Full text of DOI:10.1162/003355300554926

Measuring Trust
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Glaeser, Edward, David Laibson, Jose Scheinkman, and Christine
Soutter. 2000. Measuring trust. Quarterly Journal of Economics
115(3): 811-846.
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MEASURING TRUST*
EDWARD L. GLAESER
DAVID I. LAIBSON
´
J OSE A. SCHEINKMAN
CHRISTINE L. SOUTTER
We combine two experiments and a survey to measure trust and trustworthi-
ness—two key components of social capital. Standard attitudinal survey questions
about trust predict trustworthy behavior in our experiments much better than they
predict trusting behavior. Trusting behavior in the experiments is predicted by
past trusting behavior outside of the experiments. When individuals are closer
socially, both trust and trustworthiness rise. Trustworthiness declines when
partners are of different races or nationalities. High status individuals are able to
elicit more trustworthiness in others.
I. INTRODUCTION
A growing body of research suggests that ‘‘social capital’’
influences a wide range of significant economic and political
phenomena. For example, Arrow [1972] and Fukuyama [1995]
believe that the level of trust in a society strongly predicts its
economic success. Putnam [1993] uses Italian cross-regional data
to show that local governments are more efficient where there is
greater civic engagement. In recent years, economists have tried
to identify the impact of social capital by using attitudinal
measures of trust from survey questionnaires. Knack and Keefer
[1997], for example, show that an increase of one standard
deviation in country-level trust predicts an increase in economic
growth of more than one-half of a standard deviation. La Porta,
Lopez-de-Silanes, Shleifer, and Vishny [1997] find that a standard
deviation increase in trust increases judicial efficiency by 0.7 of a
standard deviation and reduces government corruption by 0.3 of a
standard deviation.1
The great lacuna in this research agenda is the measurement
of trust. Much of the social capital research relies upon attitudinal
survey questions from the General Social Survey (GSS) such as
* The MacArthur Foundation has generously funded this research which is
part of the MacArthur Foundation Network on Norms and Preferences. Glaeser
and Laibson also thank the National Science Foundation, the Sloan Foundation,
and the Olin Foundation. David Cutler, Lawrence Katz, George Loewenstein,
Andrei Shleifer, and Steven Tadelis provided helpful comments. Beth Bellman,
Meghana Bhatt, Elizabeth Dunn, Elizabeth Kelsinger, Lars Nesheim, J oseph
Robbins, and Stephen Weinberg provided excellent research assistance.
1. See also J acobs [1961], Loury [1977], and Coleman [1990] for additional
claims about the importance of social capital.
2000 by the President and Fellows of Harvard College and the Massachusetts Institute of
Technology.
௠
The Quarterly J ournal of Economics, August 2000
811

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QUARTERLY J OURNAL OF ECONOMICS
‘‘Generally speaking, would you say that most people can be
trusted or that you can’t be too careful in dealing with people?’’
While these survey questions are interesting, they are also vague,
abstract, and hard to interpret. Putnam [1995], for example,
laments this problem: ‘‘since trust is so central to the theory of
social capital, it would be desirable to have strong behavioral
indicators of trends in social trust or misanthropy. I have discov-
ered no such behavioral measures.’’
In this paper we measure trust and trustworthiness by
conducting experiments with monetary rewards. Because we
measure subjects’ attitudes, background characteristics, and so-
cial connectedness, we can identify individual and situational
correlates of trust. For example, we test whether the standard
attitudinal trust questions predict actual trusting behavior with
real money. The primary methodological point of this paper is that
experiments can be integrated with surveys to measure individual-
level variation in traditionally hard-to-measure characteristics
such as trust and trustworthiness.
We first ask survey questions of a sample of 258 Harvard
undergraduates. Three to four weeks later, a subgroup of 196
undergraduates plays two experimental trust games. In the first
game, subjects are paired and meet their partner. They are then
separated, and one member of the pair (the sender) has the
opportunity to send between 0 and 15 dollars to his or her partner
(the recipient).2 The experimenter doubles each dollar that is sent.
After the second player receives the transfer (i.e., twice the
amount sent), he or she may return money back to the first
player.3 This game (based on Berg, Dickhaut, and McCabe [1995])
is similar to many economically relevant settings such as invest-
ment with imperfect contracts or production of a public good. We
think of the amount sent by the ‘‘sender ’’ as a natural measure of
trust. The sender trusts the ‘‘recipient’’ to return a fair share of the
amount the recipient receives. Similarly, controlling for the
amount sent, the amount returned is a measure of trustworthiness.
In our second game, subjects report valuations for a series of
‘‘envelope drops.’’ Subjects are told that an envelope, addressed to
the subject and containing 10 dollars, will be intentionally
dropped by an experimenter. If a subject typically places a high
2. One-half of the sample of trustees (chosen randomly) were given the
opportunity to promise beforehand to return at least as much money as they were
sent by the trustor.
3. All of the rules of the game are common knowledge.

MEASURING TRUST
813
value on the dropped envelopes, then we infer that the subject is
more likely to trust the anonymous strangers who will find the
apparently lost envelope.
Previous research has explored both types of experiments
that we study. The primary difference between our work and most
previous work is that we ask whether subject characteristics
predict the choices that subjects make in these experiments.
We first examine the predictive power of two types of survey
questions: questions about trusting attitudes and questions about
past trusting behavior. In both of our games, the standard
attitudinal questions generally do not predict subject choices in
our experiments.4 Of ten different variants of broad attitudinal
questions, none has a significant correlation with trusting choices
in either experiment that we conducted.5 However, we identify
two relatively precise attitudinal questions about trusting strang-
ers that did predict trust in both games.
Measures of past trusting behavior are better than the
abstract attitudinal questions in predicting subjects’ experimen-
tal choices. An index of past trusting behavior—based on specific
behavioral questions that we developed—has a 22.4 percent
correlation with the amount sent in the trust game, and a 14.6
percent correlation with the average valuation in the envelope
drop. These positive correlations suggest that a component of
trusting behavior may be stable across time and choice domains.
We also find a 15.8 percent correlation (marginally significant)
between trust in the envelope drop experiment and trust in the
two-person trust game.
Although questions about trusting attitudes do not predict
trusting behavior, such questions do appear to predict trustworthi-
ness. An index of an individual’s response to GSS attitudinal trust
questions has a 34 percent correlation with the amount of money
that the individual himself gives back. While attitudinal trust
surveys at best weakly predict any individual’s level of trust, they may
be good at predicting the overall level of trustworthiness in society.
While our primary purpose is methodological, the experi-
4. This finding is consistent with numerous studies that report a lack of
correlation between attitudes and behavior (e.g., review by Ajzen and Fishbein
[1977], although see Kraus [1995] for a different perspective). The classic example
is LaPiere’s [1934] finding that self-reported unwillingness to serve racial minori-
ties was inconsistent with restaurant or motel owners’ actual behavior toward
minorities.
5. Because of our small sample size we cannot rule out a small positive
relationship between the trust survey questions and trust in the experiments.

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QUARTERLY J OURNAL OF ECONOMICS
ments in this paper also produce three additional substantive
results. First, as theory predicts, the degree of social connection
between the sender and recipient—the number of friends they
have in common and the duration of their acquaintanceship—
generally predicts the levels of trust and trustworthiness in the
two-person trust game. These results support the idea that
repeated play in dense social networks facilitates trust (as in
Abreu [1988] and Greif [1993]).6 This result is not surprising, and
we consider it to be less important as validation for the theory
than as validation for the experiments.
Second, we find that subjects who are paired with a partner of
a different race or nationality send back less money to their
partner.7 Eleven out of the twelve times in which the recipient
sent back nothing, the sender and the recipient were of different
races. These effects are stronger than the social network effects
and survive controls for the social connection of the sender and
recipient. This finding is also unsurprising, but serves as a
reminder of the continuing barriers that racial and national
differences may create.
Third, we find that background characteristics capturing the
level of status and organization membership—variables meant to
serve as proxies for an individual’s own social capital—strongly
predict the amount of money that senders receive back from
recipients, and strongly predict the financial returns for senders.
People with better educated parents, students who work fewer
hours for pay, individuals with more friends, and members of
volunteer organizations all earn more money in the experiment.
These results imply that in at least one stylized setting, noncognitive
social skills may be important determinants of economic returns.
II. EMPIRICAL MEASUREMENT OF TRUST—THE CURRENT APPROACH
The empirical literature on trust has focused on responses to
the question: ‘‘Generally speaking, would you say that most
people can be trusted or that you can’t be too careful in dealing
with people?’’ This question is taken from the National Opinion
6. Fershtman and Gneezy [1998] also use a variant of this game to examine
trust in Israel and find a similar result. They document the importance of group
membership by showing that males (not females) are less trusting of Sephardic
males. In their version of the game, players do not meet one another, and they are
left to deduce ethnic background from their opponents’ last name.
7. We use country of residence at age sixteen as a proxy for nationality.

MEASURING TRUST
815
Research Center ’s General Social Survey (GSS). The survey is the
primary source for U. S. evidence on trust and social capital. Since
its inception in 1972 the survey has been administered twenty
times to a sample of between one and two thousand respondents.
The set of questions on the GSS changes from survey to survey,
but the GSS trust question has been asked almost continuously.
Subject responses to the GSS trust question are difficult to
interpret.8 Variation in responses might arise for numerous
reasons: e.g., differences in beliefs about the trustworthiness of a
common set of people; differences in interpretation of who com-
prises ‘‘most people;’’ differences in interpretation of what it
means to be able to trust someone; or differences in the ability to
elicit trustworthy behavior from other people.9 Variation may also
arise because some respondents are not willing to answer truth-
fully when asked such a question on a survey. Our experiments
suggest a new framework for interpretation of the GSS trust
question.
Before turning to our experimental analysis, we first discuss
the standard empirical analysis of the GSS trust question.
Putnam [1995] and others have analyzed the GSS data and drawn
two important conclusions. First, younger cohorts are dramati-
cally less likely to report that ‘‘most people can be trusted.’’
Second, organization membership, an important measure of social
capital, exhibits a similar downward trend. These stylized facts
have generated a substantial debate about declining social capital
in the United States. Using a multiple regression framework, we
replicate these earlier findings.
Table I gives mean answers to the trust question for both the
entire sample of GSS respondents and for different subpopula-
tions. This crude evidence suggests substantial variation in
responses by cohort, education, and race: e.g., 42.3 percent of the
cohort with birth years between 1911 and 1915 report that ‘‘most
people can be trusted,’’ compared with 30.1 percent of the cohort
born between 1961 and 1965. Table I also compares GSS data with
the responses of Harvard undergraduates who participated in our
trust experiment: 42.6 percent of young and college-educated GSS
8. Schwarz [1999] notes that all self-reported instruments are subject to
distortion, with various features of the questions such as ambiguity and format
readily producing unintended effects on subjects’ responses.
9. It seems unlikely that differences in altruism drive answers to this
question (although certainly altruistic attitudes might correlate with the answers
to this question).

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QUARTERLY J OURNAL OF ECONOMICS
TABLE I
AVERAGE LEVELS OF TRUST
Q. ‘‘Generally Speaking, would you say that most people can be trusted or that
you can’t be too careful in dealing with people?’’
Percent responding that. . .
‘‘. . . most people can be trusted’’
US (1972–1996):
US (White):
US (Black):
US (other races):
US (1911–1915 birthyear):
US (1961–1965 birthyear):
US (no high school diploma):
US (high school diploma):
US (college diploma):
US (college diploma, 1996):
US (college diploma and birthyear after 1965):
Harvard Undergraduates (1997)
39.9%
44.2%
16.1%
26.6%
42.3%
30.1%
26.3%
45.0%
58.5%
49.7%
42.6%
44.4%
Harvard data are from the authors’ survey.
Source: The National Opinion Research Center ’s General Social Survey, 1972–1994.
respondents report that ‘‘most people can be trusted,’’ close to the
rate of 44.4 percent in our Harvard sample.
Mean response rates by demographic group confound many
different effects in the GSS data. Table II identifies these separate
effects with probit regressions that estimate how different charac-
teristics explain trust.10 The first regression of Table II presents
our benchmark results. Trust is much lower for later cohorts. The
gap in the level of trust between individuals who were born before
1915 and those who are born after 1959 is 21.4 percent.11 Trust is
much higher among richer and well-educated individuals. College
graduates are more than 30 percent more likely to answer yes to
the trust question than high school dropouts. Blacks are 21
percent less likely to say that they are trusting than whites.12 Men
are slightly more trusting. Married persons are also more trust-
ing. City size has a slightly negative effect on the amount of trust.
Members of more educated (or wealthier) religious denominations
10. Table II reports the marginal effects of the variables.
11. We cannot separately identify age, cohort, and time effects, due to
multicollinearity. We identify age and cohort effects by assuming away time effects.
12. The gap between the races diminishes in states where blacks are less of a
minority.

MEASURING TRUST
817
TABLE II
GENERAL SOCIAL SURVEY RESULTS
Organization membership
(# of types of organizations)
(2)
GSS trust
(1)
Dependent variable:
Born before 1915
0.2142
(0.0216)
0.1538
(0.0176)
0.1331
(0.0141)
0.0782
(0.0107)
Ϫ0.0238
(0.0124)
0.0229
(0.0141)
0.0417
(0.0164)
0.0219
(0.0185)
Ϫ0.0175
(0.0198)
0.1720
(0.0088)
Ϫ0.1638
(0.0077)
0.0154
0.4929
(0.0837)
0.5689
(0.0690)
0.3712
Born between 1915 and 1929
Born between 1930 and 1944
Born between 1945 and 1959
Age between 25 and 34
Age between 35 and 44
Age between 45 and 54
Age between 55 and 64
Age between 65 and 99
College education
Dropout
(0.0571)
Ϫ0.0088
(0.0443)
Ϫ0.0686
(0.0470)
0.0940
(0.0547)
Ϫ0.1250
(0.0662)
Ϫ0.2087
(0.0732)
Ϫ0.3004
(0.0800)
1.1743
(0.0344)
Ϫ0.6922
(0.0308)
0.0715
(0.0182)
0.0941
Log (real income)
Black
(0.0051)
Ϫ0.2091
(0.0093)
0.0343
(0.0411)
0.2562
Male
(0.0066)
0.0338
(0.0249)
0.0802
Married
(0.0761)
Ϫ0.0227
(0.0117)
Ϫ0.0200
(0.0138)
Ϫ0.0505
(0.0145)
0.0120
(0.0098)
Ϫ0.0216
(0.0234)
Ϫ0.0041
(0.0134)
Ϫ0.0582
(0.0103)
0.0363
(0.0294)
Ϫ0.0734
(0.0455)
Ϫ0.1174
(0.0542)
Ϫ0.2208
(0.0575)
Ϫ0.0194
(0.0372)
0.1356
(0.0915)
Ϫ0.5868
(0.0533)
Ϫ0.1116
(0.0532)
0.1397
Town
Small city
Big city
Catholic
J ew
No religion
Baptist
Methodist
(0.0126)
0.0749
(0.0144)
0.0842
(0.0465)
0.1821
(0.0532)
0.3122
Lutheran
Presbyterian
(0.0177)
0.0758
(0.0224)
0.3828
(0.0638)
0.2260
(0.0840)
1.3282
Episcopalian
Constant
(0.0762)
0.1431
19133
R2
0.0855
23867
Observations
Data are from the General Social Survey, 1972–1994. Standard errors are in parentheses. Regression (1)
is a probit. We report derivatives at sample means. Regression (2) is OLS. In regression (1) the constant is the
mean probability at mean values of the explanatory variables. R2 is pseudo R2 for regression (1) and adjusted
R2 for regression (2). Town population is between 2000 and 100,000. Small City population is between 100,000
and 500,000. Big City population is above 500,000. The omitted category for religion is Protestant, no
denomination.

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QUARTERLY J OURNAL OF ECONOMICS
report that they are more trusting, but J ews, a relatively highly
educated religious group, report that they are less trusting.13
Goldin and Katz [1999] find that the proportion of residents
in an area who were Lutheran in the early part of this century
strongly predicts current measures of social capital. We find that
the proportion of Lutherans in a state is a strong predictor of
state-level trust,14 but that state effects can only explain a small
amount of individual variation in trust.15
Most of these results have multiple interpretations. For
example, the positive effect of education on trust might occur
because more educated people associate with other more educated
people who are, for some reason, more trustworthy.16 Alterna-
tively, education might create individual social capital by raising
social skills or because high status increases the ability to reward
and punish others.
The second regression of Table II repeats this analysis using
membership in nonprofessional organizations—an observable mea-
sure of social behavior—as the dependent variable. Specifically,
this variable represents the number of different types of organiza-
tions in which the individual is a member. The correlation of this
variable with the GSS trust measure is high, and many of the
same patterns continue to hold. For example, the basic cohort,
education, and income effects remain. There are only two real
differences. Age effects peak between 35 and 44, and the race
dummy (Blacks ϭ 1) now takes a positive coefficient.17 This racial
effect on organization membership follows from the high rate of
religious affiliation of African-Americans.
We have run similar regressions outside the United States.
The positive effect of education on trust and organization member-
ship is close to ubiquitous. Measured trust does not, however,
generally decline for younger cohorts outside of the United States.
We now proceed to our experiments. Putnam and others have
13. La Porta et al. [1997] argue that hierarchical religions reduce social
capital at the country level because the operation of these religions entails less
cooperative interaction between lay people. We see no evidence for this in the
United States. Iannaccone [1991] argues that religion serves a large social
purpose, and we might expect to find significantly more trust among members of
particular religious groups (see also Glaeser and Glendon [1998]).
14. This analysis is available from the authors upon request.
15. Percent Lutheran explains 30 percent of the variation in the mean level of
trust across states.
16. For example, generally acting in a trustworthy manner may be a luxury
good, which is consumed disproportionately by people with high incomes.
17. This finding does not change when we control for the number of children
in the household.

MEASURING TRUST
819
shown alarming cohort trends in U. S. responses to the GSS trust
question, and we have confirmed the existence of these trends.
However, it remains unclear whether these trends in survey
responses accurately reflect trends in social capital. Our primary
goal is to understand what the survey question about trust
actually measures.
III. SURVEY AND EXPERIMENTAL DESIGN
Subjects were recruited from Harvard’s introductory econom-
ics course (Social Analysis 10, or ‘‘Ec10’’) during the first week of
class.18 Out of approximately 1000 Ec10 students, 274 agreed to
participate, of whom 189 completed all parts of the study.19
Our experimental procedure has three components. First,
subjects are asked to fill out a survey. Three to four weeks later,
subjects participate in two experiments, the ‘‘Trust Game’’ and the
‘‘Envelope Drop.’’
Part 1, Survey. Subjects fill out an anonymous 137-question
survey, which typically takes 20 to 30 minutes. The first half of the
survey contains demographic and behavioral questions (e.g.,
gender, parental education, race, college activities, etc.). The
second half contains attitudinal and self-reported behavioral
measures of subjects’ trustfulness and trustworthiness.
The trust questions were chosen from several sources. In our
selection we emphasized questions from the General Social Sur-
vey, which contains a wide range of attitudinal questions about
trust. In addition, we designed numerous trust questions of our
own, including three questions to elicit past trusting behaviors.
Such behavioral information is not elicited by any of the GSS
questions. We ask:
ᮀ ‘‘How often do you lend money to your friends?’’
ᮀ ‘‘How often do you lend personal possessions to your
friends (e.g., CDs, clothes, bicycle, etc.)?’’
ᮀ ‘‘How often do you intentionally leave your rooming group’s
hallway door unlocked (when nobody is home)?’’
A complete copy of our survey is available upon request.
Part 2, The Trust Game. Three to four weeks after subjects
fill out the survey, they come to a Harvard classroom to participate
18. Our recruitment handout and all of our other subject materials (e.g.,
consent forms, instructions, and debriefing forms) are available upon request.
19. The Ec10 students are roughly representative of Harvard undergradu-
ates, since nearly two-thirds of the undergraduates take this course.

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QUARTERLY J OURNAL OF ECONOMICS
in two experiments: the ‘‘Trust Game’’ and the ‘‘Envelope Drop.’’
When communicating with the subjects, we refer, respectively, to
the ‘‘Transfer Game’’ and the ‘‘Bonus Winnings Procedure.’’ For
clarity, we use the former, more descriptive titles here.
Subjects arrive at the experiment site, sign in, fill out a
consent form, and are then paired with another subject to
participate in the ‘‘Trust Game.’’ Those who arrive together and
wish to play together are allowed to do so, raising the likelihood
that subjects who know each other will be paired.20 Others are
paired in order of arrival. After being paired, the subjects jointly
fill out a social connection survey, which includes nine questions
about social links between the subjects. For example, we ask the
subjects to produce a list of all personal acquaintances whom they
have in common. Subjects tally and report the number of names
on their joint list, but keep the actual list of names to assure
anonymity of the subjects (and their friends).
After filling out the social connection survey, the subjects are
separated and told that they will not see each other again during
the course of the experiment. The rest of the game (steps 1–5 below) is
then explained to the separated subjects. Then the game is played.21
In the experimental instructions we refer to the subjects as
either RED or GREEN players. Each pair of subjects contains one
RED player and one GREEN player. In the current summary, we
use more meaningful labels: ‘‘sender ’’ and ‘‘recipient.’’ The five
steps of the game are as follows.
(1) The sender is given $15.
(2) The recipient sends the sender a message/promise about
the recipient’s intended future actions in the game.
(3) The sender chooses to send all, some, or none of his/her
$15 to the recipient. We refer to this transfer as the
‘‘amount sent.’’
(4) The experimenters double whatever the sender chooses to
send. For example, if the amount sent is $4, the recipient
receives $8, and the sender keeps $11 of the original $15.
(5) The recipient chooses to send all, some, or none of the
received money back to the sender. We refer to this
transfer amount as the ‘‘amount returned.’’ For example,
20. In a small pilot study, we found that randomly paired subjects were highly
unlikely to know each other at all. Our nonrandom pairing procedure generates
more variation in social connection.
21. A formal analysis of this game appears in an earlier version of this paper
[Glaeser, Laibson, Scheinkman, and Soutter 1999].

MEASURING TRUST
821
if the recipient receives $8, and the amount returned is $1,
then the recipient gets to keep $7, and the sender gets to
keep $1 ϩ $11 ϭ $12.
To implement this procedure, subjects write their decisions on
a record sheet, which is placed in a coded envelope and collected
by a subset of experimental assistants who never see the contents
of the envelope. The other subset of experimental assistants who
actually open the envelopes (in a different room) never see the
subjects. Hence, subject anonymity (vis-a`-vis the experimenters)
is assured.
We implement step (2)—which allows the recipient to make a
promise—by giving the recipient (GREEN) the opportunity to
check one of two statements: (a) ‘‘I, person GREEN, promise to
repay RED at least as much as RED sends me. For example, if
RED sends me $4, which will be doubled by the experimenters to
$8, then I will repay RED at least $4,’’ or (b) ‘‘I, person GREEN,
22
make no promise to RED.’’ One of these two statements must be
checked, and no other type of message is allowed. Our instructions
note that promises, if made, are not binding.
Half of our pairs of subjects are given the opportunity to make
a promise in the form described above. The other subjects receive
no opportunity to send a message, and no mention of a promise is
made in their experimental instructions.
Our procedure differs from the Berg-Dickhaut-McCabe [1995]
experiment on which it is based in three ways. First, unlike Berg,
Dickhaut, and McCabe we include a promise condition. Second,
the Berg-Dickhaut-McCabe procedure guarantees that individual
subject decisions are unobservable to all parties (i.e., both experi-
mentalists and other subjects). Our game only provides anonym-
ity vis-a`-vis the experimenters; the subjects know the identity of
the other subject in their pair. This knowledge creates variation in
social connection—some subject pairs know each other well, while
other pairs have only just met—enabling us to determine how
different levels of social connection influence trusting behavior.
However, removing subject-to-subject anonymity engenders an
undesirable ancillary effect: a sharp rise in the cooperative
behavior of senders. This increased cooperation is undesirable
because full and universal cooperation eliminates variation in
22. As we intended, all but one of the 47 subjects who were given the chance to
make the scripted promise did so. Our investigation differentiates between people
randomly given the opportunity to promise, not between people who did promise
versus people who could have promised and did not.

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QUARTERLY J OURNAL OF ECONOMICS
trusting behavior. To avoid this possibility, we deviate from the
Berg-Dickhaut-McCabe experiment in a third way. We only
double—rather than triple—the money that the sender sends to
the recipient, thereby reducing the incentive to cooperate.23
Part 3, The Envelope Drop. After completing the trust game,
subjects participate in a second experimental procedure that
provides an additional behavioral measure of trust. In this game
subjects report valuations for a series of ‘‘envelope drops.’’ Specifi-
cally, subjects are told that an experimental assistant will inten-
tionally drop in a public place an envelope containing 10 dollars
that is addressed to the subject. The envelope may be dropped in
one of several different public places (e.g., Harvard Square) under
one of several different conditions (e.g., sealed and stamped). For
each place and condition of the envelope drop, the subject reports
a valuation. We believe that the subject’s valuation of such an
envelope drop primarily measures confidence that a random
pedestrian in that location will return the envelope to the subject
(say by putting it into a mailbox). The procedure may also
measure the subject’s trust that the experimenter will carry out
the envelope drop in the first place.
To elicit truthful subject reporting, we use a standard revela-
tion mechanism.24 We randomly generate a payoff that is indepen-
dent of the subject’s valuation. We give the subject this payoff if
the subject’s reported valuation is below the payoff value. If the
subject’s reported valuation is above the payoff value, we carry out
the envelope drop. We vary properties of the envelope drop (e.g.,
location, time of day, stamp on envelope, envelope sealed). Each
subject provides valuations for fifteen different envelope drop
conditions. Subjects report sensible changes in valuations across
conditions (see Appendix 3). We average each subject’s responses
across the fifteen different envelope conditions offered to each
subject, and use this mean reservation value as our second
measure of trust.
We use the amount sent in the Trust Game and the mean
reservation value in the Envelope Drop as our two experimental
measures of trust. To measure trustworthiness, we use
return ratio Ϫ amount returned/amount available to return.
23. Despite this reduction in the incentive to cooperate, we still find that
cooperation is ‘‘too’’high: 71 percent of our sample of senders send the upper limit of
the amount they are allowed to send (i.e., 15 dollars).
24. See Becker, DeGroot, and Marschak [1964].

MEASURING TRUST
823
Naturally, this ratio is only defined for subject pairs with a
positive value for the amount available to return. Finally, recall
that the amount available to return is twice the amount sent. A
ratio of less than one-half indicates that the sender did not receive
back as much money as he or she risked and might thus be seen as
having been cheated by the recipient.
We use this ratio as a measure of trustworthiness for two
reasons. First, return ratio is always bounded between 0 and 1,
and hence is automatically scaled. Second, in our experimental
data there is a roughly proportional relationship between amount
returned and amount available to return. We adopt this proportion-
ality benchmark in our analysis.
IV. RESULTS
The average amount sent is $12.41, which is 83 percent of the
maximal amount that could be sent ($15). Of our 96 senders, 68, or
71 percent, chose to send exactly $15. However, the amount sent
data still exhibit substantial variation, with a standard deviation
of $4.54. Figure I plots the individual data points, with amount
sent on the x-axis and return ratio on the y-axis. The floating
numbers report the frequency with which a data point was
FIGURE I
The Relationship between Amount Sent and Amount Returned

824
QUARTERLY J OURNAL OF ECONOMICS
observed. The average amount returned is $12.30, and the
average value of return ratio is 45.5 percent.
The average mean reservation value from the Envelope Drop
is normalized to zero. The standard deviation is $1.77. The
distribution of mean reservation values approximates a bell curve
with little or no apparent truncation at the endpoints.
There exists substantial heterogeneity in trusting and trust-
worthy behavior, and our survey data enable us to identify the
variables that explain this variation.25 The observed heterogene-
ity could arise from individual fixed effects, situationally specific
effects (e.g., partnership-specific attributes in the trust game), or
random noise.
We organize our analysis conceptually. First, we identify
individual fixed effects in trust and trustworthiness. We look for a
relationship between behavior in the experiments and responses
to attitudinal survey questions. We also look for a relationship
between behaviors in different situations. Second, we identify the
effects of social connection between the sender and recipient.
Third, controlling for social connection, we ask whether some
subjects tend to fare well financially in social interactions, per-
haps because of status effects. Such people may be thought of as
having individual social capital.
A. Individual Effects in Trust and Trustworthiness
We begin by looking at the level of trust our senders display
toward their partners. In Table III we examine whether survey
questions and other individual background characteristics predict
the amount sent in the Trust Game. In all regressions we include
six basic control variables: a promise condition dummy, a mixed-
gender pair dummy, a male sender dummy, a nonwhite sender
dummy, a freshman sender dummy, and an only child sender
dummy.26 Generally, these control variables are insignificant, and
their inclusion or exclusion does not affect any of our other results.
In the first column of Table III, we evaluate the predictive
value of the GSS trust question. Senders who believe ‘‘that most
people can be trusted’’ send 22 cents more to their partners than
senders who believe ‘‘that you can’t be too careful in dealing with
25. Appendices 1 and 2 give the means and correlations from the survey and
the two experiments.
26. The dummy variables were chosen so that approximately 50 percent of the
sample had a value of one for the variable. The only child dummy is an exception to
this rule.

MEASURING TRUST
825
TABLE III
AMOUNT SENT AS A FUNCTION OF SENDER CHARACTERISTICS
(1)
(2)
(3)
(4)
(5)
Different sexes
Promise
Ϫ0.670
(1.130)
0.043
(1.024)
0.147
(1.197)
Ϫ0.330
(1.030)
Ϫ0.205
(1.136)
Ϫ1.620
(1.53)
Ϫ0.128
(1.112)
Ϫ0.097
(1.015)
0.623
(1.174)
Ϫ0.640
(1.025)
Ϫ0.434
(1.125)
Ϫ1.724
(1.474)
Ϫ1.043
(1.120)
0.440
(1.040)
Ϫ0.028
(1.148)
0.055
(1.031)
Ϫ0.254
(1.092)
Ϫ1.555
(1.496)
Ϫ0.358
(1.106)
Ϫ0.038
(.992)
Ϫ0.643
(1.082)
Ϫ0.153
(0.995)
Ϫ0.013
(1.138)
Ϫ0.329
(1.006)
Ϫ0.305
(1.086)
Ϫ1.569
(1.492)
Male
0.457
(1.149)
Ϫ0.227
(1.003)
Ϫ0.970
(1.081)
Ϫ1.775
(1.530)
White
Freshman
Only child
GSS trust
Trust index
Trust strangers
0.220
(1.022)
Ϫ0.094
(0.222)
2.209
(1.060)
Trusting behavior
index
0.403
(0.214)
Mean reservation
value
Constant
0.417
(0.312)
13.336
(1.639)
Ϫ0.034
95
13.361
(2.448)
Ϫ0.059
93
13.009
(1.735)
Ϫ0.050
90
9.836
(2.272)
Ϫ0.009
92
12.707
(1.648)
Ϫ0.007
93
Adj. R2
Observations
Standard errors are in parentheses. All regressions are ordinary least squares.
people.’’ This effect is not statistically distinguishable from zero.
In the next regression we replace the basic GSS trust question
with an index of responses to three GSS attitudinal questions: the
original GSS trust question and two additional questions that
measure one’s confidence in other people.
GSS fair: Do you think most people would try to take
advantage of you if they got the chance, or would they try to be
fair?
GSS helpful: Would you say that most of the time people try to
be helpful, or that they are mostly just looking out for themselves?
We form an index of responses to these questions by adding
the three variables after they are de-meaned, normalized by their
standard deviations, and re-signed for comparability. Increases in

826
QUARTERLY J OURNAL OF ECONOMICS
this index measure of trust insignificantly reduce the actual level
of trust.
We included twelve different attitudinal measures of trust in
our survey, including two widely used multiquestion trust scales
from the psychology literature: the Rosenberg [1957] Faith in
People Scale (which has twelve component questions) and the
Rotter [1967, 1971] Interpersonal Trust Scale (which has 25
component questions). Of these twelve different attitudinal mea-
sures, all but two have no statistically significant covariation with
the actual amount of trust in our experiment. Trust survey
questions at best only weakly predict trust. However, it is
important to highlight the statistical imprecision of these results.
Some of our standard errors are quite large, including our
standard errors for the GSS trust question.27
The two attitudinal survey questions that do significantly
predict trusting behavior in the experiment ask specifically about
trust of strangers. In column (3) in Table III we find that subjects
who disagree with the statement ‘‘you can’t trust strangers
anymore’’ are more trusting. Individuals who disagree with this
statement send over an average of $2.21 more than comparable
individuals who agree with the statement. Disagreement with
another statement from our survey—‘‘when dealing with strang-
ers, one is better off using caution before trusting them’’—is also
significantly correlated with the amount of trust observed in our
experiment.
There are two plausible interpretations of these findings.
First, among so many trust questions it is unsurprising to find two
27. Our attitudinal survey questions may not measure behavioral propensi-
ties, but may instead measure subjects’ beliefs about social norms. McClelland,
Koestner, and Weinberger [1989] report a distinction between explicit and implicit
attitudes in their study of ‘‘achievement motivation.’’ Explicit responses to an
attitude survey on achievement appeared to reveal beliefs about social norms for
achievement. These self-reports did not reflect durable personal commitments to
action and did not correlate with behaviors that could actually enhance achieve-
ment. Rather than depending on subjects’ explicit self-reports, McClelland,
Koestner, and Weinberger [1989] resorted to an implicit measure. They used
independent judgments of the extent to which subjects’indirectly obtained thought
patterns displayed associations typical of high interest in achievement. The
explicit measures were uncorrelated with these implicit measures, which did
predict actual behavior. The poor performance of explicit measures may reflect
limited self-knowledge, since much of the thinking process takes place outside of
consciousness (e.g., Nisbett and Wilson [1977] and Hirst [1998]). Alternatively,
subjects may distort their self-reports for presentational reasons. There is a
growing trend (e.g., Banaji and Greenwald [1994], and Greenwald and Banaji
[1995]) toward use of implicit cognitive measures. For example, Spalding and
Hardin [1999] have found behavioral links to implicit but not explicit measures of
self-esteem.

MEASURING TRUST
827
that are significant, even if the questions actually have little or no
predictive value.28 Second, the attitudinal questions regarding
strangers are more precise and meaningful than completely
general, nonspecific questions regarding trust. This high degree of
specificity might make these variables genuinely more predictive
than those of a more general nature.29 To further test whether the
connection between these variables and the amount sent is the
result of spurious correlation, we examine separately sender-
recipient pairs who are composed of two strangers and those who
are composed of two friends. We find that the questions about
strangers only predict the amount of trust between strangers,
which supports their validity as measures of trust. This repre-
sents our first piece of evidence in support of the hypothesis that
trusting behavior has a component that is a persistent, individual
characteristic.
In the fourth and fifth regressions we examine the connection
between trusting behavior reported in the survey and trust in the
experiment. The fourth regression shows the connection between
an index of past trusting behavior and the amount sent. This index
is a weighted average of responses to questions about lending
possessions, lending money, and leaving your door unlocked.30
A
one-standard-deviation increase in this variable (2.13) increases
the dollar amount sent over by 86 cents (one-fifth of a standard
deviation). In the fifth regression we show a positive, but insignifi-
cant, correlation between the mean reservation value and the
amount sent. Without controls, this relationship is significant at
the 12.5 percent level.
We have also investigated several other potential determi-
nants of variation in the amount sent, including variation in
altruism and variation in early life experiences. Our measures of
28. However, the fact that the two significant questions have similar concep-
tual content suggests more than a spurious correlation.
29. Declines in the attitude-behavior link occur when the level of specificity in
the survey question does not match that of the behavior under observation. The
problem is found here in the lack of correspondence between general GSS
questions and specific trusting behavior measured in our two experimental games.
McClelland, Koestner, and Weinberger [1989] found a similar discrepancy between
self-reports of general value placed on achievement and actual behavior to
increase achievement. The problem has been documented in other settings in a
review by Oskamp [1991]. In a meta-study, Kraus [1995] found that certain types
of questions tend to increase attitude-behavior correlation, including those
addressing direct experience and those with a focus on specific issues correspond-
ing to the specific behavior under observation. Both of our predictive questions
meet these two criteria.
30. The index is formed by de-meaning these three variables, dividing by
their standard deviations, and summing the resulting values.

828
QUARTERLY J OURNAL OF ECONOMICS
altruism (financial generosity to the poor, hours spent volunteer-
ing) do not predict amount sent and generally do not affect our
other coefficient estimates. To investigate the potential roots of
trust, we investigate proxies for past experiences that might have
led to a cynical or untrusting outlook (parental divorce, childhood
violence, etc.). These also had no effect.
In Table IV we examine the determinants of the level of trust
in the Envelope Drop game. We include an extra control variable,
lost mail, which measures the recency with which the respondent
lost an item in the mail. Responses to this question take on a value
between one (never) and four (within the last six months). A
one-standard-deviation increase in this variable (.99) predicts a
TABLE IV
MEAN RESERVATION VALUES AS A FUNCTION OF SUBJ ECT CHARACTERISTICS
(1)
(2)
(3)
(4)
(5)
(6)
Male
0.1680
0.0975
0.1469
0.1923
0.1237
0.1716
(0.2810) (0.2890) (0.2820) (0.2850) (0.2784) (0.2870)
0.1599 0.1590 0.2028 0.1535 0.2036 0.1865
(0.2740) (0.2810) (0.2760) (0.2780) (0.2715) (0.2860)
Ϫ0.0857 Ϫ0.0924 Ϫ0.0633 Ϫ0.0059 0.0561 0.1792
(0.2880) (0.2990) (0.2880) (0.2910) (0.2844) (0.2930)
Ϫ0.2336 Ϫ0.2487 Ϫ0.2124 Ϫ0.2488 Ϫ0.2274 Ϫ0.2559
(0.1370) (0.1390) (0.1370) (0.1380) (0.1348) (0.1380)
White
Freshman
Lost mail
Only child
GSS trust
Trust index
Trust strangers
0.0243
0.0203 Ϫ0.2483
0.2049 Ϫ0.1443 Ϫ0.1429
(0.4380) (0.4400) (0.4330) (0.4420) (0.4317) (0.4290)
0.2020
(0.2620)
0.0396
(0.0610)
0.6774
(0.2740)
Trusting
behavior
index
0.1354
0.1299
0.1324
(0.0640) (0.0621) (0.0650)
Pro-transfer
0.4570
(0.1448)
0.8779
Past windfall
Constant
(0.2720)
0.7239
0.5187 Ϫ0.5439
0.4486 Ϫ0.6265
1.6145
(0.6360) (0.5240) (0.6680) (0.5180) (0.6092) (0.6290)
Adj. R2
Observations
Ϫ0.004
Ϫ0.005
0.029
183
0.022
183
0.069
183
0.076
166
182
177
Standard errors are in parentheses. All regressions are ordinary least squares.

MEASURING TRUST
829
decline of $.22, or one-seventh of a standard deviation, in the
mean reservation value. The impact of the lost mail variable
suggests the importance of past experiences, working presumably
through beliefs.31
In the first regression of Table IV, we include the basic GSS
trust question. Individuals who answer yes to this question are
willing to pay 20 cents more for the 10-dollar envelope drop. This
effect goes in the right direction but is not statistically significant.
In regression (2) we include the index of responses to the three
GSS attitudinal questions. A one-standard-deviation increase in
this GSS index (2.22) causes an insignificant 9-cent increase in
the mean reservation value. Ten of the twelve attitudinal trust
measures that we included in our survey are not significantly
correlated with the mean reservation value.
Again, the two survey questions that specifically ask about
trusting strangers positively predict trust. As regression (3)
illustrates, individuals who believe that you can trust strangers
are willing to pay 68 cents more for the envelope. Again, this
result may be spurious, but if it is real, it suggests the presence of
stable individual attributes that create trust.
The fourth regression in Table IV shows the connection
between our index of past trusting behavior and the mean
reservation value. This index has a modest, significant effect. A
one-standard-deviation increase in the index raises the level of
mean reservation value by 29 cents. The strongest connection
occurs between lending possessions and the mean reservation
value.
In the fifth regression we show that being in favor of
redistribution to the poor predicts one’s mean reservation value.32
This may occur because dropping the envelope itself is seen as an
act of charity. Alternatively, people who favor redistribution may
simply have a higher level of general trust or a higher level of
confidence in the behavior of individuals with low income who
might pick up the envelope.
To further explore the predictive value of the redistribution
question, we examine the influence of this variable on subject
reservation values for envelope drops in low income areas (e.g.,
Central Square, a relatively less affluent community near Har-
31. Unlike the rest of our survey questions, the lost mail question was asked
after the experiment, as part of a debriefing.
32. Behavioral measures of altruism (hours spent on volunteer work or
dollars given to charity) are orthogonal to this redistribution variable.

830
QUARTERLY J OURNAL OF ECONOMICS
vard Square) and high income areas (e.g., Harvard Square). The
strongest connection between the responses to the redistribution
question and reservation value occurs in low income areas. Indeed
there was no connection between the redistribution question and
reservation values for the envelopes dropped in Harvard Square.
Hence, subjects who favor redistribution appear either to believe
that dropping the envelope is an act of charity when the envelope
is dropped in a low income community, or to have greater
confidence in the honesty of low income individuals who find
dropped envelopes.
In the sixth regression we show that there appears to be some
cognitive basis for higher trust. People who say that they have
benefited from the generosity of an anonymous stranger in the
past give more. This suggests that trust does not just reflect
altruism or risk tolerance, but also beliefs about others which are
formed by past experiences.
Turning now from the senders’ trust, we look at the recipients’
trustworthiness. In Table V we examine the effect of recipient
characteristics on the value of return ratio (i.e., amount returned
divided by amount available to return). We add the amount of
money sent over in the first round (i.e., amount sent) as a control
variable and find that this variable has a statistically significant
but economically small positive effect on return ratio. As Figure I
shows graphically, on average recipients return as much as they
are sent. This might reflect reciprocal altruism as in Rabin [1993],
but it might also reflect prevailing norms about fair play.33
These norms were influenced by the promise condition.
Figures II and III plot histograms of return ratio values for subject
pairs in the ‘‘no promise’’ and ‘‘promise’’ conditions. In the no
promise condition 48 percent of recipients returned exactly as
much as they were sent. By contrast, in the promise condition 68
percent of recipients returned exactly as much as they were sent.
But on average return ratio did not vary between the two
conditions. Instead, the promise condition seemed to anchor
responses on the rule, ‘‘send back as much as you were sent,’’
thereby reducing heterogeneity in the distribution of return ratio.
The promise pulled mass away from both the selfish and generous
tails of the distribution.
33. This finding is harder to reconcile with inequality aversion which would
generally imply that senders who send 5 dollars or less should not receive anything
in return. Even if nothing is returned, the sender will have at least as much
experimental earnings as the recipient.

MEASURING TRUST
831
TABLE V
RETURN RATIO AS A FUNCTION OF RECIPIENT CHARACTERISTICS
(1)
(2)
(3)
(4)
Amount sent
Different sexes
Promise
0.018
(0.007)
0.003
(0.053)
Ϫ0.043
(0.051)
0.027
0.018
(0.006)
Ϫ0.007
(0.052)
Ϫ0.007
(0.051)
0.048
0.019
(0.007)
0.006
(0.055)
Ϫ0.031
(0.052)
0.013
0.014
(0.008)
0.001
(0.065)
0.017
(0.063)
Ϫ0.015
(0.073)
0.061
Male
(0.059)
0.075
(0.058)
0.072
(0.061)
0.074
White
(0.054)
Ϫ0.072
(0.055)
Ϫ0.217
(0.092)
0.106
(0.052)
Ϫ0.052
(0.055)
Ϫ0.242
(0.089)
(0.055)
Ϫ0.083
(0.056)
Ϫ0.218
(0.088)
(0.065)
Ϫ0.009
(0.071)
Ϫ0.191
(0.112)
Freshman
Only child
GSS trust
Trust index
(0.051)
0.043
(0.012)
Self-reported trustworthi-
ness
Ϫ0.026
(0.026)
Honesty index
0.010
(0.008)
0.246
(0.147)
0.036
64
Constant
0.414
(0.149)
0.161
90
0.212
(0.120)
0.232
88
0.386
(0.185)
0.138
91
Adj. R2
Observations
Standard errors are in parentheses. All regressions are ordinary least squares.
By examining the effect of individual characteristics on the
level of trustworthiness, we can test whether trustworthiness is a
stable characteristic. In the first regression in Table V, we find
that our controls actually have some impact. Being nonwhite and
being a freshman slightly depress trustworthiness. More signifi-
cantly, only children are much less likely to return money. Being
an only child reduces the amount sent back by 22 percent. This
result would be even stronger without control variables. The
average subject without siblings returns 40 percent of the amount
that was sent over. While this result is certainly among the most
provocative of this study, our small sample size (ten only children)
leads us to withhold judgment until there is further independent
verification of an only child effect on trustworthiness.

832
QUARTERLY J OURNAL OF ECONOMICS
FIGURE II
Distribution of Return Ratio in ‘‘No Promise’’ Condition
FIGURE III
Distribution of Return Ratio in ‘‘Promise’’ Condition

MEASURING TRUST
833
We also find a significant correlation between the ratio of
money returned and the GSS trust question. In regression (2) in
Table V we find an even stronger relationship between the level of
trustworthiness and the index of trust-related questions (GSS
Trust, GSS Helpful, and GSS Fair). The strongest subcomponent
of that index is the question about whether a subject thinks other
people are fair. There are significant correlations between many of
the attitudinal measures of trust and the experimental measure
of trustworthiness.
These findings suggest that the standard trust questions may
be picking up trustworthiness rather than trust. Tables I and II
take on a substantially different meaning when viewed in that
light. The micro-evidence on cohorts or education might then be
interpreted as suggesting that these groups differ in their trustwor-
thiness, not their trust. When aggregated up to the country or
region level, presumably a measure of trustworthiness is as good
(or better) a measure of social capital as a measure of trust.34
In regression (3) of Table V we show that there is a negative,
insignificant connection between self-reported trustworthiness
and actual trustworthiness. We are not surprised that those
people who are willing to admit to being untrustworthy are not
the least trustworthy of our subjects. This result adds further
weight to our earlier findings that subjects’ responses to attitudi-
nal questions can rarely be taken at face value. Instead, our
results imply that the best way to determine whether or not a
person is trustworthy is to ask him whether or not he trusts
others.
The final regression in this table presents an index of past
honesty. This is a normalized average of subject answers to four
questions about the frequency of lying to parents, roommates,
acquaintances, and close friends. This reverse-scored self-
reported behavioral measure of honesty weakly predicts the level
of trustworthiness. The important components of the index relate
to lying to acquaintances and lying to close friends. Again, it
34. One possible explanation for our trustworthiness effects is that people
asked to report how much they trust others must search for information with
which to answer the question. Their first step might be to determine whether they
think people are trustworthy. People regularly overestimate the extent to which
others are like them (the ‘‘false consensus effect’’ [Ross, Green, and House 1977], so
people who are themselves trustworthy would be likely to construe others as
trustworthy. Having decided that others are usually trustworthy, it would be a
reasonable final step to conclude that one’s trust of others was high. Schwarz
[1999] suggests that a process such as this lies at the heart of all attitudinal
self-evaluations.

834
QUARTERLY J OURNAL OF ECONOMICS
appears that asking about past actions is more successful than
asking about opinions.
B. Social Connections
The social capital literature assumes that social connections
(e.g., clubs, organizations, friendships, etc.) mitigate the free-
rider problem and facilitate cooperative social interaction. In
Table VI we determine whether social connection between sender
and recipient increases trust and trustworthiness in our experiment.
We use two basic measures of social connections: months
since first meeting and number of friends that the sender and
recipient have in common. To lessen the impact of outliers, we
have topcoded the number of months at 36 and the number of
friends at 30. We include both the index of past trusting behavior
and the GSS survey question on trust as added controls.
The first and fifth regressions of Table VI show the effect of
months since first meeting on amount sent and return ratio. The
coefficient in the amount sent regression is significant at the 90
percent level; the coefficient in the return ratio regression is
significant at the 95 percent level. The coefficients are not small. A
one-standard-deviation increase in time known raises amount
sent by 80 cents and return ratio by 5 percent.
In the second and sixth regressions we look at the number of
friends in common. There is a positive, insignificant effect of this
variable on amount sent and return ratio. The economic magni-
tudes of the coefficients, though, are not inconsequential. For
example, ten extra friends apparently raises return ratio by 2.6
percent, at least in our relatively small sample.
In the third and seventh regressions we test whether individu-
als from different countries trust each other less. We find a small
but insignificant negative effect on amount sent, but a large and
very significant effect on return ratio. People are much more likely
to return low amounts if they are facing someone from a different
country. This result is much stronger than the results on social
connection, and it is unchanged when we control for social
connection.
The differences between regressions (3) and (7) pose a puzzle.
If trustworthiness between nationalities is so low, why is trust
itself not affected by national differences within a subject pair?
Perhaps our coefficient in the trust equation is imprecisely
measured. Alternatively, senders may truly fail to infer that they
will receive less back from recipients from a different national-

MEASURING TRUST
835
TABLE VI
INFLUENCE OF SOCIAL CONNECTION ON AMOUNT SENT AND RETURN RATIO
Amount sent as function of
sender and pair characteristics
Return ratio as function of
recipient and pair characteristics
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
0.0143
0.0151
0.0170
0.0140
Amount sent
Promise
(0.0069) (0.0069) (0.0066) (0.0069)
0.0416 Ϫ0.0597 Ϫ0.0548 Ϫ0.0539 Ϫ0.0358 Ϫ0.0691
Ϫ0.0796
0.0308
(1.0060) (1.0153) (1.0319) (1.0380) (0.0511) (0.0515) (0.0501) (0.0519)
Ϫ0.2899 0.0455 Ϫ0.2118 Ϫ0.2243 0.0067 0.0331 0.0328 0.0050
(1.1372) (1.1890) (1.1750) (1.1657) (0.0530) (0.0577) (0.0528) (0.0536)
0.3777 0.5750 0.6190 0.6453 0.0477 0.0622 0.0458 0.0448
(1.1950) (1.2007) (1.2168) (1.2251) (0.0589) (0.0621) (0.0570) (0.0584)
Different
sex
Male
Ϫ0.3568 Ϫ0.1940 Ϫ0.2490
0.0589
0.0497
0.0567
White
(1.0082) (1.0203) (1.0274)
(0.0541) (0.0553) (0.0527)
0.3029 Ϫ0.0344
0.0387
0.0215 Ϫ0.0557 Ϫ0.0668 Ϫ0.0730 Ϫ0.0641
Freshman
Only child
(1.1270) (1.1251) (1.1484) (1.1406) (0.0549) (0.0550) (0.0532) (0.0553)
Ϫ1.9766 Ϫ1.6304 Ϫ1.8404 Ϫ1.7288 Ϫ0.2222 Ϫ0.2447 Ϫ0.2149 Ϫ0.2302
(1.5499) (1.5724) (1.5906) (1.5966) (0.0933) (0.0944) (0.0909) (0.0950)
0.3997
0.3788
0.4020
0.3964
0.0027
0.0061
0.0021
0.0061
Trusting
behavior
index
(0.2157) (0.2199) (0.2206) (0.2216) (0.0153) (0.0153) (0.0148) (0.0153)
0.1581
0.1978
0.1580
0.2080 Ϫ0.1004 Ϫ0.1057 Ϫ0.1048 Ϫ0.0800
GSS trust
(1.0136) (1.0260) (1.0323) (1.0461) (0.0530) (0.0537) (0.0516) (0.0541)
0.1016
0.0060
Months
(0.0614)
(0.0032)
since first
meeting
0.0310
(0.0321)
0.0026
(0.0017)
Number of
common
friends
Ϫ0.2174
(1.2509)
Ϫ0.1749
(0.0616)
Different
nationality
White sender,
Nonwhite
recipient
Nonwhite
sender,
Ϫ0.7496
(1.4726)
Ϫ0.1092
(0.0623)
Ϫ0.2350
(1.1579)
Ϫ0.1231
(0.0665)
white
recipient
Nonwhite
sender, non-
white
Ϫ0.1040
(2.5213)
Ϫ0.0893
(0.1250)
recipient
Constant
12.0169 11.6161 12.2148 12.1904
0.4327
0.4058
0.4533
0.5433
(2.4486) (2.5578) (2.4951) (2.5012) (0.1501) (0.1527) (0.1462) (0.1455)
Adjusted R2
Ϫ0.0006 Ϫ0.0224 Ϫ0.0337 Ϫ0.0433
92 92 92 92
0.159
89
0.1457
89
0.2029
89
0.1471
89
Observations
Standard errors are in parentheses. All regressions are ordinary least squares.

836
QUARTERLY J OURNAL OF ECONOMICS
ity.35 Perhaps this failure arises because of the novelty of the
experiment and the complexity of implementing backward induc-
tion. Perhaps this failure arises because Harvard students are
loathe to assume/acknowledge that their partners may exhibit
nationalistic preferences.
Regressions (4) and (8) of Table VI look at the impact of
within-pair racial differences. In our sample, more than 35
percent of the subjects are Asian, so there is considerable racial
heterogeneity. To analyze race, we divide the subject pairs into
four groups: white sender/white recipient (the omitted category),
white sender/nonwhite recipient, nonwhite sender/white recipi-
ent and nonwhite sender/nonwhite recipient. Note that subject
pairs in the last group may still exhibit within-pair heterogeneity,
since the nonwhite category is quite broad.
None of the group effects are significant in the amount sent
regressions, but all three groups have lower return ratios than the
white/white omitted category. The lowest return ratios occur
when white recipients return money to nonwhite senders. Most
strikingly, 92 percent of the cases where the recipient sent back
nothing occurred when the individuals were of different races,
while only 59 percent of the pairings were racially diverse.
The negative effect of different races may occur because
people from different races or countries have a lower probability of
interacting in the future, but the nationality and race effects
change little when we control for the two social connection
variables. Alternatively, lower levels of trustworthiness between
races may instead reflect lower levels of reciprocal altruism.
Whatever the interpretation, these results suggest that heteroge-
neity may decrease trustworthiness in social groups.36
C. Social Status and Individual Social Capital
Social capital has two rival conceptualizations. Many original
users of the term, J ames [1904], and more recently Loury [1977])
saw social capital as an individual-specific variable reflecting
35. These results support those of Fershtman and Gneezy [1998], but differ in
important ways. First, they examine trust of all people toward a low status
minority and find that there is less trust. Second, their subjects have no possibility
of repeated interaction after the game. Third, they allow no personal contact
between subjects, who must infer ethnicity from the last name of their partners.
Fershtman and Gneezy find no ethnic effects on amounts returned, but they look
only at the effect of the sender being Sephardic, not at any effects of sender-
recipient ethnic similarity on the amount returned.
36. La Porta et al. [1997] argue that ethnic heterogeneity may decrease the
quality of government by limiting the formation of aggregate social capital.

MEASURING TRUST
837
one’s ability to do well in social situations. In the 1990s Coleman
[1990] and Putnam [1993, 1995] have used the term to describe
group-level attributes, like the existence of a social network
among a group of friends. We examine evidence for the former
conceptualization in this subsection.
In Table VII we test whether people with high levels of social
status systematically realize high returns from social interac-
tions. Many different mechanisms could support such regularity.
For example, high status individuals may elicit trustworthy
behavior because they are relatively skilled at socially punishing
or rewarding others.
Table VII identifies individual characteristics that predict
high individual returns in the trust experiment. Conceptually, we
demonstrate the existence of individual-specific social capital. We
focus on characteristics of the sender that predict financial
success for the sender. Characteristics of the recipient that predict
success generally work because the characteristics predict cheat-
ing (i.e., returning less than the amount sent). This cheating may
be punished after the experiment ends, during routine social
interactions among Harvard students. So the total returns to the
recipient, including nonfinancial returns, are likely not to be
observed.
In our first regression we examine two measures of the
sender ’s family status: (1) hours spent working for pay and (2)
whether one’s father has a college degree. Hours spent working for
pay as a college student is strongly correlated with low family
income (44 percent), and we believe it is a significantly better
measure than the categorical family income variable that we
have. We also include two social connection variables. First, we
include the self-reported number of close friends that the indi-
vidual says he has (top-coded at 20). Second, we include the
number of hours per week that the individual spends volunteer-
ing. Approximately two-thirds of Harvard undergraduates volun-
teer regularly, and this is a particularly general form of social
interaction. We also include two proxies for ‘‘coolness’’ or charisma
in this subject population: beers drunk per week and whether the
individual has a sexual partner.37
In the first regression we find that working for pay has a
negative effect on amount sent but this effect is only marginally
37. This variable takes on a value of one if the individual has a current
girlfriend or boyfriend and if the individual has had sex with at least one other
person in the past five years.

838
QUARTERLY J OURNAL OF ECONOMICS
TABLE VII
SOCIAL CAPITAL, STATUS, AND THE RETURNS TO SOCIAL CAPITAL
Financial
returns to
sender as a
function
Financial
Amount
sent as a
function
of sender
Return
ratio as a
function
of sender
returns to
recipient
as a function
of sender
of sender
characteristics characteristics characteristics characteristics
(1)
(2)
(3)
(4)
Promise
Ϫ0.0450
Ϫ0.0103
0.1881
Ϫ0.2331
(0.1010)
(0.0491)
(1.2238)
(1.5552)
Different sex
White
Ϫ0.8162
0.0887
2.0264
Ϫ2.8426
(1.1147)
(0.0541)
(1.3510)
(1.7168)
0.2571
(1.0743)
Ϫ0.1849
(1.1733)
0.3741
(1.2394)
Ϫ2.5365
(1.5545)
0.0114
(0.0519)
0.1008
(0.0565)
Ϫ0.0174
(0.0602)
0.4036
(1.3021)
2.8013
(1.4220)
0.4294
(1.5021)
0.7949
(1.8840)
Ϫ0.1470
(1.6546)
Ϫ2.9861
(1.8070)
Ϫ0.0553
(1.9088)
Male
Freshman
Only child
0.0578
(0.0780)
Ϫ3.3314
(2.3941)
Father with college
degree
Ϫ0.3324
(2.0752)
0.1407
(0.0987)
2.3978
(2.5151)
Ϫ2.7302
(3.1961)
Hours worked for
pay
Ϫ0.1441
(0.0869)
Ϫ0.0092
(0.0043)
Ϫ0.2273
(0.1053)
0.0832
(0.1338)
Number of close
friends
Ϫ0.0919
(0.0658)
0.0112
(0.0032)
0.1684
(0.0798)
Ϫ0.2603
(0.1014)
Hours spent volun-
teering
0.0306
(0.2031)
0.0261
(0.0099)
0.6893
(0.2462)
Ϫ0.6586
(0.3128)
Sexual partner
Beer servings
Amount sent
Constant
2.8618
0.1726
4.7588
Ϫ1.8969
(1.4861)
(0.0723)
(1.8012)
(2.2889)
0.0471
(0.1243)
0.0136
(0.0063)
0.0118
(0.0065)
Ϫ0.0690
(0.1591)
0.308
0.3399
(0.1507)
Ϫ0.2929
(0.1915)
13.7772
(2.7993)
Ϫ0.0061
93
5.8516
(3.3926)
0.2006
93
22.9256
(4.3112)
0.0735
93
Adjusted R2
Observations
89
Standard errors are in parentheses. All regressions are ordinary least squares.
significant at the 10 percent level.38 The effect of father ’s educa-
tion is insignificant. Of the other variables, only having a sexual
partner positively predicts trust.
In the second regression we regress return ratio on character-
istics of the sender. This regression identifies several sender
38. The impact of the working for pay variable may reflect standard income
effects.

MEASURING TRUST
839
characteristics that significantly predict which senders will be
well treated by the recipients. We find significant coefficients on
all variables except for father ’s education. Father ’s education,
however, becomes significant if hours worked for pay is dropped
from the regression. The effects are often quite large. For example,
people without sexual partners receive 17 percent less back than
people who do have sexual partners (this is true of both men and
women).
These two regressions provide only partial snapshots of the
impact of social capital, because the regressions evaluate sepa-
rately amount sent and return ratio. The artificial but controlled
setting of our experiment has the advantage that we can precisely
measure total financial returns from this particular social interac-
tion. We next regress total financial returns (from the Trust
Game) on personal characteristics of our subjects. We perform this
regression separately for individuals in the sender and the
recipient position. All returns are measured in dollars.
Column (3) in Table VII reports the results of the sender
regression. Again, all variables except for father ’s college status
are significant. Without controls, the father ’s education variable
becomes much stronger. The average return for senders whose
father graduated from college is 14.75 dollars. The average return
for senders whose fathers did not graduate from college is 9.29
dollars. It appears that senders from families with lower human
capital would have been better off financially if they had not
trusted their partners. Comparing senders from high and low
income families also demonstrates these effects. The average
returns for senders from high income families was more than 2
dollars greater than the average returns for senders from low
income families. These higher returns appear to come solely from
the ability to elicit trustworthy behavior.
We find that senders who work for pay receive less from the
social interaction. Senders with sexual partners take home over 4
dollars more than their celibate classmates. Individuals who
drink beer earn more. Finally, a one-standard-deviation increase
in the volunteering variable raises financial returns from the
game by almost 2 dollars.
Since social capital of the sender does not predict higher
values of amount sent, but does predict higher values of return
ratio, it seems likely that social capital of the sender has negative
financial externalities for the recipient. Regression (4) in Table
VII confirms this conjecture. We regress the total financial returns