Abstract
We present results from an artefactual field experiment conducted in rural Peru that considers whether observing non-reciprocal behavior influences an individual’s decision to reciprocate.
Specifically, we consider the behavior of second movers in a trust game, assessing whether their decision to reciprocate is influenced by the observed behavior of others, and the extent to which their actions can be observed. In documenting whether an external shock to the number observed not to reciprocate influences reciprocation, the paper endeavors to provide some insight into how a norm of reciprocity can develop or unravel when individuals are observing each other’s behavior, as may be the case in a new market institution.
∗
Meetings, the International Food Policy Research Institute (IFPRI) and the 2009 Latin American Econometric
Society Meetings for meaningful comments.
We also thank Danielle Wainer for her assistance with conducting the experiments. The IFPRI Mobile Experimental Economics Laboratory (IMEEL) is gratefully acknowledged for financial support.
1

Mutual cooperation is essential to the development of many market institutions. Whilst simple spot market exchanges can take place in the presence of limited trust (Fafchamps, 2004) market exchanges that entail trade in unobserved characteristics (such as trade in organic produce), trade with delayed delivery (such as in credit or insurance markets), or trade in which delivery is conditional on acts of nature (such as is often the case in contract farming) require a certain degree of trust and reciprocity or mutual cooperation. When the extent to which individuals are willing to trust and behave trustworthily is low, it is much more difficult for such markets to develop. Studies conducted in rural (Karlan, 2007) and urban (Ambrus et al., 2008; Karlan et al., 2009) settings in Peru, for instance, have focused on how trust, through informal social networks, have made group lending schemes feasible by facilitating the monitoring and enforcement of joint liability loan contracts.
Recent experimental analyses have shown that there is considerable variation across societies in the probability that an individual will chose to cooperate when there is a short term gain to defection (Bowles et al., 2004). A number of empirical studies have examined the determinants of this heterogeneity. The starting point for this paper is the observation that the similarity in behavior of individuals from the same society is consistent with a model of human behavior in which an individual’s decision to reciprocate is influenced by the social environment that surrounds him (Manski, 2000). This is in keeping with a large theoretical
1 and empirical
2 literature that suggests the utility received from undertaking a particular action is in part determined by the extent to which it mimics the observed behavior of others.
1
Bernheim (1994), and subsequently Becker and Murphy (2000), delineate three channels by which the actions of others influence utility. The most basic is that of externalities: actions taken by others may increase (or decrease) returns an individual receives from undertaking the same action (such as in the case of contributing to a public good). The second mechanism is informational: to the extent that an individual is unsure about appropriate or optimal behavior, and to the extent he believes others in the group are better informed, the behavior of others may provide a source of information on the course of action he should take. Thirdly, social interactions can influence an individual’s preferences (Jones, 1984; Bernheim, 1994; Becker and Murphy, 2000). In particular the models of conformism set out in Jones (1984) and Bernheim (1994) allow for an individual to derive utility from minimizing the extent to which his actions deviate from the average behavior of others.
2
There are many empirical studies which have documented how choices may be taken to mimic the observed behavior of others, but ones closely related to the case considered here are Asch (1951), Asch (1955), Rosenbaum and Blake (1955), Rosenbaum (1956), Helson et al. (1958), Bryan and Test (1967), Cason and Mui (1998), Falk and
Knell (2004), Bardsley and Sausgruber (2005), Croson and Shang (2008) and Krupka and Weber (2008).
2

In this paper we present results from an artefactual field experiment (Harrison and List, 2004) conducted in rural Peru that considers how observing non-reciprocal behavior in a twice repeated trust game influences an individual’s decision to reciprocate. Specifically, we consider the behavior of a second mover,
3 assessing how her decision to reciprocate is influenced by the observed behavior of other second movers in the same room, and the extent to which her actions can be observed.
4
Empirically identifying the processes which give rise to a positive relationship between the propensity of an individual to behave in a certain way and the prevalence of that behavior in the group is difficult.
5
This paper uses an experiment conducted in a controlled environment to identify the presence of endogenous interactions. In particular, we use our experimental design to create an instrument for identification of this endogeneity. This approach is comparable to
Casari et al. (2007) who use their experimental design to create instruments that can be used to identify typical selection effects in common value experiments. Credible variation was exogenously introduced into the average observed behavior of the group by providing true information to player
As about the probability that player Bs would reciprocate. This information affects the average rate of unconditional reciprocation observed in the group of player Bs and serves as the source of exogenous variation that is used to identify the influence of observed behavior on individual decision making. These endogenous interactions are likely to arise as a result of preference interactions between group members. Our findings suggest that one mechanism by which this may occur is the following: as more group members are observed not to reciprocate the cost of deviation for any individual falls resulting in a higher propensity to deviate.
The paper thus endeavors to provide some insight into how a norm of reciprocity (and mutual cooperation) can unravel when individuals are observing each other’s behavior, as may be the case in a new market institution. In particular, this study contributes to the existing literature on the importance of trust, reciprocity and mutual cooperation in the development of market institutions for the poor in Peru.
6
In the microfinance literature, trustworthiness, as measured by the standard
3
Although we present results for both the first mover (the player who decides whether or not to trust the other player by choosing to send money, denoted throughout as player A) and the second mover (the player who decides, having been trusted, whether or not to reciprocate that trust by sending money back to the the first mover), the interest of our analysis is the second mover (player B).
4 Throughout the paper we use the convention that player B is female and player A is male.
5 As Manski (2000) argues, a positive relationship between individual and group behavior could arise as a result of the influence of observed behavior (endogenous interactions), the influence of observed characteristics (contextual interactions), or individual and environmental characteristics shared by group members (correlated effects).
6
Other studies have also used artefactual field experiments to better understand the links between behavior and
3

trust game, and “network based trust”,
7 used as “social” collateral to secure credit, have been shown to be important predictors for success of group lending programs in rural areas and informal borrowing schemes in urban shantytowns, respectively, where loan repayment is enforced mainly through social pressure (Karlan, 2005; Karlan, Mobius, Rosenblat, and Szeidl, Karlan et al.).
8
Based on these lessons, Castillo et al. (2007) have also proposed the use of artefactual field experiments to test contractual arrangements that aim to help resolve the incentive misalignment and trust problems in contract farming between farmers and firms in the coffee sector in Peru.
In the following sections we describe the experiments (Section 2); and present empirical results
(Section 3). Section 4 concludes.
We study whether adherence to a norm unravels at the individual level when an individual observes deviation from this norm at the group level. Our experimental design is based on three central issues. First, given our interest to study norm unraveling, we study behavior in an artefactual environment that has extensively been used to study normative behavior such as trust and reciprocity, i.e. the trust game (Berg et al., 1995). Second, since we are concerned with the second mover’s decision to reciprocate or not, in the presence of what is observed at the group level, we build “peer observability” into the design of the experiment. Finally, since individual behavior is not independent from group behavior, we use our experimental design to create an instrument for identification of this reflection problem (Manski, 2000). This approach can be compared to that of
Casari et al. (2007) who use their experimental design to create instruments for identifying typical selection effects that arise in common value auction experiments. Below we discuss the different components of our experimental design and how those enable us to study our main question.
ship (Castillo et al., 2008), the effect of ambiguity aversion on farm decisions (Engle-Warnick et al., 2008), and the behavioral effects of index insurance on cotton farmers (Carter et al., 2008).
7
Defined as the largest amount one agent can borrow from another agent.
8
Karlan (2005) also provides evidence that show that the motives behind Player A’s actions in a trust game remain unclear, as they are positively correlated to preferences for gambling rather than trust (understanding trust as an ability for social norms and relationships to mitigate risks inherent in informal contracts). This reinforces our decision to concentrate on Player B’s actions on this study.
4

Subjects in our experiment completed a standard dictator game protocol (DG) prior to participating in the main treatment (we discuss details related to the main treatment in the next section). The
DG was conducted when listing potential participants for the study (complete instructions are available upon request). This occurred a week prior to participation in the main treatment. The subject played the role of dictator and had to decide whether or not to divide 4 Peruvian soles
(heretofore referred to as “soles”) equally between herself and another person. If so, she and her partner in the main treatment would earn an additional 2 soles at the end of the study. If not, she would earn an additional 4 soles and her partner would earn 0 additional soles. The partner’s
DG choice would affect earnings in the same way, although the subject was not aware of this when making her DG choice. So, the subject could earn a maximum of 6 soles in addition to her earnings from the main treatment if selected. It was clarified to the subject that her choice in the DG would not be taken into account when determining whether or not she would be selected for the main treatment.
The procedures for the DG were primarily intended to assure anonymity of subject decisionmaking. We find this particularly important given recent evidence on audience effects in social preference experiments (e.g., Andreoni and Bernheim, 2009). Since the DG was conducted by enumerators (who were trained collectively by one of the experimenters), the following procedure was maintained to mitigate such effects. The subject was explained the decision she had to make
(i.e., whether to divide equally or not), the procedure for recording her decision (discussed below) and the consequence of her decision for earnings if selected (i.e., an additional 2 or 4 soles depending on her choice). The procedure for recording the decision was as follows. Once the enumerator explained the DG and answered any questions, he gave the subject a paper with the two options and an envelope. The enumerator then separated himself from the subject. The subject circled her option, folded the paper, put it in the envelope, sealed the envelope and handed it back to the enumerator. The enumerator then codified the envelope with a unique household id assigned by the experimenters.
To further mitigate the effect of another type of audience, the person who would pay the subject
(in this case, the assistant experimenter), we chose to conduct the DG during the listing phase of the study as opposed to the day of the main treatment. By separating the timing of decisionmaking from the timing of payment and thus, separating the person that obtained the response
5

(the enumerator) from the person that paid for it (the assistant experimenter), we thought that the subject was less likely to feel judged when making her decision.
Our design left minimal need to mitigate an audience effect towards the subject’s partner, whose earnings were actually being affected by the subject’s choice, since he was unknown to the subject.
Even during the main treatment, subjects were unable to learn each others’ identities since first and second movers were in separate communities by design of the experiment. We explain this further in the next section.
Apart from mitigation of audience effects, we had additional secondary reasons for conducting the DG during the listing phase of the study. First, we thought this would mitigate potential wealth
(order) effects from participating in the DG just prior to participating in the main treatment.
9
Second, since we used the DG decisions to provide information in one of the main treatments (as will be explained in the next section), it was useful to have the DG responses sorted in advance of the main treatment.
Each subject participated in one of the following main treatments: a twice repeated standard trust game protocol (TG) or a twice repeated modified trust game protocol (MTG).
10
The extensive form of the TG is presented in figure 1. Each period entailed the following, where time subscripts t
= 1
,
2 are suppressed.
11
At the beginning of the period, both the first mover (player A) and the second mover (player B) were given an endowment equal to x
.
12
The first mover had to choose between keeping x
(a move denoted by
E for “exit”) or sending x to player B (a move denoted by
T for “trust”). If player A chose
E
, the period ended and both players earned x
. If player A chose
T
, then player B would receive 3 x in addition to the initial endowment x
. At this point, player
B had to choose between keeping all 4 x and leaving player A with 0 (a move denoted by
D for
“defect”) or returning 2 x to player A and keeping 2 x
(a move denoted by
R for “reciprocate”).
This artefactual environment can be seen as studying “normative” behavior. Move
T is typically taken as a measure of “trust” since player A takes a risk by trusting player B with all her stakes
9 Our results are robust to controlling for subjects’ choices in the DG.
10 The twice repeated nature of the game protocol enables us to capture any strategic behavior such as first-period reciprocation (to gain second-period trust) followed by second-period defection.
11
The main graphic used to explain the game protocol is included in figure 7. Complete instructions are available upon request.
12 Our sessions varied x within the set
{
1,5,10
}
.
6

given the potential of gaining an additional x
. Indeed, social norms may dictate that player A should trust, since those same norms dictate that player B should reciprocate if trusted. So, the norm will make player A more likely to risk his stakes. Move
R is taken to be a measure of
“reciprocity” since player B holds all the stakes and any incentive to return money to player A is likely to be driven by reciprocity, although some have warned against potential confounds such as altruism (e.g., Cox, 2004). In this case also, social norms may dictate that player B should reciprocate when trusted since this is “the right thing to do”.
To study the effect of group behavior on individual behavior, we had to address two main questions. First, how to convey group behavior at the individual level within an artefactual experiment with field subjects (i.e., rural farmers). Second, having done that, how to identify the effect of group behavior on individual behavior given these are not independent.
To address the first question, we departed from the typical experiment setup in which subjects are separated from peers. While we still separated player As from player Bs by randomly assigning the role of player A and player B to different communities, we allowed player As to observe each other’s choices and player Bs as well. This was possible since players of the same role (A or B) were from the same community and thus, in the same room while making decisions. While subjects were instructed to not interact with each other, our experiment protocol did allow for visual observation of one’s peers. This was promoted by using white envelopes for “keeping” (
E or
D
) and yellow envelopes for “sending” (
T or
R
). We chose this form of “peer observability” since we found it to be quite natural for the subject pool under consideration. Indeed, it has been shown that decisions in rural areas such as adoption of new technologies tend to be affected by observation of neighbors’ yields as a result of their choices (Munshi, 2004). To exploit within session heterogeneity in “observability” using individual specific measures of what was observed, we randomly assigned seating at the beginning of the experiment session and held it fixed throughout. The results section discusses robustness of our results with regard to different spatial specifications.
To address the second question posed above, i.e., identification of the group effect, we used our experimental design to create an instrument in the following way. In addition to the TG, we conducted an MTG. The MTG was identical to the TG with the exception that player As received the following additional information. First, based on a baseline TG session conducted days prior, all player As were informed about second-period results from that session, where almost half of player Bs chose not to reciprocate (we call this “information”). Second, those player As that were paired with a player B that chose to “keep all 4 soles” in the DG were informed thereof (we call
7

this “personal information”). It is important to note that while we revealed the partner’s choice, we did not reveal her identity. Furthermore, revealing this information was not inconsistent with the DG protocol, which assured subject anonymity and privacy of decision-making towards the enumerator.
Since the MTG only provided information to player As, the TG and MTG were identical as far as player B is concerned. In particular, given player As and Bs were in completely separate communities when making their decisions, there was no possibility for informational spillovers from player As to player Bs.
The MTG information shock thus satisfies the conditions for a valid instrument, if we want to study the group effect on player B behavior. First, since the provision of information across treatments (MTG versus TG sessions) and the pairing of player Bs with player
As (provided with personal information or not) is randomly assigned, the shock is exogenous to player Bs’ decisions. Second, the shock affects the environment in which player Bs make their decisions in a credible and observable manner by changing the likelihood that player As trust and hence, the likelihood of observing a lower unconditional rate of reciprocation.
The TG captures individual behavior in the presence of group behavior conditional on any pre-existing norms of reciprocity. The MTG captures individual behavior in the presence of group behavior conditional on the information shock , which, as we hypothesize in the next section, was likely to increase norm deviation by player Bs. We compare player B decisions across the TG and the MTG and use the information shock to create an instrument for identification of the group effect. Further details are discussed in the results section.
This section discusses some hypotheses for how the MTG enables us to test the group effect, particularly, towards norm deviation. The statements that follow are made with regard to the
MTG relative to the TG.
The information shock provided to player As is expected to induce lower trust. In particular, we expect player As who received personal information not to trust, since this information clearly
“signals” that one’s partner is not trustworthy. So, the information shock in the MTG is expected to give rise to a decision-making environment that has a lower level of trust and thus, a lower level of unconditional reciprocation.
The main issue is whether this environment is conducive to unraveling of the norm of reciprocity. We hypothesize that the following is a main mechanism by which this could occur. As the
8

unconditional rate of reciprocation falls, player Bs feel that they are better able to hide or perhaps, justify selfish moves. Accordingly, they defect more frequently since the cost of norm deviation is lower. The group effect arises because an individual player B makes her decision observing the actions of her peers. This is supported by the protocol of “peer observability” that was discussed earlier.
Hill et al. (2010) develop a simple model to derive these hypotheses more formally; however, empirical support for these hypotheses can be found in two strands of related literature.
13
First,
Castillo and Leo (2009) show that the opportunity for an individual player B to hide selfish acts in the trust game generates more selfish behavior among player Bs. Also, Tadelis (2008) indicates the importance of “shame” and/or “guilt” for decisions made in the trust game. These findings provide empirical support for why player Bs may be less likely to reciprocate in the MTG. Since there is less unconditional reciprocation at the group level, this provides player Bs with an opportunity or reason to defect at lower cost.
Second, the vast literature on social interactions (e.g., Manski, 2000, and the references within), social learning (e.g., Chamley, 2004, and the references within) and social norms and conformism
(e.g., Bernheim, 1994; Lindbeck et al., 1999; Becker and Murphy, 2000) all delineate channels through which more defection at the group level is expected to increase the likelihood that an individual player B defects. As mentioned previously, the instrument enabled by our experimental design allows us to identify this endogenous effect.
There may also be other mechanisms by which an unconditional rate of reciprocation may induce the norm of reciprocity to unravel. For example, a player B who was trusted may consider it “unjust” that other player As chose not to trust her peers. Accordingly, she may choose to punish the player A she is paired with in order to “signal” the importance of trust as a norm to the player
A population. Alternatively, a player B who was trusted may update her belief towards the player
A population and expect her partner to be less likely to trust in the next period. In expectation thereof, she may choose to defect this period.
Disentangling these potential mechanisms is interesting and we attempt to address some of them in the results section. However, we note that for our instrument to be valid it is sufficient that there exists some mechanism by which lower unconditional reciprocity leads to unraveling of the norm. For that purpose, the exact mechanism is irrelevant.
13
Also see Bower et al. (1997) for a discussion of a twice repeated trust game without
“peer observability”.
9

We conducted 8 sessions with 308 randomly selected individuals from 7 rural communities surrounding the city of Huaral, 75 kilometers north from Lima (see Figure 2).
14
Each session comprised a group of around 18 player As and a group of around 18 player Bs located in separate communities.
The TG was conducted in 5 sessions and the MTG was conducted in 3 sessions.
15
Each session consisted of the following components implemented in community A for player As and in community B for player Bs. On average two hours before the experiment session started, enumerators would locate selected participants within their respective communities to inform them of the exact time and location of the study. Subjects were instructed to bring picture identification.
Upon arrival subjects would present their picture ID and get signed in by an enumerator. They would then draw a number out of a bag, which was recorded on the sign-in sheet. This number randomly determined their seat and partner throughout the experiment session. It also functioned as their identity during the experiment. Since subjects were not separated by dividers, random seating determined their degree of “peer observability” during the experiment. The layout of the sessions was typically the same as indicated in figure 6.
The experimenter was located at the front of the room, with three to five rows of four subjects spread across the room and the assistant experimenter in an adjacent room or hallway. Once all subjects were seated, the explanation would begin. Since some subjects were expected to have difficulty reading, all subjects were instructed orally. The exact text for the instructions can be obtained from the authors upon request; however, the gist involved the following.
Subjects were informed that they were players A or B. They were then informed that they would be playing a game twice with someone in another community of Huaral. They were informed that they would not learn the identity of this person and vice versa. Subjects were explained the details of the game (i.e., moves and earnings), how they would reveal their preferences and how anonymity would be maintained. The subject instructions included the graphic in figure 7, which was used to explain the details of the game.
Subjects were told the following. They would receive two envelopes: one white and one yellow
(this facilitated observation of peers’ actions). The white envelope was to be used to “keep” vouchers
(
E or
D
) and the yellow envelope was to be used to “send” vouchers (
T or
R
). Player As would
14
Prior to these sessions, one pilot session was conducted in the same communities for smaller stakes ( x
= 1).
These data are not used in the analysis.
15
The empirical analysis controls for unobserved session-specific heterogeneity by including session dummies.
10

reveal their preferences by either placing the voucher in the yellow envelope or not. Experimenter
A would then collect all yellow envelopes, place them in an accordion folder (organized/coded by seat number) and deliver the folder to assistant experimenter A. Assistant experimenter A would register the decisions and call assistant experimenter B to transfer the decisions.
Assistant experimenter B would register and confirm the decisions by repeating them, place the corresponding number of vouchers (either three or zero) in the yellow envelopes and place the envelopes in the corresponding slots of another identical accordion folder. Experimenter B would hand out the yellow envelopes and instruct player Bs to check the contents of the yellow envelopes.
Experimenter B would request player Bs to reveal their preferences according to the contents of the yellow envelope. In particular, those player Bs who were sent vouchers had a choice to make.
Player Bs would reveal their preferences by putting two vouchers in the yellow envelopes or not.
Those player Bs who were not sent vouchers had no decision to make and would place their one voucher in the white envelope. Experimenter B would collect the yellow envelopes, place them in the accordion folder and hand the folder to assistant experimenter B. Assistant experimenter B would register the decisions and call assistant experimenter A who would in turn register and confirm the decisions, and then, place the number of vouchers in the yellow envelopes. Experimenter A would then hand out the yellow envelopes and instruct player As to review the contents of their yellow envelopes. Any remaining vouchers at the end of the period would go into the white envelope. This process would be repeated twice.
Once this process was explained, subjects were quizzed on their understanding of the game and the process. In particular, the experimenter would propose hypothetical strategies and request players’ feedbacks on their set of available moves or earnings. This served as an indication of issues that needed clarification prior to play of the game. After the quiz, decision-making would take place.
In order to maintain consistency throughout the sessions, both experimenters maintained the same script throughout their respective sessions. These scripts were identical across player A and B sessions, with the exception of the MTG sessions where additional information was given to player
As. The information on the proportion of player Bs that had reciprocated in the baseline session was publicly announced to all player As, whilst personal information was relayed to the respective player A privately. This was done by informing those subjects individually outside of the room.
All subjects participated in a short household survey that was conducted by the enumerators.
A session lasted on average two and one half hours. Upon completion of the session, subjects were
11

paid in private by the assistant experimenter for their (i) session earnings, (ii) show-up earnings (1 sol), (iii) survey earnings (1 sol) and (iv) DG earnings (2, 4 or 6 soles). Average earnings were 34.08
soles (standard deviation: 16.88). This represents more than 6% of the local monthly minimum wage for our subject pool (additional characteristics of our sample will be discussed in the next section).
Situated in the valley of the Chancay river, the Huaral area is one of Lima’s main providers of fresh produce, poultry and pork, which is why it is known as “Lima’s pantry”. Not surprisingly the main income generating activity for most of the households in Huaral is market-oriented agriculture. In spite of this, the majority of parcels are small and poverty is still highly prevalent in the area.
The 7 communities selected for the intervention were chosen based on: (i) classification as rural by Peru’s National Statistics Bureau (INEI), and (ii) size. Selected communitied had at least
100 households in the community.
16
Player A and player B sessions were conducted in separate communities simultaneously in order to guarantee that participants knew as little as possible about the person they had been paired with.
Every participant responded to a short household survey near the end of their session from which basic characteristics of our sample were obtained. These are summarized in Table 1, compared by player role and type of game. T-tests of the differences in means between types of game (TG and
MTG) for each group of players (A and B) are provided in the table in order to determine if the participants in the MTG sessions were different in observable characteristics from those in the TG sessions (even though participation in MTG and TG sessions was determined randomly).
Table 1 shows that there are some significant differences among participants in TG and MTG sessions. Compared to the average player in an MTG session, the average player A in a TG session is older, less likely to have children, less likely to have a mother that is a native Quechua speaker, lives in a larger house, has more land, has a higher annual income, and is more likely to have received payments in advance. The average player B in a TG session is older, lives in a larger house, has a higher annual income, considers himself better off, has received payments in advance more often, and has lent money more often.
16
The communities were San Jose, Cuyo, Esperanza, La Huaca, La Caporala, Retes, and Miraflores.
12

For our purposes, however, what matters is whether any of these differences have an effect on decisions to keep or send back money in the game, in the absence of the information treatment. We argue that the dictator game response from the listing stage of the experiment is a good proxy for reciprocal tendencies and we run a regression of this against basic characteristics. The results are shown in Table 2. In the basic dictator game, we found that 24 percent of individuals responded that they would choose to keep all of the money given to them (25 percent of player As and
23 percent of player Bs). We observe that only income and having lent money in the past are significantly related to the decision to send money in the dictator game. Given there are some significant differences in these variables between players in TG and MTG sessions (particularly for player B participants) we use them as controls in all our estimations to control for possible selection bias on these observable characteristics.
17
Figures 3, 4 and 5 show the game trees (full, and separating sessions with and without information), indicating how the 140 pairs of participants are distributed along the decision process. Only slightly more (26 percent) player Bs chose to keep the money in round 1 than in the DG, however a much higher proportion, 36 percent, chose to keep the money in round 2. The game tree suggests that in the MTG sessions there was a difference in both player A and B behavior: fewer player As sent and, conditional on being sent, fewer player Bs reciprocated in the the second and final round.
It is these differences, particularly the latter, that we seek to explain in the following analysis.
We begin by assessing the impact of information on player A behavior. We would expect that being provided with the information that one has been partnered with an untrustworthy type would discourage player A from sending, and the game tree also seems to suggest this is the case
(figures 4 and 5). This is tested in Tables 3 and 4 which regress trusting behavior on whether information was provided, the level of stakes and individual controls. It is important to control for the history of round 1 in assessing round 2 results. To do this, we construct the history variable as 1 if player B defected in round 1, i.e. behaved untrustworthily, and 0 if he reciprocated or had not been trusted by player A for starters. The key finding from these tables is that introducing information greatly reduces the probability that player A will trust. This exogenously affects the environment in which player Bs make their decisions (given player B is unaware player A was
17
Our results are robust to the inclusion as controls of the full set of characteristics that are significantly different between TG and MTG sessions from Table 1.
13

provided with information), which is crucial for our analysis.
Although information has strong effects in both rounds, the role of information changes between rounds 1 and 2. In round 1 it is personal information that plays the largest role in determining behavior, with no impact of information on trusting behavior, for those who were not provided with information on the person they were playing with. In round 2, the provision of information now has an impact at the group level, with those that were provided personal information being no more likely to exit than other player As in the room who were not provided with information. The results suggest that when player A observes more non-reciprocal behavior of the partners of their fellow player As (as is the case in the information treatments as shown below), they will choose not to send.
To analyze player B’s decision to defect or reciprocate we regress the choice to defect on the same controls, and additionally on the proportion of other player Bs that do not reciprocate (whether they were trusted or not) in each round. We now know that this proportion is driven in part by the information provided in player A’s sessions. However, given we hypothesize the presence of interdependence between the choices of player Bs we cannot assume that, for a given player B, the proportion of other player Bs in the room that chose to defect was not in turn caused by the behavior of that player (what Manski, 2000, refers to as the reflection problem). It is thus necessary to instrument for the proportion of player Bs observed to defect. Given this proportion increases exogenously with the provision of information (as fewer player As trusted), we use a dummy of the provision of information as an instrument. In particular we use a dummy that takes the value of 1 if player B was in a session in which, unbeknownst to her, information was provided to player As thereby discouraging trusting. OLS and IV results for first round behavior are presented in Table
5, and OLS and IV results for second round behavior are presented in Table 6.
Table 5 indicates that in round 1, the proportion of other participants not reciprocating, has no significant effect on player B behavior. This is true for both the OLS and instrumented regressions.
However, in round 2 this proportion has a strong effect on player Bs behavior. The more players observed not reciprocating , the more probable it is that player B will decide to defect when having the choice.
18
The insignificance of social influences in the first round, despite their significance in the second, is consistent with the hypothesis that strategic motives play a role in whether or not a
18 We run regressions (1) and (3) using the proportion of other players not reciprocating in the previous round instead of the concurrent round. The effect seems to be immediate, as what happens in the room in the present round seems to explain more of the variation in behavior than the behavior of others in previous rounds.
14

self-regarding individual reciprocates or defects at this stage.
As discussed in Section 2.3, player B behavior may also be driven by whether or not other player Bs are trusted. In other words, player B may observe other player Bs not reciprocating purely because they were never trusted. This is different than a situation in which player B is trusted and decides to defect. If player B is indeed reacting to this information, the main story would be one of updating priors about the player A population. We believe this story to be unlikely for a few reasons. First, player B already knows the action that her paired player A took when she takes her decision. So, updating is less relevant in this context, particularly, since players knew that they were playing with the same person in both rounds. Second, even if player B were reacting to this information, we would expect her to be more likely to defect in the first round in anticipation of her paired player A exiting in the next round. Given our main effects are for the second round we think this is an implausible story. Finally, we ran an auxiliary regression including the number of player Bs not reciprocating, the number being trusted, and an interaction term between these two terms which showed that the number of player Bs being trusted has no direct effect on defecting behavior, but only an indirect one through its impact on reciprocation.
In columns (2) and (4) of tables 5 and 6 we also include the proportion of people sitting behind a given player as a measure for “being observed” which may proxy for shame or other emotions that affect conformity to norms (Elster, 1989, 1998). Seating was randomly assigned to individuals so variation in this measure was randomly determined. Seating remained constant between rounds such that this measure was also stable across rounds. As the proportion of people sitting behind the player increases we would expect the probability that the player adheres to the norm of reciprocity rises (as the disutility that arises from being observed to deviate from the social norm increases). Again in round 1 this measure of the social environment is insignificant in explaining player behavior. However, in round 2 we observe that the players location in the room does have an influence on reciprocating behavior, with those located at the front of the room being more inclined to reciprocate, than those located at the back of the room where their actions are less observed.
Before assessing the robustness of our results, we first explore whether observed behavior is encouraging individuals to conform or deviate to their previously disclosed preference for reciprocating.
One way to test this idea is to find a proxy for what the individual would do in the absence of
15

the group. We can think of this as a measure of the participant’s true choice or raw preference for altruism or equality. However, when the participant has to choose in a group setting he might prefer to conform or deviate from this preference, dependent on what he or she observes others doing. As a proxy for what the individual might do in the absence of the group, we use a preference for equality that was expressed in the choices made in the DG prior to participating in the TG or
MTG.
In Table 7 we test the effect of the dictator game results and its interaction with the proportion not reciprocating in the room. We can appreciate in the second column that the proportion not reciprocating appears to matter for those who sent in the dictator game, while non-senders (in the
DG) are unaffected. This is only true for round 2 behavior.
19
In Table 8 we constructed a new dependent variable: 1 if the player’s response diverges from what she did in the dictator game, and 0 otherwise. This measure of divergence is regressed on the proportion of other player Bs not reciprocating and the usual set of controls. The first two columns present results for all player Bs, whilst the second two columns only include those that chose to send in the DG.
20 The results in column 3 show that for those participants that claim they would send in the dictator game, the probability of diverging increases as more people around them do not reciprocate. This confirms that, in the second round, player B is more likely to diverge from her DG response when she observes others not reciprocating.
21
These results suggest that people who would normally reciprocate, are encouraged not to when they observe others deviating from the norm of reciprocation.
22 However, we note that in both cases, once the proportion of other players not reciprocating is instrumented, the variables of interest become insignificant (although the sign remains consistent).
In the following we explore alternative measures of the proportion of people observed not to reciprocate. However, first, we consider whether there is any evidence of imitation as a result of limited understanding of how to play the game.
19
In round 1 the dictator game results did not have any explanatory power, either when entered directly or interacted with the proportion of people sending.
20 We cannot run a regression for those that chose to keep in the DG due to insufficient observations.
21
Again, a similar exercise for round 1 behavior yielded no significant results, and these results are omitted to save space.
22
Given small numbers it is hard to tell what the impact of group behavior is on those who would normally keep.
16

A participant might be influenced by what other players in the session are doing if he does not understand the game or lacks the ability to decide on his own. In this case a participant may choose to imitate the behavior of others assuming that this is indeed optimal behavior for the novel situation with which he is presented. We attempt to proxy the lack of ability to decide with education, age, and mother’s native language. If the imitation hypothesis is right, we would expect that the influence of other participants (the proportion not reciprocating) should be less for players with higher ability (more educated, younger, or with Spanish-speaking mothers). The interaction between the proportion not reciprocating in the room and the proxy for ability would be significant and negatively correlated with reciprocating.
Table 9 shows the results for these tests, and offers little support for the imitation hypothesis.
Although education does appear to play a role in round 2 in that the R-squared increases to 0.29, the level of schooling and the interaction between the proportion of keepers and schooling is not significant. This suggests that imitation does not have a stronger effect for those who we might expect to be less likely to understand the game.
23
Thus far we have just considered the impact of the average behavior of other player Bs in influencing player Bs choice to reciprocate. However, given the location of the players varies in the room we would expect players’ ability to observe the actions of other players to vary. As a result, a measure of the average behavior of other player Bs may not be the appropriate measure for what a given player observes. In this section we test the robustness of our results for alternate measures. First, we define:
•
Players seen: Number of participants in the same row and in the rows in front of the player.
•
Proportion of seen that do not reciprocate: Number of players seen not reciprocating divided by the number of players seen.
23
It is possible that education could be capturing an income effect. However, interestingly (and rather surprisingly) the effect of education on household income is not significant when we estimate a basic earnings equation. A possible explanation for this might be the high number of women not participating in the labor market in our sample of participants, as well as the low returns to education in the type of jobs the household members in our sample are engaging in.
17

In columns 1 and 2 of Tables 10 and 11 we use the proportion of seen that do not reciprocate in place of the total proportion of other player Bs that do not reciprocate. When including the proportion of seen that do not reciprocate, we observe very similar results to those presented earlier for the total proportion of other players in the room that do not reciprocate. However, in these regressions the proportion of players not seen no longer has a significant effect on behavior. This suggests that the significance of the proportion of players not seen in previous regressions arose as a result of the fact that an individual’s position in the room determines the degree to which average behavior was observed. The insignificance of the proportion not seen in the Table 10 regressions indicates that shame or other related emotions is not such an important determinant of player behavior.
We further explore this issue by constructing a more flexible (and less dichotomous) variable to capture the impact of the players’ ability to see other players’ actions (given their location in the room). As before, the players not seen by any given player are those sitting in the rows behind him. However, we no longer assume that the player is able to observe the actions of everybody else in his row and in the rows in front of him, at least not to the same degree. Building concentric semi-circles around each player, we can assume that each of them can observe the actions of the other players in the different semi-circles around him with varying degrees of difficulty. Evidently, the further away the other player is, the harder it will be to observe his actions.
The logic behind the concentric semi-circles measure is better understood by looking at Figure
6. From player 15’s point of view, all the players in the back row (17 to 20) are in his “blind spot”.
Players 10, 11, 12, 14, and 15, are immediately next to him, and therefore are the most observable to him. Players in the second row (5 to 8) and also players 9 and 13, have one player in between player 15 and themselves, so we can assume their actions are slightly more hidden. Players in the front row (1 to 4) are “two players away” from player 15, and hence even harder to observe. Thus, we build this measure by giving different weights to the players seen not reciprocating depending on the semi-concentric circles they belong to.
24
Columns 3 and 4 of Tables 10 and 11 include the concentric semi-circles measure assuming only the first semi-circle around him is visible to the player, while columns 5 and 6 assume the first semi-circle is 4 times as visible as the other semi-circles. We find that this last specification improves the
R 2 considerably giving us more robust results.
24
Notice that our initial measure, the proportion of seen that do not reciprocate used in columns 1 and 2 of Tables
10 and 11, is just a special case of the concentric semi-circles measure where all the circles have the same weight.
18

In this paper we present results from an artefactual field experiment conducted in rural Peru that considers how observing deviation from a norm of reciprocity influences an individual’s decision to reciprocate. Empirically identifying the processes which give rise to a positive relationship between the propensity of an individual to behave in a certain way and the prevalence of that behavior in the group is difficult (Manski, 2000). Possible explanations include influence of observed behavior, observed characteristics of group members, and common characteristics across individuals. We use exogenous variation in the average observed behavior of the group, to identify the influence of observed behavior on individual decision making. We find that the probability an individual will deviate from a norm of reciprocity increases with the number of others observed to deviate.
Our evidence suggests that this endogenous interaction arises as a result of preference interactions between group members: as more group members are observed to deviate the cost of deviation for any individual falls resulting in a higher propensity to deviate.
We also used random variation in the position of group members to assess how observability affects behavior. We did not find that individuals that were more likely to be observed were less likely to reciprocate once we had controlled for what the individual observed.
In documenting whether an external shock to the number observed not to reciprocate encourages others to deviate, the paper endeavors to provide some insight into how a norm of reciprocity can develop or unravel when individuals are observing each other’s behavior, as may be the case in a new market institution. Further analysis on how behavior is influenced by the relationship between those who were observing and those who were observed to deviate would be a nice extension to this analysis.
19

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23

E
1
(2 x,
2 x
E
2
)
D
2
T
2
B
R
2
( x,
5 x
) (3 x,
3 x
)
T
1
E
2
D
2
D
1
T
2
R
2
B
( x,
5 x
) (0
,
8 x
) (2 x,
6 x
)
E
R
2
1
D
2
T
2
R
2
(3 x,
3 x
) (2 x,
6 x
) (4 x,
4 x
)
Figure 1: Extensive form of twice-repeated trust game
24

Figure 2: Huaral communities in the intervention
25

E
2
(2 x,
= 14
2 x
)
D
2
= 6
( x,
5 x
)
E
1
= 27
T
2
B
= 13
R
2
= 7
(3 x,
3 x
)
T
1
= 113
B
D
1
= 30
R
1
= 83
E
2
= 17
D
2
= 9
T
2
= 13
R
2
= 4
E
2
= 15
D
2
= 20
T
2
= 68
R
2
= 48
( x,
5 x
) (0
,
8 x
) (2 x,
6 x
) (3 x,
3 x
) (2 x,
6 x
) (4 x,
4 x
)
Figure 3: Distribution of moves along twice-repeated trust game (All sessions)
(2
E
2 x,
2
= 2 x
)
D
2
= 2
( x,
5 x
)
E
1
= 8
T
2
B
= 6
R
2
= 4
(3 x,
3 x
)
T
1
= 75
B
D
1
= 21
R
1
= 54
E
2
= 11
D
2
= 7
T
2
= 10
R
2
= 3
E
2
= 7
D
2
= 10
T
2
= 47
R
2
= 37
( x,
5 x
) (0
,
8 x
) (2 x,
6 x
) (3 x,
3 x
) (2 x,
6 x
) (4 x,
4 x
)
Figure 4: Distribution of moves along twice-repeated trust game (“No-info” sessions)
E
2
(2 x,
= 12
2 x
)
D
2
= 4
( x,
5 x
)
E
1
= 19
T
2
B
= 7
R
2
= 3
(3 x,
3 x
)
T
1
= 38
B
D
1
= 9
R
1
= 29
E
2
= 6
D
2
= 2
T
2
= 3
R
2
= 1
E
2
= 8
D
2
= 10
T
2
= 21
R
2
= 11
( x,
5 x
) (0
,
8 x
) (2 x,
6 x
) (3 x,
3 x
) (2 x,
6 x
) (4 x,
4 x
)
Figure 5: Distribution of moves along twice-repeated trust game (“Info” sessions)
26

Figure 6: Semi-concentric circles measure of observability from player 15’s point of view
27

1.
Player A and Player B are given 5 soles
Player A Player B
2.
Player A chooses to SEND
Player B 5 soles or KEEP 5 soles
Player A
KEEP SEND
GAME
3.
If Player A KEEPS , the game ends with both players having 5 soles
Player A Player B
4.
If Player A SENDS , we multiply the amount given to player B by 3
X 3 =
Player B now has 20 soles and Player A, none
Player A Player B
0
6.
If Player B KEEPS , the game ends with Player
A having 0 soles and Player B having 20 soles
7.
If Player B SENDS , the game ends with Player
A having 10 soles and Player B having 10 soles
5.
Player B now CHOOSES to SEND 10 soles to Player A or KEEP all 20 soles
Player B
KEEP SEND
Player A
0
Player B Player A Player B
Figure 7: Graphical explanation of the game
28

29

Table 1: Sample means of basic characteristics by player role and type of game
Female
Age
Schooling
Any children
Household size
Quechua speaking mother
Father’s schooling
Catholic
Rooms in house
Land (has.)
Household annual income b
Household wealth status
Ever paid in advance
Ever received payment in advance
Lent money often
Sent in dictator game d c
Player A
TG MTG Diff.
0.687
0.702
-0.015
(0.051) (0.061) (0.080)
44.517
36.381
8.136
(1.749) (1.673) (2.602)
∗∗∗
5.215
4.992
0.224
(0.108) (0.135) (0.175)
0.892
1.000
-0.108
(0.034) (0.000) (0.044)
∗∗
4.458
4.720
-0.262
(0.202) (0.262) (0.331)
0.313
0.491
-0.202
(0.051) (0.067) (0.083)
∗∗
5.048
4.200
0.848
(0.428) (0.434) (0.646)
0.819
0.807
0.012
(0.042) (0.053) (0.067)
3.892
3.140
0.752
(0.181) (0.225) (0.291)
∗∗
1.495
0.332
1.164
(0.369) (0.172) (0.494)
∗∗
8.667
5.906
2.762
(1.138) (0.779) (1.519)
∗
4.494
4.460
0.034
(0.102) (0.141) (0.171)
0.157
0.080
0.077
(0.040) (0.039) (0.060)
0.205
0.080
0.125
(0.045) (0.039) (0.065)
∗
1.518
1.360
0.158
(0.065) (0.080) (0.104)
0.727
0.750
-0.023
(0.051) (0.063) (0.082)
Player B
Observations 83 57 83 57 a
Standard errors in parentheses.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at 10%.
b
In thousands of Soles.
c
Self-reported, 1 being “Richest” and 6 being “Poorest”.
d
Dictator game results were not available for 6 pairings in the TG, and 9 pairings in the MTG.
TG MTG Diff.
0.554
0.649
-0.095
(0.055) (0.064) (0.085)
44.428
39.825
4.603
(1.678) (1.782) (2.513)
∗
5.003
5.113
-0.110
(0.099) (0.118) (0.154)
0.940
0.893
0.047
(0.026) (0.042) (0.047)
4.554
4.875
-0.321
(0.174) (0.292) (0.320)
0.325
0.228
0.097
(0.052) (0.056) (0.078)
4.819
4.571
0.248
(0.381) (0.451) (0.594)
0.892
0.842
0.049
(0.034) (0.049) (0.058)
4.169
3.375
0.794
(0.192) (0.203) (0.287)
∗∗∗
1.010
0.482
0.528
(0.283) (0.168) (0.372)
8.667
5.280
3.387
(1.146) (0.549) (1.457)
∗∗
4.590
4.911
-0.320
(0.097) (0.115) (0.151)
∗∗
0.145
0.071
0.073
(0.039) (0.035) (0.055)
0.146
0.036
0.109
(0.039) (0.025) (0.052)
∗∗
1.518
1.250
0.268
(0.067) (0.058) (0.095)
∗∗∗
0.803
0.750
0.053
(0.049) (0.083) (0.093)
30

Table 2: Determinants of sending behavior in dictator game
Dependent variable: 1 if sent, 0 if kept
Female
Age c
Schooling c
Any children
Household size
Mother’s 1st language: Quechua
Father’s schooling
Catholic
(0.009)
-0.029
(0.082)
Rooms in house -0.001
(0.018)
0.017
Land (Has.)
Household annual income
(0.013)
0.007
(0.004)
∗∗
Household self-reported wealth status -0.001
Ever paid in advance
Ever received payment in advance
Lent money often
Constant
(0.032)
0.007
(0.088)
-0.008
(0.086)
0.089
(0.052)
∗
0.396
(0.326)
0.022
(0.063)
0.001
(0.002)
0.035
(0.032)
-0.022
(0.115)
-0.006
(0.016)
-0.052
(0.061)
0.001
Observations
R 2
246
0.08
a
Standard errors in parenthesis.
∗∗ significant at 5%,
∗
∗∗∗ significant at 1%, significant at 10%.
b
For this regression we pooled together the responses of all participants (player As and Bs).
c
Imputed missing values for 29 observations.
31

Table 3: Player A in round 1
Dependent variable: 1 if trust, 0 if exit
Stake = 10
Personal information
-0.015
(0.065)
-0.377
(0.113)
∗∗∗
Information -0.119
(0.074)
Household annual income 0.005
(0.004)
Lent money often 0.013
(0.057)
Constant 0.854
(0.102)
∗∗∗
-0.010
(0.065)
-0.460
(0.102)
∗∗∗
-0.026
(0.067)
0.005
(0.004)
0.016
(0.057)
0.805
(0.098)
∗∗∗
-0.231
(0.068)
∗∗∗
0.003
(0.004)
0.037
(0.059)
0.833
(0.105)
∗∗∗
Observations
R 2
133
0.18
133
0.16
133
0.10
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at
5%,
∗ significant at 10%.
32

Table 4: Player A in round 2
Dependent variable: 1 if trust, 0 if exit
Stake = 10
Personal information
0.241
(0.073)
∗∗∗
0.296
Information
(0.129)
-0.154
(0.083)
∗
B did not reciprocate in round 1
-0.426
(0.074)
Household annual income -0.002
∗∗∗
Lent money often
Constant
(0.004)
0.048
(0.064)
0.703
(0.115)
∗∗∗
0.248
(0.073)
∗∗∗
-0.075
(0.117)
-0.241
(0.072)
∗∗∗
-0.433
(0.075)
∗∗∗
-0.001
(0.004)
0.052
(0.064)
0.642
(0.111)
∗∗∗
-0.146
(0.074)
∗
-0.423
(0.073)
∗∗∗
-0.002
(0.004)
0.045
(0.063)
0.704
(0.114)
∗∗∗
Observations
R 2
133
0.29
133
0.27
133
0.29
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at
5%,
∗ significant at 10%.
33

0 if reciprocate b
Proportion of Bs not reciprocating,
M
1 c
Proportion of Bs not seen,
M
2
Stake = 10
Household annual income
Lent money often
Constant
Table 5: Player B in round 1
Dependent variable: 1 if defect, (1)
OLS
(2)
OLS
(3)
IV
(4)
IV
0.069
(0.321)
0.063
(0.096)
-0.003
(0.005)
-0.112
(0.077)
0.369
(0.183)
∗∗
0.067
-0.777
-0.787
(0.324) (0.676) (0.685)
0.010
(0.162)
0.059
(0.170)
0.064
0.164
0.166
(0.097) (0.121) (0.123)
-0.003
-0.003
-0.003
(0.005) (0.005) (0.005)
-0.112
-0.136
(0.077) (0.081)
∗
0.364
(0.203)
∗
0.713
(0.305)
∗∗
-0.137
(0.081)
∗
0.681
(0.305)
∗∗
Observations
R 2
112
0.04
112
0.04
112 112 a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at 10%.
b
Conditional on being trusted by Player A.
c
Defecting (by own choice) or because they were not trusted by Player A.
34

0 if reciprocate b
Proportion of Bs not reciprocating,
M
1 c
Proportion of Bs not seen,
M
2
Stake = 10
A trusted in round 1
B did not reciprocate in round 1 c
Household annual income
Lent money often
Constant
Table 6: Player B in round 2
Dependent variable: 1 if defect, (1)
OLS
(2)
OLS
(3)
IV
(4)
IV
0.606
(0.195)
∗∗∗
-0.002
(0.005)
-0.007
(0.077)
-0.254
(0.281)
-0.011
(0.108)
0.259
(0.183)
0.385
(0.141)
∗∗∗
-0.002
(0.005)
-0.009
(0.077)
-0.020
(0.305)
0.622
(0.192)
∗∗∗
-0.332
(0.179)
∗
0.001
(0.107)
0.211
(0.182)
0.364
(0.140)
∗∗∗
0.692
(0.329)
∗∗
-0.015
(0.109)
0.263
(0.184)
0.385
(0.141)
∗∗∗
-0.002
(0.005)
-0.003
(0.081)
∗
-0.308
(0.326)
0.770
(0.325)
∗∗
-0.338
(0.180)
∗
-0.006
(0.108)
0.217
(0.183)
0.364
(0.140)
∗∗
-0.001
(0.005)
-0.003
(0.081)
∗
-0.108
(0.343)
Observations
R 2
94
0.18
94
0.21
94
0.18
94
0.21
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at
10%.
b
Conditional on being trusted by Player A.
c
Defecting (by own choice) or because they were not trusted by Player A.
35

Table 7: Comparing player B in round 2 with dictator game results
B defects, round 2
(1)
OLS
(2)
OLS
(3)
IV
(4)
IV
Sent in DG
Proportion of Bs not
M reciprocating,
M
1
M
1
×
Sent in DG
1
×
Kept in DG
B did not reciprocate in R1
Constant
0.111
-0.045
(0.151) (0.346)
0.549
(0.246)
∗∗
0.604
(0.271)
∗∗
0.255
(0.639)
Proportion of Bs not seen,
M
2
Stake = 10
-0.403
(0.233)
0.087
∗
-0.400
(0.234)
0.111
(0.138) (0.147)
Household annual income -0.002
-0.002
∗
Lent money often
A trusted in R1
(0.011) (0.011)
-0.005
-0.011
(0.099) (0.100)
0.005
-0.021
(0.253) (0.260)
0.163
0.156
(0.220) (0.222)
0.105
0.243
(0.384) (0.475)
0.080
0.206
(0.160) (0.609)
0.835
(0.501)
0.645
(0.518)
0.890
(1.211)
-0.377
-0.393
(0.239) (0.240)
0.053
0.054
(0.149) (0.174)
-0.002
-0.002
(0.011) (0.011)
-0.013
-0.004
(0.101) (0.104)
0.015
0.025
(0.256) (0.276)
0.185
0.178
(0.226) (0.228)
-0.013
-0.047
(0.429) (0.673)
Observations
R 2
65
0.20
65
0.20
65
0.18
65
0.18
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at 10%.
36

Table 8: Explaining divergence from dictator game results
B diverges, round 2
(1)
All
OLS
(2)
All
IV
(3)
Sending Sending types
OLS
(4) types
IV
Proportion of Bs not reciprocating,
M
1
Proportion of Bs not seen,
M
2
Stake = 10
Lent money often
0.177
-0.310
-0.040
0.124
-0.315
-0.038
0.586
(0.279) (0.552) (0.282)
-0.484
(0.267) (0.272) (0.281)
0.042
0.049
0.139
(0.158) (0.170) (0.156)
Household annual income -0.010
-0.010
-0.000
(0.012) (0.012) (0.012)
-0.037
(0.113) (0.114) (0.111)
∗∗
∗
A trusted in round 1 -0.042
-0.045
-0.120
(0.290) (0.291) (0.327)
-0.055
-0.061
0.010
B did not reciprocate in round 1
Constant
(0.251) (0.256) (0.286)
0.686
0.712
0.380
(0.426) (0.489) (0.459)
-0.043
(0.113)
-0.129
(0.329)
0.016
(0.288)
0.319
(0.512)
0.714
(0.551)
-0.470
(0.286)
0.135
(0.157)
-0.000
(0.012)
Observations
R 2
65
0.06
65
0.06
65
0.18
65
0.18
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at 10%.
37

Table 9: Testing for imitation in round 2
B defects, round 2 (1) (2) (3)
Proportion of Bs not reciprocating,
M
1
Schooling
M
1
×
Schooling
1.629
(0.977)
-0.054
(0.116)
-0.193
(0.190)
Age
M
Quechua speaking mother
M
1
1
×
×
Age
Quechua speaking mother
Proportion of Bs not seen,
Stake = 10
Household annual income
Lent money often
A trusted in round 1
B did not reciprocate in round 1
Constant
M
2
0.515
(0.647)
0.647
(0.234)
∗∗∗
0.002
(0.008)
0.002
(0.014)
-0.436
(0.177)
∗∗
-0.026
(0.102)
0.001
(0.005)
-0.018
(0.081)
0.042
(0.182)
0.304
(0.135)
∗∗
0.462
(0.663)
-0.350
(0.184)
∗
-0.001
(0.107)
-0.003
(0.005)
-0.011
(0.085)
0.223
(0.184)
0.386
(0.143)
∗∗∗
-0.114
(0.465)
0.049
(0.251)
-0.116
(0.492)
-0.335
(0.183)
∗
0.012
(0.118)
-0.002
(0.005)
-0.010
(0.086)
0.213
(0.185)
0.362
(0.143)
∗∗
-0.037
(0.332)
Observations
R 2
94
0.30
94
0.22
94
0.21
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at
5%,
∗ significant at 10%.
38

Table 10: Robustness checks: Improving the measure of what is observed
B defects, round 2
(1)
OLS
(2)
IV
(3)
OLS
(4)
IV
(5)
OLS
(6)
IV
Prop. of Bs seen 0.570
not reciproc.
(0.181)
∗∗∗
Semi-circle measure
Stake = 10 0.032
(0.106)
Household annual -0.002
income
Lent money often
A trusted in round 1
B did not recip.
in round 1
Prop. of Bs not seen
Constant
(0.005)
0.006
(0.084)
0.193
(0.183)
0.360
(0.140)
∗∗
-0.201
(0.183)
-0.047
(0.310)
0.668
(0.282)
∗∗
0.117
(0.038)
∗∗∗
0.023
0.032
(0.107) (0.107)
-0.001
-0.003
(0.005) (0.005)
0.014
0.013
(0.086) (0.085)
0.194
0.144
(0.183) (0.184)
0.359
(0.140)
∗∗
0.330
(0.141)
∗∗
-0.183
-0.026
(0.187) (0.201)
-0.115
-0.031
(0.345) (0.309)
0.194
(0.084)
∗∗
0.018
0.083
(0.023)
∗∗∗
0.003
(0.109) (0.105)
-0.003
-0.002
(0.005) (0.005)
0.045
0.013
(0.092) (0.083)
0.117
0.185
(0.190) (0.180)
0.307
(0.146)
∗∗
0.347
(0.138)
∗∗
0.159
-0.174
(0.273) (0.181)
-0.285
-0.071
(0.400) (0.303)
0.094
(0.039)
∗∗
-0.000
(0.106)
-0.001
(0.005)
0.020
(0.085)
0.184
(0.180)
0.345
(0.139)
∗∗
-0.157
(0.188)
-0.129
(0.344)
Observations
R 2
94
0.21
94
0.21
94
0.21
94
0.17
94
0.23
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at 10%.
94
0.23
39

Table 11: Robustness checks: Improving the measure of what is observed
B diverges, round 2
(1)
OLS
(2)
IV
(3)
OLS
(4)
IV
(5)
OLS
(6)
IV
Prop. of Bs seen 0.529
not reciproc.
(0.258)
∗∗
Semi-circle measure
Stake = 10 0.168
0.558
(0.430)
0.124
(0.062)
0.168
0.131
∗
0.204
0.112
0.090
(0.160) (0.038)
0.107
(0.156) (0.156) (0.157) (0.163) (0.155)
∗∗
Household annual 0.001
income (0.012)
0.002
(0.012)
-0.001
(0.012)
-0.002
(0.012)
0.000
(0.012)
Lent money often
-0.013
(0.110)
-0.013
(0.110)
-0.019
(0.111)
-0.024
(0.113)
-0.025
(0.109)
A trusted in round 1
B did not recip.
in round 1
Prop. of Bs not seen
Constant
-0.138
(0.328)
-0.001
(0.286)
-0.369
(0.292)
0.336
-0.141
(0.330)
0.000
(0.287)
-0.359
(0.314)
0.318
-0.122
(0.328)
0.015
(0.287)
-0.159
(0.341)
0.286
-0.149
(0.338)
0.036
(0.295)
0.089
(0.574)
0.046
-0.107
(0.322)
0.039
(0.283)
-0.301
(0.294)
0.265
(0.467) (0.512) (0.478) (0.659) (0.464)
-0.107
(0.323)
0.040
(0.286)
-0.297
(0.333)
0.258
(0.530)
0.091
(0.069)
0.106
(0.159)
0.000
(0.012)
-0.025
(0.109)
Observations
R 2
53
0.18
53
0.18
53
0.17
53
0.14
53
0.20
53
0.20
a
Standard errors in parenthesis.
∗∗∗ significant at 1%,
∗∗ significant at 5%,
∗ significant at
10%.
40