. On the other hand charitable appeals and charitable giving are regular-
3E.g., in Hoffman et al. (1996) the "single blind 2" treatment combines both a decreased social distance from
the experimenter (relative to "single blind 1") and "a decision form for making the decision, instead of money".
4In addition to the treatments mentioned above, we also vary the choice set. As a robustness check, we offer
three charities instead of two in the expanded choice set treatment. This allows us to demonstrate that our results
are not sensitive to a variation in the choice set.
ities, so subjects will have more experience with such decisions and their decisions should
be less easily perturbed. While dictator giving to other subjects is highly sensitive to the
level of social isolation, falling to very low levels in “double-blind” environments Hoffman
et al. (1996)), charitable giving persists at signiﬁcant levels even under highly anonymous
conditions (Eckel and Grossman, 1996). Our setting may also better isolate the effect of asset
legitimacy: intuition suggests that in the charitable giving context, subjects will focus less
on their desert relative to the recipient(s) then they would in deciding how much to give to a
All treatments are assigned orthogonally; we have a (nearly) fully balanced design.5By
construction, the distribution of initial endowments is the same for each treatment. Finally,
all of our treatments involve the same strong level of anonymity.6The time spent in each
treatment of our experiment is approximately the same, so subjects in each of our treatments
should have the same earnings expectations.
The sessions were run at the University of Jena Experimental Economics lab using the
standard subject pool. In total 190 subjects participated in the experiments of which 54.2%
were female.7The sessions were conducted in October 2008 (39 subjects), February 2009
(79 subjects), and September 2009 (72 subjects). While we ran each of the four payment
regime treatments in a separate session, the participants were from the same subject pool and
the times and dates of the experiment were stratiﬁed by treatment.8To avoid mixing payment
types, we did not give subjects any pre-experiment “show-up fee.”
5Because the treatments were run in separate sessions and their were some no-shows, the actual observations
are very slightly off-balance, and the endowments are not precisely identically distributed by treatment, nor is
the “choice set” treatment. However, these slight differences are controlled for in our multivariate regressions
and in our balanced bootstrapped rank-sum tests. The lack of balance does not measurably affect any of our
results. Our treatments are also not perfectly balanced over time. To test for session-speciﬁc effects, in online
Appendix 5 Table 5 we also report regressions with standard errors clustered by session, and controls for time-
of-day and date of session effects; our results are robust to all of these, and none of these are signiﬁcant.
6See the protocol in online Appendix 1 for a full description of our careful procedure to insure subject-
experimenter and subject-subject anonymity.
7We did not collect extensive demographics on our subjects in order to preserve subject-experimenter
8Appendix 5, Table 4 illustrates this balance, and shows our results are insensitive to the time and date of
To guarantee anonymity, the lab was divided into an outer partition - which serves as a
meeting room before the experiment and as a room for the administrators during the experi-
ment - and an inner partition with computer terminals on which the subjects make decisions
and answer questions. These were separated so that it was impossible to see the inner parti-
tion from the the outer partition and vice-versa. For administrative purposes, a volunteer from
the participants helped with the procedures whenever communication between the inner and
the outer part of the lab was necessary. Furthermore, to ensure our credibility, this volunteer
supervised the online donations made by the experimenters after the other participants had
At the beginning of the experiment all subjects were assured that we would not be able to
connect their name to the decisions they made. Next we asked for a volunteer to help us with
administrative issues, mainly allocating the sealed envelopes with payouts at the end of the
The task. Subjects in the performance treatments (PA and PC, described below) were told
that their endowment would depend on their performance on a simple task. They were asked
to add up ﬁve two-digit numbers9using only scratch paper and a pencil. The numbers were
randomly drawn and presented to the subjects as in the example below:
12 77 34 55 62 __
The participants were given ﬁve minutes to solve as many tasks as possible. We argue that
this task was sufﬁciently tedious to make subjects feel that they earned the money recieved.
This task, although numerical, is less likely to cue self-interested “economic” thinking than
the GMAT questions used in many previous studies.
The charitable giving stage (donation decision). The subjects were not given any indication
that this experiment would involve an opportunity for charitable giving until they reached the
9This task has been used in various occasions for testing competitiveness (e.g., Niederle and Vesterlund,
“charitable giving stage”. This stage was a one-shot dictator game in which subjects could
donate none, some, or all of their endowment to any combination of the available charities
in units of 50 Euro cents. All subjects were presented with Brot für die Welt (BfdW) –
“Bread for the World”, a German development aid agency and the World Wild Life Fund for
Nature (WWF), a nature conservancy charity. For the expanded choice set treatment we also
included Deutsches Rotes Kreuz (DRK) - the German Red Cross - which operates in similar
areas as BfdW. Subjects were given information about each of the charities on the computer
screen and next had to decide how much (if anything) to donate to each available charity and
enter this into the computer.10 By using multiple charities we reduced the noise surrounding
heterogeneous tastes for charities, and gained more useful data on a wider range of subjects.
Treatment 1: Performance / (on-screen) Account (PA). Subjects in the performance treat-
ments were told that the probability of higher earnings increased in the number of tasks cor-
rectly completed, but we did not specify exactly how performance translated into payoffs.11
After completing the task they were told how much this earned them. In account treatments
they were endowed C5, C7.50 or C10 (shown on their computer screen) but were not yet
given cash.They next made their donation decisions. At the end of the experiment they were
(anonymously) given envelopes containing their earnings minus their total donations.
Treatment 2: Performance / Cash (PC). As in PA, subjects ﬁrst completed the task and
learned how much they earned. However, unlike in the account treatments, subjects in cash
treatments were paid in cash before they made giving decisions. After the task stage, the
volunteer was prompted to come outside and bring the numbered envelopes containing the
10The order of the presentation of the charities, both on the description screens and on the actual donation
screen are stratiﬁed over subjects, in order to balance any potential order effects.
11We did not tell them that their pay was based on relative performance. They were instead told that “the
more sums you solve, the more likely it is that you will get a higher payment” (in German: “Je mehr Aufgaben
Sie lösen desto wahrscheinlicher ist es, dass sie mehr verdienen.”), because we did not want them to compare
themselves to other subjects in making their charitable contributions. Such a comparison might have lead them
to believe that that subjects who earned more had a greater obligation to donate. In the treatments of October
2008, the subject who solved the most sums received C10, the second C7.50 and the rest of the subjects in the
same session got C5. In the sessions conducted in February, March, and September 2009, the participants who
were in the upper tercile of solved tasks received C10, in the middle tercile C7.50 and in the lower tercile C5.
cash earnings into the inner part , where they hand each subject the envelope with his or her
subject number on it. The payment envelopes were carefully assembled to look identical and
have similar weights.12 Subjects were instructed to inspect and count the money in private at
their computer desks. Next, they made their donation decision(s) by entering these choices
on the computer screen. Finally, subjects were asked to put the chosen contributions (in cash)
into the donation envelope and seal it.
Treatment 3: Random / on screen Account (RA). In this treatment, subjects were endowed
C5, C7.50 or C10 randomly on their computer screen. The donation stage followed, and
payments were distributed as in PA.
Treatment 4: Random / Cash (RC). In the RC treatment the endowments were randomly
determined (as in RA), and given to the subjects in identical envelopes as in PC. The donation
and payments procedure also followed PC.
3.1. Summary Statistics
Table 1 compares the proportion of the endowments donated to any of the two (or three)
charities, pooling across choice set treatments.13 Subjects donated signiﬁcantly less14 when
they were paid in cash than when their endowment was only shown on the computer screen
(13% versus 23% of the total funds, pooling across all other treatments).15
Figure 1 shows the cumulative distribution of the share of earnings donated over the earn-
ings and payment treatments. The distribution of contributions under on-screen entitlements
12We did this by using coins of different increments. To the extent that small coins are less desirable then
bills this would lead to a bias against our ﬁnding of a tangibility effect. Since payments in performance and
random treatments had the same distribution, this should not impact our “earnings effect” ﬁndings.
13We performed robustness checks and found no signiﬁcant differences in contribution behavior between the
two and three charity choice set treatments. Details available by request.
14These differences are signiﬁcant in Wilcoxon rank-sum tests, as well as in familiar parametric tests (avail-
able by request). Because of the aforementioned lack of balance (stemming from no-shows), we also report
bootstrapped rank-sum tests in brackets, with each of the 1000 random draws (with replacement) exactly bal-
anced by payment treatment, earnings treatment, choice set treatment, and stake size.
15This rate of giving is fairly consistent with results of previous experiments. E.g., in Eckel and Grossman
(1996) subjects give 30% of their $10 cash endowment (they were also given a $5 show-up fee).
Table 1: Average proportion contributed by payment regimes
Endowment Random Performance Total N
Account 0.27 0.18 0.23 99
Cash 0.14 0.12 0.13 91
Total 0.21 0.15 0.18
N102 88 190
Wilcoxon rank sum tests
P(Account> Cash) 0.57+ (0.06); [0.05]
P(Random> Performance) 0.58* (0.05); [0.03]
P(Account/Random > Cash/Performance) 0.64** (0.01); [0.00]
P(Account/Random > Cash/Random) 0.61+ (0.06); [0.05]
P(Account/Performance > Cash/Performance) 0.53 (0.59); [0.57]
P(Account/Performance > Cash/Random) 0.49 (0.86); [0.85]
p-values for simple rank sum tests in parentheses, +: p< 0.10, *: p<0.05, **: p<0.01
In square brackets: p-values for bootstrapped rank sum tests, 1000 draws, balanced by all treatments and stake sizes.
(RA and PA) stochastically dominates the distribution under cash payments (RC and PC).
Similarly, the distribution under random payments (RA and RC) stochastically dominates the
distribution under performance-based earnings (PA and PC).
Figure 1: Cumulative distribution functions of share of earnings donated
On the other hand, as Table 2 demonstrates, the performance treatment has a stronger
extensive margin effect; subjects are signiﬁcantly less likely to donate at all if they have
earned their endowment through their performance. To give an intuitive spin, some people
may feel more comfortable keeping all of their money if they think they have earned it and
thus deserve it, while those who do feel compelled to donate ﬁnd that giving away cash feels
Table 2: Number of subjects who donated by treatment
Random Performance Account Cash
Donated N(column %) N(col. %) N(col. %) N(col. %)
No 37 (36%) 44 (50%) 42 (42%) 39 (43%)
Yes 65 (64%) 44 (50%) 57 (58%) 52 (57%)
Total number 102 88 99 91
p-values of tests
Pearson c20.06 0.95
Fisher’s exact 0.07 1.00
more “costly” in terms of sacriﬁced consumption than giving away money on a computer
screen. This result is conﬁrmed by our Probit regressions with controls for endowment size,
gender, and the larger choice set (see Appendix 4).
3.2. Multivariate Analysis
To control for observable (random) differences in treatment assignment we regress total
donations on controls for observable heterogeneity and treatment interactions.16 These re-
gressions (Table 3) again suggest that cash treatments reduced generosity. The effect of cash
is negative and signiﬁcant in the Account treatments, and negative but insigniﬁcant in Per-
formance treatments (summed coefﬁcient: Cash+cash ⇥perform).17 Donations were also
lower when subjects were paid according to their performance, but this effect was not statisti-
cally signiﬁcant here. The coefﬁcients on higher stake sizes ( C7.5 or C10) are small and not
signiﬁcant: subjects who earn more do not tend to donate more. In line with some previous
work, (e.g., Eckel and Grossman, 1998, List, 2004) women donated more than men. Total
donations were not signiﬁcantly different when a third charity was included. The interaction
16We use a standard OLS speciﬁcation for familiarity and comparability reasons. We also use a Poisson spec-
iﬁcation, both because our data resembles count data (in increments of 50 cents) and because this speciﬁcation
deals with corner-solution (non-negative) data without being as sensitive to non-normality and heteroskedastic-
ity as a standard Tobit regression Gourieroux et al. (1984); Arabmazar and Schmidt (1981). In online Appendix
5 (table 5) we ﬁnd similar results using a fractional regression speciﬁcation. The cash and performance results
are similar in zero-inﬂated Poisson regressions (available by request).
17The “Cash” dummy is also strongly signiﬁcant in a univariate linear (-0.66; p-value: <0.01) or Poisson
regression (-0.66, marginal effect; p-value: <0.01) (details by request).
effects are not signiﬁcant, although their positive sign and magnitude suggest that the treat-
ments have a sub-additive effect – the summed coefﬁcient (Cash+perform+cash ⇥perform)
representing the effect of cash and performance combined is very close to the coefﬁcient on
Table 3: Poisson and OLS regression of total donations
Add. contr. Gender contr.
(1) (2) (3) (4) (5) (6)
Psn. OLS Psn. OLS Psn. OLS
Pay cash -0.84* -0.84* -0.68* -0.84* -0.88* -0.89**
(0.33) (0.33) (0.31) (0.34) (0.38) (0.34)
Pay by performance -0.54 -0.54 -0.44 -0.54 -0.56 -0.58
(0.39) (0.39) (0.33) (0.40) (0.42) (0.41)
Cash ⇥performance 0.51 0.44 0.41 0.44 0.69 0.56
(1.02) (0.49) (0.82) (0.50) (1.14) (0.52)
Third charity 0.34 0.26 0.42 0.26
(0.33) (0.25) (0.40) (0.24)
Stake: 7.5 -0.18 -0.13 -0.14 -0.08
(0.36) (0.29) (0.44) (0.28)
Stake: 10 0.10 0.093 0.10 0.10
(0.37) (0.32) (0.44) (0.31)
Female 0.63* 0.53*
Combined coefﬁcients (sums raw coefﬁcients, not marginal effects)
Cash+perform+cash ⇥perform -0.76* -0.94** -0.76* -0.94** -0.73* -0.92**
( 0.32) ( 0.37) ( 0.32) ( 0.37) ( 0.31) ( 0.36)
Cash+cash ⇥perform -0.39 -0.40 -0.39 -0.40 -0.35 -0.34
(0.36) (0.36) (0.36) (0.36) (0.36) (0.38)
Observations 190 190 190 190 190 190
R20.048 0.056 0.079
Pseudo R20.033 0.039 0.055
Heteroskedasticity-robust standard errors in parentheses.
+ p<0.10, * p<0.05, ** p<0.01 for tests using heteroskedasticity-robust standard errors (for all columns)
All regressors are dichotomous (0,1) variables, dy/dx for discrete change of dummy variable reported.
Marginal effects evaluated at Account/Random, Female, Stake = 7.5, two charity choice set.
As we show in online Appendix 5, table 3, the tangibility and windfall effects on dona-
tions are similar across charities, and our results also hold for a fractional response (Papke
and Wooldridge, 1996) regression of “share donated”.
Our experiment is the ﬁrst to document the tangibility effect; its magnitude appears at
least as strong as the windfall effect, although the latter has a stronger effect at the extensive
margin. Furthermore, by using a charitable giving context and a relatively neutral real-effort
task, we add to the evidence that the legitimacy (absolute desert) of experimental subjects’
own assets affects their other-regarding behavior.
Our ﬁndings do not imply that experimenters should always use “tangible” cash. In the
context of our experiment, we cannot say which contribution level is more externally valid.
Whether the differences are because seeing money cues self-interest, because cash causes a
more careful consideration of trade-offs, or because parting with cash is more painful, either
frame (cash or endowment) may have external validity.18 In the ﬁeld many decisions are
made without physical cash, as credit cards and electronic payments have become dominant
in many markets. However, researchers must be aware of this framing effect and take it
into account. This distinction is important: economic experiments vary greatly along both
dimensions, often simultaneously. As noted in Hoffman et al. (1994), comparisons between
experimental results must take into account differences in the decision medium.19 To the
extent that future income is less tangible than present income, our results agree with Breman
Breman (2006), who offers ﬁeld experimental evidence that people are more generous with
the former than with the latter. Similarly, our result that the payment instrument matters
may also be generalizable to real-world decision making, particularly over intangible “warm-
glow” goods such as charitable donations.
18On the one hand, cash is obviously better if it leads to greater experimenter credibility. However, this is
unlikely to have been a driver of our results, as all of our subjects had previously participated in economic
experiments. On the other hand, cash may lead to other extraneous effects; e.g., it may cue subjects to consider
the nuisance carrying around earnings that include “small change”.
19In comparing their dictator results to those of Forsythe et al. (1994), Hoffman et al note that "other aspects
of the double blind procedures require experimental examination to identify what is driving the outcome; an
envelope containing the cash might be an important factor." Our analysis conﬁrms this speculation.
Arabmazar, A. and P. Schmidt (1981). Further evidence on the robustness of the Tobit esti-
mator to heteroskedasticity. Journal of Econometrics 17(2), 253–258.
Breman, A. (2006). Give more tomorrow: Evidence from a randomized ﬁeld experiment.
Carlsson, F., H. He, and P. Martinsson (2009). Easy come, easy go-The role of windfall
money in lab and ﬁeld experiments. rapport nr.: Working Papers in Economics 374.
Cherry, T., P. Frykblom, and J. Shogren (2002). Hardnose the Dictator. American Economic
Review 92(4), 1218–1221.
Cherry, T., S. Kroll, and J. Shogren (2005). The impact of endowment heterogeneity and
origin on public good contributions: Evidence from the lab. Journal of Economic Behavior
and Organization 57(3), 357–365.
Cherry, T. and J. Shogren (2008). Self-interest, sympathy and the origin of endowments.
Economics Letters 101(1), 69–72.
Clark, J. (2002). House Money Effects in Public Good Experiments. Experimental Eco-
nomics 5(3), 223–231.
Cookson, R. (2000). Framing effects in public goods experiments. Experimental Eco-
nomics 3(1), 55–79.
Eckel, C. and P. Grossman (1996). Altruism in anonymous dictator games. Games and
Economic Behavior 16(2), 181–191.
Eckel, C. and P. Grossman (1998). Are women less selﬁsh than men?: Evidence from dictator
experiments. The Economic Journal 108(448), 726–735.
Forsythe, R., J. Horowitz, N. Savin, and M. Sefton (1994). Fairness in simple bargaining
games. Games and Economic Behavior 6(3), 347–69.
Gourieroux, C., A. Monfort, and A. Trognon (1984). Pseudo maximum likelihood methods:
applications to Poisson models. Econometrica 52(3), 701–720.
Harrison, G. (2007, December). House money effects in public good experiments: Comment.
Experimental Economics 10(4), 429–437.
Hoffman, E., K. McCabe, K. Shachat, and V. Smith (1994). Preferences, property rights, and
anonymity in bargaining games. Games and Economic Behavior 7(3), 346–380.
Hoffman, E., K. McCabe, and V. Smith (1996). Social Distance and Other-Regarding Behav-
ior in Dictator Games. American Economic Review 86, 653–660.
Hoffman, E. and M. Spitzer (1985). Entitlements, rights, and fairness. Journal of Legal
Studies 14(2), 259–297.
Kahneman, D., J. Knetsch, and R. Thaler (1991). Anomalies: The endowment effect, loss
aversion, and status quo bias. The Journal of Economic Perspectives 5(1), 193–206.
Kroll, S., T. Cherry, and J. Shogren (2007). The impact of endowment heterogeneity and
origin on contributions in best-shot public good games. Experimental Economics 10(4),
List, J. (2004). Young, Selﬁsh and Male: Field evidence of social preferences*. The Eco-
nomic Journal 114(492), 121–149.
Locke, J. (1988). Two Treatises of Government. Cambridge: Cambridge University Press.
Loomes, G. and P. Burrows (1994). The impact of fairness on bargaining behaviour. Empir-
ical Economics 19, 201–221.
Mazar, N., O. Amir, and D. Ariely (2008). The Dishonesty of Honest People: A Theory of
Self-Concept Maintenance. Journal of Marketing Research 45(6), 633 – 644.
Mittone, L. and M. Ploner (2006). Is it just legitimacy of endowments? an experimental
analysis of unilateral giving. CEEL Working Paper N. 02/2006.
Niederle, M. and L. Vesterlund (2007). Do women shy away from competition? do men
compete too much? Quarterly Journal of Economics 122(3), 1067–1101.
Oberholzer-Gee, F. and R. Eichenberger (1999, May). Focus effects in dictator game experi-
Oberholzer-Gee, F. and R. Eichenberger (2004). Fairness in extended dictator game experi-
Oxoby, R. and J. Spraggon (2008). Mine and yours: Property rights in dictator games. Jour-
nal of Economic Behavior and Organisation 65, 703–713.
Papke, L. and J. Wooldridge (1996). Econometric methods for fractional response variables
with an application to 401 (k) plan participation rates. Journal of Applied Economet-
rics 11(6), 619–632.
Rabin, M. (1993). Incorporating Fairness into Game Theory and Economics. American
Economic Review 83(5), 1281–1302.
Rufﬂe, B. (1998). More is better, but fair is fair: Tipping in dictator and ultimatum games.
Games and Economic Behavior 23(2), 247–265.
Rutstrom, E. and M. Williams (2000). Entitlements and fairness: an experimental study of
distributive preferences. Journal of Economic Behavior and Organization 43(1), 75–89.
Sheffrin, H. and R. Thaler (1988). The behavioral life-cycle hypothesis. Economic In-
quiry 26, 609–643.
Thaler, R. (1985). Mental accounting and consumer choice. Marketing Science 4, 199–214.
Thaler, R. and E. Johnson (1990). Gambling with the house money and trying to break even:
The effects of prior outcomes on risky choice. Management Science 36, 643–660.
Vohs, K., N. Mead, and M. Goode (2006). The psychological consequences of money. Sci-
ence 314, 1154–1156.