The controlled choice design and private paternalism inpawnshop borrowing∗
Craig McIntosh

Isaac Meza
Joyce Sadka
Francis J. DiTraglia †Enrique Seira

This draft: December 13, 2023

Abstract
We use a novel three-armed RCT, including both forced and voluntary treatment
arms, to provide a unique window into choice, heterogeneous treatment effects andpaternalism in the context of pawnbroker lending. Forcing borrowers into commitment contracts with a regular repayment structure decreases the financial cost ofpawn loans by 22% inclusive of fees, increases the likelihood of recovering their pawn
by 15%, and increases the likelihood of repeat business by 19%. Leveraging the special features of our experimental design, we go on to point-identify the effects ofcommitment on both the choosers and the non-choosers simultaneously, along withthe average selection on gains. We find large and significant effects of commitment
even for borrowers who would not voluntarily choose it, and no evidence of selection on gains: borrowers who would freely choose commitment do not appear tobenefit more than borrowers who would not. A detailed analysis of treatment effectheterogeneity suggests that the potential gains from targeting commitment basedon observable characteristics are extremely small and that most borrowers stand to
gain from a policy of universal forced commitment.

Keywords:

Private paternalism, choice, treatment on the untreated, heteroge-

neous treatment effects, commitment, overconfidence.
JEL codes: G41, C93, O16, G21∗

We want to thank Mauricio Romero and Anett John for advice and encouragement. Ricardo Oli-

vares, Gerardo Melendez, and Alonso de Gortari provided excellent research assistance and Erick Molina
helped with formatting. Jose Maria Barrero, Andrei Gomberg, Emilio Gutierrez, David Laibson, Aprajit
Mahajan, Matt Rabin, Charlie Sprenger, and seminar participants at ITAM, USC, MSU, and UCSD
provided valuable feedback. Research assistance was financed through faculty grants at ITAM. Our
research partner had no say in the results.
†
Seira: MSU, enrique.seira@gmail.com (corresponding author); McIntosh: University of California
San Diego, ctmcintosh@ucsd.edu; Meza: Harvard University, isaacmezalopez@g.harvard.edu; Sadka:
ITAM, jsadka@itam.mx; DiTraglia: Oxford, francis.ditraglia@economics.ox.ac.uk

1

1

Introduction

The behavioral finance literature has established an important role for commitment devices in helping consumers to achieve their own financial goals. While most academic
studies on commitment focus on the role of voluntary self-commitment (Thaler & Benartzi, 2004; Prina, 2015; Brune et al., 2016; Callen et al., 2019; Dupas & Robinson,
2013; Ashraf et al., 2006), in reality the predominant use of rigid structure in financial services is involuntary; firms only offer a product with these features embedded.
Laibson (2018) has referred to this implicit bundling of commitment devices as “private
paternalism”, and its logic is that individuals may benefit from commitment and yet not
explicitly demand it. Comparing voluntary versus paternalistic programs requires that
we form counterfactuals for two different groups of people: those who would freely choose
commitment, and those who would not (since the latter group is treated only under paternalist policies). In this paper we present an experimental design and econometricanalysis that point-identifies and provides estimates for both the effect of treatment on
the treated (TOT) and on the untreated (TUT). This permits a clear window into thecase for paternalistic (forced) rather than voluntary commitment in financial services.
The relationship between treatment effects and treatment take-up is a core concern in the econometrics literature. In principle, the Marginal Treatment Effect (MTE)
approach allows researchers to use observational data and a single excluded instrument to study this relationship. In practice, however, unless the instrument has a richsupport set, MTEs can only be point identified by using additional modeling assumptions (Mogstad et al., 2018). An alternative research strategy to study the relation
between treatment effects and treatment take-up uses the Becker-Degroot-Marschak(BDM) mechanism, incentivizing choice prior to treatment assignment to elicit willingness to pay (WTP) for treatment (Becker et al., 1964). A number of studies, however,find that the WTP elicited under the BDM mechanism changes substantially with the
distribution of prices used in the elicitation exercise (Bohm et al., 1997; Banerji &Gupta, 2014). This falsifies the assumption of standard preferences that is required for
BDM to be incentive-compatible Mamadehussene & Sguera (2023), suggesting that themechanism may not provide a reliable measure of actual compliance in practice. Our
study avoids the drawbacks of the MTE and BDM approaches by combining a novel
three-armed randomized controlled experiment, including forced treatment and treatment choice arms, with two transparent exclusion restrictions. Together, these allow us
to point identify the relevant TOT and TUT effects in a real-world, high-stakes setting
and to study the case for paternalistic commitment head-on, with minimal assumptions.
We apply this approach to an important and understudied context: pawnshop lending. Pawn loans constitute one of the oldest and most prevalent forms of borrowing(Carter & Skiba, 2012). Our partner lender, for example, made over 4 million loans to2

more than a million clients during the past three years.1 The question of choice versus
paternalism is particularly salient in this context, as choice mistakes could arise fromborrowers’ low education and the fact that they typically borrow for emergencies undersignificant stress.2 Our experiment covers just under 5,000 pawnshop clients in 6 ofour partner lender’s Mexico City branches. Our control arm illustrates the costs of thestatus quo contract: fully 44% of borrowers default, losing lose their pawn along withany payments made towards principal.3 Our “commitment choice” arm gives borrowers the chance to opt into a structured repayment contract when taking a loan. The
structured contract requires borrowers to make three monthly payments rather than one
balloon payment at the end, with each monthly payment including the accrued interestat that time as well as a nominal fee of 2% of that month’s payment if the payment
is delinquent. The fee serves as a reminder and a means of reinforcing the importanceof these interim payments. In our “forced commitment” arm all borrowers are required
to repay using the same structured monthly contract offered on an opt-in basis in thecommitment choice arm.
We address three key questions. First, do structured repayment contracts lower
financial costs for pawnshop borrowers? Second, do borrowers recognize this benefit,
demanding commitment in sufficient numbers? Finally, and most uniquely, do the rightborrowers voluntarily demand commitment? Our ability to answer the last question
comes from our unique three-armed experimental design, which we call the “controlled
choice design” for short. This design can be viewed as a juxtaposition of two randomized encouragement designs, each with one-sided non-compliance. One of them point
identifies the effect of commitment for borrowers who would voluntarily choose commitment (TOT), while the other point identifies the effect of commitment for borrowers
who would not (TUT). By identifying both the TOT and TUT effects in the same
experiment, the controlled choice design allows us to examine the empirical relevanceof “selection on gains” also known as Roy-type selection into treatment by estimating
the “average selection on gains” ASG = TOT − TUT. This enables us to test whether
borrowers who voluntarily choose commitment have higher average treatment effects
than those who do not, rather than assuming it. The controlled choice design also point
identifies the average selection bias (ASB)–the average difference in untreated (statusquo) potential outcomes for those who choose commitment relative to those who do not–along with the average selection on levels (ASL)–the analogous comparison for treated(commitment) potential outcomes. Taken together, these causal effects allow us to “gounder the hood” of our baseline ATE results, and paint a more complete and economically relevant picture of the effects of commitment. We are unaware of any other paperthat simultaneously identifies all of these causal effects without recourse to additional1

For comparison, there were 2.3 million microfinance clients in Mexico in 2009 (Pedroza, 2010).
A large literature shows stress impairs cognitive function, e.g. Starcke & Brand (2012).
3
High pawn default rates are common, in the US they oscilate around 15% (see here).
2

3

structural modeling assumptions.
We find that commitment is strongly effective in lowering financial costs and preventing default in pawnshop lending: the average individual in the forced arm pays financing
costs inclusive of fees that are 22% lower than the control, and faces a probability ofdefault that is 6.6 percentage points lower (15% of the mean). In terms of Annual Percentage Rates, the financial cost of borrowing falls by 11 percentage points (19% of themean). In short, structured commitment saves borrowers money by charging them fees!
Our results are qualitatively robust to deducting transport costs of visiting the branch
to make interim payments along with a day of lost wages for each visit. They are also
robust to using borrowers’ subjective values of their pawns rather than the appraisedvalue of the gold, and to adjusting for lost liquidity from requiring monthly payments.
The monthly payment contract seems to achieve these cost savings by speeding up payments and by generating an early bifurcation of borrowers into those that will recover
the pawn and those that will not. The former are induced to pay faster, saving on interest; the latter pay less towards loans that ultimately default, hence losing less money
when they do.
Despite these large financial cost savings, only 11% of borrowers in the choice arm
choose commitment. Can the borrowers who did not choose commitment be those who
simply don’t need it? To answer this question, we carry out a detailed analysis oftreatment effect heterogeneity. We begin by bounding the distribution of individual
treatment effects using the marginal outcome distributions from the forced commitment
and control arms, following Fan & Park (2010). This approach imposes no assumptions
beyond the experimental randomization. We find that at least 23% of borrowers benefit
from commitment. This implies that there must be many borrowers in the choice arm
who did not demand commitment despite their individual treatment effect from (forced)
commitment being positive. Next, we impose an exclusion restriction positing that theeffect of a given contract does not depend on how borrowers obtain it. In other words,
we assume that choosing a contract results in the same potential outcome as being
assigned that contract. This is a relatively common if often implicit assumption in
causal inference.4 It also has testable implications that we fail to reject in our empiricalcontext.5 Under this restriction, the controlled choice design point identifies the TOT,
TUT, ASG, ASB, and ASL effects described above. Our estimated TUT effect onfinancial cost savings is large: $192 pesos, equivalent to a 10.6 percentage point savingsin APR. On average, the borrowers who would not choose commitment, would have faced
substantially lower financial costs if they had. Finally, we combine our experimental
4Papers that use variation in compulsory schooling laws to identify the returns to schooling, for example, typically interpret their results as the causal effect of additional education rather than additional
forced education. Chamberlain (2011) uses a closely related assumption to develop a theory of optimaltreatment choice.
5
See Appendix G. for details.

4treatment and outcome data with survey responses collected for a subset of borrowers toestimate conditional average treatment effects, both TUTs and ATE, using the Causal
Random Forest algorithm of Athey et al. (2019). We estimate positive conditional
average TUT effects for 93% of the borrowers who did not choose the commitment
contract. In short, it is extremely difficult to find identifiable groups of borrowers whoare harmed by commitment, even when restricting attention to those who would notchoose it voluntarily. While targeting commitment products to those that benefit themost is a policy that appears attractive, in this context we find that the usable targeting
variables have relatively weak predictive power and hence even our best random forest
targeting only reduces the overall mis-targeting rate from 9.7% (all to Forcing) to 9.5%
(our best-case feasible targeting mechanism).
What explains the persistence of no-commitment contracts so contrary to borrowers’ interests in the real world? From the demand side, while a simple measure of time
inconsistency does not explain the large and positive TUT effect, we show substantial
levels of over-optimism among borrowers. Among borrowers who do not choose commitment, those with the largest estimated benefits from commitment are the individuals
who most systematically over-estimate their own probability of repayment without theneed to commit, potentially decreasing their demand from commitment. From the supply side, because borrowers’ financial savings come directly from the pockets of lenders,pawnshops have an interest in retaining the no-commitment contract. Indeed, pawnshop
lending presents an inverted lending case: since these loans are over-collateralized, thelender in the contract stands to gain the most when borrowers default. Our partner’s
status quo pawn contract gave 70% of the value of gold collateral in credit, and charged
a monthly interest rate of 7% for loans of a three-month duration, with a flexible noreminders contract, that could be paid back anytime before the loan comes due at no
penalty. This contract is standard contract in the industry. This combination of features, and the fact that the gold pawn is highly liquid, means that the lender makes
90% more profit over three months from a borrower who defaults than one who repays(30% of collateral value recovered under default, 15.8% of collateral value paid in interest if loan fully repaid). While an older literature considers the exploitative potentialof over-collateralization and underpriced collateral (Basu, 1984), the implication of suchcontracts has not been analyzed in the behavioral literature.
Our paper makes a number of contributions to the literature. First, we propose
a way to use this three-armed experimental structure to recover treatment effects forchoosers and non-choosers under minimal assumptions.6 We further provide simple,
6
While Fowlie et al. (2021) likewise employ a three-armed experimental design in their study of theeffect of electricity pricing, they identified two TOT effects for different groups of “treated” households,
whereas we simultaneously identify the TOT and TUT effects defined with respect to a single “treated”
group of borrowers. This difference is what allows our design to point identify the ASG and related
quantities.

5

regression-based estimators for each of these causal parameters, along with proceduresfor computing associated cluster-robust standard errors.7 A companion STATA package provides easy-to-use commands that implement our estimators and standard errors.
The controlled choice design could be useful in other experimental settings where thequestion of interest centers on the merits of paternalism, public or private, or the relationship between choice and treatment effects. One obvious example is the designof other financial contracts beyond pawn loans. Another is education, where teachers
typically mandate quizzes, homework, and other commitment mechanisms to mitigate
student procrastination (Ariely & Wertenbroch, 2002). We further contribute to a relatively small existing literature that sheds light on private paternalism. In the context offood choice, Sadoff et al. (2019) show that individuals with the most time-inconsistentpreferences are actually least likely to demand commitment. In contrast to their paper,
we directly identify the TUT, obviating the need to first elicit preferences before testingfor negative selection. In the context of school choice, Walters (2018) combines a distance instrument with additional structural assumptions, obtaining model-based TUT
and ATE estimates. He finds that students who select into more effective schools havesmaller treatment effects from attending than those who do not select in. In contrast,
our approach point identifies TUT and TOT and a range of other interesting causal
parameters without the need for a structural model, relying instead on relatively weakexclusion restrictions whose testable implications we fail to reject.
Our study also speaks to recent research on the effects of payment frequency. While
experiments in microfinance markets have not shown the same benefits from providing amore regularized repayment environment as we find here (Field & Pande, 2008; Barboni& Agarwal, 2023), these experiments differ from ours in two important ways: they are
performed on top of already highly structured micro-finance contracts, and they involve
borrower pools who may have selected into that type of lending precisely because it
provides structure Bauer et al. (2012a). These differences may explain why (Field &Pande, 2008) finds almost no default in the control group, in stark contrast to our settingof high default. Second, we provide a deeper analysis of both take-up and the efficacy
of voluntary commitment mechanisms. A number of papers have found low demandfor commitment as we do.8 Unlike all of these papers, however, we separately pointidentify and estimate the effects of commitment for borrowers who would and would notchoose it. This allows us to conduct a more rigorous and nuanced analysis of private
paternalism.
The remainder of the paper is structured as follows: Section 2 provides context
and defines our main outcome variables. Section 3 describes the experiment and data
7

See Appendix F. for details.
Ashraf et al. (2006), Giné et al. (2010), Bai et al. (2020), Royer et al. (2015), Sadoff et al. (2019).
Others have found more robust demand for commitment (Kaur et al. (2015), Casaburi & Macchiavello(2019), Schilbach (2019), Tarozzi et al. (2009), Dupas & Robinson (2013)).
86sources, and shows pre-treatment balance across arms. Section 4 provides the standard
ITT analysis of the experiment, while Section 5 shows how to identify, estimate andcarry out inference for the TOT, TUT, ASG, ASB and ASL effects under the controlled
choice design. Section 6 investigates why paternalism functions so well in this context
and whether it can be more finely targeted and Section 7 concludes.

2

Context

2.1

Pawnshop borrowing

Pawn loans involve individuals leaving valuable liquid assets, typically jewelry, as collateral in exchange for an immediate cash loan. Collateral is typically more valuable
than the loan amount, allowing lenders to give the loan immediately without checking
a borrower’s credit history. This makes pawn loans a popular way to get cash to pay
for emergencies. In fact, they are one of the most prevalent forms of borrowing. There
are more than 11,000 pawn shops across the US, with 30 million clients and $14 billion
in yearly revenues.9 Our partner pawn lender alone served more than 1 million clientsin the last 3 years with more than 4 million contracts. For comparison there were 2.3
million micro-finance clients across all lenders in Mexico in 2009 (Pedroza, 2010).
Pawning is also one of the oldest forms of borrowing. Pawn lending existed in
antiquity at least since the Roman Empire, and there are records of it in China about
1,500 years ago (Gregg, 2016). In spite of the high prevalence and long history, pawnshop
borrowing has not received much attention in the economics literature. The closest
widely studied product is payday lending. In developing countries, however, payday
lending is likely small compared to pawnshop lending; the latter is faster and requires
less documentation, making it more accessible to informal sector workers who receive
their salaries in cash.
As with payday lending, pawnshop lending is controversial. Regulators have concerns with the sophistication of borrowers using it, speculating they may suffer frombehavioral and cognitive deficiencies that lead to making sub-optimal choices, biases
that are exacerbated by contract design.10 There is some evidence in support of thisview for payday borrowers11 but none for the large pawn-lending industry. Our study
9

See here, here, and here.
The US congress has actually banned the payday lending industry from serving active military
personnel, and some States in the US have imposed zoning restrictions, interest caps, and restrictions
on serial borrowing as consumer protection measures against payday lending (Stegman, 2007).
11
Bertrand & Morse (2011) write that “Under the view that the people borrowing from payday lenders
are making an informed, utility-maximizing choice given the constraints that they face, one would not
expect additional information disclosure about the payday product to alter their borrowing behavior”,
but to the contrary, they find that simply disclosing how financing costs add up reduced demand by
11%. Melzer (2011) finds that payday loan access leads to increased difficulty paying mortgage, rent
and utilities bills.
107reinforces the idea that a lack of sophistication may be an integral part of the way thatstandard pawn contracts are designed and structured by lenders.

2.2

Pawning Logistics and Contracts

To study this market, we partnered with one of the largest pawn shops in Mexico, an
institution with more than one hundred branches spanning multiple states in Mexico.
This lender (whom we refer to as ‘Lender P’) has a simple and typical business model.
Appraising and lending. Lender P takes gold jewelry as collateral in exchange fora fraction of the value of the piece, in cash. No other collateral and no credit history
checks are needed. The transaction takes less than 10 minutes and is conducted at thebranch in person between the client and the appraiser (i.e. a teller, see Figure OA-3).
The appraiser weighs the gold piece and runs tests on its purity. Based on these she
assigns a gold value to the piece, stores it as collateral, and gives 70% of the gold value ofthe piece in cash to the client. The borrower signs a 2-page contract with the conditionsof the loan and leaves with the cash.
Contract. Lender P had only one type of contract, henceforth the status quo contract.
It stipulated that the interest rate was 7% per month compounded daily on the outstanding amount of the loan. The loan had a 90 days term with 15 days’ grace period.
The client could make payments at the branch at any time with no penalty for prepayment. Under this status quo contract, there are no payment reminders or any otherkind of interim contact between the lender and the borrower. If the client returns to
pay the principal plus the accumulated interest within 105 days, she recovers her pawn,
otherwise the pawnbroker keeps the piece and any payments already made. Before thecontract expires, the client had the right to renew for another 3 months by going to thepawnshop, paying the accumulated interest, and signing a new contract with exactly
the same terms and the same piece as the original contract (38% of borrowers renew
at least once with a given pawn). This contract is standard in the industry. Pawnshops make money in three ways: by reselling the jewelry left as collateral on defaulted
loans, by charging interest on non-defaulted loans, and by keeping the payments madeon defaulted loans.
Borrowers. The clients that pawned understood these terms well (as we verified ininterviews).12 These clients have little or no access to other types of loans and they value
the convenience of pawn borrowing. This population of pawn borrowers is economicallyvulnerable: 30% of them could not pay either water, electricity & gas or rent in the past
6 months; 89% said they are pawning because of an emergency, and only 12% stated
12

87% of clients report in our survey that they have pawned before.

8

it was to use in a “non-urgent expense”. When asked why they are pawning this piece,
5% responded “lost a family member”, “a medical emergency” (11%), or “an urgent
expense” (72%).
Many borrowers lose their pawn. Our context is also one with high borrower default: 43% of clients lose their pawn in a time span of 230 days from the date of pawning.
One potential explanation for high default is that clients are really just knowingly selling
their gold piece through a pawn contract on which they intend to default. This appears
unlikely for several reasons: (a) clients can easily sell the gold and obtain a higher
amount of instant cash at gold-buying stores located close to almost all our pawnshop
branches (see Figure OA-4), (b) the reported subjective value of the pawn is larger than
the appraised value for 83% of clients, (c) among those that lose their pawn, 29% paid
a positive amount towards its recovery and on average paid 42% of the value of theirloan (see Figure OA-6 in Appendix) — this can only be rationalized if they expected
to recover their pawn, and (d) 72% of borrowers report a 100% probability of repaying
their loan (and 98% at least a 50% chance of repaying) in our baseline survey at thetime they take the loan.

2.3

Measuring Borrowers Financial Costs

Borrowers’ financial costs are composed of two main categories: the cost of losing theircollateral, and the interest and fees incurred during the life of the loan. For each given
loan we observe if the client lost her pawn (1(Defaulti )). If a loan has been rolled overand is still outstanding, we consider it to be non-defaulted. This approach is conservativein our context (biases treatment effects towards zero), as we show in detail in Section 4.
In our data 13% of experimental loans are ongoing (i.e. censored) when the data period
ends. Regarding interest, our administrative data classifies payments made in three
types according to their payment allocation rules: payments to principal P C , payments
on generated interests P I , and payments on penalty fees P F . We observe each and every
payment made under each category, its amount and date.
We define a borrower’s financial cost as the total monetary outflow –in cash or pawn
value– from the borrower to the lender. This includes all payments the borrower madetoward interest and fees, but also the net difference between the appraised value of thepawn and the loan amount (Value-Loan) in the event of default. When there is nodefault the borrower gets her pawn back and there is no loss of value for the borrower.
Payments towards capital are considered a cost only when the borrower defaults, as
she does not get reimbursed for these. Note however that when she does not default
payments to capital are not an actual outflow, as they sum up to the value of the loan
the lender disbursed in the first place. The formula for financial cost for person i is thus9

as follows:
Financial Costi =X
tPitI +

X

PitF + 1(Defaulti ) × (Valuei − Loani +X

Pitc )tt

where t indexes days, and 1(Defaulti ) is an indicator function for defaulting. Because
the period of the loan is only 90 days we do not apply discounting in calculating costs.
In robustness checks reported below we show that our results are virtually unchanged
when applying a wide range of time discounting factors.
We consider the above to be an accurate measure of financial cost in pesos. However,
we also report results incorporating two non-financial costs: (i) using the subjective valueof the pawn reported by the borrower in place of its appraised gold value, and (ii) adding
a measure of travel expenses and the opportunity cost of time, as clients have to go to
the branch in order to make payments.
As a second measure of cost we calculate the Annual Percentage Rate (APR) in order
to express the cost as a percentage of the loan, per year, inclusive of default costs.13
The standard definition is given in the following formula:(APR)i = 1 +Financial Costi !loan termi
Loaniloan termi

3

Experimental Design

3.1

Treatment arms and randomization−1

The Commitment Contract. For the purpose of the experiment we designed a
new contract that is identical to the status quo contract except that, informed by thedesign of micro-lending contracts, it enhances the regularity and salience of payments
as a way to encourage repayment (Morduch, 1999; Bauer et al., 2012b). It has thesame interest rate (7% per month) which accumulates daily on outstanding debt, thesame loan size/collateral ratio (70%), and the same loan term (90 days, and a grace
period of 15 days). Borrowers’ gold pawns are appraised in the same way by the same
appraisers under both the new and status quo contracts. The commitment contract
however requires the client to make regular monthly payments for the duration of thecontract, with the principal and interest payments split evenly across the three monthsof the contract (day 30, 60 and 90 after loan disbursement). The importance of thismonthly payment was made salient in the contract and payment receipts (see Figure
13

Figures OA-5(a) and OA-5(b) in the appendix display histograms for financial cost and APR. Loan
term takes into account the entire loan period, including extensions of the loan through refinancing.

10

OA-1), and by the levying of a nominal fee (2% of minimum due) on individuals who
fell behind in their payments. The fee was modest and intended to make the payment
deadlines salient. As a benchmark, the transportation cost to visit the branch to makea payment is comparable to the fee, on average.
To elicit demand for the monthly payment contract, we include an arm that allows
borrowers to opt into this contract if they choose. The existence of both a non-optional“forcing” arm, and a choice arm in our design is key to estimating a battery of treatment effects above an average treatment effect under fairly mild assumptions. We next
describe the three experimental arms in more detail.
Treatment Arms. Treatments were randomized at the branch-day level. Each day
a computer randomly assigned which types of contracts were on offer that day in the
branch, and the IT system would only offer these. We have 3 different experimental
arms14
1. Control arm: consisted of branch-days offering the status quo contract describedin Section 2, and only this contract.
2. Forced Commitment arm: consisted of branch-days requiring all borrowers to use
the Commitment contract described above.
3. Commitment Choice arm: consisted of branch-days offering the client a choice
between the Commitment contract, and the status quo contract.
We did not allocate an equal number of days across arms, since we were interested
in having more power in some of them. The number of branch days allocated to eachwere 84 to control, 80 to forced commitment, and 93 to choice. See Figure 1 for a
CONSORT-style diagram of the study design and recruitment.
Randomization. We implemented the experiment in 6 branches of Lender P beginningon September 6, 2012. The branches were selected by Lender P to be dispersed across
Mexico City and have varying sizes. In four of them the experiment ran for 102 days,
and in 2 of them we ran it for a shorter time to economize on data collection costs once
we realized we would not be constrained by sample size. Branches are more than 5 kmapart from each other, and there is no substitution among them; none of the consumers
appear in more than one of our branches.
Branch personnel did not know which treatment would be assigned to each day
and were blind to the objective of the intervention. They were told that there were 3
different “types of contract-days”, that the system chose randomly for any given date,
14

The experiment included other independent arms that involved no fee penalties and did not emphasize the structure of payments. These are being analyzed in a separate paper.

11

Timeline
6 Branches in Mexico City selected to be part of study

8/2/2012
9/10/2012

Experimental Phase: Random assignment begins at branch/day level
Hard Commitment

19 days

Forced commitment

Choicecommitment

Status-quo

80
1954
1522
1469

93
2580
2041
1982

84
1770
1421
1386

102 days

376 days

Control

Branch-Days
Loans
SurveysSurveyed&Loan

Experiment ends - All arms switched to status-quo

12/21/2012
235 days

End of observation period

8/13/2013

Figure 1: Experiment description
and that it could happen for instance that two or more consecutive dates had the same
contract. They were also told that this way of operating was in place in several of
Lender P’s branches (they did not know which ones), and that it would be in place
for several months. Randomizing at the day level limits the problem of contamination
arising from clients realizing that other clients get different contracts than theirs. It
also limits potential manipulation by appraisers, who in the presence of individual-level
randomization could potentially pick their preferred customer from the line or tell themto wait until their desired contract shows up on the screen. Intra-branch day correlationon the probability of default (ICC) is small, at 0.05, so we lose little power vis-a-vis
individual-level randomization.
Some clients pawned more than one time during the duration of the experiment,with 14% pawning 2 times and 8% more than 2 times. To have a clean comparison weare considering only the first pawn conducted during the experimental window. It isalso the case that 30% of those first pawns involve more than 1 loan, as 2 or more piecesof gold were submitted. We treat each of them as separate loans. In the appendix weshow that our results are robust to this analysis choice.
Timeline. Figure 1 shows the experimental timeline along with the length of time forwhich we observe payments. For loans made in the first week of the experiment, weobserve up to 338 subsequent days of loan information; for loans made in the last week12

we observe up to 235 days. Figure 1 also illustrates the number branch-days per arm,
the number of loans, and the number of surveys.
Explanation. Since we are interested in measuring the effect of different contract
terms on client behavior, it is important that clients understand these terms. To ensure
this, we built two “check-points” as follows. Two enumerators were present in eachbranch for the whole day during the duration of our experiment. At the first checking,these enumerators explained the contract terms to clients, emphasizing that the frequent
payment contract involved the commitment to pay a third of the outstanding amounteach month, along with the nature of the fees associated with the Commitment arm.
Figure OA-2 presents an excerpt of the materials we used to explain the contracts,
translated into English. The explanation took about 3-5 minutes and continued until
the client said she understood the contract terms. Enumerators then asked clients to
explain the contract back to them before correcting any misunderstandings. At thesecond check-point the appraiser made clients read the “Contract Terms Summary”
sheet shown in Figure OA-1 before they signed the contract. This summary was a pieceof paper given to clients after their piece had been appraised and the size of the loan
determined, but before they signed their contract. The appraiser read it aloud and thenasked the client to sign it as proof of understating. We are confident the overwhelming
majority of clients understood the contracts and that those in the choice arm madeinformed choices.

3.2

Data

Administrative data. The study exploits two types of data: administrative data fromthe lender, and a short survey that we implemented. The administrative data contains
a unique identifier for each client, an identifier for the piece she is pawning, and thetransactions relating to that piece. These transactions include the value of the item asassessed by the appraiser, the amount of money loaned (70% of the item’s value), thedate of the pawn transaction, and the type of contract for that pawn: commitment or
status quo. Within the period of the loan, we followed each transaction related to thatpiece in the administrative data: when payments were made and for what amounts,
whether there was default (i.e. the client lost her pawn), and whether any late-payment
fees were imposed. After the experimental loan, we are able to track subsequent behavior
and to see whether that borrower took a subsequent loan. We have this information for
all the pawns that occurred in the experiment’s 6 branches between August 2, 2012 andAugust 13, 2013. This includes all the pawns that took place during our experimentalong with those that one month before and eight months after our experiment. Figure
1 shows the design and timing of the experiment, along with the sample sizes in each13

arm. The experiment comprises 8,519 pawns while our administrative data covers atotal of 26,180 pawns.
Survey data. An additional team of enumerators stationed in each branch asked clients
to complete a 5-minute survey before going to the teller window to appraise their pieceand before they learned which contracts would be available on that day. The survey was
intentionally short to avoid discouraging the potential clients from pawning. It measured
demographics, proxies for income/wealth, education, present-biased preferences, experience pawning, if family or friends commonly asked for money, how time-consuming andcostly it was to come to the branch, the subjective probability of recovering the piecethat they intended to pawn, the subjective value of their piece in money terms (howmuch money they would sell it for), among others. We surveyed 7,210 clients, and oursurvey response rate was 78% among clients who took loans.15 We only use the survey
in Section 6 of the paper.

3.3

Experimental Integrity

Attrition. There are two main channels through which attrition could complicate theinterpretation of our results. The first, and more serious, is the possibility that clientsmight change their pawning decisions in response to the treatment they encounter in agiven branch on the day they enter the branch. If this occurred it would introduce aself-selection dimension which would still reflect the overall impact of a treatment for
the lender’s portfolio but would no longer deliver ceteris paribus effects of treatments
on individual borrowers. Narrative reports and the way the treatment was implemented
make us believe that selection into treatment is unlikely.16
If the treatments had induced demand-side selection, we would expect to see that the
number of pawns successfully conducted differ in a systematic way across arms. Thatis, if potential borrowers disliked being forced into a commitment contract, we would
expect a lower number of pawns on branch days where only the commitment contract isavailable compared to control days. Table OA-2 shows that this is not the case. Thereis no difference at all between the Control and Forced Commitment arm in terms of thenumber of pawns per branch-day. This is consistent with the findings of Table 1.
A more subtle form of sample selection could arise if the treatments induce borrowers
to re-pawn in different ways, especially given that their treatment status on subsequent
15

Appendix OA-1 transcribes the questionnaire in English.
Potential clients did not know that different days could have different contracts. If they asked,
appraisers said that whatever was offered on that day was the only available contract for an undetermined
length of time. Anecdotally, appraisers told us that they did not think refusals differed across arms, andour enumerators informed us that potential clients rarely left the branch without pawning. Lender P
also never complained to us that our different treatments were hurting sales.
16

14

Table 1: Summary statistics and BalanceCommitment arms
Control

ForcedChoicep-value

Panel A : Administrative Data
Loan amount
Weekday
Obs

2267
(76)
0.88
(0.044)

2162
(83)
0.89
(0.035)

2223
(66)
0.83
(0.048)

1770

1954

2580

0.65
0.56

Panel B : Survey Data
Subjective value
Trouble paying bills
Present bias
Makes budget
Subj. pr. of recovery
Pawn before
Age
Female+ High-school
Obs

4084
(186)
0.19
(0.024)0.14(0.02)
0.62(0.028)91.89(0.721)
0.87
0.02
43.32
(0.688)0.73(0.023)0.66(0.027)

3877
(193)
0.21
(0.023)0.13(0.01)
0.59(0.036)91.65(1.031)0.89(0.013)42.85(0.949)0.72(0.019)0.67(0.022)

4173
(172)
0.18
(0.02)
0.13(0.01)
0.65(0.021)93.61(0.582)0.9(0.011)43.82(0.792)0.71(0.02)
0.65(0.018)

1386

1469

1982

0.51
0.67
0.89
0.29
0.09
0.25
0.73
0.88
0.84

This table has two panels. Panel A uses administrative data at the loan level, while Panel B uses survey data. Eachrow in this table corresponds to a regression, where the level of observation is the individual loan originated. The
dependent variables of these regressions are displayed in the first column. Each dependent variable is regressedin a multivariate OLS regression against the experimental arms indicators (control, forced commitment, choice).
The table reports the coefficients on each of these indicators, as well as the p-value an F-test of the null hypothesisof equality of the three coefficients. The admin data was a very limited set of pre-determined variables. The
dependent variables in Panel A are the loan amount in pesos, and an indicator for whether the day of the loan
origination was a weekday (as opposed to weekend). The dependent variables in Panel B from the survey (see thequestions in Table OA-1. Subjective value of the pawn (how much would the client be willing to sell it for (Q3),
an indicator for having trouble paying bills in the last 6-months (Q28), present bias (constructed from questions
Q10 and Q29 in the standard way as in Ashraf et al. (2006)), an indicator for whether they make expenses budget
for the month ahead of time. The subjective probability of recovery was elicited a la Manski (from 0 to 100 whatis the probability that you will recoup your pawn), pawned before is a dummy=1 if the client declares to havepawned before (although not necessarily with Lender P ) age is in year, +High-school is a dummy that indicates
if the client has completed high school.

loan/days may not be the same as that initially assigned. To address this issue ouranalysis uses only the first loan taken by each borrower during the experimental window.
Balance. Table 1 presents summary statistics for the sample of actual borrowers acrossarms, showing that our randomization succeeded in achieving balance across the experimental arms. Panel A uses administrative data for the universe of borrowers in each arm,and shows that loan balances and the days on the week on which individuals pawned
are comparable across arms. The average loan size is $2267 MXN ($130 USD). Panel
B of Table 1 reports summary statistics across arms from our survey data. Among the15

78% of borrowers who completed our survey, 73% of clients are women, the average age
is 43 years, 66% have completed at least a high school education, and 87% have pawned
before, suggesting that our sample largely consists of experienced borrowers. Finally,
borrowers’ subjective probability of recovering their pawn is close to 92% on average, instark contrast to the actual recovery rate of 43%; borrowers are highly overconfident on
average. The average subjective value they report for the items they pawn is 4084 MXN,
much larger than the average appraised gold value of 3238 MXN. While this could arise
either from overconfidence in valuation or from undervaluation by the lender, in any
case it is prima facie evidence that loss of the pawn should be undesirable relative tothe quantity of liquidity leveraged by the asset.

4

Average Treatment Effects

We begin by estimating average treatment effects of assignment to the Forced commitment and the Choice arms, relative to those assigned to the Control arm. As we explain
below, only about 11% of those in the choice arm chose the monthly payment option(Figure OA-8 shows coefficient plots for the characteristics that determine choosing
commitment in the Choice arm).
Specification. Table 2 presents estimates and standard errors from a standard pooled
experimental regression
yij = α + β F TiF + β C TiC + γXij + ϵij(1)where i indexes client, j indexes branch, TiF and TiC are indicator variables for receiving
the Forced or Choice arms, Xij are branch and day-of-week fixed effects. Standard
errors are clustered at the branch-day level, the unit of treatment assignment17 . Given
full compliance in the Forced arm, the coefficient β F is the ATE of forced commitment
while β C is the ITT of commitment in the Choice arm on the outcome variable yij . Our
two primary outcome variables are financial cost in pesos and Annual Percentage Rate
(APR), as defined in Section 2.3. Results for these outcomes appear in columns (1) and(7) of Table 2. The remaining columns decompose the financial cost and APR outcomes
into their components: interest payments (col 2), payment towards any fees incurred(col 3), payments toward the principal (col 4). Column 5 shows the value of lost pawn
conditional on losing it. In column 6 the dependent variable is a dummy indicating
17

A minority of clients pawned on more than one day during the experiment: 14% pawned on two
distinct days, and 8% on three or more days. To avoid contamination from earlier treatments to whichthese individuals were exposed, we restrict our sample to each client’s first visit. Note that a client may
pawn multiple items her first visit. We include these as separate observations. Because our standard
errors are clustered at the branch-day level, they automatically account for any dependence in error
terms arising from multiple pawns by the same client on her first visit.

16

Table 2: Effects on Financial Cost
Components of FC
FCInterest pymntPtForced commitment
Choice commitment

Observations
R-squared
Control MeanI
PitFee pymnt

Principal pymnt

P

1(Defi ) ×

t

F
Pit

P
t

C
Pit

Lost pawn value

Default

1(Defi ) × Value-Loani

1(Defi )

APR

(1)

(2)

(3)

(4)

(5)

(6)

(7)

-204.0***(48.1)-38.9(49.8)-157.3***(34.9)-24.9(38.4)

32.1***(1.43)
1.34**(0.54)-1.27(3.10)-0.93(3.02)-78.8**(31.6)-15.4(33.1)-0.066***(0.023)-0.023(0.021)-0.11***(0.019)-0.0086(0.019)

6304
0.013
942.4

6304
0.022
545.9

6304
0.151
0

6304
0.003
5.96

6304
0.007
396.5

6304
0.013
0.44

6304
0.031
0.57

This table shows the treatment effects for our core pecuniary outcomes. Each column is a different regression fordifferent outcomes on an indicator for the forced and choice arms, following specification in equation 1. Columns(1) & (7) analyze our core financial cost measures, while the rest of the columns decompose these into finercomponents. A few borrowers take more than one loan on the first day they appear in an experimental branch.
These are treated as different observations. Table OA-5 shows our results are similar when dealing with themultiplicity of loans per borrower. Each regression includes branch and day-of-week FE. Standard errors are
clustered at the branch-day level.

default. Finally, column 7 rescales financial cost as a function of loan size to estimate
causal effects on incurred APR.18
Results. The results are stark. The Forced Commitment arm yields large and significant decreases in the cost of loans to clients, as measured either by financial cost or
APR. Despite causing an increase in fees, the Forced arm leads to a decrease of 204
pesos in the costs of borrowing (out of a group mean of 942 in the status quo), equivalent to 22% reduction as a fraction of mean cost. These cost savings arise from a 6.6
percentage point (pp) decrease in the probability of default (out of a baseline mean of
44pp, implying cost savings of 79 pesos), and also from lower interest payments since, as
we will document below, the commitment contract speeds up payments so the interest
rate applies to a smaller principal. This translates into a large reduction in APR. A
credit product that has an effective average APR of 57% in the status quo arm (inclusive of default) is reduced to a cost of 46% through the imposition of a more regularized
payment structure. This is in stark contrast to Field & Pande (2008) for instance.
In contrast, to the impressive effectiveness of the Forced commitment arm, the Choicearm fails to deliver significant changes in any measure, with the exception of an increasein fees, for which we are highly powered, since this outcome is zero for every control
observation. Giving borrowers the choice of contract did not decrease financial cost,whereas forcing them into a structured payment contract dramatically reduced it. As we
explore later in the paper, the null effect of the Choice arm arises because few borrowers
demanded commitment (consistent with Ashraf et al. (2006), Giné et al. (2010), Bai
18

As we explained above, loans can be extended for an additional 3 months by paying the interest
owed and restarting the loan under the same treatment conditions. This means that some loans extend
for more than 3 months. We consider the entire flow of cost for the duration of our sample.

17

et al. (2020), Royer et al. (2015), Sadoff et al. (2019)), with 89% choosing the lesseffective status-quo contract.
Intermediate outcomes. To shed light on the mechanisms behind the ATEs discussed
above, Table 3 shows how commitment affects a number of intermediate outcomes. One
can group the types of intermediate outcomes into two categories: measures of the
speed of pawn recovery, and measures of the decision of when to default. While the firstpayment for borrowers in the status-quo contract occurs on average only on day 82 (ona 90 days contract), borrowers in the forced commitment arm start paying 13.8 days
earlier on average (col 1). Not only do they start paying earlier, the first payment isalso 7.9% larger (col 2), and a larger fraction of 9.7% actually pay in full and recover
their pawn in the first payment, compared to 30% in the status quo contract (col 3).
The resolution of the loan (either by payment or default) is shortened by 27.9 days (col4), and conditional on recovery (an endogenous control) by 17.9 days (col 5).
A very undesirable outcome from the borrower’s perspective is to pay towards theloan without paying in full, i.e. defaulting on the loan while still making some payments.
In this case, they lose both the collateral and any payments made toward recovery. One
could be concerned that by encouraging them to pay monthly, more borrowers mightend up in this dire scenario in the Forced commitment contract. Column 6 shows
this is not the case. On the contrary, 7 percentage points fewer borrowers end up
in this situation, compared to 12 percent in the status quo contract. Conditional on
defaulting those assigned to the Forced commitment contract have paid 4.1% less of theirloan (col 7), and a 14 percent higher proportion of borrowers pay zero conditional on
defaulting, an outcome analogous to “selling their pawn” (col 8). One interpretation ofthis bifurcation is that the Forced commitment contract forces borrowers to think earlier
about whether they will indeed be able to eventually recover their pawn, and separates
borrowers into those “selling” their pawn and those recovering it, reducing the share ofundecided borrowers that end up paying interest and end up losing the pawn anyway.
This mechanism may also help to explain why the Forced commitment contract does
not increase the number of visits to the branch to pay (col 10): those recovering theirpawn visit more, but those defaulting have 0.20 fewer visits (col 11).19 Finally, Column
9 shows that treatment effects are concentrated in the intensive margin as treatment
does not affect the fraction of clients who pay a positive amount towards pawn recovery.

19

Figure OA-9 plots the histogram of the timing of payments in each arm, and shows that commitment
does appear to bind in that it generates a highly regular pattern of payments at 30, 60, and 90 days
after the loan is taken.

18

19

(2)

(7)

(6)

6304
0.011
0.12

2492
0.024
9.68

-4.12***(1.28)-1.82*(1.05)% of pay | def-0.071***(0.015)-0.027**(0.014)

(3)

6304
0.016
0.30

0.079***(0.026)-0.010(0.022)

2492
0.034
0.71

0.14***(0.034)0.050*(0.029)(8)

Pr(Selling pawn | def)

Panel B : Variables related to default

6304
0.017
45.8

Pr(+ payment & default)

4412
0.055
82.8

9.76***(2.74)-0.58(2.23)(1)-13.8***(1.61)-3.51**(1.57)

Pr(Recovery in 1st visit)

6304
0.016
0.31

0.0050(0.021)0.0035(0.019)(9)

Pr(Selling pawn)

6304
0.054
136.6

-27.9***(4.35)-0.18(4.33)(4)

Loan duration (days)

6304
0.022
1.14

-0.031(0.049)0.085(0.053)(10)# of visits

2492
0.028
0.39

-0.20***(0.050)-0.079*(0.043)(11)# of visits | defPanel C : Visit variables

3031
0.041
103.9

-17.9***(3.88)-1.35(4.19)(5)

Loan duration | recovery

This table explores treatment effects in “intermediate variables”. Each column represents regression output for different dependent variables following equation (1). Panel A focuseson variables related to the speed of payment. While Panel B focuses on variables related to default, and Panel C related to visits. Each regression includes branch and day-of-week
FE. Standard errors are clustered at the branch-day level.

Observations
R-squared
Control Mean

Choice commitment

Forced commitment

Observations
R-squared
Control Mean

Choice commitment

Forced commitment% of payment in 1st visit

Days to 1st payment

Panel A : Speed of payment

Table 3: Effects on intermediate outcomesOther costs. We have shown that forcing borrowers to take the monthly payment contract significantly reduces their financial costs. Although the paper focuses on financial
costs, we consider three additional costs here. First, we include the cost of visiting thebranch to make a payment. This includes the self-reported transport cost (most use
public transport), as well as the opportunity cost of time. To err on the conservativeside, we subtract a whole day’s minimum wage the day of the visit, instead of just thewage corresponding to a couple of hours. Second, we consider a rough proxy of the valueof liquidity that borrowers lose by paying sooner. To do this we add the interest costs
on to the payments in the forced commitment arm and recompute treatment effects
with these payments compounding daily (as if they had to borrow in order to make themore rapid payments). Thirdly, so far we have valued the collateral at the gold value
appraised by the lender, but the piece may be worth more to the borrower than its gold
value. For many of them the pawned jewelry has sentimental value. This is reflectedin the subjective valuation they reported in the survey which is 87% higher on average.
Our third extra cost considers this higher value. Table OA-7 shows results are robust
to all these changes.
Repeat Pawns. Table 4 explores the effects of treatment on future pawning behavior.
Column (1) shows that participants assigned to the forced arm are 6.3% more likely to berepeat clients later. While this appears to be prima facie evidence of greater satisfaction
among borrowers in the forced arm, the interpretation is complicated by the fact thatmonthly payments may themselves trigger more borrowing to pay them. This is unlikely
to be the case given that the effect on re-pawning comes after 90 days (during the periodof contract demanded payments) and not before (see columns 2 and 3). Column 4 only
considers new loans which use different collateral from that of the initial one. We do
this to foreclose the explanation that those in the Forced arm, being more liquidityconstraint, return to pawn a second pawn to be able to pay the monthly payments of
their first loan. However, we cannot reject a zero effect on pawning a different collateral.
Column 5 focuses on the (endogenous) subsample of those recovering their pawn in botharms of the experiment. This means that both arms have recovered their pawn and could
re-pawn if they so wish, and also that the liquidity demands from the monthly contract
are no longer there as the contract has been closed. We find that the difference between
the Forcing contract and the status quo is even larger in this subsample, with the former
having 11pp higher likelihood of being a repeat client during our sample period.
Censoring of Loan Completion. The window of time during which we were able toobserve borrower behavior was limited in each branch, meaning that there were loansthat we do not see completed (particularly those pawns that were rolled over for one or
two further 90-day spells). Overall, 13% of all experimental loans are censored, meaning

20

Table 4: Effects on Repeat PawningEver pawns again (ITT)Forced commitment
Choice commitment

Observations
R-squared
Control Mean

After 90 days

Within 90 days

Different collateral

Cond. on rec

(1)

(2)

(3)

(4)

(5)

0.063
(0.043)0.050(0.036)

0.041***(0.013)0.022*(0.011)0.024(0.033)0.028(0.031)

0.042(0.038)0.043(0.033)0.11**(0.055)0.088*(0.045)

6302
0.003
0.34

6302
0.007
0.018

6302
0.001
0.32

6302
0.002
0.32

3032
0.008
0.36

This table estimates the specification of equation 1 but at the level of the borrower (not the loan). Each column
represents a regression with a different outcome variable. Each regression includes branch and day-of-week FE.
Standard errors are clustered at the branch-day level.

that they neither default nor repay within the observation window. In the prior analysis
we handle this issue by using outcomes such as “did not default”, which are well-definedeven when we do not observe the completion of the loan, and by only considering costs
that we observe directly. We have also showed, however, that one effect of the forcing
arm is to accelerate repayment, meaning that it is less likely for loans in this arm tobe censored. This issue is illustrated in Figure OA-11, which shows the CDF of loan
completion (either default or recovery in Panel (a)) and loan recovery (Panel (b)) by
the number of days since first pawn. Two features of these graphs are salient for ouranalysis. The first is the extent to which loan outcomes are observed more quickly
in the forced commitment arm. This is primarily due to the substantially higher rateof repayment of Forced Commitment loans at 120 days (15 pp higher than the otherarms). The second is the very low rate at which loans are recovered in any arm after
120 days. In the 180-320 day window loans are largely dormant, suggesting that manyof the censored loans will in fact end in default.
The confluence of censoring and a treatment effect on censoring is potentially problematic from an experimental point of view. The approach taken so far is a conservative
one in that it inherently assumes that all of the loans outstanding at the end of the observation window will be repaid, making it so that the acceleration of payment observedin the Forced arm does not translate mechanically into the that treatment decreasing
default. Nonetheless, to be certain that this issue is not driving our results we conduct
a bounding exercise to understand how large the effects of this problem can possibly be.
In Table OA-6 we compare the Forced and Control arms, bounding the censoring issue
by reversing assumptions about the outcome of censored loans in the treatment versus
the control. Panel B provides the lower bound for the treatment effect (closest to zero)by assuming censored control loans are always repaid and treatment loans never are;21

even in this lower-bound case the treatment effect is cost-reducing and significant at the
1% significance level and indeed the magnitude of this lower bound estimate is only 6%
closer to zero than our headline result.
Finally, Panel E of this table conducts a logit prediction model that uses all of theavailable information on loans that were completed to predict the outcome of loansthat were not. This is a “best guess” of the outcome on censored loans. Using thisprediction, we replicate the main experimental results and find that the treatment effecton financial cost increases from -204 (main results) to -264 (censored loans predicted),
and the APR from -11% to -17%. Hence, while the censoring issue does have an effecton the magnitude of our estimated treatment effects, these checks confirm that (a) thecore results are fully robust to censoring, and (b) the headline approach that we take tothe issue is conservative and likely understates the true magnitude of impacts.

5

Choice and Heterogeneous Treatment Effects

The results from Section 4 show that commitment works: clients who were assigned to
the forced commitment arm experienced substantially lower financial costs on average.
In spite of this, given the opportunity, only 11% of borrowers chose commitment. If
the effect of commitment were homogeneous, this would be enough to conclude thatthe 89% who did not choose it would have been financially better-off if they had. In aworld of heterogeneous treatment effects, however, low demand for commitment could
still be consistent with borrowers adhering to a standard model of rational choice. The
borrowers who did not choose commitment could simply be those who don’t need it.
Indeed, we find strong evidence that the effect of forced commitment varies substantiallyacross individuals in our experiment: Appendix E.1 tests and rejects the null hypothesisof homogeneous treatment effects, following the methodology of Chernozhukov et al.
(2018). So the question remains: do the 89% who do not choose commitment know
something about their personal situations that we as researchers do not, or are mostpeople in the choice arm making a costly financial mistake? In this section we present
a series of econometric exercises that sheds light on this question, leveraging uniquefeatures of our experimental design. Among other results, we show that commitment
would lower average financial costs even for the subset of borrowers who choose not tocommit voluntarily. To simplify the exposition in this and all sections that follow, we redefine all outcome variables so that beneficial treatment effects are positive. Using thisconvention, a positive treatment effect of commitment on financial cost, for example,
reflects the average cost savings caused by commitment.

22

5.1

Bounding the Distribution of Individual Treatment Effects

If we knew the distribution of individual treatment effects, it would be easy assess how
many individuals would win and lose under a policy of universal forced commitment,along with the magnitude of any individual harm. Because we can never simultaneously
observe the same borrower in both the control and forced commitment arms, however,the distribution of individual treatment effects cannot be point identified. It can, however, be bounded. We begin our exploration of heterogeneous treatment effects bycomputing assumption-free bounds on the share of individuals who benefit from forced
commitment.
Let Yi0 be borrower i’s potential outcome under the control condition, Yi1 be her
potential outcome under forced commitment, and ∆i ≡ Yi0 − Yi1 . Because it randomly
assigns borrowers to the control and forced arms, our experimental design point identifies
the marginal distributions of Yi0 and Yi1 , call them F0 and F1 . Now, define the functions
F and F as follows:()

F (δ) ≡ max 0, sup F1 (y) − F0 (y − δ) ,yF (δ) ≡ 1 + min 0, inf F1 (y) − F0 (y − δ) .
y

Since F0 and F1 are point identified, so are F and F . Fan & Park (2010) show thatthe sharp (best possible) pointwise bounds for F∆ are given by F (δ) ≤ F∆ (δ) ≤ F (δ).
These bounds are simple to compute, and can be surprisingly informative. Here we usethem to bound the fraction of borrowers who benefit from forced commitment. Given
the way that we have defined our outcome variables, this is the share of borrowers whose
treatment effect is positive, i.e. P(∆i > 0) = 1 − F∆ (0). To construct the sharp bounds
for this quantity, we simply substitute δ = 0 into the preceding equations and estimate
F0 and F1 using their empirical analogues constructed from the forced commitment andforced no-commitment arms of the experiment.
Figure OA-15 plots the sharp bounds for F∆ based on the APR outcome. Our
point estimates of F (0) and F (0) are 0.03 and 0.77 respectively, with associated 95%
confidence intervals of [0.025, 0.050] and [0.75, 0.80]. Since we are interested in P(∆i >0) = 1 − F∆ (0), this means that at least 23% of individual borrowers benefit fromcommitment (and at most 97%).20
The bounds we have just described are constructed by considering all possible joint
distributions of Y0 and Y1 that are compatible with the observed marginal distributions
F1 and F0 . With stronger assumptions, it is possible to say more. One such assumption
is rank invariance, which posits that a person’s rank in the distribution of Y0 equals
her rank in the distribution of Y1 . While strong, this assumption or variants of it
have appeared in a number of settings in the literature, e.g. Chernozhukov & Hansen
20
Confidence intervals are constructed using the asymptotic distribution for the bounds. See Fan &Park (2010) for details.

23

(2005), so we consider it here for purposes of comparison. Under rank invariance, thedistribution of treatment effects is point identified and given byF∆ (δ) =Z 1
01{F1−1 (u) − F0−1 (u) ≤ δ} du

where F1−1 and F0−1 are the quantile functions of Y1 and Y0 . Figure OA-17 in Appendix
E.2 plots our estimates of F∆ under rank invariance. For the financial benefit outcome,Y1 first-order stochastically dominates Y0 in our experiment: every quantile of the distribution of financial cost savings under forced commitment is higher than the corresponding quantile under the control condition. Since this implies that F1−1 (u) − F0−1 (u)is always positive, rank invariance yields an extremely stark conclusion: all borrowers
have positive individual treatment effects of forced commitment. For the APR outcome,the results under rank invariance are slightly less stark: we estimate that just under 90%
of borrowers have positive individual treatment effects.

5.2

Potential Outcomes and Exclusion

Our assumption-free bounds from the preceding section show that more than 23% ofborrowers would benefit from a policy of forced commitment. This suggests that someof the 89% of borrowers in the choice arm who did not choose commitment would have
faced lower borrowing costs if they had. Making this intuition precise, however, requires
a careful consideration of the relationship between choice and heterogeneous treatment
effects. To this end, we now provide a full definition of the potential outcomes in ourempirical setting, and introduce a pair of assumptions that will allow us to go beyond
the assumption-free bounds from above.
Let Zi ∈ {0, 1, 2} denote the treatment arm to which to participant i was assigned:
Zi = 0 denotes the forced no-commitment arm, Zi = 1 denotes the forced commitment
arm, and Zi = 2 denotes the choice arm. Now let Di be the treatment that participant
i actually received, where Di = 0 denotes no-commitment and Di = 1 denotes commitment. We assume perfect compliance in the Zi = 0 and Zi = 1 arms.21 It is only in
the Zi = 2 arm that participants are free to choose between alternative contracts. Let
Ci ∈ {0, 1} denote a participant’s “choice type.” If Ci = 1 then participant i would
choose commitment, given the option; if Ci = 0 she would not. As shorthand, we callborrowers with Ci = 1 “choosers” and those with Ci = 0 “non-choosers.” Whereas a participant’s choice type Ci is only observed if she is allocated to the choice arm (Zi = 2),
her treatment Di and experimental arm Zi are always observed. Given the design of
our experiment, these quantities are related by
Di = 1(Zi ̸= 2)Zi + 1(Zi = 2)Ci .
21

For more discussion on this point, see Section 3.3 above.

24

(2)

We maintain the stable unit treatment value assumption (SUTVA) throughout. Thismeans that borrower i’s outcomes depend only on her own values of Zi and Di , not thoseof any other person in the experiment. Under this assumption, a fully general model forthe potential outcomes in our experiment would take the form Yi (d, z) for d ∈ {0, 1} andz ∈ {0, 1, 2}, allowing participant i’s potential outcome to depend both on the treatment
she actually receives, Di , and the experimental arm to which she is assigned, Zi . Thismodel is too general, however, to point identify meaningful causal effects. For thisreason, we consider two exclusion restrictions.
Before stating these restrictions, we first define some additional notation. Because
our experimental design implies that any borrower with with Zi = 0 has Di = 0, we
abbreviate the potential outcome Yi (d = 0, z = 0) as Yi0 . Similarly, since any borrower
with Zi = 1 has Di = 1, we abbreviate Yi (d = 1, z = 1) as Yi1 . This is in keeping with
our notation from section 5.1 above. Using this notation, our first exclusion restriction
is given byYi (d = 0, z = 2) = Yi (d = 0, z = 0) ≡ Yi0 .

(3)Equation 3 only restricts the potential outcomes of non-choosers, individuals with Ci =0, because they are the only borrowers for whom Di = 0 when Zi = 2. In words,
this condition assumes that every non-chooser experiences the same potential outcome
regardless of whether she is assigned to the choice arm or the control arm. Similarly,
our second exclusion restriction is given byYi (d = 1, z = 2) = Yi (d = 1, z = 1) ≡ Yi1 .

(4)Equation 4 only restricts the potential outcomes of choosers, individuals with Ci = 1,
because they are the only borrowers for whom Di = 1 when Zi = 2. In words, thiscondition assumes that every chooser experiences the same potential outcome regardlessof whether she is assigned to the treatment arm or the choice arm.
Mathematically (3) and (4) have the same structure as the standard LATE exclusion
restriction that Yi (d, z) depends only on d, not on z. Substantively, however, they areslightly different, given that there is no explicit reference to the “chosen” versus “forced”
treatment distinction in the usual LATE setup.22 In essence, (3) and (4) assume thatbeing assigned a particular treatment has the same result as choosing it for yourself,
provided that you are assigned the same treatment that you would have chosen. If themere fact of having been given a choice has a direct effect on outcomes, one or bothof our exclusion restrictions will be violated. One can imagine situations in which thismight be the case. For example, even someone who would have voluntarily chosen to22

For related discussion, see Chamberlain (2011) who uses an assumption similar to our exclusion
restrictions to develop a theory of optimal treatment choice for an individual who has access to datafrom an RCT.

25

undergo drug rehabilitation, given the choice, might respond differently when coerced.
In our empirical setting, however, both (3) and (4) are plausible. Moreover, each has
testable implications that we fail to reject. For details, see Appendix G. 23
Under the exclusion restrictions from (3) and (4), each participant’s observed outcome Yi is related to her potential outcomes (Yi0 , Yi1 ) according to
Yi = 1(Zi = 0)Yi0 + 1(Zi = 1)Yi1 + 1(Zi = 2) [(1 − Ci )Yi0 + Ci Yi1 ] .

(5)Equation 5 is the key to understanding the results that follows. As noted above, by randomly assigning Zi = 0 and Zi = 1 our experiment identifies the marginal distributionsof Yi0 and Yi1 in the population as a whole. By randomly assigning Zi = 2, it likewise
point identifies the share of choosers (Ci = 1), the distribution of Yi1 for choosers, andthe distribution of Yi0 for non-choosers (Ci = 0). Because Zi is assigned independentlyof pre-treatment covariates Xi , our design also identifies the corresponding conditional
distributions of Yi0 and Yi1 given Xi .

5.3

The “Controlled Choice” Design

We now show how our experimental design, henceforth the “controlled choice design,”
combined with the exclusion restrictions from (3) and (4) can be used to point identify anumber of interesting and economically-relevant causal quantities without the need for
additional structural restrictions. First we identify the treatment on the treated (TOT)and treatment on the untreated (TUT) effects, defined as follows:
TOT ≡ E(Yi1 − Yi0 |Ci = 1),

TUT ≡ E(Yi1 − Yi0 |Ci = 0).

The TOT is the causal effect of commitment on borrowers who would voluntarily choose
it, while the TUT is the causal effect on borrowers who would not. If the TUT is
positive, this means that those who did not choose commitment would have experienced
better outcomes, on average, if they had. In a canonical Roy model, the TOT should
exceed both the TUT and average treatment effect (ATE). If the TOT is statisticallydistinguishable from and substantially larger than the TUT, this provides empiricalsupport for the relevance of selection-on-gains in real-world decision-making. Because
our design identifies all three quantities (as discussed below and in Appendix F.), it
allows us to test this implication directly and to calculate the average selection on gains
23
As mentioned above, this is a frequently used assumption even if often implicit. A significant
literature uses schooling compulsory laws to estimate the return and then interprets that schooling in
general has this return. Fertilizer yields are measured by researchers in experimental plots and then
expected to have these returns regardless of whether farmers choose or the government provides these
fertilizers. We are not the first paper to use this assumption, see Chamberlain (2011).

26

(ASG), namely the difference between the TOT and TUT effects:
ASG ≡ E[Yi1 − Yi0 |Ci = 1] − E[Yi1 − Yi0 |Ci = 0] = TOT − TUT.
The controlled choice design also identifies both the average selection bias (ASB) andthe average selection on levels (ASL).
ASB ≡ E[Yi0 |Ci = 1] − E[Yi0 |Ci = 0],

ASL ≡ E[Yi1 |Ci = 1] − E[Yi1 |Ci = 0].

The ASB tells us whether borrowers who voluntarily choose commitment are those who
are worse off, on average, under the status quo. Similarly, the ASL tells us whether
borrowers who voluntarily choose commitment are those who are better off, on average,
under the commitment contract. A companion STATA package accompanying this paper
provides estimators of the TOT, TUT, ASG, ASB, and ASL, along with cluster-robust
standard errors for each, and a test for the validity of the exclusion restriction following
Huber & Mellace (2015).24
A number of recent papers compare estimates of the TOT and TUT to better understand who selects into treatment and why, e.g. Cornelissen et al. (2018) and Walters(2018). This line of work relies, at least to some extent, upon structural modeling assumptions to extrapolate from the reduced-form quantities that are identified by thedata alone to more interesting, and economically relevant, causal parameters.25 An alternative approach aims to avoid structural assumptions by calculating conditional local
average treatment effects (LATE) given observed covariates X and re-weighting themaccording to the distribution of covariates in some population of interest to yield, forexample, an average treatment effect (Aronow & Carnegie, 2013; Angrist & FernandezVal, 2013). But there is no free lunch: this “LATE-and-reweight” approach relies uponassumptions of its own, most crucially the assumption that there is no selection-ongains conditional on X, i.e. that the conditional LATE equals the conditional ATE. In
contrast to both approaches, the controlled choice design uses exogenous experimental
variation to point identify the ATE, TOT, and TUT without ruling out unobserved
selection-on-gains or relying on additional structural modeling assumptions. Figure 2
provides graphical intuition for our identification approach.
The key insight can be read directly from (2) and (5). Viewing Zi as an instrumental
variable, the controlled choice design can be interpreted as a pair of RCTs, each subject
to one-sided non-compliance. The first of these compares Zi = 0 to Zi = 2. For
24

See Appendix Appendix F. for more details.
While the marginal treatment effects (MTE) approach (Heckman & Vytlacil, 2007) can in principle
be used to identify the TOT and TUT without parametric restrictions, doing so requires an instrumental variable Z with sufficiently rich support that the probability of treatment take-up given Z varies
continuously between zero and one. In practice, instrumental variables are usually discrete and, evenwhen continuous, typically have a more modest effect on take-up.
25

27

Figure 2: The Controlled Choice Design.
This figure provides graphical intuition for the way in which the controlled choice design from Section point
identifies both the treatment on the treated (TOT) and treatment on the untreated (TUT) effects, as discussed
in Section 5.3 and Appendix F.. The gray shaded regions denote borrowers with a commitment contract; thewhite shaded regions denote borrowers with a status quo contract. A comparison of means across control andforcing arms identifies the ATE of forcing commitment. The TOT and TUT effects of commitment are identified
as follows. In the choice arm, anyone with a commitment contract is a chooser; in the control and forcing arms,
we do not know who is a chooser and who is not. Because borrowers are randomly assigned to experimental
treatment arms, however, the share of choosers will be the same, on average, across experimental arms. Thisis depicted using dashed vertical lines in the control and forcing arms. This overall share of choosers and nonchoosers is point identified from the choice arm. Now, the difference of mean outcomes across the choice andcontrol arms gives the intent-to-treat effect of offering choice. Under the exclusion restriction that moving nonchoosers between the choice and forcing arms does not change their outcomes, this comparison “nets out” thenon-choosers. Hence, the ITT of offering choice equals the TOT multiplied by the share of choosers. Similarly,
under the exclusion restriction that moving choosers between the choice and forcing arm does not affect theiroutcomes, the difference of means across the forcing and choice arms “nets out” the choosers and hence equals
the TUT multiplied by the share of non-choosers.

each individual with Zi = 0 we have Di = 0 and observe Yi0 . For those with Zi = 2
we have Di = Ci and observe (1 − Ci )Yi0 + Ci Yi1 . This is identical to a “randomized
encouragement” design in which treatment is only available to those who are encouraged:
Zi = 2. Under this interpretation, those with Ci = 1 are “the compliers” and it follows
that

E(Yi |Zi = 2) − E(Yi |Zi = 0) E(Yi |Zi = 2) − E(Yi |Zi = 0)=
= E(Yi1 − Yi0 |Ci = 1)
E(Di |Zi = 2) − E(Di |Zi = 0)
E(Di |Zi = 2)

(6)

since E(Di |Zi = 0) = 0 by (2). A closely related argument can be used to constructa Wald estimand that identifies the TUT. Here we consider Zi = 1 to be the “encouragement” and compare the outcomes for these individuals to those with Zi = 2. If
Zi = 1 then Di = 1 and we observe Yi1 . If instead Zi = 2 then Di = Ci and we
observe (1 − Ci )Yi0 + Ci Yi1 . Again, we can view this as an experiment with one-sided
non-compliance, but now the situation is reversed. Everyone with Zi = 1 is treated,but some people with Zi = 2 are “always-takers” who obtain the treatment (Di = 1)
despite having been allocated to the “control” arm Zi = 2. Under this interpretation,
the “compliers” are those with Ci = 0: when Zi = 1 they take the treatment, and when28

Zi = 2, they do not. Thus,

E(Yi |Zi = 1) − E(Yi |Zi = 2) E(Yi |Zi = 1) − E(Yi |Zi = 2)=
= E(Yi1 − Yi0 |Ci = 0)
E(Di |Zi = 1) − E(Di |Zi = 2)
1 − E(Di |Zi = 2)

(7)

since E(Di |Zi = 1) = 1 by (2). Equations (6) and (7) are useful for understanding why
the controlled choice design identifies the TOT and TUT, but they are less convenient
for estimation and inference. In Appendix F., we show that
Yi = E(Yi0 ) + (ATE)1(Zi = 1) + (TOT) [1(Zi = 2) × Di ] + Ui

(8)Yi = E(Yi1 ) + (ATE) [−1(Zi = 0)] + (TUT) [−1(Zi = 2) × (1 − Di )] + Vi

(9)where E(Ui |Zi ) = E(Vi |Zi ) = 0. It follows that a pair of just-identified, linear instrumental variables regressions can be used to estimate and carry out inference for the
ATE, TOT, and TUT. To identify the ATE and TOT, run IV on (8) with instruments

1(Zi = 1) and 1(Zi = 2). An F-test based on this regression can then be used to test
the restriction ATE = TOT, and the usual IV output can be used to carry out inference
for the TOT. Similarly, to identify the ATE and TUT run IV on 9 with instruments

1(Zi = 0) and 1(Zi = 2). An F-test based on this regression can then be used to test
the restriction ATE = TUT, and the usual IV output can be used to carry out inference
for the TUT.
Because they identify both the TOT and TUT, (8) and (9) also identify the average
selection on gains: ASG = TOT − TUT. Carrying out inference for this quantity isa bit more involved, because ASG is a difference of coefficients from two separate IV
regressions. In Appendix F. we show how to use the residuals from (9) and (8) to carryout cluster-robust inference for ASG, a procedure that is automated in our companion
STATA package. As mentioned above, the controlled choice design also identifies theaverage selection bias (ASB) and average selection on levels (ASL). In particular,E(Y |Z = 0) − E(Y |Z = 2, D = 0)
E(D|Z = 2)
E(Y |Z = 2, D = 1) − E(Y |Z = 1)
ASL ≡ E(Yi1 |Ci = 1) − E(Yi1 |Ci = 0) =.
1 − E(D|Z = 2)

ASB ≡ E(Yi0 |Ci = 1) − E(Yi0 |Ci = 0) =

(10)
(11)

For purposes of inference, both the ASB and ASL can be re-written as the difference ofcoefficients from a pair of just-identified linear IV regressions.26
26

For details, along with a description of how our companion STATA package carries out cluster-robust
inference for these quantities, see Appendix F..

29

Table 5: Treatment on the Treated (TOT), Treatment on the Untreated (TUT),
Selection-on-gains (TOT - TUT), Average Selection Bias (ASB), and Average Selection
Bias, calculated using the results from Section 5.3.

ATE
ToT
TuT
E[Y1 ]
E[Y0 ]
ToT-TuTASB
ASL

Observations
H0 : ATE-TuT=0
H0 : ATE-ToT=0
H0 : ToT-TuT=0
H0 : ToT-TuT≥ 0

APR % benefit

FC benefit% (1-Default)% (1-Refinance)

(1)

(2)

(3)

(4)

9.41***(2.06)-0.59(21.4)
10.6***(2.47)-47.4***(1.42)-56.8***(1.49)

183.0***(50.8)
111.9(528.3)191.5***(50.8)-759.4***(27.3)-942.4***(42.9)

7.74***(2.50)
37.4*(21.6)
4.20*(2.41)
64.2***(1.69)
56.4***(1.84)

6.34**(2.90)-25.9(29.1)
10.2***(2.90)
67.2***(1.70)
60.9***(2.35)-11.2(22.9)
15.8(22.3)
4.58(3.55)-79.6(556.2)291.5(551.2)211.9***(59.5)

33.2(22.6)-39.1*(22.3)-5.90(4.29)-36.1(30.6)
22.7(30.1)-13.4***(4.20)

6304
0.62
0.63
0.63
0.69

6304
0.89
0.89
0.89
0.56

6304
0.14
0.14
0.14
0.071

6304
0.23
0.24
0.24
0.88

This table presents results computed using the derivations from Section 5.3 and Appendix F.. The APR andfinancial cost outcomes have been multiplied by −1 so that a positive causal effect benefits the borrower in eachof the four columns. See Appendix F.3 for more details on how we compute standard errors for the middle panel.
The bottom panel present p-values for a number of null hypothesis tests of treatment effect heterogeneity.

TOT and TUT results. Table 5 calculates the causal quantities described above–
TOT, TUT, ASG, ASB, and ASL–for our experimental data, along with robust standard
errors for each. For purposes of comparison, the table also presents the ATE results from
Section 4 above (row 1),27 along with the corresponding average potential outcomes

E[Y0 ] and E[Y1 ] (rows 4–5). The columns of the table correspond to different outcome
variables defined above. For all four outcome definitions, the TUT effect is positive,
statistically and economically significant, and comparable in magnitude to the ATE.
In other words: commitment is beneficial, on average, to the people who would notchoose it, and these benefits are large. Due to the low take-up rate of commitmentin the choice arm, the corresponding TOT effects are imprecisely estimated. Only oneof them, %(1-Default) from column (3), is statistically significant. This imprecision
carries over into our estimates of the average selection on gains, TOT-TUT. Our point
estimates are negative for all but the (1 - Default) outcome, but none is statisticallydistinguishable from zero. For the (1 - Default) outcome, we have sufficient precision to27

Coefficients are not exactly the same since Table 4 includes branch and day-of-week FE.

30

conclude that the average selection bias (ASB) is large and negative. This means thatborrowers who choose commitment would have faced a higher probability of default
under the status quo contract than borrowers who do not choose commitment. We may
not want to read too much into TOT vs TUT comparisons as they are imprecise. But
taken at face value, the result that TOT>TUT for default, while the opposite is true forfinancial cost, suggests that, while voluntary commitment has a slightly stronger effecton allowing borrowers to avoid default, forcing reduces payments in a strong enoughmanner as to overcome the default-benefits of choice.
Overall, Table 5 suggests that commitment works but that not enough people choose
to commit: the commitment contract is beneficial on average even to those who would
not choose it voluntarily. We believe this result is new in the household finance literature. It also illustrates how the “Controlled-Choice” design can be used to study moregenerally whether low take-up of an intervention is problematic, based on the impacts
among non-choosers.28

6

The Case for Paternalism

6.1

Why does paternalism work in this context?

A behavioral literature has highlighted voluntary commitment as an attractive way ofallowing the “right” people to self-select. The argument for compulsory treatment,
centers on the surprising result that TUT > 0. We now investigate several potential
explanations for this result. For simplicity, we focus on causal effects for the APR
outcome throughout this section. We view this section as an exploratory analysis tostimulate ideas for future research. We examine four potential explanations for the
positive TUT: the need to learn, time discounting, present bias, and overconfidence. To
explore the last two dimensions we will use survey data.29
Learning. A first explanation involves learning. Our experiment introduced a newcontract into an environment that had not previously featured commitment; perhaps
clients required experience to understand its benefits. Are clients who experienced
the commitment contract more likely to choose commitment subsequently than those
assigned to the status-quo contract? To test this we look to the subset of 22% clientsfrom our experimental sample who returned to pawn again on another day before the28

For instance, in the debate on financial commitment take-up, some papers argue it is low (Ashraf
et al. (2006), Giné et al. (2010), Bai et al. (2020), Royer et al. (2015) while others argue it is high(Kaur et al. (2015), Casaburi & Macchiavello (2019), Schilbach (2019), Tarozzi et al. (2009), Dupas &Robinson (2013),), but none estimates the benefits for non-takers. In a different domain, doctors claimthat medical treatment abandonment is too high in a broad range of diseases (McDonald et al., 2002),
without knowing the treatment benefits for those that abandon.
29
Since merging with survey data reduces our sample, Table OA-4 demonstrates that the subsample
on whom we have survey data appears to be representative in terms of treatment effects.

31end of the experiment. We have already shown above that those who experienced theForcing contract were more likely to borrow again. We now ask whether the subset
who were assigned to the Choice arm when they returned were more likely to choose
commitment. We do this in Appendix Table OA-8.30 We find no statistically discernible
difference in commitment take-up rates for those assigned to forced commitment versus
those assigned to status quo control. The implication is that while those who haveexperienced commitment feel more positively towards the pawn contract, the experience
does not lead them to conclude that they need commitment on the subsequent loan.
While these exercises cannot completely exclude the possibility that learning plays arole, they provide no indication that the lack of voluntary compliance is simply a matterof inexperience with commitment, but more research and larger samples are needed totest whether learning obviates the need for paternalism.
Time discounting. Discounting is a second potential explanation for our results.
Highly impatient individuals might rationally choose the status quo contract, despite
the benefits that commitment yields returns, since monthly payments are front-loaded
while pawn recovery is back-loaded, even if by only a few days. To investigate this
explanation we calculate the net present value (NPV) of the financial cost TUT effectunder different hypothetical discount rates, given the actual timing of repayment andpawn recovery. Figure OA-13 presents the results of this exercise. The solid line gives
the TUT effect adjusted for a specified annual discount rate, while the shaded regions
give the associated 95% & 90% confidence interval. We see that non-choosers continue
to experience significant decreases in NPV financial costs up to annual discount rates
of 1,000%, and the NPV remains positive, although not significant, at 5,000% discountrates. As such, discounting is unlikely to explain why those who benefit, on average,from commitment fail to choose it when offered.
Present bias. If the benefits of commitment among non-choosers cannot be explainedby standard models of rational choice, the canonical behavioral story would center ontime inconsistency. While commitment is useful to anyone with hyperbolic time preferences, only those who are sophisticated–i.e. aware that they are hyperbolic discounters–
will demand it. A large share of “naı̈ve” hyperbolics in the population–borrowers who areunaware that they are hyperbolic discounters–could therefore drive a large and positive
TUT. Our baseline survey included standard questions about discount rates between
today and a month in the future versus discount rates between three and four months
in the future. This allows us to classify borrowers who display more impatience over
immediate delays as present biased. This measure of financial hyperbolicity is widely
30

Table OA-8 presents information about participants’ immediate subsequent pawning behavior. For
borrowers who returned to pawn again more than once, this analysis considers only their first repeat
pawn.

32

400

200

0

-200

-400
P.B.

Sure-confidence
TuT | X=0

TuT

TuT | X=1

Figure 3: Heterogeneity of the TUT by behavioral variables.
Each panel in this figure shows how the estimated treatment on the untreated (TUT) effect varies with a binary
survey variable Xi . In the left panel (P.B.), Xi = 1 if borrower i is “present-biased” based on her responses tothe time preference questions from our survey. In the right panel (Sure-confidence) Xi = 1 if borrower i reported
that she was certain to recover her pawn, zero otherwise.

used in survey research, although it is not without problems.31
If we could perfectly measure present bias and sophistication, we could divide thesample into three groups: sophisticated hyperbolics (who chose commitment), timeconsistent non-choosers (for whom forcing will not be effective), and naı̈ve hyperbolic
non-choosers (who will benefit from forced commitment). If present bias fully explains
the low take-up rate of voluntary commitment, we should find that the TUT for presentbiased borrowers is positive. This is because among the group of non-takers, a comparison of present-biased borrowers against everyone else is a comparison of naı̈ve hyperbolics
against time-consistent non-choosers.
The left panel of Figure 3 carries out a feasible version of this exercise using oursurvey measure of present bias. The overall TUT estimate along with a 95% confidence
interval is given in blue.32 The corresponding TUT estimate and confidence interval forpresent-biased borrowers identified with the survey question is given in green; results
for all other borrowers are shown in red. The overall TUT is a weighted average of the
impact in these two sub-groups. The TUT among the present biased is insignificant andless than half the size of the strongly significant TUT among those who are not present
biased. Therefore, taking our survey measure of hyperbolicity at face value, we find no
indication that present-bias explains our positive estimated TUT.
31

Our measure is dichotomous, and it is not incentivized. Recent empirical work has shown the
superiority of more elaborate measures such as “convex time budgets” (Andreoni et al., 2015) whilequestioning the interpretation of measures of hyperbolicity that are not based on consumption (Andreoni & Sprenger, 2012; Cohen et al., 2020), suggesting that real effort tasks provide a better measure(Augenblick et al., 2015). Given that we had only a few minutes to interview real pawnshop clients prior
to a commercial transaction, our simple measure was a necessary compromise.
32
For all borrowers who answered our present-bias survey questions.

33Sure confidence. While 72% of survey respondents believe they have a 100% chanceof recovering their pawn, in reality only 43% will go on to do so. This suggests a
borrower pool characterized by over-optimism. Incorrect expectations about recovery
probabilities could explain low take-up if individuals who believe that they are certain to
repay choose, rationally given their incorrect beliefs, to forgo the costs associated withcommitment that are designed to induce repayment. We now explore whether overoptimistic expectations of recovery probability can explain our positive overall TUT
estimate. To do this, we carry out an analysis that is analogous to our present bias
exercise from the preceding paragraph, comparing the overall TUT estimate to estimates
computed for two sub-groups. Here, however, the groups are defined by a binary variable
that we call “sure-confidence.” This measure equals one for any individuals who say at
the time of borrowing that they have a 100% probability of recovering their pawn, zerootherwise. The right panel of Figure 3 presents the results for this exercise. The overall
TUT estimate for all borrowers who answered our sure-confidence survey questions isgiven in blue, along with a 95% confidence interval. The corresponding TUT estimate
and confidence interval for sure-confident borrowers is given in green; results for allother borrowers are shown in red. In contrast to our results for present bias, the TUT is
almost entirely confined to the sure confident individuals, with the effect among thosesaying they have some chance of defaulting at baseline being very close to zero.
As discussed above, our measure of hyperbolicity is based on un-incentivized responses in a short survey and so is likely to be noisy; nonetheless we see no evidence
here that it drives the forcing effect. Rather, the analysis from Figure 3 suggests thatthe effectiveness of paternalism in our experiment may be driven by overconfident borrowers who, heedless of the risk of default, fail to choose commitment despite benefiting
substantially when they are forced to commit.
If the attribute of “sure confidence” proves so important in explaining the positive
TUT, what are its determinants? In Figure OA-14 we plot the coefficient estimates froma regression that predicts sure confidence with a battery of individual-level characteristics. Older males are more likely to be sure-confident, as are those with more education.
Taken at face value, the sure-confident also report less financial stress, less trouble paying bills, and to be more frequently relied upon financially by family members. Viewed
through a behavioral lens, however, it is also possible that the type of person who isover-confident in their ability to repay a loan also exaggerate their degree of economic security in their response to survey questions. In any case, it appears that sure confidence
may be difficult to predict with easily-observed and objective demographic criteria, apoint to which we return below.

34

6.2

Analyzing Choice versus Paternalism Using Causal Forests

Causal forests. On average, the commitment contract benefits both those who would
choose it and those who would not. In Section 5.1, we briefly went beyond average effects
by presenting bounds on the distribution of individual treatment effects. Because they
made no assumptions beyond random assignment, these bounds were relatively wide.
Adding the assumption of rank invariance yielded a distribution of treatment effects
in approximately 90% of borrowers had positive individual treatment effects for the
APR outcome, implying that practically everyone would benefit from treatment andhence that there would be hardly any no losers from paternalism. Rank invariance,
however, is an extremely strong assumption.33 In this section, we explore a middle way
between the two extremes, using a causal forest analysis to consider conditional averagetreatment effects and conditional TOT and TUT effects.34 This exercise provides morefine-grained information about treatment effect heterogeneity. Among other things, itwill potentially allow us to identify groups of borrowers who are on average harmed
by commitment. Under the stronger assumption that our observed survey measures
capture the main sources of treatment effect heterogeneity, this exercise will allow us toapproximate individual-level counterfactuals, to consider whether particular borrowers
made “mistakes” in their choice of contract.
To estimate conditional average treatment effects given administrative and survey
data, we use the function causal forest() of the grf R package; to estimate conditional
TOT and TUT effects we use the instrumental forest() function from the same
package. In each case, we use the default parameter values from the grf package with
one exception: we increase the number of trees from the default value of 2000 to 5000.
The functions causal forest() and instrumental forest() implement special casesof the “generalized random forest” methods of Athey et al. (2019). In broad strokes,
these functions combine a large number of regression trees that recursively partition thecovariate space to estimate conditional average effects. The trees are “honest” in thatobservations used to determine the optimal partition are not used to estimate effects,
and vice-versa. While closely related to more familiar “regression-tree” random forests,
the generalized random forest approach explicitly targets the parameter of interest–aconditional ATE or IV estimand–when choosing the optimal covariate partition. 35
33
For the financial cost outcome, rank invariance implies that all invididual treatment effects are
positive.
34
Note that this approach imposes our exclusion restriction from 5.3 conditional on observed covariates:
administrative data and survey responses.
35
For more details, see Athey et al. (2019) and the grf documentation: https://grf-labs.github.
io/grf/. When constructing our random forest estimates of heterogeneous treatment effects, we use
observations for all borrowers who answered at least part of the intake survey. We impute the median
response for the missing values, while also including an indicator whether the variable originally had
a missing value. Results are similar if we manually include interactions between the original/imputed
variable and an indicator for missingness. This is as expected, given that tree-based methods by theirnature “automatically” consider interactions of arbitrary orders.

35

1.5

8

8

6

6

4

4

2

2

1

.5

0

0
-1

0

1

2

3

4

0
-.2

0

.2

APR

.4

-.1

APR

(a) ToT

0

.1

.2

.3

APR

(b) TuT(c) ATE

Figure 4: Heterogeneous Treatment Effects.
Treatment effect distributions. Figure 4 plots densities of the estimated conditional
ATE, TOT, and TUT effects from the generalized random forest models described above.
In each case, the outcome variable is APR benefit, i.e. the reduction in APR from acommitment contract. As we see from the figure, the conditional average effects are
overwhelmingly positive. The TUT density is particularly interesting for the questionof paternalism since, as emphasized above, it presents conditional average effects forborrowers who would not voluntarily choose commitment. Only 7% of our estimatedconditional TUTs are negative, with a 95% confidence interval of [4%, 9%].36 To be clear,this is a probability statement about conditional average effects over the distribution ofcovariates. In particular, we estimate that1

{E[Y1 − Y0 |X = x, C = 0] < 0} f (x|C =370) dx is approximately 0.07. Figure 4 strengthens our argument, introduced in Section
R

5, that not enough borrowers choose commitment.
“Mistake” tresholds. Under the assumption that our instrumental forest estimates
capture the main sources of treatment effect heterogeneity, we can use them to assess
whether particular borrowers in the choice arm made “mistakes” in their decision toaccept or refuse the commitment contract, in terms of predicted financial costs of theloan. To do this we use the same information that is depicted in Figure 4, but present
it in a different way. For each non-chooser in the choice arm, we use our instrumental
forest from above to estimate the conditional TUT effect, given her observed covariates.
Of course conditional average effects need not equal individual treatment effects, and
our APR outcome may not capture all of the costs and benefits that are relevant forindividual borrowers’ decisions. To account for this, we define a “mistake” for a nonchooser to be a conditional TUT estimate that significantly exceeds some large andpositive APR threshold, e.g. 10%. At any such threshold, we can calculate the percentage
36

The generalized random forest approach of Athey et al. (2019) produces conditional average effectestimators that are asymptotically normal, and includes methods for computing correct standard errors.
Our inferences in this section are carried out by “bootstrapping the limit experiment,” i.e. simulatingfrom the normal limit distributions using the estimated standard errors.
37
The share of non-choosers with negative conditional average treatment effects need not equal theshare with a negative individual effects, i.e. (Y1 < Y0 |C = 0). But the more treatment effect heterogeneity that Xi explains, the closer these two values become.

P

36

of non-choosers in the choice arm who have benefited by more than that threshold fromhaving chosen commitment.
The results of this exercise can be read off from the green curve in Figure 5. Defining
FTUT (δ) to be the CDF corresponding to the density of conditional TUT estimatesfrom Figure 4, the green curve in Figure 5 is merely [1 − FTUT (δ)] × 100%. In otherwords, the green curve gives the percentage of non-choosers who made a “mistake” when
mistakes are defined increasing APR by a given threshold. The green shaded region gives
associated 95% pointwise confidence bounds.
For choosers we follow an analogous approach, defining a “mistake” as a negative
conditional TOT effect that exceeds a particular APR threshold. The results for choosers
can be read from the red curve in Figure 5. If FTOT (δ) denotes the CDF corresponding
to the density of conditional TOT estimates from Figure 4, then the red curve is merely
FTOT (−δ) × 100%. In other words, the red curve gives the percentage of choosers who
made a “mistake” when mistakes are defined at a particular APR threshold. The red
shaded region gives associated 95% pointwise confidence bounds. Note that we use apositive APR threshold to denote a mistake for both choosers and non-choosers. This
ensures that bigger mistakes are always to the right of smaller mistakes for both the green
and red curves. The blue curve in Figure 5 gives the overall percentage of borrowers
in the choice arm who made a “mistake” at a particular APR threshold. This total iscomputed by taking a weighted average of the green (non-choosers) and red (choosers)
curves, with weights equal to their shares in the choice arm.38
The results in Figure 5 suggest that a large fraction of non-choosers made mistakes
by not choosing commitment. Even at an APR threshold as large as 10%, we estimatethat more than half of them should have chosen commitment in order to lower financial
costs. In contrast, relatively few choosers appear to have made mistakes by choosing
commitment. This now allows us to make a stronger statement in favor of paternalism
in our context; not only does forced commitment generate large benefits on average, but
it also benefits the vast majority of borrowers who would be coerced under a policy offorced commitment.
38
The blue curve is very similar to the green curve because 89% of borrowers in the choice arm are
non-choosers.

37

100
90
80

% of mistakes

70
60
50
40
30
20
10
0
-50

-30

-10

10

30

50

APR % threshold
Choice commitment

Non-choosers

Choosers

Figure 5: “Mistakes” in the choice arm.
This figure presents conditional average TUT and TOT effects for the APR outcome from Figure 4 in an alternative manner, to consider the fraction of borrowers in the choice arm who made “mistakes” in their decision toaccept or refuse the commitment contract. A “mistake” for a non-chooser is defined as a positive conditional TUT
effect that significantly exceeds a specified threshold APR value. The green curve equals [1 − FTUT (δ)] × 100%,
where FTUT is the CDF corresponding to density of conditional TUT effects from Figure 4, computed using the
instrumental forest approach from Athey et al. (2019). Evaluated at any positive value on the horizontal axis, it
gives the fraction of non-choosers in the choice arm who made a “mistake” by not choosing commitment. The
green shaded region gives associated 95% pointwise confidence bands. Analogously, a “mistake” for a chooser isdefined as a negative conditional TOT effect that exceeds a specified threshold APR value. The red curve equals
FTOT (−δ) where FTOT is the CDF corresponding to the density of conditional TOT effects from Figure 4. The
red shaded region gives associated 95% pointwise confidence bands. For both the red and green curves, we define
the APR threshold so that larger mistakes are to the right of smaller mistakes. This allows us to construct theoverall fraction of mistakes in the choice arm, the blue curve, as a weighted average of the green and red curves.
The weights equal the share of choosers and non-choosers in the choice arm.

6.3

Can we target paternalism?

Despite having shown such a large majority of individuals benefit from paternalism, it
is still natural to ask whether we are able to target commitment in such a manner as
to only force it upon those who benefit. For a financial firm to engage in this typeof targeting under real-world circumstances, we must impose several constraints on thetargeting rule. First, it will in general not be possible to use the numerous subjective andunverifiable questions we asked in the baseline survey as inputs to the rule because theanswers to these questions can be manipulated by the clients, and would likely change
when they become incentivized. This leaves us with only a few objective covariatesthat could be used to target: age, gender, high school education or above, desired loansize, and whether that individual has ever pawned before. We call these the “narrow”
covariate set below, to contrast with the full set of survey variables, which we call the“wide” covariate set. Secondly, it will not be attractive for a commercial firm to ask
individuals whether they want to voluntarily accept commitment, only to then force itupon those who say no. So the choice variable itself cannot be used to target other thanin a voluntary program. For this reason, the relevant causal effect for this exercise is theconditional average treatment effect (ATE) rather than the conditional TUT or TOT
as considered above. As shown in Figure OA-18, an estimated 90% of borrowers, with38

a 95% confidence interval of [87%, 92%] have a positive conditional ATE as estimatedfrom the causal forest from Section 6.2 above. In the remainder of this section we ask
how accurately it is possible to identify these borrowers.
Narrow inputs targeting. To consider targeting effectiveness we must begin from anindividual-specific ground truth, which we take from our estimated conditional average[ i ) from the causal forest described in Section 6.2,
treatment effects (CATEs) ATE(X
which used the “wide” set of covariates (wide RF).We then analyze how well we canpredict the losers from paternalism using the “narrow” set of non-manipulable covariates listed above (narrow RF) for the same subset of borrowers. Figure OA-19 shows
the relationship between the CATEs estimated from the RF using the “wide” and “narrow” covariate sets. We can generate substantially less heterogeneity when using thenarrow covariate set, although we still reject the null hypothesis of no treatment effectheterogeneity, following the approach of Chernozhukov et al. (2018).39
Targeting assessment. To more directly investigate our ability to target commitment,
we use two different methods to predict who should be assigned to the commitment arm.
In each, we estimate a classification model using the “narrow” set of covariates to predictwhether the CATE estimated from the wide random forest model (using all available
covariates) is positive. The first method uses a simple logistic regression, while thesecond uses a random forest classification model.40 Each of these methods yields anestimated probability of a positive CATE, allowing us to rank borrowers from highest
to lowest probability. Since 90% of borrowers have a positive CATE as estimated fromthe wide random forest model from above, we consider a decision rule that assigns aborrower to forced commitment if her estimated probability is in the top 90% of thesample.
We compare the in-sample performance of targeting rules against a policy of universal
forced commitment. Table 6 shows error rates for six possible assignment rules: assigning
all borrowers to control, all to treatment (Forcing), the optimal (infeasible) assignment,
narrow RF targeting, Logit targeting, and we evaluate ex-post the voluntary choice,taking the wide RF as the ground truth. While the narrow RF correctly assigns roughly
half of those who do not benefit from commitment to control, it also incorrectly allocates
4.38% of the sample that would have gained from treatment to control. As such, it only
improves the overall correct targeting rate by about half of a percentage point relative
to universal Forcing. The Logit assignment rule is less successful at predicting benefits
and harms, with a higher share of borrowers incorrectly assigned to both treatment andcontrol, meaning that the overall correct targeting rate for the Logit is 5 pp lower than39

See E.1 for details of this method.
We use the STATA package rforest and use the default parameters for the estimation. For further
detail see Schonlau & Zou (2020).
40

39

Table 6: Type I & II errors using targeting narrow rules

Rule% incorrectly assigned to control% incorrectly assigned to treatment

Overall Error Rate

All to control
All to forcing
OptimalNarrow rule (RF)
Narrow rule (Logit)
Allow choice

90.22
0
0
4.38
6.9
93.81

0
9.78
0
5.21
7.76
37.18

90.22
9.78
0
9.59
14.66
87.4

This table reports error rates for six different rules for allocating individuals to commitment. The first row
allocates all borrowers to control. Taking the conditional ATE estimates from the “wide” causal forest, describedin Section 6.2 as ground truth, this results in 90% of individuals losing by not receiving commitment. The second
row assigns all borrowers to forced commitment, yielding error rates that are the exact mirror image of those fromthe first row. The third row considers the infeasible optimum in which each borrower is allocated the “correct”
treatment, treating the estimate from the “wide” causal forest as ground truth. The fourth and fifth rows assign
borrowers to commitment based on a classification model that uses the narrow covariate set to predict an indicator
for whether the “wide” random forest CATE estimate is positive. Row four uses a random forest classification
model while row five uses a simple logistic regression model. In each of these rows, the assignment rule ranksborrowers from highest to lowest by their estimated probability of having a positive CATE. The 90% of borrowers
with the highest estimated probabilities are assigned to treatment, matching the overall rate of positive CATE
estimates from the “wide” RF model. The sixth row gives the percentage of miss-classification that would follow
from the observed choice.

universal Forcing. The underlying cause of the weak performance of targeting is thatthe attribute that predicts gains from forcing (being sure confident and not choosing
the commitment) is largely behavioral and not easily predicted with basic covariates, asseen in Figure 3.
Self-targeting through choice proves to be little better than assigning everyone tothe control condition, given the low take-up rate and the presence of both Type I andType II errors in the choice arm. Fully 87% of individuals in the Choice arm made a“mistake”, weighting the error rates among choosers and non-choosers by their relative
frequency in the Choice arm. The takeaway is that given low take-up, the large fractionof the sample benefiting from commitment, and the weak predictive power of the narrowcovariates, in this case universal paternalism assigning all borrowers to the commitment
contract appears to be an attractive targeting method.

7

Conclusion

This paper makes several contributions. First, it analyzes the large but understudied
industry of pawn loans, and shows that a simple change to contract terms results insubstantial financial savings for pawn borrowers: forced commitment lowers the APR
from 57% to 46%, and reduces the fraction of borrowers who default by 6.6 pp, or15%. That this new contract generated large benefits for borrowers and yet was notoffered, and that a contract that generated default was the industry standard instead,is related to the idea of “veiled paternalism” Laibson (2018), put on its head. In “veiledpaternalism” principals embed forms of commitment into their products but mask this40

fact from consumers who may need but do not desire commitment, in pawn lending,over-collateralization means that lenders stand to make more money from defaulting
borrowers, generating incentives for “veiled non-paternalism,” embedding features thatlead to high borrower costs in non-obvious ways.
Second, our novel “controlled choice” design allows us to go beyond ATE results anddraw an important set of conclusions about the relationship between take-up and heterogeneous treatment effects. In particular, we simultaneously point-identify the impact
of commitment on those who would naturally choose it and those who only experience
commitment when forced. Estimating this later quantity is critical in thinking aboutpaternalism. We find substantial benefits of treatment for non-choosers and no evidenceof selection on gains by borrowers who choose commitment. Given that the rate of voluntary commitment in our sample is only 11%, in order to achieve widespread benefits
in this context compulsory commitment appears to be necessary.
Why do borrowers leave such substantial returns on the table? Our results suggestthat over-optimism is the characteristic most strongly associated with benefiting fromthe commitment despite not having chosen it. Our borrower pool overestimates theirprobability of repayment by more than 50%, and our positive TUT estimate is largely
confined to borrowers who incorrectly believe that they have little chance of defaulting.
Using machine learning methods, we find the benefits of commitment close to universal. The benefits of targeting commitment based on characteristics that lenders canobserve and participants would truthfully reveal are extremely limited, suggesting that
universal commitment is an attractive policy in our empirical setting.
Where lenders have no incentive to engage in veiled paternalism and customers
display inefficiently low demand for it, financial policy regulation may prove an attractive
option. Pawnshops, along with other over-collateralized credit products such as payday
lending, exist in an environment where the lender may desire customers to lose theircollateral on the loan, hurting especially low-income populations who are its main users.
With a now well-established toolkit of regular small payments and incentives delivering
small default rates in microfinance, regulators may fruitfully investigate the possibilityof requiring pawnbrokers to embed features of commitment and regularity into their
repayment structures in more consistent ways.41 An important question for future
research will be the extent to which borrowers are able to learn about the benefits ofcommitment over time, making it so that temporary, lighter-touch policies could achieve
lasting benefits for borrowers. Pawning with commitment may provide an importantmechanism to preserve flexible credit access while allowing more poor borrowers to retain
their assets.
41

If employed at scale in a competitive lending sector this would redistribute welfare from those who
would have repaid (whose interest rates must now rise to cover lower returns from collateral seizure)towards those who would only repay in the presence of commitment. In a setting of lender market power
however, redistribution from lenders to borrowers could occur.

41

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45

The controlled choice design and private paternalism inpawnshop borrowing
Appendix − For Online Publication
Craig McIntosh Isaac Meza Joyce Sadka Enrique Seira Francis J. DiTraglia

Contents
Appendix A.Treatment Explanation Materials and Pictures . . . . . OA - 2
A.1 Materials
OA - 2A.2 Pictures
OA - 3A.3 Survey
OA - 4A.4 More descriptives
OA - 6
Appendix B.Internal Validity . . . . . . . . . . . . . . . . . . . . . . . . . OA - 7
Appendix C.Main treatment effects: Additional material . . . . . . .OA - 11
C.1 Multiple loans
OA - 11
C.2 Censoring
OA - 12
C.3 Robustness accounting for other costs
OA - 16
Appendix D.Alternative explanations . . . . . . . . . . . . . . . . . . .OA - 17
D.1 Learning
OA - 17
D.2 Discount rates
OA - 18
D.3 Sure Confidence
OA - 18
Appendix E. Heterogeneity and Bounds . . . . . . . . . . . . . . . . . .OA - 19
E.1 Testing for heterogeneity
OA - 19
E.2 Bounds, FOSD and Rank Invariance
OA - 20
Appendix F. Derivations for Section 5.3 . . . . . . . . . . . . . . . . . .OA - 21
F.1 Point Identification
OA - 21F.2 Regression-based Estimation of TOT, TUT, ASG, ASL, and ASB
OA - 23
F.3 Inference for ASG, ASB, and ASL
OA - 27
Appendix G.Testable Implications of the Exclusion Restriction . . .OA - 29
Appendix H.Causal Random Forest, HTE, and ‘mistakes’ . . . . . .OA - 32
H.1 Conditional ATE estimates
OA - 32
H.2 Targeting rule comparisons
OA - 33

OA - 1

Appendix A.

A.1

Treatment Explanation Materials and Pictures

Materials
Figure OA-1: Contract Terms Summary

We show a sample receipt that was given to clients that got assigned to the fee-forcing contract (the font andformat were changed to protect Lender’s P identity). We want to highlight the salience of some items. First thetitle clearly indicated which contract the client has (arrow 1). Second, in the case of the fee contract it clearly
indicates that there is a fee for paying late equivalent to 2% of the value of the monthly payment (arrow 2).
Third, there is a calendar for payments clearly specifying the dates and amounts to pay each month.

Figure OA-2: Explanatory Material

Status-quo Contract
Pay when you want (before 3months)Forced-commitment Contract
3 mandatory monthly payments✓ Term: loan must be paid before 3months.

✓ Term: loan must be paid before 3 months.

✓ Amount owed: Loan + Accumulated
interest before loan term ends. Interest
accumulates daily on outstanding amount.

✓ Amount owed: Loan + Accumulated interest
before loan term ends. Interest
accumulates daily on outstanding amount.

✓ Flexibility: you can pay any quantity at
any time before 90 days with noprepayment penalty.

✓ Commitment: to give you structure, eachmonth you must pay at least 1/3 of theloan; that is: 3 equal sized payments. By
missing it you incur in a penalty fee of 2% of
the monthly payment due.

This is a (translated) sample information slide shown to clients. The real ones were twice the size of this figure
and were laminated. Different ones were shown for each treatment arm.

OA - 2

A.2

Pictures
Figure OA-3: Some Pawnshops(a) Appraiser/tellers inside a pawnshop(b) Pawnshop(d) Lost pawns which are for sale(c) Pawnshop

This figure shows pictures of pawnshops in Mexico city. They do not necessarily coincide with Lender P for
confidentiality.

Figure OA-4: Gold buyers next to pawnshops(b) Gold buyer next to pawnshop 1(a) Gold buyer next to pawnshop 1

This figure shows pictures of gold buyers next to pawnshops in Mexico city. They do not necessarily coincidewith Lender P for confidentiality.

OA - 3

A.3

SurveyWe now present analysis of the extent to which the survey-responding sample is representative and balanced. Table OA-3 presents information about survey non-response.
Panel A is a balance table that compares loan amount and day of the week across treatment arms for the subset of borrowers who responded to at least one survey question.
The p-values in the fourth column are for the F-test of no difference of means acrosstreatment arms. Panel B presents response-rates by question for each arm of the experiment, along with p-values for the F-test of no difference in question-specific response
rates across treatment arms. This panel uses data from participants who answered atleast one survey question and went on to pawn on the same day as their survey response.
From the table, we see that loan amount and weekday are balanced across treatment
arms among survey respondents and that response rates are likewise stable across treatment arms. Table OA-4 shows how the estimated TUT effect changes if we restrict ourestimation sample based on survey response. The first row of the table presents TUT
results for the financial cost outcome, while the second presents corresponding results
for the APR outcome. In each row, column (1) presents the full-sample TUT estimate
and standard error while the remaining columns restrict the sample to borrowers who
answered a particular survey question or set of questions. For example, column (4)presents results for borrowers who answered the two questions needed to compute ourmeasure of “present bias” discussed in the next paragraph, while column (9) present
results restricted to participants who disclosed their sex. As seen from the table, ourTUT estimates are quite stable across sub-samples defined by survey response. In eachcase they are positive and of the same magnitude as the corresponding full-sample estimate, although statistical significance varies depending on the size of the corresponding
sub-sample. For these reasons, we are comfortable relying on data for survey respondents in the empirical exercises that follow. In exercises that rely on a single survey
question, we use data for every borrower who answered that question. In the random
forest exercises described below, we use data for every borrower who answered at least
one survey question.

OA - 4

Table OA-1: Baseline survey questions (translated to English)
Baseline Survey
1
2
3
4
5
6
7
8
9
10
11
12

13
14
15
16
17

18
19
20
21
22
23
24
25
26
27
28
29
30

Your pawn was:(a) Inherite, (b) a gift, (c) bought by me, (d) lend to me, (e) otherMark with an ”X” in the line below how likely is that you recover your pawn.
Where 0 is impossible and 100 is completely certain
pesos
How much do you think the item you plan to pawn is worth?
Gender
Age
Civil Status(a) married, (b) single, (c) divorced, (d) widowed
Work status(a) employed, (b) own business, (c) houseshores, (d) don’t work, (e) retired, (f) study
Education(a) no formal education, (b) primary, (c) middle school, (d) highschool, (e) more than highschool
In the last month, did a friend or family member asked you for money?
(a) yes (b) no
What would you like to have: 100 pesos tomorrow or 150 pesos in one month?
How often do you feel stressed by your economic situation?
(a) always, (b) very often, (c) sometimes, (d) neverWhat is the main reason you want to pawn?
(a) Need the money because somebody in my family lost his/her job(b) Need the money to pay for a sickness in the family(c) Need the money for an urgent expense(d) Need the money for some non urgent expense.
How stressed do you feel from the situation that led to to pawn?
(a) very stressed, (b) somwhat stressed, (c) a little stressed, (d) not stressedsituation
In 3 months, I expect to have a(a) better, (b) similar, (c) worse
Have you panwned before?
(a) yes (b) no
How many times have you pawned on a Lender P branch?
(a) NO(b) 1-2 times(c) 3-5 times(d) More than 5
If you are saving money and a family member wants to use it for something(a) I would only give him the money for an urgent expenze(b) I would give him the money even if it was not an urgent expense(c) I would not give him/her the money regardless(d) No one would ask me for my money
Do you make an expenses budget for the month ahead of time?
(a) always, (b) very often, (c) sometimes, (d) neverDo you have other items you could pawn?
(a) yes (b) no
Do you have savings?
(a) yes (b) no
Do you participate in a ROSCA?
(a) yes (b) no
Is it common that family or friends ask for money?
(a) yes (b) no
How much did you spend to come to the branch today? $pesos
How much time does it usually take to come to this branch?
How much does your family spend in a normal week? $pesos
How much do you manage to save in a normal week? $pesos
Does it happen to you that you spend more than you wanted because you fall into temptation?
(a) never, (b) almost never, (c) sometimes, (d) very often
In the last 6 months, has it happened that at some point you lacked money to pay(a) rent? (b) food (c)food (d) medicine (e) electricity (f) heating (g) telephone (i) water
What would you like to have: 100 pesos in 3 months or 150 pesos in four months?
Would you like to receive (free) reminders for upcomming payments?
(a) yes (b) no

Translation of the baseline questionnaire.

OA - 5

A.4

More descriptives
Figure OA-5: Financial cost.
50

80

40

Percent

Percent

60

30

20

40

20
10

0

0
0

1000

2000

3000

4000

5000

0

100

200

Financial Cost
Default

300

400

APR %

Recovery

Default(a)

Recovery(b)

Panel (a) plots a histogram of this financial cost in pesos for all loans in the experiment, stratified by whether weobserved that they ended in default or recovery of the pawn. Panel (b) shows the analogous histogram for the
APR. We see that borrowers who default incur higher costs; part of this is mechanical as losing their collateralis part of the cost. Most of the APR costs indeed come from clients who do not recover their pawn.

Figure OA-6: Behavior of borrowers who lost their pawn(a) Elapsed days to first payment (b) Elapsed days to last payment
40

60

30

Percent

Percent

40

20

20
10

0

20

40

60

80

100

0

120

0

100

Elapsed days(c) Payments as % of loan
80

60

60

Percent

Percent300(d) Number of payments

80

40

20

0

200

Elapsed days to last payment

40

20

0

.5

1

1.5

0

Percentage of payment (total)

0

1

2

3

4

5

Number of payment

This figure provides more details on the behavior of clients who were assigned to the control group and did notrecover their pawn. Panel (a) shows a histogram of days elapsed from the pawn to the first payment, while panel(b) displays a histogram of days elapsed until the last payment. Some borrowers make payments after day 105,
the end of the grace period: if they pay all interest owed, they can “restart” the loan. This amounts to starting a
new loan with the same conditions and same pawn. Panel (c) shows a histogram of the fraction of the loan paid,
while panel (d) presents a barplot of the number of times that borrowers went to the branch to make payments.

OA - 6

Table OA-2: Limited and balanced attrition
Commitment arms
Control

ForcedChoicep-value

31
(5.5)
27

31
(5.4)
28

36
(6.4)
31

0.21

21
(3.3)
19

23
(3.8)
21

25
(4.3)
21

0.24

Obs

101

97

129

Ended up pawning

0.98(0.01)
0.79(0.02)

0.97(0.01)
0.76(0.02)

0.97(0.01)
0.77(0.02)

1770

1954

2580

Number of branch-day pawns
medianNumber of branch-day borrowers
medianSurvey response rate
Obs

0.15

0.46

0.62
0.62

Each row in this table corresponds to a regression. The dependent variables are: the number of pawns-loans
originated per day per branch, the number of borrowers per day-branch, a variable indicating whether a person
who answered the baseline survey (before knowing contract terms) ended up pawning, and an indicator of whether
the person that obtained the loan answered the baseline survey. Each dependent variable is regressed in a
multivariate OLS regression against the experimental arms indicators (control, forced commitment, choice). The
table reports the coefficients on each of these indicators, as well as the p-value of an F-test of the null hypothesisof equality of the three coefficients. Figure OA-7, in the appendix shows a box-plot of the first two variables,
showing the distribution across arms is balanced.

Appendix B.

Internal Validity

If potential borrowers disliked being forced into a commitment contract, we would expect
a lower number of pawns on branch days where only the commitment contract is available
compared to control days. Table OA-2 shows that this is not the case. There is nodifference at all between the Control and Forced Commitment arm in terms of thenumber of pawns per branch-day. Although we cannot reject equality across the threearms (p-value=0.21), the Choice arm appears to have a somewhat larger number ofborrowers than the Control and Forced arms.42 This seems to be due to sampling
variability. The differences across arms are smaller when we look at medians, or when
we look at the number of borrowers pawning (some borrowers pawn more than one
piece). Figure OA-7 shows that full distribution of loans per day is very similar acrosstreatment arms. The only noticeable difference is that the choice arm has a few morepositive outliers.43
The bottom panel of Table OA-2 shows balance in a more focused way, given thatthe surveys were conducted prior to the revelation of treatment status. We find that in
no arm did more than three percent of individuals who responded to the survey go on torefuse loans. That is, the overwhelming marjority of potential borrowers did not leave
the branch after learning which contract was on offer. Moreover, the extremely small
fraction that did leave is balanced across arms. Therefore it appears that the treatments
have not induced any endogenous shifts in the composition of borrowers.
42

p-value=0.23 and 0.12 respectively.
If we winzorize at the 90th percentile, the mean number of branch-day pawns becomes identicalacross arms.
43

OA - 7

A less critical form of attrition is differential refusal to answer the survey questions.
The survey was conducted before treatment status was revealed, and we observe loan
outcomes regardless of whether the survey was conducted. Our core experimental estimates do not use the survey data as covariates, but the analysis in Section 6 is restricted
to the subset of borrowers who answered at least some survey questions. The bottom
row of Table OA-2 shows that the survey response rate is broadly similar across arms(about 78 percent).
Figure OA-7: Box-plot across arms(a) Number of pawns(b) Number of borrowers

100

Number of pawns

Number of pawns

100

50

0

50

0
Control

Forced Commitment Choice commitment

Control

Forced Commitment Choice commitment

This figure presents box-plot for the number of pawns and borrowers per branch-day across different arms. The
solid black line represent the median, while the gray line represent the mean. The dots on top of the box-plot
represent an implicit CDF.

OA - 8

Table OA-3: Balance conditional on survey response and question-by-question response
rates by treatment arm
Commitment arms
Control

ForcedChoicep-value

Panel A : Administrative Data (conditional on survey)
Loan amount
Weekday
Obs

2199
(86)
0.88
(0.045)

2196
(106)
0.89
(0.038)

2216
(81)
0.85
(0.045)

1386

1469

1982

0.98
0.8

Panel B : Survey Data - response rate
Subjective value
Trouble paying bills
Present bias
Makes budget
Subj. pr. of recovery
Pawn before
Age
Woman
+ High-school
Obs

0.73
(0.022)0.49(0.023)0.43(0.02)
0.55(0.023)0.74(0.024)0.55(0.023)0.54(0.023)0.58(0.025)0.54(0.025)0.69(0.024)0.48(0.022)0.44(0.02)
0.56(0.023)0.72(0.025)0.57(0.024)0.55(0.023)0.59(0.024)0.55(0.025)0.71(0.024)0.44(0.022)0.39(0.02)
0.53(0.019)0.74(0.025)0.53(0.02)
0.52(0.018)0.58(0.02)
0.51(0.019)

1386

1469

1982

0.39
0.29
0.17
0.56
0.71
0.57
0.59
0.93
0.39

Panel A of this table presents the same information as Panel A of Table 1, but restricts attention to the subsample
of borrowers who answered at least one question in our baseline survey. Conditional on survey response, loan
amount and weekday are balanced across treatment arms. Panel B presents response rates to each individual
survey question across treatment arms, along with p-values for the F-test of no difference in response rates acrosssurvey arms. This panel uses data for borrowers who pawned on the same day as their survey response.

OA - 9OA - 10

6304

4465

187.6***(58.1)(12)(11)

191.5***(50.8)

10.6***(2.39)

10.6***(2.47)

(2)

(1)

2948

147.0**(67.8)(13)

11.6***(2.64)(3)

Trouble paying bills

2613

187.6**(82.0)(14)

12.4***(2.70)(4)

Present bias

3433

157.6**(69.9)(15)

10.7***(2.72)(5)

Makes budget

4625

183.1***(60.8)(16)

11.4***(2.32)(6)

Subj. pr. of recovery

3468

144.1**(68.7)(17)

10.8***(2.71)(7)

Pawn before

3393

163.4**(74.6)(18)

11.3***(2.94)

(8)

Age

3677

140.5**(69.2)(19)

11.7***(2.95)

(9)

Woman

3352

129.0*(72.5)(20)

11.0***(2.84)(10)+ High-schoolSome borrowers did not respond to our survey; others only completed part of the survey. This table computes the TUT effect for a number of sub-groups by survey response, andcompares them against the overall TUT effect. The top panel uses financial cost as the outcome variable, while the bottom panel uses APR. Each group is defined by the borrowers
who responded to a particular subset of the survey questions. For example, column (4) computes TUT effects for the subgroup of borrowers who responded to the two questions
needed to compute our measure of present bias, while column (8) computes the TUT for the subgroup of borrowers who provided their age. The bottom row of the table counts
the number of borrowers in each category. TUT estimates are quite stable across sub-groups and generally similar to the full-sample estimates. Because standard errors increaseas sample size falls, some of the sub-group estimates are not statistically significant.

Observations

FC benefit TuT

Apr % benefit

Subjective value

Full-sample

Table OA-4: Survey Non-response: TUT estimates for respondents to each survey question.

OA - 11

6304
0.013
942.4

6304
0.031
0.57

6304
0.019
0.43

0.14***(0.025)0.0094(0.022)(3)

Recovery

6304
0.013
0.44

-0.066***(0.023)-0.023(0.021)(4)

Default

8519
0.016
907.9

-176.8***(42.8)-33.3(43.9)

(5)

FC

8519
0.031
0.54

-0.080***(0.017)0.0037(0.016)

(6)

APR

8519
0.018
0.46

0.099***(0.021)0.00054(0.018)(7)

Recovery

8519
0.010
0.42

-0.033(0.020)-0.0042(0.018)(8)

Default

Multiple visits - multiple treatments

8813
0.016
907.9

-161.5***(38.9)-32.3(40.6)

(9)

FC

8813
0.030
0.55

-0.087***(0.015)-0.017(0.014)

(10)

APR

8813
0.020
0.44

0.11***(0.021)0.029(0.018)(11)

RecoveryFirst treatment (ITT)

8813
0.015
0.44

-0.052***(0.019)-0.031*(0.018)(12)

Default

This table provides robustness for our main results for different ways to handling the multiplicity of loans. Columns 1-4 repeat the main analysis of financial cost and APR using
the baseline approach from our main results,i.e. it only considers the first visit, while allowing multiple loans for the same-day. Columns 5-8 considers all loans including dummies
for the order of pawns for an individual, essentially making the identification within-order. Columns 9-12 pursue the ITT strategy of always assigning the first treatment status toall subsequent pawns. The core treatment effects are robust to any of these ways of handling repeat pawning.

An additional empirical issue generated by repeat pawning is the question of how to handle the treatment status of those who take multiple loans within the experiment. 43%
of borrowers take more than one loan within the study period, and 19% are assigned multiple treatment statuses on their different loans. The issue of sequential endogenous
treatments has been extensively studied in the context of school lotteries, where the convention is to use the treatment status from the first exposure (ITT) (Cullen et al., 2006;
Abdulkadiroğlu et al., 2011).

Observations
R-sq
Control Mean

Choice Commitment-0.11***(0.019)-0.0086(0.019)(2)(1)-204.0***(48.1)-38.9(49.8)APR

FCFirst visit (Baseline approach)

Table OA-5: Multiple-loans robustness check

Main treatment effects: Additional material

Multiple loans

Forced Commitment

C.1

Appendix C.

Figure OA-8: Determinants of choice
FamilyFam asks money
Common asks money

IncomeTrouble paying bills
Savings

Self Control

Present bias
Sure confidence
Impatience
Makes budget
TemptedWant SMS Reminder

Experience

Pawn before
Rosca participant
Prob recovery

Other

Age
FemaleMore high school
Stressed< med transport time
< med transport cost
-.2

-.1

0
Bivariate.1.2

Multivariate

The above figure shows the determinants in a bivariate and multivariate OLS regression of choosing commitment.
Choice commitment is a binary variable equal to one, whenever subjects choose the forced commitment contract
in the choice arm.

Figure OA-9: Histogram of payments(b) Forced commitment(c) Choice commitment

500

500

400

400

400

300

300

300

Count

500

Count

Count

(a) Status-quo

200

200

200

100

100

100

0

0
0

30

60

90

120

0
0

30

60

90

120

0

30

60

90

120

This figure shows the schedule of payments for each treatment arm. In other words it records the time after theloan origination when the borrower makes a payment toward recovery of the pawn. We can see that for both
the Forced commitment and Choice commitment arm, payments are bunching at the 30 and 60 days, while most
payments are done around the due date of the loan (90 days).

C.2

CensoringSome loans in our sample are “censored” in that they continue beyond our observation
period. For these loans, we do not know whether the borrower ultimately defaulted
or recovered her pawn. In this appendix, we show that our main results are robust todifferent ways of addressing censoring.
Our main results, presented above, make no assumption on the default/recovery
status of this loans. However, we compute the Financial Cost & APR considering all
the payments done so far. We now consider some alternative approaches.
One way of considering the effect that this issue could have on our results is to makeextreme assumptions about the outcome of these loans in the treatment and control so as
to bound the possible influence of censoring. In Table OA-6 we compare the Forced andControl arms, making the bracketing assumptions about repayment on censored loans.
Panel A assumes all censored loans are repaid, and Panel D that all default. Because
OA - 12

forced commitment causes borrowers to make payments earlier than they otherwise
would have, In Panel A we make a conservative assumption. To see why, suppose forthe sake of argument that commitment affects payment timing, but does not not default.
In other words, suppose that treatment makes censoring less likely but has no effect on
uncensored outcomes. If we were to treat all outstanding loans as defaults–the opposite
of our convention–this would artificially inflate the rate of default among control loans
relative to treatment loans.
Panel B provides the lower bound for the treatment effect by assuming censoredcontrol loans are always repaid and treatment loans never are, and Panel C the upper bound by making the reverse assumption. Comfortingly, even with these extreme
assumptions the significance on the main treatment effects never flips and treatment
effects on financial cost and interests payments remain negative and significant in all
scenarios. So there appears to be no scope for the censoring issue to overturn our main
results.
Finally, Panel E of this table conducts a lasso logit prediction model that uses all of
the available information on loans that were completed to predict the outcome of loansthat were not. This is a best guess of the outcome on censored loans. Using this prediction, we replicate the main experimental results and find that the treatment effect onfinancial cost increases from -204 (main results) to -264 (censored loans predicted), and
the APR from -11% to -17%. Hence, while the censoring issue does have a substantial
influence on the magnitude of our estimated treatment effects, these checks confirm thata) the core results are robust to censoring, and b) the headline approach that we taketo the issue is conservative and is likely understating the true magnitude of impacts.
Table OA-6: Bounding censoring

FC

Interest pymnt
Panel A :Forced commitment

Observations
R-sq
Control Mean

Observations
R-sq
Control Mean

Lost pawn value

Default

Control = 0

Forced Commitment = 0

APR

(1)

(2)

(3)

(4)

(5)

(6)

-236.0***(48.1)-191.7***(37.6)-0.63(3.01)-75.9**(30.5)-0.064***(0.023)-0.14***(0.022)

3724
0.016
989.9

3724
0.025
593.4

3724
0.004
5.96

3724
0.012
396.5

3724
0.019
0.44

3724
0.043
0.61

Panel B :Forced commitment

Principal pymnt

Control = 0

Forced Commitment = 1

(7)

(8)

(9)

(10)

(11)

(12)

-191.2***(49.7)-207.7***(37.4)

1.17(3.45)-15.1(31.2)

0.0083(0.024)-0.076***(0.026)

3724
0.013
989.9

3724
0.026
593.4

3724
0.004
5.96

3724
0.009
396.5

3724
0.014
0.44

3724
0.023
0.61

OA - 13

FC

Interest pymnt
Panel C :Forced commitment

Observations
R-sq
Control Mean

Observations
R-sq
Control Mean

Choice commitment

Observations
R-sq
Control Mean

Default

APR

(14)

(15)

(16)

(17)

(18)

-319.0***(50.9)-140.4***(34.1)-2.33(3.16)-210.3***(30.3)-0.21***(0.023)-0.24***(0.027)3724
0.021
1069.2

3724
0.020
545.9

3724
0.004
7.69

3724
0.021
523.3

3724
0.053
0.57

3724
0.061
0.70

Control = 1

Forced Commitment = 1

(19)

(20)

(21)

(22)

(23)

(24)

-274.2***(52.5)-156.3***(33.8)-0.53(3.58)-149.6***(31.1)-0.13***(0.024)-0.17***(0.030)3724
0.017
1069.2

3724
0.021
545.9

3724
0.003
7.69

3724
0.013
523.3

3724
0.028
0.57

3724
0.032
0.70

Panel E :Forced commitment

Lost pawn value

Forced Commitment = 0(13)

Panel D :Forced commitment

Principal pymnt
Control = 1

Prediction with lasso-logit model

(25)

(26)

(27)

(28)

(29)

(30)

-264.9***(53.8)-42.4(56.9)-169.6***(37.2)-29.1(41.8)-1.43(3.52)-2.66(3.24)-127.4***(33.1)-14.6(34.9)-0.12***(0.025)-0.017(0.024)-0.17***(0.028)0.0026(0.029)6304
0.018
1034.5

6304
0.022
563.4

6304
0.002
7.69

6304
0.010
471.2

6304
0.016
0.52

6304
0.042
0.66

Given the censored loans, i.e. loans that have not finished by the end of the observation period, we estimate‘a la Manski’ bounds for these loans, meaning that we impute all loans to either default= 1 or recovery= 0
depending on the treatment arm. Different panels perform different imputations for the censored loans for all
possible combinations for the imputation, and computes the ATE for the same outcomes of Table 2. Panel A,
for instance, assumes that all outstanding loans are fully payed. Panel B is the most conservative imputation
since it assumes all outstanding loans in the control arm are payed, while all the outstanding loans in the forced
commitment arm default. Panel C, on the other hand, is the most optimistic scenario opposite to that of Panel
B. Panel D assumes all remaining loans default. The last panel makes the imputation to the censored loans
according to the best prediction using a piecewise lasso logit model for default. In concrete, we build two logit
models with lasso regularization, depending whether the loan duration is less than 220 days (two cycles) or morethan 220 days. For prediction we use the former whenever the last recorded payment was done within 220 days,
and the latter otherwise. Both models includes loan characteristics (loan size, branch), and payment behavior(loan duration so far, days to first payment, % of first payment, % of payments at 30, 60, 90, and 105 days, and% of interest payed at 105 days), but the latter model also includes % of payments at 150, 180, and 210 days.
This predictive model achieves an accuracy rate of 92% both in-sample and out-of-sample.
Note that in all panels we maintain significant results for Financial Cost as dependent variable, while only in themost conservative scenario (Panel B) we lose significance for the APR outcome.

OA - 14

Figure OA-10: Interpolation on bounding censoring for Default% imputation default T=1

100

D

B

80

60

40

20

0

C

A

0

20

40

60

80

100

% imputation C=0
10%

5%

1%

The next figure aims to answer the following question: For how many loans in the control arm can we impute
recovery, and for how many in the treatment arm can we impute default and still have significance? This figure
shows exactly the boundary separating significance when we vary the percentage of imputed censored loans withrecovery and default respectively for control and treatment. Each corner in the square will correspond to oneof the panels from the Table OA-6. For instance, the origin is the best-case scenario (Panel C) and the point(100,100) (Panel B) is the worst-case scenario. Thus we can think of this graph as an ‘interpolation’ from thefour extreme cases. The ‘x’ indicates the proportions imputed by the lasso logit model, and the different lines
correspond to setting different significance levels. We do not include the plot for APR nor financial cost, sincefor any imputation we still have significant results.

Figure OA-11: Survival graph(b) Recovery(a) Ended contract
100

60

Percentage %Percentage (%)

80

60

40

40

20

20

0

0
0

30

60

90

180

270

320

0

30

60

Elapsed days

Status-quo

Forced commitment

90

180

270

320

Elapsed days to recovery

Choice commitment

Status-quo

Forced commitment

Choice commitment

This Figure shows the CDF of loan completion either default or recovery in Panel (a), or loan recovery in Panel(b), by the number of days since first pawn.

OA - 15

Figure OA-12: % of payment over time(a) Unconditional(b) Conditional on default

80

10β105 = 16.59
σ105 = 2.98% of payment% of payment60

β90 = 18.25
σ90 = 2.5

40

6

4

β105 = -2.83
σ105 = .9

β60 = 11.67
σ60 = 1.620

2β30 = 7.48
σ30 = 1.1

0

0
0

30

60

90

180

270

320

0

30

60

90

180

Elapsed days
Status-quo

Forced commitment

270

320

Elapsed days
Choice commitment

Status-quo

Forced commitment

Choice commitment

This Figure shows the accumulated percentage of recovery in time by treatment arm.

C.3

Robustness accounting for other costs
Table OA-7: Effects on more comprehensive cost measures

Forced commitment
Choice comitment

Observations
R-squared
Control Mean

Forced commitment
Choice comitment

Observations
R-squared
Control MeanFC

FC (subj.value)

FC + tc

FC - interest

FC (subj.value) + tc - int

(1)

(2)

(3)

(4)

(5)

-204.0***(48.1)-38.9(49.8)-299.9***(83.3)-56.4(83.5)-207.7***(49.0)-32.6(50.9)-98.5***(36.7)-30.7(39.2)-146.3**(72.8)-25.3(74.4)

6304
0.013
942.4

6304
0.009
1389.96304
0.014
1026.1

6304
0.005
480.7

6304
0.006
927.7

APR

APR (subj.value)

APR + tc

APR - interest

APR (subj.value) + tc - int

(6)

(7)

(8)

(9)

(10)

-0.11***(0.019)-0.0086(0.019)-0.22***(0.051)-0.053(0.045)-0.13***(0.028)-0.0035(0.028)-0.062***(0.019)-0.031*(0.018)-0.097**(0.044)-0.043(0.040)

6304
0.031
0.57

6304
0.011
1.12

6304
0.027
0.72

6304
0.008
0.31

6304
0.007
0.84

This table augments the measure of financial cost presented in Table 2 with measures of transaction costs,
subjective costs, and adjustments for liquidity costs. Panel A reports financial cost in pesos, while Panel B shows
APR. Columns (1) and (6) replicate our previous results for comparability. Columns (2) and (7) of Table OA-7
use the subjective value of the pawn reported by the borrower rather than its appraised value. Columns (3) and(8) adjust for self-reported transport costs per visit plus an entire day’s wage, both multiplied by the number ofvisits that each individual made.44 Columns (4) and (9) adjust to consider the liquidity cost. Finally, columns(5) and (10) include all three changes together. The main takeaway from the table is that results are quite robust
to including a much expanded measure of costs. Each regression includes branch and day-of-week FE. Standard
errors are clustered at the branch-day level.

OA - 16

Appendix D.
D.1

Alternative explanations

Learning

Table OA-8 presents information about borrowers’ future pawning behavior as a functionof treatment assignment. Column (1) considers the 228 clients who returned only asecond time to pawn again at a day/branch that was randomly assigned to the choicearm. Each of the two rows in this column presents a difference of mean commitment takeup rates, and associated standard error. The first row compares those who were initiallyassigned to forced commitment against those where were assigned to control; the second
row compares those who were initially assigned to the choice commitment arm to those
who were assigned to the other two arms. In each case, there is no statistically discernible
difference in the rates of commitment take-up. Granted, this is a selected sample because
the decision to pawn again is potentially endogenous to the initial treatment allocation.
For this reason, Column (2) considers the full sample of 4441 borrowers by re-defining
the outcome variable to be an indicator for returning to pawn again at a branch/day
when commitment was offered and choosing commitment. This composite outcome
variable is not subject to the sample selection problem (although it is directly driven
by the decision to repeat borrow). The comparison in the two rows remains the same:forced commitment versus control in row one and choice commitment versus forced arms
in row two. Again, there is no statistically discernible difference in commitment take-up
rates in either row. While these exercises cannot completely exclude the possibility thatlearning plays a role, they provide no indication that the lack of voluntary compliance
is simply a matter of inexperience with commitment.
Table OA-8: Effect of Prior Assignment on Subsequent Choicet
Forced commitment (ATE)
Choice commitment (ITT)

Observations
R-sq
DepVarMean

Choose commitment in t + 1

Ever choose commitment in t + 1

(1)

(2)

-0.0047(0.048)0.034(0.057)0.00014(0.0027)0.0015(0.0030)

228
0.004
0.092

4441
0.000
0.0047

Column (1) reports results for the 228 borrowers who returned to pawn again at a day/branch that was randomly
assigned to the choice arm, enabling us to observe whether they chose commitment or the status quo contract.
Each row presents a difference in mean commitment take-up rates and associated standard errors. The firstrow (ATE) compares borrowers who were initially assigned to forced commitment against those were assigned
to the control condition. The second row (ITT) compares borrowers who were initially assigned to the choicecommitment condition to those who were not. Whereas column (1) conditions on the (endogenously) selected
sample of borrowers who return to pawn again, column (2) considers the full sample by re-defining the “outcome”
to be an indicator for whether a borrower pawned again on a day when choice was offered and chose commitment.

OA - 17

D.2

Discount rates
Figure OA-13: Financial benefit TUT effect for different discount rates

FC Benefit (TuT)

300

200

100

0

0

1000

2000

3000

4000

5000

Annual discount rate %This Figure re-estimates the treatment on the untreated (TUT) effect from Table 5, introducing a daily discountfactor in the definition of financial benefit. The discount factor reflects time preference, i.e. the fact that payments
made in the present are more costly for the borrower. At a given annual discount rate in percentage points (xaxis) the solid line gives the adjusted TUT and the shaded regions 90% & 95% confidence bands. A discountfactor of one corresponds to the estimate from Table 5. For higher discount rates, the adjusted financial cost
will be higher, so the financial cost savings will be lower. As seen from the figure, borrowers would need to face
unrealistically large discount rates to reverse our headline result of a large, positive, and statistically significant
TUT effect.

D.3

Sure Confidence
Figure OA-14: Determinants sure confidence
FamilyFam asks money
Common asks money

IncomeTrouble paying bills
Savings

Self Control

Present bias
Impatience
Makes budget
TemptedWant SMS Reminder

Experience

Pawn before
Rosca participant

Other

Age
FemaleMore high school
Stressed< med transport time
< med transport cost
-.3

-.2

-.1

0

Bivariate

Multivariate.1.2

The above figure shows the determinants in a bivariate and multivariate OLS regression of sure confidence among
the non-choosers. Sure confidence is a binary variable defined to be one when people report a 100% probabilityof recovery.

OA - 18

Appendix E.
E.1

Heterogeneity and Bounds

Testing for heterogeneity

If the treatment effects Yi1 − Yi0 are constant across i, then we must have
ATE(Xi ) ≡ E[Yi1 − Yi0 |Xi ] = E[Yi1 − Yi0 ] ≡ ATE
for any covariates Xi that vary across i. If, on the other hand, ATE(Xi ) can be predictedusing some scalar function τ (·) of Xi , then the average treatment effect function is notconstant so there must be treatment effect heterogeneity.
We operationalize this idea using a two-step approach proposed by Chernozhukov
et al. (2018). We begin by randomly dividing the participants in the forced arms of theexperiment (Zi ̸= 2) into two groups: a training set and a test set. These sets are constructed to ensure that all observations from a given branch-day cluster are allocated tothe same set. This avoids inferential problems that could arise from correlated unobservables within clusters. In the first step, we apply the generalized random forest approachof Athey et al. (2019) to the training set to estimate two proxy predictors: ψ(·|Training)approximates the untreated potential outcome function, E[Yi0 |Xi ] = E[Yi |Zi = 0, Xi ],while τ (·|Training), approximates the ATE function
ATE(Xi ) = E[Yi |Zi = 1, Xi ] − E[Yi |Zi = 0, Xi ].
The proxy predictors need not be unbiased or even consistent estimators of the functions
they aim to approximate: the goal of this exercise is merely to find a scalar function of
Xi that accurately predicts ATE(Xi ). In the second step we fit a linear regression model
to data from the training set using regressors constructed from the proxy functions
ψ(·|Training) and τ (·|Training) constructed in the first step. In particular, we estimate
Yi = α0 + α1 ψi + β1 (Zi − E[Zi ]) + β2 (Zi − E[Zi ])(τi − E[τi ]) + ϵi(12)where ψi ≡ ψ(Xi |Training) and τi ≡ τ (Xi |Training).45 As shown by Chernozhukov
et al. (2018), the coefficients β1 and β2 from (12) identify the best linear predictor of theconditional ATE based on τ (·|Training), namely
β1 = E[ATE(Xi )] = ATE,

β2 =Cov[ATE(Xi ), τi ].
Var(τi )If treatment effects are homogeneous we must have β2 = 0. Rejecting this hypothesis establishes that τi predicts ATE(Xi ) and hence that ∆i varies. Since τi and ψido not depend on the test set, inference for the regression in (12) is straightforward
conditional on the Training/Test split. Our estimate for β2 is 2.56 with a one-sided
heteroskedasticity-robust (HC3) standard error of 0.43. Thus we easily reject the null
hypothesis of homogeneous treatment effects.

45This is a slightly simpler regression than the one proposed in equation (3.1) of Chernozhukov et al.
(2018), which involves propensity score weights. Because the random assignment of Z in our experimentdoes not condition on X, the propensity score weights in our case are constant over X and hence dropout.

OA - 19

E.2

Bounds, FOSD and Rank Invariance
Figure OA-15: Fan & Park bounds for benefit in APR%(a) APR
1

.8

.6

.4

.2

0
-4

-2

0

2

4

∆ : Treatment effectLower boundUpper boundThis figure depicts the Fan & Park (2010) bounds on the distribution F∆ of individual treatment effects ∆ ≡(Y1 − Y0 ), described in Section 5.1, for the APR outcome. The dark red curve and light red shaded region givethe estimated upper bound function F for F∆ and associated (pointwise) 95% confidence interval. The dark blue
curve and light blue shaded region give the estimated lower bound function F for F∆ and associated (pointwise)
95% confidence interval. Confidence intervals are computed using the asymptotic distribution for the bounds.
See Fan & Park (2010) for details. The bounds are pointwise sharp: at any specified value of δ the bounds
F (δ) ≤ F∆ (δ) ≤ F (δ) cannot be improved without imposing additional assumptions. Evaluating the bounds at
δ = 0, we see that between 23% and 97% of borrowers have a positive individual treatment effect. This is greaterthan the share of borrowers who chose commitment: 11%.

Figure OA-16: Empirical CDF: Forced commitment vs Control FOSF(a) APR benefit(b) Financial benefit

1

1

.8

.8

.6

.6

.4

.4

.2

.2

0

0
-1.5

-1
Forced commitment-.5
Control

0-4000

Control-Forced-3000
Forced commitment-2000
Control-1000

0Control-Forced

This figure plots the empirical CDF of experimental outcomes separately for the control (status quo) in dashes,and forced commitment contracts (solid). In panel (a), the outcome is APR benefit; in panel (b) the outcome is
Financial benefit. The empirical CDF under forced commitment first-order stochastically dominates the empirical
CDF under the status quo. This can be seen by examining the dotted line, which shows the difference (Control −Commitment).

OA - 20

Figure OA-17: Distribution of treatment effects under rank invariance.
(b) Financial benefit
1

.8

.8

∫1(F1 (u)-F0 (u)≤δ)du

1

.4

-1

-1

.6

-1

.6

-1

∫1(F1 (u)-F0 (u)≤δ)du(a) APR benefit

.2

.4

.2

0

0
-.1

0

.1

.2

.3

.4

0

200

δ

400

600

800

δ

This figure shows the CDF of individual treatment effects under the assumption of rank invariance, computed
from
Z
1

F∆ (δ) =1{F1−1 (u) − F0−1 (u) ≤ δ} du

0where F1−1 and F0−1 are the quantile functions of Y1 and Y0 .

Appendix F.

Derivations for Section 5.3

This appendix provides proofs of the results described in Section 5.3, using the notation
and assumptions described in Section 5.2. To simplify the presentation, we omit i
subscripts throughout this section. We also use the shorthand Z0 ≡ 1(Z = 0), Z1 ≡1(Z = 1), and Z2 ≡ 1(Z = 2). For convenience, the following assumption collects our
exclusion restriction and the key features of the constrained choice design.
Assumption 1.
(i) Z is independent of (Y0 , Y1 , C)(ii) D = 1(Z ̸= 2)Z + 1(Z = 2)C(iii) Y = 1(Z = 0)Y0 + 1(Z = 1)Y1 + 1(Z = 2)[(1 − C)Y0 + CY1 ]F.1

Point Identification

We first show that the TOT, TUT, ASB, and ASL effects are point identified under
the constrained choice design. It follows that the ASG effect, (TOT − TUT), is likewise
point identified.
Lemma 1. Under Assumption 1,(i) E(D|Z = 2) = P(C = 1)(ii) E(Y |Z = 0) = E(Y0 )(iii) E(Y |Z = 1) = E(Y1 )(iv) E(Y |D = 0, Z = 2) = E(Y0 |C = 0)
OA - 21(v) E(Y |D = 1, Z = 2) = E(Y1 |C = 1).
Proof. Part (i) follows because Z = 2 implies D = C and Z is independent of C. Parts(ii) and (iii) follow similarly: given Z = 0 we have Y = Y0 , given Z = 1 we have Y = Y1 ,and Z is independent of (Y0 , Y1 ). For parts (iv) and (v), first note that Assumption 1(iii) implies that Z is conditionally independent of (Y0 , Y1 ) given C. Now, Z = 2 implies
that D = 0 if and only if C = 0. Hence,E(Y |D = 0, Z = 2) = E(Y0 |D = 0, Z = 2) = E(Y0 |C = 0, Z = 2) = E(Y0 |C = 0)establishing part (iv). For part (v) Z = 2 implies that D = 1 if and only if C = 1 andhence

E(Y |D = 1, Z = 2) = E(Y1 |D = 1, Z = 2) = E(Y1 |C = 1, Z = 2) = E(Y1 |C = 1).

Proposition 1. Under Assumption 1,(i) TOT ≡ E(Y1 − Y0 |C = 1) =E(Y |Z = 2) − E(Y |Z = 0)
E(D|Z = 2)(ii) TUT ≡ E(Y1 − Y0 |C = 0) =E(Y |Z = 1) − E(Y |Z = 2)
1 − E(D|Z = 2)(iii) ASB ≡ E(Y0 |C = 1) − E(Y0 |C = 0) =E(Y |Z = 0) − E(Y |Z = 2, D = 0)
E(D|Z = 2)(iv) ASL ≡ E(Y1 |C = 1) − E(Y1 |C = 0) =E(Y |Z = 2, D = 1) − E(Y |Z = 1).
1 − E(D|Z = 2)

Proof. For parts (i) and (iii) we require an expression for E(Y0 |C = 1) in terms of theobservables (Y, D, Z). By Lemma 1(ii) and iterated expectations

E(Y |Z = 0) = E(Y0 ) = E(Y0 |C = 0)P(C = 0) + E(Y0 |C = 1)P(C = 1).
Re-arranging and substituting Lemma 1(i) and (iv),

E(Y |Z = 0) − E(Y0 |C = 0)P(C = 0)
P(C = 1)
E(Y |Z = 0) − E(Y |Z = 2, D = 0)E(1 − D|Z = 2)=.
E(D|Z = 2)

E(Y0 |C = 1) =(13)

Part (i) follows by combining (13) with Lemma 1(v) and simplifying; part (iii) follows
by combining (13) with Lemma 1(iv) and simplifying. Similarly, for parts (ii) and (iv)
we require an expression for E(Y1 |C = 0) in terms of observables. By Lemma 1(iii) anditerated expectations,

E(Y |Z = 1) = E(Y1 ) = E(Y1 |C = 0)P(C = 0) + E(Y1 |C = 1)P(C = 1).

OA - 22Re-arranging and substituting Lemma 1(i) and (v),

E(Y1 |C = 0) =E(Y |Z = 1) − E(Y1 |C = 1)P(C = 1)

P(D = 0)E(Y |Z = 1) − E(Y |Z = 2, D = 1)E(D|Z = 2)=.
E(1 − D|Z = 2)

(14)Part (ii) follows by combining (14) with Lemma 1(iv) and simplifying; part (iv) follows
by combining (14) with Lemma 1(v) and simplifying.

F.2

Regression-based Estimation of TOT, TUT, ASG, ASL, and ASB

We now show how a collection of just-identified, linear IV regressions can be used toconsistently estimate the ATE, TOT, and TUT effects, along with each of the ingredientsneeded to construct the ASL and ASB. These results are used below to provide a recipe
for cluster-robust inference for the ASG, ASL, and ASB effects. The first result provides
a regression-based approach to estimate the ATE and TOT.
Proposition 2. Under Assumption 1,
Y = E(Y0 ) + ATE × Z1 + TOT × Z2 D + U
where E(U |Z) = 0. Therefore, under standard regularity conditions, an IV regressionof Y on an intercept, Z1 and Z2 D with instruments (1, Z0 , Z1 ) provides a consistentestimator of the ATE and TOT effects.
Proof. By Assumption 1 (iii),
Y = Z0 Y0 + Z1 Y1 + Z2 [(1 − C)Y0 + CY1 ]= (Z0 + Z2 )Y0 + Z1 Y1 + Z2 C(Y1 − Y0 )= (Z0 + Z1 + Z2 )Y0 + Z1 (Y1 − Y0 ) + Z2 D(Y1 − Y0 )= Y0 + Z1 (Y1 − Y0 ) + Z2 D(Y1 − Y0 ).
since Z2 D = Z2 C and (Z0 + Z1 + Z2 ) = 1. Thus, definingU ≡ [Y0 − E(Y0 )] + Z1 [(Y1 − Y0 ) − ATE] + Z2 D[(Y1 − Y0 ) − TOT]by construction we have
Y = E(Y0 ) + ATE × Z1 + TOT × Z2 D + U.
Now, since Z2 D = Z2 C and Z is independent of (Y1 , Y0 ) by Assumption 1 (i), we haveE(U |Z) = [E(Y0 |Z) − E(Y0 )] + Z1 [E(Y1 − Y0 |Z) − ATE] + E [Z2 D {(Y1 − Y0 ) − TOT} |Z]= [E(Y0 ) − E(Y0 )] + Z1 [E(Y1 − Y0 ) − ATE] + Z2 E [C {(Y1 − Y0 ) − TOT} |Z]= Z2 E [C {(Y1 − Y0 ) − TOT} |Z] .

OA - 23

Finally, by iterated expectations

E [C {(Y1 − Y0 ) − TOT} |Z] = P(C = 1|Z) [E(Y1 − Y0 |C = 1, Z) − TOT]= P(C = 1) [E(Y1 − Y0 |C = 1) − TOT] = 0
since Z is conditionally independent of (Y0 , Y1 ) given C, an implication of 1 (i).
The next proposition provides regression-based estimates of the ATE and TUT.
Proposition 3. Under Assumption 1
Y = E(Y1 ) + ATE × −Z0 + TUT × −Z2 (1 − D) + V
where E(V |Z) = 0. Therefore, under standard regularity conditions, an IV regression of
Y on an intercept, −Z0 and −Z2 (1 − D) with instruments (1, Z0 , Z1 ) provides consistentestimates of the ATE and TUT effects.
Proof. By Assumption 1 (iii),
Y = Z0 Y0 + Z1 Y1 + Z2 [(1 − C)Y0 + CY1 ]= Z0 Y0 + Z1 Y1 + Z2 [(1 − C)(Y0 − Y1 ) + Y1 ]= Z0 Y0 + (Z1 + Z2 )Y1 + Z2 (1 − C)(Y0 − Y1 )= Z0 Y0 + (1 − Z0 )Y1 + Z2 (1 − D)(Y0 − Y1 )= Y1 − Z0 (Y1 − Y0 ) − Z2 (1 − D)(Y1 − Y0 )since Z2 (1 − C) = Z2 (1 − D) and (Z1 + Z2 ) = 1 − Z0 . Thus, definingV ≡ [Y1 − E(Y1 )] − Z0 [(Y1 − Y0 ) − ATE] − Z2 (1 − D)[(Y1 − Y0 ) − TUT]
by construction we have
Y = E(Y1 ) + ATE × −Z0 + TUT × −Z2 (1 − D) + V.
Now, since Z2 (1 − D) = Z2 (1 − C) and Z is independent of (Y0 , Y1 ) by Assumption 1(i),E(V |Z) = [E(Y1 |Z) − E(Y1 )] − Z0 [E(Y1 − Y0 |Z) − ATE] − E[Z2 (1 − D) {(Y1 − Y0 ) − TUT} |Z]= [E(Y1 ) − E(Y1 )] − Z0 [E(Y1 − Y0 ) − ATE] − Z2 E[(1 − C) {(Y1 − Y0 ) − TUT} |Z]= −Z2 E[(1 − C) {(Y1 − Y0 ) − TUT} |Z].
Finally, by iterated expectations,
E[(1 − C) {(Y1 − Y0 ) − TUT} |Z] = P(C = 0|Z) [E(Y1 − Y0 |C = 0, Z) − TUT]
= P(C = 0|Z) [E(Y1 − Y0 |C = 0) − TUT] = 0
since Z is conditionally independent of (Y0 , Y1 ) given C, an implication of Assumption
1 (i).
Since ASG = TOT − TUT, the preceding two propositions provide consistent estimates of ASG effect. The ASB effect, E(Y0 |C = 1) − E(Y0 |C = 0), can likewise be
OA - 24

estimated by taking the difference of coefficients across two linear IV regressions, as
shown in the following proposition.
Proposition 4. Under Assumption 1(1 − D)Y = E(Y0 ) × Z0 + E(Y0 |C = 0) × (1 − D)Z2 + U0

(15)

(1 − D)Y = E(Y0 ) × (Z0 + Z2 ) + E(Y0 |C = 1) × −DZ2 + U1

(16)

where E(U0 |Z) = E(U1 |Z) = 0. Thus, under standard regularity conditions, an IV
regression of (1 − D)Y on Z0 and (1 − D)Z2 with instruments (Z0 , Z2 ) and no intercept
provides consistent estimates of E(Y0 ) and E(Y0 |C = 0). Similarly, an IV regression of(1 − D)Y on (Z0 + Z2 ) and −DZ2 with instruments (Z0 , Z2 ) and no intercept provides
consistent estimates of E(Y0 ) and E(Y0 |C = 1).
Proof. Assumption 1 (ii) implies (1 − D) = Z0 + Z2 (1 − C). Hence, by Assumption 1(iii),(1 − D)Y = [Z0 + Z2 (1 − C)] {Z0 Y0 + Z1 Y1 + Z2 [(1 − C)Y0 + CY1 ]}= Z0 Y0 + Z2 (1 − C)[(1 − C)Y0 + CY1 ]= Z0 Y0 + Z2 (1 − C)Y0 .
because Zj2 = Zj for any j and Zj Zk = 0 for any j ̸= k and, similarly, (1 − C)2 = (1 − C)
and C(1 − C) = 0. Therefore, since Z2 (1 − C) = Z2 (1 − D),(1 − D)Y = Z0 Y0 + Z2 (1 − D)Y0
(1 − D)Y = (Z0 + Z2 )Y0 + (−DZ2 )Y0 .
Now, defining
U0 ≡ Z0 [Y0 − E(Y0 )] + Z2 (1 − D)[Y0 − E(Y0 |C = 0)]U1 ≡ (Z0 + Z2 )[Y0 − E(Y0 )] + (−Z2 D)[Y0 − E(Y0 |C = 1)]
by construction, we have
Y = E(Y0 ) × Z0 + E(Y0 |C = 0) × Z2 (1 − D) + U0
Y = E(Y0 ) × (Z0 + Z2 ) + E(Y0 |C = 1)(−Z2 D) + U1 .
Finally, since Z2 (1 − D) = Z2 (1 − C), and Z is independent of Y0 ,E(U0 |Z) = Z0 [E(Y0 |Z) − E(Y0 )] + Z2 E{(1 − C)[Y0 − E(Y0 |C = 0)|Z}= Z2 E[Y0 − E(Y0 |C = 0)|C = 0, Z] = 0
where the final two steps follow by iterated expectations and the fact that Z is conditionally independent of Y0 given C. Since Z2 D = Z2 C, a nearly identical argument
gives

E(U1 |Z) = (Z0 + Z2 )[Y0 − E(Y0 |Z)] − Z2 E{C[Y0 − E(Y0 |C = 1)|Z}= −Z2 E[Y0 − E(Y0 |C = 0)|C = 1, Z] = 0.
OA - 25

The next results shows that the ASL effect, E(Y1 |C = 1) − E(Y1 |C = 0), can be
estimated as the difference of coefficients across two linear IV regressions, as shown in
the following proposition.
Proposition 5. Under Assumption 1,
DY = E(Y1 ) × (Z1 + Z2 ) + E(Y1 |C = 0) × (D − 1)Z2 + V0

(17)

DY = E(Y1 ) × Z1 + E(Y1 |C = 1) × DZ2 + V1

(18)

where E(V0 |Z) = E(V1 |Z) = 0. Thus, under standard regularity conditions, an IV
regression of DY on (Z1 +Z2 ) and −Z2 (1−D) with instruments (Z1 , Z2 ) and no intercept
provides consistent estimates of E(Y1 ) and E(Y1 |C = 1). Similarly, an IV regression of
DY on Z1 and DZ2 with instruments (Z1 , Z2 ) and no intercept provides consistentestimates of E(Y1 ) and E(Y1 |C = 1).
Proof. By Assumption 1, D = Z1 + Z2 C. Hence, by Assumption 1 (iii),
DY = (Z1 + Z2 C) {Z0 Y0 + Z1 Y1 + Z2 [(1 − C)Y0 + CY1 ]}= Z1 Y1 + Z2 C[(1 − C)Y0 + CY1 ]= Z1 Y1 + Z2 CY1because Zj2 = Zj for any j and Zj Zk = 0 for any j ̸= k and, similarly, (1 − C)2 = (1 − C)
and C(1 − C) = 0. Therefore, since Z2 (1 − C) = Z2 (1 − D),
DY = (Z1 + Z2 )Y1 + Z2 (D − 1)Y1
DY = Z1 Y1 + Z2 DY1 .
Now, defining
V0 = (Z1 + Z2 )[Y1 − E(Y1 )] + Z2 (D − 1)[Y1 − E(Y1 |C = 0)]
V1 = Z1 [Y1 − E(Y1 )] + Z2 D[Y1 − E(Y1 |C = 1)]
by construction we have
Y = E(Y1 ) × (Z1 + Z2 ) + E(Y1 |C = 0) × Z2 (D − 1) + V0
Y = E(Y1 ) × Z1 + E(Y1 |C = 1) × Z2 D + V1 .
Finally, since Z2 (1 − D) = Z2 (1 − C) and Z is independent of Y1 ,E(V0 |Z) = (Z1 + Z2 )[E(Y1 |Z) − E(Y1 )] − Z2 E{(1 − C)[Y1 − E(Y1 |C = 0)|Z}= −Z2 E[Y1 − E(Y1 |C = 0)|C = 0, Z] = 0
where the final two steps follow by iterated expectations and the fact that Z is conditionally independent of Y1 given C. Since Z2 D = Z2 C, a nearly identical argument
gives

E(V1 |Z) = Z1 [E(Y1 |Z) − E(Y1 )] + Z2 E{C[Y1 − E(Y1 |C = 1)|Z}= Z2 E[Y1 − E(Y1 |C = 1)|C = 1, Z] = 0.
OA - 26

F.3

Inference for ASG, ASB, and ASL

We now explain how to carry out cluster-robust inference for the ASG, ASB, and ASL
effects, as implemented in our companion STATA package. Each of these effects canbe expressed as a difference of coefficients from two just-identified linear IV regressions.
The ASG effect is the difference of the TOT effect from Proposition 2 and the TUT
effect from Proposition 3. Similarly, the ASB effect is the difference of E(Y0 |C = 1) andE(Y0 |C = 0) from Proposition 4 while the ASL effect is the difference of E(Y1 |C = 1)
and E(Y1 |C = 0) from Proposition 5. Within each pair of IV regressions the outcome
variable and instrument set is identical; only the regressors differ. Since our estimators of
all three effects share the same structure, our discussion of inference abstracts from thespecific regressors and instruments used in each case to avoid duplication. To implement
these results in practice without relying on our STATA package, simply substitute supply
the regressors and instruments specified in the relevant propositions.
Let g = 1, ..., G index clusters and i = 1, ..., Ng index individuals within a particular cluster g. In our experiment, a cluster is a branch-day combination and theexperimentally-assigned treatment (control, forced, or choice arm) is assigned at thecluster level. We assume that observations are iid across clusters but potentially correlated within cluster. Now consider a pair of just-identified linear IV regressions givenby′
Yig = X1,ig
θ0 + Uig′
Yig = X0,igθ1 + Vigwith common instrument vector Wig . Stacking observations in the usual manner, e.g.
′
W1g
 . 
. 
Wg ≡ 
 . ,



WN′ g g





W1
 . 

W=
 ..  ,WG

we can write the preceding equations in matrix form as
Y = X1 θ1 + U
Y = X0 θ0 + V
with instrument matrix W. Now, the IV estimators for θ1 and θ0 can be expressed asθb1 = W′ X1

−1

W′ Y = θ1 + W′ X1

−1

W′ U

θb0 = W′ X0

−1

W′ Y = θ0 + W′ X0

−1

W′ V.

Our parameter of interest is an element of the difference (θ1 − θ0 ), so it suffices tocalculate the asymptotic distribution of (θb1 − θb0 ).

OA - 27

Re-arranging the preceding two equations, we have


−1 



−1 

G
  W′ X −1  W′ U 
√ 
1 X
1
b
√
G θ1 − θ1 ==W′ X1,g GG g=1 g
G



G
1 X
√
Wg′ Ug 
G g=1

G  W′ X −1  W′ V 
√ 
1 X
0
b

√
=
G θ0 − θ0 =Wg′ X0,g 
G
G
G
g=1

G
1 X

√

G g=1



Wg′ Vg  .

Now, define Q0 ≡ E[Wg′ X0g ] and Q1 ≡ E[Wg′ X1g ] and suppose that these expectations
exist and that the matrices Q0 and Q1 are invertible. Then, as G → ∞


G
1 X



G g=1

−1

Wg′ X0,g →p Q−1
0 ,



G
1 X



G g=1

−1

→p Q−1
1Wg′ X1,g 

by the continuous mapping theorem. Now, by our experimental design and exclusion
restriction, Wig is independent of Uig both unconditionally and conditional on cluster
size. Therefore,


 

Ng
Ng
X

X
Wig Uig Ng 
E[Wg′ Ug ] = E  Wig Uig  = ENg E


i=1
i=1




Ng
Ng
X
X
= EN  E(Wig Uig |Ng ) = EN  E(Wig Uig ) = 0
g

g

i=1

i=1

by iterated expectations, and similarly smilarly, E[Wg′ Vg ] = 0. Thus, under mild
regularity conditions (e.g. finite fourth moments), as G → ∞ we have
G
1 X
Ug
√
Wg′ ⊗
→d N(0, Ω)
Vg
G g=1

"

#

where the heteroskedasticity– and cluster–robust variance-covariance matrix Ω is defined
as
!# "
"
#


ΩU U ΩU V
Ug U′g Ug Vg′′≡.
Ω ≡ E Wg Wg ⊗
ΩV U ΩV V
Vg U′g Vg Vg′
Therefore, the joint limiting distribution of θb1 and θb0 is given by
"√
" #
" # "
#
"
#" #
G(θb1 − θ1 )
Q−1
0
ξU
ξU
0
Ω
1
√
,
∼N
, UU
→d
−1
b
ξV
0
ΩV U
0
Q0
ξV
G(θ0 − θ0 )

ΩU V
ΩV V

#!

from which it follows by the continuous mapping theorem that
i
h
i ξ
√ h
U
−1
.
G (θb1 − θb0 ) − (θ1 − θ0 ) →d Q−1
−Q
1
0
ξV
"

#

To use this result in practice, we estimate the standard errors of (θb1 − θb0 ) as the square

OA - 28

root of the diagonal elements of the matrixh[ θb1 − θb0 ) = (W′ X1 )−1 − (W′ X0 )
Avar(

"
i S
UU
−1

SV U

SU V
SV V

(X′1 W)−1− (X′0 W)−1

#"

#

where
SU U ≡GX

b gU
b ′ Wg
Wg′ U
g

g=1

SU V ≡GX

b gVb ′ Wg
Wg′ U
g

g=1

SV U ≡ S′U V
SV V ≡GX

b gVb ′ Wg
Wg′ V
g

g=1

and we define the IV residualsb g ≡ Yg − X1,g θb1
Ub g ≡ Yg − X0,g θb0 .
VIn our application the number of clusters, G, is large. If desired, an ad hoc degrees ofpfreedom correction can be applied by multiplying the standard errors by G/(G − 1).

Appendix G.

Testable Implications of the Exclusion Restriction

This section describes the testable implications of our exclusion restrictions: (3) and(4) from Section 5.2. To consider possible violations of these conditions, it is helpful to introduce some additional notation. As above, let Y0 ≡ Y (d = 0, z = 0) andY1 ≡ Y (d = 1, z = 1) denote the potential outcomes under forced treatment: Y0 is thepotential outcome when forced into the status quo contract and Y1 when forced into thecommitment contract. Further let Y0,2 ≡ Y (d = 0, z = 2) and Y1,2 ≡ Y (d = 1, z = 2)
denote the potential outcomes under free choice of treatment: Y0,2 is the potential outcome when choosing the status quo contract and Y1,2 when choosing the commitment
contract. Using this notation, (3) becomes Y0 = Y0,2 and while (4) becomes Y1 = Y1,2 .
If we do not impose this pair of equalities, part (iii) of Assumption 1 becomes
Y = 1(Z = 0)Y0 + 1(Z = 1)Y1 + 1(Z = 2) [(1 − C)Y0,2 + CY1,2 ]but parts (i) and (ii) continue to hold. Accordingly, parts (i)–(iii) of Lemma 1 areunchanged, while parts (iv) and (v) becomeE(Y |D = 0, Z = 2) = E(Y0,2 |C = 0), E(Y |D = 1, Z = 2) = E(Y0,1 |C = 1).

OA - 29

Using these expressions, the testable restrictions we consider here are as follows:

E(Y0 |C = 0) = E(Y0,2 |C = 0)
E(Y1 |C = 1) = E(Y1,2 |C = 1).

(19)
(20)

Equation 19 is a restriction on the average potential outcomes of non-choosers that we
use to point identify the TUT effect. It says that someone who would choose the control
condition when given a choice, experiences the same potential outcome, on average, whenassigned to the control condition. Equation 20 is a restriction on the average potential
outcomes of choosers that we use to point identify the TOT effect. It says that someone
who would choose the commitment contract when given a choice, experiences the samepotential outcome, on average, when assigned to this condition. Because they refer todifferent groups of people, either of (19) and (20) could hold when the other is violated.
For this reason we consider each in turn. Our approach is closely related to argumentsfrom Huber & Mellace (2015) and DiTraglia & Garcia-Jimeno (2019), among others. As
such, the following is a heuristic explanation rather than a fully-rigorous proof. See theaforementioned papers for more details of how to make this argument fully rigorous.
Consider first (19). Let p ≡ P(C = 1) = P(D = 1|Z = 2) denote the share ofchoosers in the population. This value is point identified regardless of whether the
exclusion restriction holds. Because Z was randomly assigned, a fraction p of borrowers
with Z = 0 are choosers while the remaining (1 − p) are non-choosers. It follows
that, regardless of whether the exclusion restriction holds, the observed distribution of
Y |Z = 0 is a mixture of Y0 |C = 0 and Y0 |C = 1 with mixing weights (1 − p) and p. This
allows us to construct a pair of bounds for E(Y0 |C = 0) as follows. The non-choosers
must lie somewhere in the distribution of Y |Z = 0. Consider the two most extreme
possibilities: they could occupy the bottom (1 − p) × 100% of the distribution or the
top (1 − p) × 100% of the distribution. For this reason, computing the average of thetruncated distribution of Y |Z = 0, cutting out the top p × 100%, provides a lower boundfor the average of Y0 among non-choosers. Similarly, cutting out the bottom p × 100%0provides an upper bound. Let y1−pdenote the (1 − p) quantile of Y |Z = 0 and yp0 denotethe p quantile of the same distribution. Using this notation, the bounds are given by






0
E Y |Z = 0, Y ≤ y1−p
≤ E(Y0 |C = 0) ≤ E Y |Z = 0, Y ≥ yp0



These bounds do not rely on the exclusion restriction. Under Equation 19, however, weknow that E(Y0 |C = 0) = E(Y |D = 0, Z = 2). Therefore, if the exclusion restriction for
non-choosers holds, we must have








0
E Y |Z = 0, Y ≤ y1−p
≤ E(Y |D = 0, Z = 2) ≤ E Y |Z = 0, Y ≥ yp0 .

(21)

Equation 21 provides a pair of testable implications of (19). If either inequality isviolated, then the exclusion restriction for non-choosers fails. In our experiment, pb =b (D = 1|Z = 2) = 0.11. For the APR outcome we estimatePb (YAPR |Z = 0, YAPR ≤ y 0 ) = 0.48, E
b (YAPR |Z = 0, YAPR ≥ y 0 ) = 0.62.
E
0.89
0.11
b (YAPR |D = 0, Z = 2) = 0.58 falls between these bounds, we find no evidence
Since EOA - 30

against the exclusion restriction for non-choosers. Repeating this exercise for the finanb (YFC |D = 0, Z = 2) = 973 likewise falls between
cial cost outcome, we see that Eb (YFC |Z = 0, YFC ≤ y 0 ) = 626, E
b (YFC |Z = 0, YFC ≥ y 0 ) = 1046
E
0.89
0.11

so we again find no evidence against the exclusion restriction for non-choosers.
We can use an analogous approach to construct testable implications for 20. Because
Z was randomly assigned, a fraction p of participants with Z = 1 are choosers so the
distribution of Y |Z = 1 is a mixture of Y1 |C = 1 and Y1 |C = 0 with mixing weights
p and 1 − p. The participants with C = 1 must lie somewhere in the distribution of
Y0 |Z = 1 so again consider the two most extreme cases: they could occupy the bottomor the top p × 100% of the distribution. Hence,
1
E Y |Z = 1, Y ≤ yp1 ≤ E(Y1 |C = 1) ≤ E Y |Z = 1, Y ≥ y1−p









1
where yp1 and y1−p
are the p and 1 − p quantiles of the distribution of Y |Z = 1. Asabove, these bounds do not rely on the exclusion restriction. If Equation 20 holds,
however, we know that E(Y |D = 1, Z = 2) = E(Y1 |C = 1), yielding the following
testable implications for choosers
1
E Y |Z = 1, Y ≤ yp1 ≤ E(Y |D = 1, Z = 2) ≤ E Y |Z = 1, Y ≥ y1−p
.









(22)

If either inequality is violated, then the exclusion restriction from Equation 20 fails.
Again, in our experiment pb = 0.11. For the APR outcome we estimateb (Y |Z = 1, Y ≤ y 1 ) = 0.06, E
b (Y |Z = 1, Y ≥ y 1 ) = 1.28
E
0.11
0.89
b (YAPR |D = 1, Z = 2) = 0.43 falls between these bounds, we find no evidence
Since Eagainst the exclusion restriction for the choosers. Repeating this exercise for the financialb (YFC |D = 1, Z = 2) = 570 likewise falls between
cost outcome, we see that Eb (Y |Z = 1, Y ≤ y 1 ) = 53, E
b (Y |Z = 1, Y ≥ y 1 ) = 2934
E
0.11
0.89

so we again find no evidence against the exclusion restriction for the choosers.
The aforementioned bounds for E(Y0 |C = 0) and E(Y1 |C = 1) can alternatively be
used construct partial identification bounds for the TOT and TUT effects that do not
rely on our exclusion restrictions. If the TOT or TUT expression from Appendix F. falloutside the partial identification bounds, this is equivalent to finding a violation of 21
or 22. We implement these bounds for the TOT and TUT in our companion STATA
package.

OA - 31

Appendix H.
H.1

Causal Random Forest, HTE, and ‘mistakes’

Conditional ATE estimates

Figure OA-18: Cumulative Distribution Function of Conditional ATE Estimates
100
90
80

% benefitted

70
60
50
40
30
20
10
0
-50

-30

-10

10

30

50

APR % threshold

This figure shows the share of borrowers who benefit from forced commitment, where “benefit” is defined ashaving an estimated conditional average treatment effect (ATE) above a specified threshold value. Results are
based on the causal forest model from Section 6.2. The solid line equals 1 − FATE (δ) where FATE (δ) denotes
the CDF corresponding to the density of conditional ATE estimates from Figure 4. The blue shaded regions areassociated 95% confidence intervals. We estimate that at least 90% of borrowers have a positive conditional ATE.

Figure OA-19: Conditional ATEs from “wide” and “narrow” covariate sets.5

R-squared : .028

0

Narrow forest

.25

-.25

-.5

Wide forest
-.5

-.25

0

.25

.5

This figure plots the relationship between the causal forest conditional ATE estimates from Section 6.2 that use
the “wide” set of covariates (all intake survey responses) and those based on a restricted “narrow” set of covariates(age, gender, HS education, and previous borrowing). The scatterplot graphs one estimate versus the other, withthe “wide” covariate set on the horizontal axis and the “narrow” set on the vertical axis. The density plots oneach axis show the estimated marginal distribution of conditional ATEs under each covariate set. The density
for the “wide” covariate set is considerably more dispersed, as the causal forest based on this set of covariates
captures considerably more treatment effect heterogeneity.

OA - 32

Figure OA-20: Targeting rules

100% benefitted

90

80

70

60

50
-10

-5

0

5

10

Narrow rule (RF)

Narrow rule (Logit)

APR threshold
Optimal rule (WF)

Universal paternalism

This figure plots the percentage of borrowers who would benefit from a program in which commitment is targetedusing the “narrow” covariate set (age, gender, HS education, and previous borrowing). In this exercise “benefit”
is defined to mean having a conditional ATE above a particular threshold, taking the estimated conditional effects
from the “wide” causal forest as ground truth. The plot compares the estimated percentage of borrowers who
benefit, along with associated 95% confidence bands, for three targeting rules: universal forced commitment inblue, targeting based on a random forest classification model in green, and targeting based on the logit model in
red. For each of the classification models, the outcome variable is an indicator for whether the CATE estimate fromthe “wide” random forest model is positive. Each of the classification models produces an estimated probabilityof a positive CATE. For each, the assignment rule ranks borrowers by this estimated probability, and assigns thehighest 90% to forced commitment, to match the overall percentage of borrowers with positive estimated CATEs
from the “wide” random forest model. Because this is an in-sample exercise, it overstates the actual performanceof logit and RF-based targeting.

H.2

Targeting rule comparisons

Figure OA-20 compares the in-sample performance of these targeting rules against a
policy of universal forced commitment. The plot presents the estimated proportion ofborrowers who benefit from a particular treatment assignment rule, along with associated 95% confidence bands, where “benefit” is defined as having a CATE above a particular threshold. As above, we take the conditional average effects from the “wide” causal
forest as ground truth for the purposes of this exercise. Because this is an in-sample
exercise, the logistic and random forest classification rules have an unfair advantage:
there is no adjustment for overfitting. In spite of this, their performance is unimpressive
relative to a policy of universal forced commitment. The fraction of the whole sample
incorrectly targeted when moving from universal forced commitment to targeting basedon the narrow RF falls only from 9.78% to 9.59%. The logit targeting rule actually
makes things marginally worse.

OA - 33