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\begin{center}
	\LARGE Supplementary Appendix for ``The controlled choice design and private paternalism in pawnshop borrowing'' \\[0.5em]
	%\Large{Appendix $-$ For Online Publication} \\[1em]
	\large \author{Craig McIntosh \and Isaac Meza \and Joyce Sadka \and Enrique Seira \and Francis J.\ DiTraglia}
\end{center}


\appendix
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\linespread{1}


%\section{ Treatment Explanation Materials and Pictures}
\section{Treatment Explanation Materials} 
%\vspace{.2in}

%\subsection{Materials}

\begin{figure}[H]
     \caption{Contract Terms Summary}
    \label{PaperSlip}
    \begin{center}
    %\begin{subfigure}{0.65\textwidth}
    %\caption{Receipt for client}
     %   \centering
        \includegraphics[width=0.5\textwidth]{Figuras/TicketLenderP.png}
    %\end{subfigure}
    
    %\vspace{3ex}
    %\begin{subfigure}{0.65\textwidth}
    %\caption{Personal promise signed by client}
     %   \centering
    %    \includegraphics[width=\textwidth]{Figuras/Personal Promise2.png}
    %\end{subfigure}
    \end{center}
    \scriptsize{
        We show a sample receipt that was given to clients that got assigned to the fee-forcing contract (the font and format were changed to protect Lender's P identity). We want to highlight the salience of some items. First the title 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. %The bottom panel of the figure shows a ``promise slip'', the paper that those who were assigned (or chose) to the monthly payment with promise had to sign to make the promise salient. It emphasizes that the client is giving his word, and that the promise is not a legal document.
        }
\end{figure}



\begin{figure}[H]
     \caption{Explanatory Material}
    \label{ExplanatoryMaterial}
    \begin{center}
        \centering
        \includegraphics[width=0.6\textwidth]{Figuras/micas.pdf}

    \end{center}
    \scriptsize{
        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.}
\end{figure}




%\subsection{Pictures}
%
%\begin{figure}[H]
%     \caption{Some Pawnshops}
%    \label{PawnshopPicture}
%    \begin{center}
%    \begin{subfigure}{0.405\textwidth}
%    \caption{Appraiser/tellers inside a pawnshop}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/empenio9_.png}
%    \end{subfigure}
%        \begin{subfigure}{0.45\textwidth}
%    \caption{Pawnshop}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/empenio11_.png}
%    \end{subfigure}
%    
%        \vspace{3ex}
%
%    \begin{subfigure}{0.45\textwidth}
%    \caption{Pawnshop}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/empenio2_.png}
%    \end{subfigure}
%    \begin{subfigure}{0.415\textwidth}
%    \caption{Lost pawns which are for sale}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/empenio3_.png}
%    \end{subfigure}
%    \end{center}
%    \scriptsize{
%        This figure  shows pictures of pawnshops in Mexico city. They do not necessarily coincide with Lender P for confidentiality.} 
%\end{figure}



%\vspace{.1in}
%\begin{figure}[H]
%     \caption{Gold buyers next to pawnshops}
%    \label{GoldBuyers}
%    \begin{center}
%    \begin{subfigure}{.49\textwidth}
%    \caption{Gold buyer next to pawnshop 1}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/empenio7_.png}
%    \end{subfigure}
%    \begin{subfigure}{.49\textwidth}
%    \caption{Gold buyer next to pawnshop 1}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/empenio8_.png}
%    \end{subfigure}
%       \vspace{3ex}
%       
%    \end{center}
%    \scriptsize{
%        This figure shows pictures of gold buyers next to pawnshops in Mexico city. They do not necessarily coincide with Lender P for confidentiality. }
%\end{figure}



\begin{comment}
\\
\begin{table}[H]
\caption{Number of pawns balance before and after the experiment}
\label{num_pawns_bal}
\begin{center}
\scriptsize{\input{./Tables/num_pawns_bal.tex}}
\end{center}
 \scriptsize 
%\textit{Do file: } \texttt{num\_pawns\_bal.do}
\end{table}
\end{comment}
%\todo[inline]{removed}




\newpage
\subsection{Survey}   \label{app:survey_data}



\normalsize
\linespread{1.05}
%Really force it to normal size and linespread
\normalsize
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\begin{table}[H]
\caption{Baseline survey questions (translated to English)}
\label{baseline_survey}
\begin{center}
\scriptsize{\input{./Tables/transcribed.tex}}
\end{center}
\scriptsize{
Translation of the baseline questionnaire.}
\end{table}

\newpage

We now present analysis of the extent to which the survey-responding sample is representative and balanced.
Table \ref{SS_cond_survey} 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 across treatment 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 at least 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 \ref{TUT_cond_survey} shows how the estimated TUT effect changes if we restrict our estimation 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 our measure 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, our TUT estimates are quite stable across sub-samples defined by survey response.
In each case 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.



%\newpage
\subsection{More descriptives}


%The second thing to note is that those that are not closed at the end of our sample period have already incurred substantial financial cost, even though they have not defaulted yet. 
 
%Of those who renew, 83\% lose the pawn. Figure \ref{fc_hist}(a) suggest that financial cost is significant, even for those that do recover their pawn. Panel (b) normalizes the cost by loan size. It shows that as a percentage of their pawn, most of the cost comes from clients that do not recover their pawn. For them the cost is between 140\% and 250\% of the loan value. %{The difference between panel (a) and (b) arises since clients who lose their pawn tend to be those that pledge cheaper pieces.} 


\begin{figure}[!h]
\caption{Financial cost.}
  \label{fc_hist}
    \begin{center}
    \begin{subfigure}{.42\textwidth}
        \centering
        \includegraphics[width=\textwidth]{Figuras/hist_fc.pdf}
        \caption{}
    \end{subfigure}
     \begin{subfigure}{0.42\textwidth}
       \centering
      \includegraphics[width=\textwidth]{Figuras/hist_apr.pdf}
      \caption{}
    \end{subfigure}
    \end{center}
 
 \scriptsize{Panel (a) plots a histogram of this financial cost in pesos for all loans in the experiment, stratified by whether we observed that they ended in default or recovery of the pawn. Panel (b) shows the analogous histogram for the APR.
%defaulted (44\%), recovered their pawn (43\%), or whether they are censored in our data (13\%). 
We see that borrowers who default incur higher costs; part of this is mechanical as losing their collateral is part of the cost. Most of the APR costs indeed come from clients who do not recover their pawn.}
    
      %\footnotesize{ } \textit{Do file: }  \texttt{hist\_fc.do}
\end{figure}

\begin{figure}[!h]
    \caption{Behavior of borrowers who lost their pawn}
    \label{proxy_naive}
    \begin{center}
    \begin{subfigure}{0.35\textwidth}
        \caption{Elapsed days to first payment}
        \centering
        \includegraphics[width=\textwidth]{Figuras/hist_firstdays_default.pdf}
    \end{subfigure}
    \begin{subfigure}{0.35\textwidth}
        \caption{Elapsed days to last payment}
        \centering
        \includegraphics[width=\textwidth]{Figuras/hist_days_default.pdf}
    \end{subfigure}
        \begin{subfigure}{0.35\textwidth}
        \caption{Payments as \% of loan}
        \centering
        \includegraphics[width=\textwidth]{Figuras/hist_percpay_default.pdf}
    \end{subfigure}
    \begin{subfigure}{0.35\textwidth}
        \caption{Number of payments}
        \centering
        \includegraphics[width=\textwidth]{Figuras/hist_numpay_default.pdf}
    \end{subfigure}
    \end{center}
        \scriptsize 
        This figure provides more details on the behavior of clients who were assigned to the control group and did not recover 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.
      %\textit{Do file: }  \texttt{hist\_den\_default.do}
\end{figure}


%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%
\newpage
\section{ 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 \ref{attrition_table} shows that this is not the case. There is no difference at all between the Control and Forced Commitment arm in terms of the number of pawns per branch-day. Although we cannot reject equality across the three arms (p-value=0.21), the Choice arm appears to have a somewhat larger number of borrowers than the Control and Forced arms.\footnote{p-value=0.23 and 0.12 respectively.} This seems to be due to sampling variability. Differences across arms are smaller when for medians, or when we compare the number of borrowers pawning (some borrowers pawn more than one piece). Figure \ref{boxplot_attrition} shows that distribution of loans per day is comparable across arms. The only noticeable difference is that the choice arm has a few more positive outliers.\footnote{If we winzorize at the 90th percentile, the mean number of branch-day pawns becomes identical across arms.}

\begin{table}
\caption{Limited and balanced attrition}
\label{attrition_table}
\begin{center}
\scriptsize{\input{./Tables/Attrition.tex}}
\end{center}
\scriptsize{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 hypothesis of equality of the three coefficients. Figure \ref{boxplot_attrition}, in the appendix shows a box-plot of the first two variables, showing the distribution across arms is balanced.}
%\textit{Do file: } \texttt{ss\_att.do}
\end{table}


The bottom panel of Table \ref{attrition_table} shows balance in a more focused way, given that the 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 to refuse 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. 

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 \ref{Paternalism} is restricted to the subset of borrowers who answered at least some survey questions. The bottom row of Table \ref{attrition_table} shows that the survey response rate is broadly similar across arms (about 78 percent). 


\begin{figure}[H]
     \caption{Box-plot across arms}
    \label{boxplot_attrition}
    \begin{center}
    \begin{subfigure}{0.35\textwidth}
    \caption{Number of pawns}
        \centering
        \includegraphics[width=\textwidth]{Figuras/box_plot_num_pawns.pdf}
    \end{subfigure}
        \begin{subfigure}{0.35\textwidth}
    \caption{Number of borrowers}
        \centering
        \includegraphics[width=\textwidth]{Figuras/box_plot_num_pawns.pdf}
    \end{subfigure}
    \end{center}
    \scriptsize
        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 blue dots represent an implicit CDF. 
\end{figure}


% \begin{figure}[H]
%      \caption{Number of pawns and borrowers before and after the experiment}
%     \label{line_pawns_before_after}
%         \centering
%         \includegraphics[width=\textwidth]{Figuras/after_before_bal.pdf}
%     \scriptsize
%         This figure shows the number of pawns and borrowers before, during, and after the experiment for the different branches.
% \end{figure}


% \begin{figure}[H]
%      \caption{No discontinuity in the number of pawns before and after experiment}
%     \label{rd_pawns}
%        \begin{center}
%     \begin{subfigure}{0.45\textwidth}
%     \caption{Number of pawns - before}
%         \centering
%         \includegraphics[width=\textwidth]{Figuras/rd_before_pawns.pdf}
%     \end{subfigure}
%         \begin{subfigure}{0.45\textwidth}
%     \caption{Number of pawns - after}
%         \centering
%         \includegraphics[width=\textwidth]{Figuras/rd_after_pawns.pdf}
%     \end{subfigure}
%      \begin{subfigure}{0.42\textwidth}
%     \caption{Number of borrowers - before}
%         \centering
%         \includegraphics[width=\textwidth]{Figuras/rd_before_borr.pdf}
%     \end{subfigure}
%         \begin{subfigure}{0.45\textwidth}
%     \caption{Number of borrowers - after}
%         \centering
%         \includegraphics[width=\textwidth]{Figuras/rd_after_borr.pdf}
%     \end{subfigure}
%     \end{center}
%     \scriptsize
%         This figure shows the number of pawns and borrowers before, during, and after the experiment for the different branches.
% \end{figure}

\vspace{-1em}

\begin{table}[H]
\caption{Balance conditional on survey response and question-by-question response rates} %by treatment arm}
\label{SS_cond_survey}
\begin{center}
\scriptsize{\input{./Tables/SS_cond_survey.tex}}
\end{center}
\scriptsize

Panel A of this table presents the same information as Panel A of Table \ref{SS}, restricted to the subsample of borrowers who answered at least one survey question. Conditional on survey response, loan amount and weekday are balanced across arms. Panel B presents response rates to each survey question across arms, along with p-values for the F-test of no difference in response rates across arms, using data for borrowers who pawned on the same day as their survey response. 
%\textit{Do file: } \texttt{ss\_att.do}
\end{table}



\begin{landscape}
\begin{table}[H]
\caption{Survey Non-response: TUT estimates for respondents to each survey question.}
\label{TUT_cond_survey}
\begin{center}
\scriptsize{\input{./Tables/tut_cond_survey.tex}}
\end{center}
\scriptsize

Some 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, and compares 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 \emph{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 increase as sample size falls, some of the sub-group estimates are not statistically significant.
%\textit{Do file: } \texttt{tut_cond_survey.do}
\end{table}
\end{landscape}



\newpage


\section{ Main treatment effects: Additional material}

%\begin{landscape}
%\subsection{Multiple loans}
%
%\begin{table}[H]
%\caption{Multiple-loans robustness check}
%\label{multiple_loans}
%\begin{center}
%\scriptsize{\input{./Tables/multiple_loans.tex}}
%\end{center}
% \scriptsize
% 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) \citep{cullen2006effect, abdulkadirouglu2011accountability}.\\
% 
% 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 to all subsequent pawns. The core treatment effects are robust to any of these ways of handling repeat pawning.  
% 
%%\textit{Do file: } \texttt{multiple\_loans.do}
%\end{table}
%
%
%\end{landscape}


\begin{figure}[H]
    \caption{Determinants of choice}
    \label{determinants_choose}
    \begin{center}
    \begin{subfigure}{0.6\textwidth}
        \centering
        \includegraphics[width=\textwidth]{Figuras/determinants_choose_commitment.pdf}
    \end{subfigure}
    \end{center}
      \scriptsize

      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. 
%\textit{Do file: } \texttt{determinants_choice.do}       
\end{figure}



\begin{figure}[H]
    \caption{Histogram of payments}
    \label{hist_payments}
    \begin{center}
    \begin{subfigure}{0.31\textwidth}
        \caption{Status-quo}
        \centering
    \includegraphics[width=\textwidth]{Figuras/hist_payments_sq.pdf}
    \end{subfigure}
    \begin{subfigure}{0.31\textwidth}
        \caption{Forced commitment}
        \centering
    \includegraphics[width=\textwidth]{Figuras/hist_payments_fc.pdf}
    \end{subfigure}
    \begin{subfigure}{0.31\textwidth}
        \caption{Choice commitment}
        \centering
    \includegraphics[width=\textwidth]{Figuras/hist_payments_cc.pdf}
    \end{subfigure}    
    \end{center}
     \scriptsize
     This figure shows the schedule of payments for each treatment arm. In other words it records the time after the loan 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).
     
      %\footnotesize{ \textit{Do file: }  \texttt{hist\_payments.do}}
\end{figure}


\subsection{Censoring} \label{App_censoring}


\normalsize
\linespread{1.05}
%Really force it to normal size and linespread
\normalsize
\linespread{1.05}

Some 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 to different 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 make extreme assumptions about the outcome of these loans in the treatment and control so as to bound the possible influence of censoring.  In Table \ref{bounding_censoring} we compare the Forced and Control 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 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 for the sake of argument that commitment affects payment timing, but does not not default.
In other words, suppose that treatment makes censoring \emph{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 censored control 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 loans that 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 on 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 a substantial influence on the magnitude of our estimated treatment effects, these  checks confirm that a) the core results are robust to censoring, and b) the headline approach that we take to the issue is conservative and is likely understating the true magnitude of impacts.

\begin{table}[H]
\caption{Bounding censoring} 
\label{bounding_censoring}
\begin{center}
\resizebox{1.0\textwidth}{!}{
\scriptsize{\input{./Tables/censoring_imp_1.tex}}
}
\end{center}
 
\end{table}
\begin{table}[H]
\begin{center}
\resizebox{1.0\textwidth}{!}{
\scriptsize{\input{./Tables/censoring_imp_2.tex}}
}
\end{center}
 
 \scriptsize {
 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 \emph{default}$=1$ or \emph{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 \ref{main_impact_table}. 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 more than 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.

\noindent Note that in all panels we maintain significant results for Financial Cost as dependent variable, while only in the most conservative scenario (Panel B) we lose significance for the APR outcome. }
\end{table}

\begin{figure}[H]
        \caption{Interpolation on bounding censoring for Default}
        \vspace{-1em}
    \label{interpolation_censoring_imp}
    \begin{center}
   % \begin{subfigure}{0.49\textwidth}
   % \caption{Significance area for APR}
   %      \centering
   %      \includegraphics[width=\textwidth]{Figuras/frontera_sig_apr.pdf}
   %  \end{subfigure}     
   %  \begin{subfigure}{0.49\textwidth}
   % \caption{Significance area for Default }
        \centering
        \includegraphics[width=0.5\textwidth]{Figuras/frontera_sig_def_imp.pdf}
    % \end{subfigure} 
    \end{center}
    \vspace{-1em}
     \scriptsize  {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 with recovery and default respectively for control and treatment. Each corner in the square will correspond to one of the panels from the Table \ref{bounding_censoring}. 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 the four 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, since for any imputation we still have significant results.}

     %\textit{Do file: }  \texttt{interpolation_censoring_imp.do}
\end{figure}





\begin{figure}[H]
        \caption{Survival graph}
        \vspace{-2em}
    \label{survival_graph}
    \begin{center}
   \begin{subfigure}{0.49\textwidth}
   \caption{Ended contract}
        \centering
        \includegraphics[width=\textwidth]{Figuras/survival_graph_ended.pdf}
    \end{subfigure} 
   \begin{subfigure}{0.49\textwidth}
   \caption{Recovery}
        \centering
        \includegraphics[width=\textwidth]{Figuras/survival_graph_unpledge.pdf}
    \end{subfigure}     
    \end{center}
    \vspace{-1em}
     \scriptsize  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.
     %\textit{Do file: }  \texttt{survival\_graph.do}
\end{figure}

\begin{figure}[H]
        \caption{\% of payment over time}
        \vspace{-2em}
    \label{porc_payment_over_time}
    \begin{center}
   \begin{subfigure}{0.49\textwidth}
        \caption{Unconditional}
        \centering
        \includegraphics[width=\textwidth]{Figuras/cumulative_porc_pay_time.pdf}
    \end{subfigure} 
   \begin{subfigure}{0.49\textwidth}
        \caption{Conditional on default}
        \centering
        \includegraphics[width=\textwidth]{Figuras/cumulative_porc_pay_time_default.pdf}
    \end{subfigure}     
    \end{center}
     \scriptsize  This Figure shows the accumulated percentage of recovery in time by treatment arm. 
     %\textit{Do file: }  \texttt{cumulative\_porc\_pay\_time.do}
\end{figure}




\subsection{Robustness accounting for other costs}

\begin{table}[!h]
\caption{Effects on more comprehensive cost measures}
\label{table_robustness_fc}
\begin{center}
\scriptsize{\input{./Tables/fc_robustness.tex}}
\end{center}
 \scriptsize{ This table augments the measure of financial cost presented in Table \ref{main_impact_table} 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 \ref{table_robustness_fc} 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 of visits that each individual made.\footnote{For clients who did not complete the individual survey, we adjust using the mean self-reported transport cost among respondents of the respective branch.} 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.}
%\textit{Do file: } \texttt{fc\_robustness.do}
\end{table}

\section{ Alternative explanations}


\subsection{Learning}
\normalsize
Table \ref{learning_table} presents information about borrowers' \emph{future} pawning behavior as a function of treatment assignment. Column (1) considers the 228 clients who returned only a second time to pawn again at a day/branch that was randomly assigned to the choice arm. Each of the two rows in this column presents a difference of mean commitment take-up rates, and associated standard error. The first row compares those who were \emph{initially} assigned 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 \emph{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 that learning plays a role, they provide no indication that the lack of voluntary compliance is simply a matter of inexperience with commitment.





\vspace{.1in}
\begin{table}[!h]
        \caption{Effect of Prior Assignment on Subsequent Choice}
    \label{learning_table}
\begin{center}
\scriptsize{\input{./Tables/learning_exp.tex}}
\end{center}
 \scriptsize  


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 first row (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 choice commitment 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 \emph{and} chose commitment.

%This table explores learning by focusing on a subsample of borrowers in the experiment and observing their subsequent behavior. Column 1 conditions the sample on borrowers who (a) pawned during the experiment a subsequent time after being assigned to control, forced commitment or choice (the regressors), and (b) when pawning again they went to a branch day when (randomly) choice was available, thus enabling us to observe if they chose the commitment contract or the status quo.  in this sample it estimates a linear probability model where the dependent variable is equal to one if the borrower chose the commitment contract in that subsequent `choice' occasion and zero otherwise. The regressors are indicators for the treatment arms in their first pawn in the experiment. Column 1 conditions the sample on the (endogenous) event of pawning again. Column 2 does not condition the sample, but instead defined the dependent variable as equal to one \hl{if the borrower pawned subsequently and choice was available that day and chose commitment, and zero otherwise.}

\end{table}


\subsection{Discount rates}


\begin{figure}[H]
        \caption{Financial benefit TUT effect for different discount rates}
    \label{fc_discount_rates}
    \begin{center}
        \centering
        \includegraphics[width=0.55\textwidth]{Figuras/discount_effect_tut.pdf}
    \end{center}
     \scriptsize This Figure re-estimates the treatment on the untreated (TUT) effect from Table \ref{tot_tut}, introducing a daily discount factor 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 (x-axis) the solid line gives the adjusted TUT and the shaded regions 90\% \& 95\% confidence bands. A discount factor of one corresponds to the estimate from Table \ref{tot_tut}. For higher discount rates, the adjusted financial cost will be higher, so the financial cost \emph{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.
     %It estimates the effect of the treatment arms  for different discount factors, where a discount factor of 1 corresponds exactly to the estimate of column 1 of Table \ref{main_impact_table}. Because the commitment contract induces earlier payments, this adjusted financial cost will be higher, and thus financial savings will be lower. This figure shows the range of estimated effects and their confidence intervals, where the discount rate used is ploted in the x-axis annualized.    %\textit{Do file: }  \texttt{discounted\_noeffect.do}
\end{figure}





\begin{comment}
    

\vspace{.2in}
\begin{table}[H]
\caption{FOSD by demographic groups \textcolor{red}{\hl{MAY NEED UPDATING}}}
\label{stochastic_dominance}
\begin{center}
\scriptsize{\input{./Tables/dominance.tex}}
\end{center}
 \footnotesize
This table does two things. First, it tests whether the observed empirical distribution of financial cost is well approximated by a log normal. It does this using two tests, the Anderson-Darling and the Kolmogorov-Smirnoff tests. Second, it fits a log normal distribution by maximum likelihood to observed empirical distribution of financial cost, separately for the fee-forcing arm and the status-quo arm. Using the fitted log normal, it tests whether the fee-forcing financial cost distribution would be preferred by any expected utility agent using Proposition \ref{lognormal_fosd} below. The different rows of the table do this for different sub-populations.  The first row of the table does it for every client in the fee forcing and status quo arms. The ``*'' show that we cannot reject at the 5\% level that both distribution are log normal for any of the two tests. The column entitled ``Dominance'' shows whether any client that dislikes higher cost would prefer the fee-forcing cost distribution over the status quo one, with $\succeq_{1}$ meaning he should (with $\succeq_{1}^*$ indicating the difference is statistically significant). It turns out to be the case that for the overwhelming majority of sub-populations, the conditions of preferring the fee-forcing distribution hold.
%\textit{Do file: } \texttt{stoch\_dominance.do}
\end{table}

\newpage


\vspace{.2in}
\begin{prop}
\label{lognormal_fosd}

Let $F$ and $G$ be the cumulative distributions of two alternative log-normal prospects. The following are equivalent:

\begin{enumerate}[(a)]
    \item For every weakly decreasing utility function $u$: $E_{F}(u(FC))\leq E_G(u(FC))$
    \item $E_F \log(FC)\geq E_G\log(FC)$ and $Var_F \log(FC)= Var_G\log(FC)$
\end{enumerate}
\end{prop}

\begin{proof}
See Theorem 4 in \cite{lognormal_dominance}.
\end{proof}


\vspace{.1in}
\begin{prop}
\label{eq_fosd}

This is a standard result. 
\\
\vspace{.1in}
The following are equivalent:
\begin{enumerate}[(a)]
    \item For every weakly decreasing utility function $u$: $E_{sq}(u(FC))\leq E_{fee}(u(FC))$
    \item $F_{sq}(FC)\leq F_{fee}(FC)$ 
\end{enumerate}

\end{prop}
\begin{proof} \;

[$(a)\Longrightarrow (b)$] Suppose  $(b)$ does not hold. So there exists $FC^*$ such that $F_{sq}(FC^*)>F_{fee}(FC^*)$, Define $u:=\mathds{1}_{FC\leq FC^*}$. Then
\[E_{sq}(u(FC)) = \int u(FC)dF_{sq} = F_{sq}(FC^*)>F_{fee}(FC^*)= \int u(FC)dF_{fee} =E_{fee}(u(FC))\]
which contradicts $(a)$.\\

[$(a)\Longleftarrow (b)$] On the other hand for $u$ weakly decreasing,

\[\int u(y(FC))dF_{sq}(y(FC)) = \int u(y(FC))dF_{fee}(FC) \leq \int u(FC)dF_{fee}(FC)\]
with $y(FC) = F_{sq}^{-1}F_{fee}(FC)$.

\end{proof}

Note the proof was done in the case of absolutely continuous and strictly increasing distribution functions $F_{sq}$ and $F_{fee}$.

\end{comment}



\normalsize
\linespread{1.05}
%Really force it to normal size and linespread
\normalsize
\linespread{1.05}


\begin{comment}
\section{ Causal Forest and individual predictions of `Mistakes'}

    \begin{figure}[H]
        \caption{Example of a Causal Tree \textcolor{red}{WHAT IS THE DIFFERENCE OF THIS AND FIGURE OA-17?}}
        \label{causal_tree_example}
        \begin{center}
\includegraphics[width=\textwidth]{Figuras/ct_eff.pdf}
\end{center}
     \scriptsize This Figure shows an example of the splits for the leaves that emerge in our data for the Athey et al (2019) Causal Forest estimation.  
        \end{figure}
\end{comment}

\subsection{Sure Confidence} \label{App_sureconfidence}

\begin{figure}[H]
    \caption{Determinants sure confidence}
    \label{determinants_sure}
    \begin{center}
    \begin{subfigure}{0.6\textwidth}
        \centering
        \includegraphics[width=\textwidth]{Figuras/determinants_confidence_100.pdf}
    \end{subfigure}
    \end{center}
      \scriptsize

      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\% probability of recovery.
%\textit{Do file: } \texttt{determinants_sure_confidence.do}       
\end{figure}




%\section{ Heterogeneity and Bounds}
\section{Bounds, FOSD and Rank Invariance} \label{bounds_FOSD}

%\subsection{Testing for heterogeneity}
%\label{append:chernozhukov}
%If the treatment effects $Y_{i1} - Y_{i0}$ are constant across $i$, then we must have
%\[
%\text{ATE}(X_i) \equiv \mathbbm{E}[Y_{i1} - Y_{i0} |X_i] = \mathbbm{E}[Y_{i1} - Y_{i0}] \equiv \text{ATE}
%\]
%for any covariates $X_i$ that vary across $i$. If, on the other hand, $\text{ATE}(X_i)$ can be predicted using some scalar function $\tau(\cdot)$ of $X_i$, then the average treatment effect function is not constant so there must be treatment effect heterogeneity. 
%
%We operationalize this idea using a two-step approach proposed by \cite{chernozhukov2018generic}.  We begin by randomly dividing the participants in the forced arms of the experiment ($Z_i \neq 2$) 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 to the same set.
%This avoids inferential problems that could arise from correlated unobservables within clusters.
%In the first step, we apply the generalized random forest approach of \cite{atheygrf} to the training set to estimate two proxy predictors: $\psi(\cdot|\text{Training})$ approximates the untreated potential outcome function, $\mathbbm{E}[Y_{i0}|X_i] = \mathbbm{E}[Y_i|Z_i=0,X_i]$, while  $\tau(\cdot|\text{Training})$, approximates the ATE function
%\[
%\text{ATE}(X_i) = \mathbbm{E}[Y_i|Z_i=1,X_i] - \mathbbm{E}[Y_i|Z_i=0, X_i].
%\]
%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 $X_i$ that \emph{accurately predicts} $\text{ATE}(X_i)$.
%In the second step we fit a linear regression model to data from the training set using regressors constructed from the proxy functions $\psi(\cdot|\text{Training})$ and $\tau(\cdot|\text{Training})$ constructed in the first step. In particular, we estimate 
%\begin{equation}
%Y_i = \alpha_0 + \alpha_1 \psi_i + \beta_1 (Z_i - \mathbbm{E}[Z_i]) + \beta_2 (Z_i - \mathbbm{E}[Z_i])(\tau_i - \mathbbm{E}[\tau_i]) + \epsilon_i
%\label{eq:chernreg}
%\end{equation}
%where $\psi_i \equiv \psi(X_i|\text{Training})$ and $\tau_i \equiv \tau(X_i|\text{Training})$.\footnote{This is a slightly simpler regression than the one proposed in equation (3.1) of \cite{chernozhukov2018generic}, which involves propensity score weights. Because the random assignment of $Z$ in our experiment does \emph{not} condition on $X$, the propensity score weights in our case are constant over $X$ and hence drop out.} As shown by \cite{chernozhukov2018generic}, the coefficients $\beta_1$ and $\beta_2$ from \eqref{eq:chernreg} identify the \emph{best linear predictor} of the conditional ATE based on $\tau(\cdot|\text{Training})$, namely
%\[
%\beta_1 = \mathbbm{E}[\text{ATE}(X_i)] = \text{ATE}, \quad
%\beta_2 = \frac{\text{Cov}[\text{ATE}(X_i), \tau_i]}{\text{Var}(\tau_i)}.
%\]
%If treatment effects are homogeneous we must have $\beta_2 = 0$. Rejecting this hypothesis establishes that $\tau_i$ predicts $\text{ATE}(X_i)$ and hence that $\Delta_i$ varies. 
%Since $\tau_i$ and $\psi_i$ do not depend on the test set, inference for the regression in \eqref{eq:chernreg} is straightforward conditional on the Training/Test split.  
%Our estimate for $\beta_2$ 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.

%\todo[inline]{Discuss the results here.}

%\todo[inline]{Issac: re-run this exercise with removing the propensity score weights $p(Z)$. Presumably it shouldn't change anything, but it's simpler to explain what we do and probably less noisy}

%\begin{table}[H]
%\begin{center}
%\scriptsize{\input{./Tables/test_calibration_2.tex}}
%\end{center}
%\end{table}

%\todo[inline]{Some Questions for Issac: (1) How are we carrying out the sample splitting? If we cluster standard errors at the branch-day level, we should take this into account when we split. (2) How are you carrying out inference for $\beta_2$? Chernozhukov et al discuss two approaches: ``conditional'' and ``variational.'' The former is simpler as it conditions on the training/test split. The latter is a bit more involved, since one accounts for uncertainty arising from different splits. (3) What are the details of the random forest procedure employed here? (Tuning parameters choice, etc.) We should put them into the appendix.}

%\newpage



\begin{figure}[!h]
    \caption{Fan \& Park bounds for benefit in APR\%}
    \label{fan_park_bounds}
    \begin{center}
    \begin{subfigure}{0.55\textwidth}
        \caption{APR}
        \centering
        \includegraphics[width=\textwidth]{Figuras/fan_park_bounds_apr.pdf}
    \end{subfigure}
    \end{center}
        \scriptsize
    This figure depicts the \cite{fan2010sharp} bounds on the distribution $F_\Delta$ of individual treatment effects $\Delta \equiv (Y_1 - Y_0)$, described in Section \ref{sec:bounds}, for the APR outcome.
    The dark red curve and light red shaded region give the estimated upper bound function $\overline{F}$ for $F_\Delta$ and associated (pointwise) 95\% confidence interval. 
    The dark blue curve and light blue shaded region give the estimated lower bound function $\underline{F}$ for $F_\Delta$ and associated (pointwise) 95\% confidence interval.
    Confidence intervals are computed using the asymptotic distribution for the bounds. See \cite{fan2010sharp} for details.
    The bounds are pointwise sharp: at any specified value of $\delta$ the bounds $\underline{F}(\delta) \leq F_\Delta(\delta) \leq \overline{F}(\delta)$ cannot be improved without imposing additional assumptions.
    Evaluating the bounds at $\delta = 0$, we see that between 23\% and 97\% of borrowers have a positive individual treatment effect.
    This is greater than the share of borrowers who chose commitment: 11\%.
%\textit{Do file: } \texttt{fan\_park\_bnds.do}       
\end{figure}



\begin{figure}[!h]
        \caption{Empirical CDF: Forced commitment vs Control FOSF}
    \label{ecdf_fc}
    \begin{center}
        \begin{subfigure}{0.49\textwidth}
         \caption{APR benefit}
         \centering
         \includegraphics[width=\textwidth]{Figuras/cdf_apr.pdf}
     \end{subfigure} 
   \begin{subfigure}{0.49\textwidth}
        \caption{Financial benefit}
        \centering
        \includegraphics[width=\textwidth]{Figuras/cdf_fc_admin.pdf}
    \end{subfigure} 
    \end{center}
    \scriptsize 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 $(\text{Control} - \text{Commitment})$. 
    %The dotted line at the bottom of panels (a) and (b)   the empirical cumulative distribution function APR and financial cost of financial cost. It does this separately for the fee-forcing contract and for the status-quo contract. The dotted line at the bottom is the difference of the control CDF minus the forced CDF arm. It shows that the CDF of the status quo contract is always below that of the fee-forcing (and this difference is significant for the points indicated by the blue line).
    % \texttt{fosd_ecdf.do}}
\end{figure}
   


\begin{figure}
        \caption{Distribution of treatment effects under rank invariance.}
    \label{te_rankinvariance}
    
    \begin{center}
       \begin{subfigure}{0.49\textwidth}
        \caption{APR benefit}
        \centering
        \includegraphics[width=\textwidth]{Figuras/te_rankinvariance_apr.pdf}
    \end{subfigure} 
   \begin{subfigure}{0.49\textwidth}
        \caption{Financial benefit}
        \centering
        \includegraphics[width=\textwidth]{Figuras/te_rankinvariance_fc_admin.pdf}
    \end{subfigure} 
    \end{center}
    \scriptsize This figure shows the CDF of individual treatment effects under the assumption of rank invariance, computed from 
    \[F_\Delta(\delta) = \int_0^1 \mathbbm{1}\{ F_1^{-1}(u) - F_0^{-1}(u)\leq \delta\}\,\mathrm{d}u\]
where $F_1^{-1}$ and $F_0^{-1}$ are the quantile functions of $Y_1$ and $Y_0$.
    %The dotted line at the bottom of panels (a) and (b)   the empirical cumulative distribution function APR and financial cost of financial cost. It does this separately for the fee-forcing contract and for the status-quo contract. The dotted line at the bottom is the difference of the control CDF minus the forced CDF arm. It shows that the CDF of the status quo contract is always below that of the fee-forcing (and this difference is significant for the points indicated by the blue line).
    % \texttt{te_rankinvariance.do}}
\end{figure}



\newpage



\section{ Derivations for Section \ref{sec:randchoice}}
\label{append:randchoice}


This appendix provides proofs of the results described in Section \ref{sec:randchoice}, using the notation and assumptions described in Section \ref{sec:potentialOutcomes}. 
To simplify the presentation, we omit $i$ subscripts throughout this section.
We also use the shorthand $Z_0 \equiv \mathbbm{1}(Z=0)$, $Z_1 \equiv \mathbbm{1}(Z=1)$, and $Z_2 \equiv\mathbbm{1}(Z=2)$.
For convenience, the following assumption collects our exclusion restriction and the key features of the constrained choice design.

\begin{assumption}\mbox{}
\label{assump:randchoice}
   \begin{enumerate}[(i)]
   \item $Z$ is independent of $(Y_{0}, Y_{1}, C)$
   \item $D = \mathbbm{1}(Z \neq 2)Z + \mathbbm{1}(Z = 2)C$
   \item $Y = \mathbbm{1}(Z = 0) Y_{0} + \mathbbm{1}(Z = 1) Y_{1} + \mathbbm{1}(Z = 2) [ (1 - C) Y_{0} + C Y_{1}]$
   \end{enumerate}
\end{assumption}


\subsection{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, $(\text{TOT} - \text{TUT})$, is likewise point identified. 

\begin{lem}
Under Assumption \ref{assump:randchoice},
\label{lem_randchoice}
   \begin{enumerate}[(i)]
       \item $\mathbbm{E}(D|Z=2) = \mathbb{P}(C=1)$
       \item $\mathbbm{E}(Y|Z=0) = \mathbbm{E}(Y_0)$
       \item $\mathbbm{E}(Y|Z=1) = \mathbbm{E}(Y_1)$
       \item $\mathbbm{E}(Y|D=0,Z=2) = \mathbbm{E}(Y_0|C=0)$
       \item $\mathbbm{E}(Y|D=1,Z=2) = \mathbbm{E}(Y_1|C=1)$.
   \end{enumerate} 
\end{lem}

\begin{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 $Y = Y_0$, given $Z=1$ we have $Y = Y_1$, and $Z$ is independent of $(Y_0,Y_1)$.
For parts (iv) and (v), first note that Assumption \ref{assump:randchoice} (iii) implies that $Z$ is conditionally independent of $(Y_0,Y_1)$ given $C$.
Now, $Z=2$ implies that $D=0$ if and only if $C=0$. Hence,
\[
\mathbbm{E}(Y|D=0, Z=2) = \mathbbm{E}(Y_0|D=0, Z=2) = \mathbbm{E}(Y_0|C=0, Z=2)=\mathbbm{E}(Y_0|C=0)
\]
establishing part (iv).
For part (v) $Z=2$ implies that $D=1$ if and only if $C=1$ and hence
\[
\mathbbm{E}(Y|D=1, Z=2) = \mathbbm{E}(Y_1|D=1, Z=2) = \mathbbm{E}(Y_1|C=1, Z=2)= \mathbbm{E}(Y_1|C=1). %\qedhere
\]
\end{proof}

\begin{prop} 
Under Assumption \ref{assump:randchoice},
    \begin{enumerate}[(i)]
        \item $\text{TOT} \equiv \mathbbm{E}(Y_1 - Y_0|C=1)  = \displaystyle \frac{\mathbbm{E}(Y|Z=2) - \mathbbm{E}(Y|Z=0)}{\mathbbm{E}(D|Z=2)}$
        \item $\text{TUT} \equiv \mathbbm{E}(Y_1 - Y_0|C=0) = \displaystyle \frac{\mathbbm{E}(Y|Z=1) - \mathbbm{E}(Y|Z=2)}{1 - \mathbbm{E}(D|Z=2)}$
        \item $\text{ASB} \equiv \mathbbm{E}(Y_0|C=1) - \mathbbm{E}(Y_0|C=0) = \displaystyle \frac{\mathbbm{E}(Y|Z=0) - \mathbbm{E}(Y|Z=2,D=0)}{\mathbbm{E}(D|Z=2)}$
        \item $\text{ASL} \equiv \mathbbm{E}(Y_1|C=1) - \mathbbm{E}(Y_1|C=0) = \displaystyle \frac{\mathbbm{E}(Y|Z=2,D=1) - \mathbbm{E}(Y|Z=1)}{1 - \mathbbm{E}(D|Z=2)}$.
    \end{enumerate}
\end{prop}

\begin{proof}
For parts (i) and (iii) we require an expression for $\mathbbm{E}(Y_0|C=1)$ in terms of the observables $(Y, D, Z)$.
By Lemma \ref{lem_randchoice}(ii) and iterated expectations 
\[
\mathbbm{E}(Y|Z=0) = \mathbbm{E}(Y_0) = \mathbbm{E}(Y_0|C=0) \mathbbm{P}(C=0) + \mathbbm{E}(Y_0|C=1) \mathbbm{P}(C=1).
\]
Re-arranging and substituting Lemma \ref{lem_randchoice}(i) and (iv),
\begin{align}
\mathbbm{E}(Y_0|C=1)  &= \frac{\mathbbm{E}(Y|Z=0) - \mathbbm{E}(Y_0|C=0) \mathbbm{P}(C=0)}{\mathbbm{P}(C=1)}\nonumber\\ 
&=  \frac{\mathbbm{E}(Y|Z=0) - \mathbbm{E}(Y|Z=2,D=0) \mathbbm{E}(1 - D|Z=2)}{\mathbbm{E}(D|Z=2)}.
\label{eq:Y0C1}
\end{align}
Part (i) follows by combining \eqref{eq:Y0C1} with Lemma \ref{lem_randchoice}(v) and simplifying; part (iii) follows by combining \eqref{eq:Y0C1} with Lemma \ref{lem_randchoice}(iv) and simplifying.
Similarly, for parts (ii) and (iv) we require an expression for $\mathbbm{E}(Y_1|C=0)$ in terms of observables.
By Lemma \ref{lem_randchoice}(iii) and iterated expectations,
\[
\mathbbm{E}(Y|Z=1) = \mathbbm{E}(Y_1) = \mathbbm{E}(Y_1|C=0)\mathbbm{P}(C=0) + \mathbbm{E}(Y_1|C=1) \mathbbm{P}(C=1).
\]
Re-arranging and substituting Lemma \ref{lem_randchoice}(i) and (v),
\begin{align}
\mathbbm{E}(Y_1|C=0) 
&= \frac{\mathbbm{E}(Y|Z=1) - \mathbbm{E}(Y_1|C=1)\mathbbm{P}(C=1)}{\mathbb{P}(D=0)} \nonumber\\
&=\frac{\mathbbm{E}(Y|Z=1) - \mathbbm{E}(Y|Z=2,D=1)\mathbbm{E}(D|Z=2)}{\mathbb{E}(1-D|Z=2)}.
\label{eq:Y1C0}
\end{align}
Part (ii) follows by combining \eqref{eq:Y1C0} with Lemma \ref{lem_randchoice}(iv) and simplifying; part (iv) follows by combining \eqref{eq:Y1C0} with Lemma \ref{lem_randchoice}(v) and simplifying.
\end{proof}

\subsection{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 to consistently estimate the ATE, TOT, and TUT effects, along with each of the ingredients needed 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.

\begin{prop} 
\label{prop:TOTreg}
Under Assumption \ref{assump:randchoice}, $Y = \mathbbm{E}(Y_0) + \text{ATE}\times Z_1 + \text{TOT} \times Z_2 D + U$ where $\mathbb{E}(U|Z) = 0$.
Therefore, under standard regularity conditions, an IV regression of $Y$ on an intercept, $Z_1$ and $Z_2 D$ with instruments $(1, Z_0, Z_1)$ consistently estimates the ATE and TOT. 
\end{prop}

\begin{proof}
By Assumption \ref{assump:randchoice} (iii),
\begin{align*}
Y &= Z_0 Y_0 + Z_1 Y_1 + Z_2[(1 - C) Y_0 + CY_1] = (Z_0 + Z_2)Y_0 + Z_1 Y_1 + Z_2C(Y_1 - Y_0)\\
&= (Z_0 + Z_1 + Z_2)Y_0 + Z_1 (Y_1 - Y_0) + Z_2D(Y_1 - Y_0) = Y_0 + Z_1 (Y_1 - Y_0) + Z_2D(Y_1 - Y_0).
\end{align*}
since $Z_2 D = Z_2 C$ and $(Z_0 + Z_1 + Z_2) = 1$.
Thus, defining 
\[
U \equiv [Y_0 - \mathbbm{E}(Y_0)] + Z_1[(Y_1 - Y_0) - \text{ATE}] + Z_2 D[(Y_1 - Y_0) - \text{TOT}]
\]
by construction we have $Y = \mathbbm{E}(Y_0) + \text{ATE} \times Z_1 + \text{TOT} \times Z_2 D+ U$.
Now, since $Z_2 D = Z_2 C$ and $Z$ is independent of $(Y_1, Y_0)$ by Assumption \ref{assump:randchoice} (i), we have
\begin{align*}
\mathbbm{E}(U|Z) &= [\mathbbm{E}(Y_0|Z) - \mathbbm{E}(Y_0)]  + Z_1[\mathbbm{E}(Y_1 - Y_0|Z) - \text{ATE}] +  \mathbbm{E}\left[Z_2 D\left\{(Y_1 - Y_0) - \text{TOT}\right\}|Z\right]\\
&= [\mathbbm{E}(Y_0) - \mathbbm{E}(Y_0)]  + Z_1[\mathbbm{E}(Y_1 - Y_0) - \text{ATE}] + Z_2 \mathbbm{E}\left[C\left\{(Y_1 - Y_0) - \text{TOT}\right\}|Z\right]\\
&= Z_2 \mathbbm{E}\left[C\left\{(Y_1 - Y_0) - \text{TOT}\right\}|Z\right].
\end{align*}
Finally, by iterated expectations
\begin{align*}
\mathbbm{E}\left[C\left\{(Y_1 - Y_0) - \text{TOT}\right\}|Z\right] &=  \mathbbm{P}(C=1|Z) \left[\mathbbm{E}(Y_1 - Y_0|C=1,Z)  - \text{TOT}\right]\\
&= \mathbbm{P}(C=1)\left[\mathbbm{E}(Y_1 - Y_0|C=1) - \text{TOT} \right]=0
\end{align*}
since $Z$ is conditionally independent of $(Y_0, Y_1)$ given $C$, an implication of \ref{assump:randchoice} (i).
\end{proof}

%The next proposition provides regression-based estimates of the ATE and TUT.
\begin{prop}
\label{prop:TUTreg}
Under Assumption \ref{assump:randchoice} $Y = \mathbbm{E}(Y_1) + \text{ATE}\times -Z_0 + \text{TUT} \times -Z_2 (1 - D) + V$ where $\mathbb{E}(V|Z) = 0$.
Therefore, under standard regularity conditions, an IV regression of $Y$ on an intercept, $-Z_0$ and $-Z_2(1-D)$ with instruments $(1, Z_0, Z_1)$ provides consistent estimates of the ATE and TUT effects.
\end{prop}

\begin{proof}
By Assumption \ref{assump:randchoice} (iii),
\begin{align*}
Y &= Z_0 Y_0 + Z_1 Y_1 + Z_2[(1 - C) Y_0 + CY_1] = Z_0 Y_0 + Z_1 Y_1 + Z_2[(1 - C) (Y_0 - Y_1) + Y_1]\\
&= Z_0 Y_0 + (Z_1 + Z_2) Y_1 + Z_2(1 - C) (Y_0 - Y_1) = Z_0 Y_0 + (1 - Z_0) Y_1 + Z_2(1 - D) (Y_0 - Y_1) \\
&= Y_1 - Z_0 (Y_1 - Y_0) - Z_2(1 - D) (Y_1 - Y_0)
\end{align*}
since $Z_2(1 - C)= Z_2(1 - D)$ and $(Z_1 + Z_2) = 1 - Z_0$.
Thus, defining 
\[
V \equiv [Y_1 - \mathbb{E}(Y_1)] - Z_0[(Y_1 - Y_0) - \text{ATE}] - Z_2(1 - D)[(Y_1 - Y_0) - \text{TUT}]
\]
by construction we have $Y = \mathbb{E}(Y_1) + \text{ATE} \times -Z_0 + \text{TUT} \times -Z_2(1 - D) + V$.
Now, since $Z_2(1 - D) = Z_2 (1 - C)$ and $Z$ is independent of $(Y_0, Y_1)$ by Assumption \ref{assump:randchoice} (i),
\begin{align*}
\mathbb{E}(V|Z) &= [\mathbb{E}(Y_1|Z) - \mathbb{E}(Y_1)] - Z_0[\mathbb{E}(Y_1 - Y_0|Z) - \text{ATE}] - \mathbb{E}[Z_2(1 - D)\left\{(Y_1 - Y_0) - \text{TUT}\right\}|Z]\\
&= [\mathbb{E}(Y_1) - \mathbb{E}(Y_1)] - Z_0[\mathbb{E}(Y_1 - Y_0) - \text{ATE}] - Z_2\mathbb{E}[(1 - C)\left\{(Y_1 - Y_0) - \text{TUT}\right\}|Z]\\
&= -Z_2\mathbb{E}[(1 - C)\left\{(Y_1 - Y_0) - \text{TUT}\right\}|Z].
\end{align*}
Finally, by iterated expectations,
\begin{align*}
\mathbb{E}[(1 - C)\left\{(Y_1 - Y_0) - \text{TUT}\right\}|Z]&= \mathbb{P}(C=0|Z)\left[ \mathbb{E}(Y_1 - Y_0|C=0, Z) - \text{TUT}\right]\\
&= \mathbb{P}(C=0|Z) \left[ \mathbb{E}(Y_1 - Y_0|C=0) - \text{TUT}\right] = 0
\end{align*}
since $Z$ is conditionally independent of $(Y_0, Y_1)$ given $C$, an implication of Assumption \ref{assump:randchoice} (i).
\end{proof}

Since $\text{ASG} = \text{TOT} - \text{TUT}$, the preceding two propositions provide consistent estimates of $\text{ASG}$ effect.
The $\text{ASB}$ effect, $\mathbbm{E}(Y_0|C=1) - \mathbb{E}(Y_0|C=0)$, can likewise be estimated by taking the difference of coefficients across two linear IV regressions. %as shown in the following proposition.

\begin{prop}
\label{prop:ASBreg}
Under Assumption \ref{assump:randchoice}
\begin{align}
\label{eq:ASB0}
    (1 - D) Y &= \mathbbm{E}(Y_{0}) \times Z_0 + \mathbbm{E}(Y_{0}|C=0) \times (1 - D)Z_2 + U_{0}\\
\label{eq:ASB1}
    (1 - D) Y &= \mathbbm{E}(Y_{0}) \times(Z_0 + Z_2) + \mathbbm{E}(Y_{0}|C=1)\times -DZ_2 + U_{1}
\end{align}
where $\mathbbm{E}(U_0|Z) = \mathbbm{E}(U_1|Z) = 0$.
Thus, under standard regularity conditions, an IV regression of $(1 - D)Y$ on $Z_0$ and $(1 - D)Z_2$ with instruments $(Z_0, Z_2)$ and no intercept consistently estimates $\mathbb{E}(Y_0)$ and $\mathbb{E}(Y_0|C=0)$. 
Similarly, an IV regression of $(1 - D)Y$ on $(Z_0 + Z_2)$ and $-DZ_2$ with instruments $(Z_0, Z_2)$ and no intercept consistently estimates $\mathbb{E}(Y_0)$ and $\mathbb{E}(Y_0|C=1)$.
\end{prop}

\begin{proof}
Assumption \ref{assump:randchoice} (ii) implies $(1 - D) = Z_0 + Z_2(1 - C)$. Hence, by Assumption \ref{assump:randchoice} (iii),
\begin{align*}
(1 - D)Y &=  [Z_0 + Z_2 (1 - C)]\left\{Z_0 Y_0 + Z_1 Y_1 + Z_2[(1 - C) Y_0 + CY_1]\right\}\\
&= Z_0 Y_0 + Z_2 (1 - C) [(1 - C) Y_0 + C Y_1] = Z_0 Y_0 + Z_2 (1 - C) Y_0.
\end{align*}
because $Z_j^2 = Z_j$ for any $j$ and $Z_j Z_k = 0$ for any $j \neq k$ and, similarly, $(1 - C)^2 = (1 - C)$ and $C (1 - C) = 0$.
Therefore, since $Z_2 (1 - C) = Z_2 (1 - D)$,
\[
(1 - D)Y = Z_0 Y_0 + Z_2 (1 - D) Y_0, \quad
(1 - D)Y = (Z_0 + Z_2) Y_0 + (-DZ_2) Y_0. 
\]
Now, defining
\begin{align*}
U_0 &\equiv Z_0 [Y_0 - \mathbbm{E}(Y_0)] + Z_2(1 - D)[Y_0 - \mathbbm{E}(Y_0|C=0)]\\
U_1 &\equiv (Z_0 + Z_2)[Y_0 - \mathbbm{E}(Y_0)] + (-Z_2 D)[Y_0 - \mathbbm{E}(Y_0|C=1)]
\end{align*}
by construction, we have
\begin{align*}
Y &= \mathbbm{E}(Y_0) \times Z_0 + \mathbbm{E}(Y_0|C=0) \times Z_2(1 - D) + U_0\\
Y &= \mathbbm{E}(Y_0) \times (Z_0 + Z_2)+ \mathbbm{E}(Y_0|C=1) (-Z_2D) + U_1.
\end{align*}
Finally, since $Z_2(1-D) = Z_2(1 - C)$, and $Z$ is independent of $Y_0$,  
\begin{align*}
\mathbbm{E}(U_0|Z) &= Z_0[\mathbbm{E}(Y_0|Z) - \mathbbm{E}(Y_0)] + Z_2\mathbbm{E}\{(1 - C) [Y_0 - \mathbbm{E}(Y_0|C=0) |Z\}\\
&= Z_2 \mathbbm{E}[Y_0 - \mathbbm{E}(Y_0|C=0) | C = 0, Z] = 0
\end{align*}
where the final two steps follow by iterated expectations and the fact that  $Z$ is conditionally independent of $Y_0$ given $C$. 
Since $Z_2 D = Z_2 C$, a nearly identical argument gives
\begin{align*}
\mathbbm{E}(U_1|Z) &= (Z_0 + Z_2)[Y_0 - \mathbbm{E}(Y_0|Z)] -Z_2\mathbbm{E}\{C [Y_0 - \mathbbm{E}(Y_0|C=1) |Z\}\\
&= -Z_2 \mathbbm{E}[Y_0 - \mathbbm{E}(Y_0|C=0) | C = 1, Z] = 0. \qedhere
\end{align*}
\end{proof}


The next result shows that the $\text{ASL}$ effect, $\mathbbm{E}(Y_1|C=1) - \mathbb{E}(Y_1|C=0)$, can be estimated as the difference of coefficients across two linear IV regressions.

\begin{prop}
\label{prop:ASLreg}
Under Assumption \ref{assump:randchoice},
\begin{align}
\label{eq:ASL0}
    D Y &= \mathbbm{E}(Y_{1}) \times(Z_1 + Z_2) + \mathbbm{E}(Y_{1}|C=0)\times (D - 1)Z_2 + V_{0}\\
\label{eq:ASL1}
    D Y &= \mathbbm{E}(Y_{1}) \times Z_1 + \mathbbm{E}(Y_{1}|C=1)\times D Z_2+ V_{1}
\end{align}
where $\mathbbm{E}(V_0|Z) = \mathbbm{E}(V_1|Z) = 0$.
Thus, under standard regularity conditions, an IV regression of $DY$ on $(Z_1 + Z_2)$ and $-Z_2(1 - D)$ with instruments $(Z_1, Z_2)$ and no intercept provides consistent estimates of $\mathbb{E}(Y_1)$ and $\mathbb{E}(Y_1|C=1)$.
Similarly, an IV regression of $DY$ on $Z_1$ and $DZ_2$ with instruments $(Z_1, Z_2)$ and no intercept provides consistent estimates of $\mathbb{E}(Y_1)$ and $\mathbb{E}(Y_1|C=1)$. 
\end{prop}


\begin{proof}
By Assumption \ref{assump:randchoice}, $D = Z_1 + Z_2 C$. Hence, by Assumption \ref{assump:randchoice} (iii),
\begin{align*}
DY &=  (Z_1 + Z_2 C)\left\{Z_0 Y_0 + Z_1 Y_1 + Z_2[(1 - C) Y_0 + CY_1]\right\}\\
&= Z_1 Y_1 + Z_2 C[(1 -C) Y_0 + C Y_1] = Z_1 Y_1 + Z_2 C Y_1
\end{align*}
because $Z_j^2 = Z_j$ for any $j$ and $Z_j Z_k = 0$ for any $j \neq k$ and, similarly, $(1 - C)^2 = (1 - C)$ and $C (1 - C) = 0$. Therefore, since $Z_2 (1 - C) = Z_2 (1 - D)$,
\[
 DY = (Z_1 + Z_2)Y_1 + Z_2 (D - 1) Y_1, \quad
 DY = Z_1 Y_1 + Z_2 D Y_1.
\]
Now, defining
\begin{align*}
V_0 &= (Z_1 + Z_2)[Y_1 - \mathbbm{E}(Y_1)] + Z_2(D - 1)[Y_1 - \mathbbm{E}(Y_1|C=0)]\\
V_1 &= Z_1[Y_1 - \mathbbm{E}(Y_1)] + Z_2D[Y_1 - \mathbbm{E}(Y_1|C=1)]
\end{align*}
by construction we have
\begin{align*}
Y &= \mathbbm{E}(Y_1) \times (Z_1 + Z_2) + \mathbbm{E}(Y_1 | C = 0) \times Z_2 (D - 1) + V_0\\
Y &= \mathbbm{E}(Y_1) \times Z_1 + \mathbbm{E}(Y_1 | C = 1) \times Z_2 D + V _1.
\end{align*}
Finally, since $Z_2(1 - D) = Z_2(1 - C)$ and $Z$ is independent of $Y_1$,
\begin{align*}
\mathbbm{E}(V_0|Z) &= (Z_1 + Z_2) [\mathbbm{E}(Y_1|Z) - \mathbbm{E}(Y_1) ]  - Z_2 \mathbbm{E}\{(1 - C)  [Y_1 - \mathbbm{E}(Y_1 | C=0)|Z\} \\
&= -Z_2 \mathbbm{E}[Y_1 - \mathbbm{E}(Y_1 | C=0)|C=0, Z] = 0
\end{align*}
where the final two steps follow by iterated expectations and the fact that  $Z$ is conditionally independent of $Y_1$ given $C$. 
Since $Z_2 D = Z_2 C$, a nearly identical argument gives
\begin{align*}
\mathbbm{E}(V_1|Z) &= Z_1 [\mathbbm{E}(Y_1 | Z) - \mathbbm{E}(Y_1)]  + Z_2 \mathbbm{E}\{C  [Y_1 - \mathbbm{E}(Y_1 | C=1)|Z\} \\
&= Z_2 \mathbbm{E}[Y_1 - \mathbbm{E}(Y_1 | C=1)|C=1, Z] = 0. \qedhere
\end{align*}
\end{proof}




\subsection{Inference for ASG, ASB, and ASL}
\label{subsec:inference}
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 can be expressed as a difference of coefficients from two just-identified linear IV regressions.
The ASG effect is the difference of the \text{TOT} effect from Proposition \ref{prop:TOTreg} and the \text{TUT} effect from Proposition \ref{prop:TUTreg}.
Similarly, the ASB effect is the difference of $\mathbb{E}(Y_0|C=1)$ and $\mathbbm{E}(Y_0|C=0)$ from Proposition \ref{prop:ASBreg} while the ASL effect is the difference of $\mathbbm{E}(Y_1|C=1)$ and $\mathbbm{E}(Y_1|C=0)$ from Proposition \ref{prop:ASLreg}.
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 the specific 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 $i = 1, ..., N_g$ index individuals within a particular cluster $g$. 
In our experiment, a cluster is a branch-day combination and the experimentally-assigned treatment (control, forced, or choice arm) is assigned at the cluster level.
We assume that observations are iid across clusters but potentially correlated within cluster.
Now consider a pair of just-identified linear IV regressions given by
\[
Y_{ig} = \boldsymbol{X}_{1,ig}' \boldsymbol{\theta}_0 + U_{ig}, \quad
Y_{ig} = \boldsymbol{X}_{0,ig}' \boldsymbol{\theta}_1 + V_{ig}
\]
with common instrument vector $\boldsymbol{W}_{ig}$. 
Stacking observations in the usual manner, e.g.\
\[
\mathbf{W}_g' \equiv \begin{bmatrix}
\boldsymbol{W}_{1g} & \cdots & 
\boldsymbol{W}_{N_gg} 
\end{bmatrix}, \quad
\mathbf{W}' = \begin{bmatrix}
\mathbf{W}_1' & \cdots & \mathbf{W}_G'
\end{bmatrix},
\]
we can write the preceding equations in matrix form as
\[
\mathbf{Y} = \mathbf{X}_1\boldsymbol{\theta_1} + \mathbf{U}, \quad
\mathbf{Y} = \mathbf{X}_0\boldsymbol{\theta_0} + \mathbf{V}
\]
with instrument matrix $\mathbf{W}$.
Now, the IV estimators for $\boldsymbol{\theta}_1$ and $\boldsymbol{\theta}_0$ can be expressed as 
\begin{align*}
\widehat{\boldsymbol{\theta}}_1 
&= \left(\mathbf{W}'\mathbf{X}_1\right)^{-1}\mathbf{W}'\mathbf{Y}  = \boldsymbol{\theta}_1 + \left(\mathbf{W}'\mathbf{X}_1\right)^{-1}\mathbf{W}'\mathbf{U}\\ 
\widehat{\boldsymbol{\theta}}_0 
&= \left(\mathbf{W}'\mathbf{X}_0\right)^{-1}\mathbf{W}'\mathbf{Y} = \boldsymbol{\theta}_0 + \left(\mathbf{W}'\mathbf{X}_0\right)^{-1}\mathbf{W}'\mathbf{V}.
\end{align*}
Our parameter of interest is an element of the difference $(\theta_1 - \theta_0)$, so  it suffices to calculate the asymptotic distribution of $(\widehat{\boldsymbol{\theta}}_1 - \widehat{\boldsymbol{\theta}}_0)$.
Re-arranging the preceding two equations, we have
\begin{align*}
\sqrt{G} \left(\widehat{\boldsymbol{\theta}}_1  - \boldsymbol{\theta}_1\right) &= 
 \left(\frac{\mathbf{W}'\mathbf{X}_1}{G}\right)^{-1}\left(\frac{\mathbf{W}'\mathbf{U}}{\sqrt{G}}\right) = \left( \frac{1}{G} \sum_{g=1}^G \mathbf{W}_g' \mathbf{X}_{1,g}\right)^{-1}\left(\frac{1}{\sqrt{G}} \sum_{g=1}^G\mathbf{W}_g' \mathbf{U}_g\right) \\ 
\sqrt{G} \left(\widehat{\boldsymbol{\theta}}_0  - \boldsymbol{\theta}_0\right) &= 
 \left(\frac{\mathbf{W}'\mathbf{X}_0}{G}\right)^{-1}\left(\frac{\mathbf{W}'\mathbf{V}}{\sqrt{G}}\right) = \left( \frac{1}{G} \sum_{g=1}^G \mathbf{W}_g' \mathbf{X}_{0,g}\right)^{-1}\left(\frac{1}{\sqrt{G}} \sum_{g=1}^G\mathbf{W}_g' \mathbf{V}_g\right).
\end{align*}
Now, define $\mathbf{Q}_0 \equiv \mathbb{E}[\mathbf{W}_g'\mathbf{X}_{0g}]$ and $\mathbf{Q}_1 \equiv \mathbb{E}[\mathbf{W}_g'\mathbf{X}_{1g}]$ and suppose that these expectations exist and that the matrices $\mathbf{Q}_0$ and $\mathbf{Q}_1$ are invertible. Then, as $G \rightarrow \infty$
\[
 \left( \frac{1}{G} \sum_{g=1}^G \mathbf{W}_g' \mathbf{X}_{0,g}\right)^{-1} \rightarrow_p \mathbf{Q}_0^{-1}, \quad
 \left( \frac{1}{G} \sum_{g=1}^G \mathbf{W}_g' \mathbf{X}_{1,g}\right)^{-1} \rightarrow_p \mathbf{Q}_1^{-1} \quad
\]
by the continuous mapping theorem.
Now, by our experimental design and exclusion restriction, $\mathbf{W}_{ig}$ is independent of $U_{ig}$ both unconditionally and conditional on cluster size. 
Therefore,
\begin{align*}
\mathbb{E}[\mathbf{W}_g' \mathbf{U}_g] &=  \mathbb{E}\left[ \sum_{i=1}^{N_g} \mathbf{W}_{ig} U_{ig} \right] = \mathbb{E}_{N_g}\left[ \mathbb{E}\left\{\left. \sum_{i=1}^{N_g} \mathbf{W}_{ig} U_{ig} \right| N_g \right\}\right]\\
&= \mathbb{E}_{N_g}\left[ \sum_{i=1}^{N_g} \mathbb{E}(\mathbf{W}_{ig} U_{ig}|N_g)\right] = \mathbb{E}_{N_g}\left[ \sum_{i=1}^{N_g} \mathbb{E}(\mathbf{W}_{ig}U_{ig})\right] = 0
\end{align*}
by iterated expectations, and similarly smilarly, $\mathbb{E}[\mathbf{W}_g'\mathbf{V}_g] = \mathbf{0}$. 
Thus, under mild regularity conditions (e.g.\ finite fourth moments), as $G \rightarrow \infty$  we have
\[
\frac{1}{\sqrt{G}} \sum_{g=1}^G \mathbf{W}_g' \otimes \begin{bmatrix} \mathbf{U}_g \\ \mathbf{V}_g \end{bmatrix} \rightarrow_d \text{N}(\mathbf{0}, \boldsymbol{\Omega})
\]
where the heteroskedasticity-- and cluster--robust variance-covariance matrix $\boldsymbol{\Omega}$ is defined as
\[
\boldsymbol{\Omega} \equiv 
 \mathbb{E} \left[\left(\mathbf{W}_g \mathbf{W}_g' \right)\otimes \begin{pmatrix}
\mathbf{U}_g \mathbf{U}_g' & \mathbf{U}_g \mathbf{V}_g' \\
\mathbf{V}_g \mathbf{U}_g' & \mathbf{V}_g \mathbf{V}_g'  
\end{pmatrix} \right] \equiv \begin{bmatrix}
\Omega_{UU} & \Omega_{UV} \\
\Omega_{VU} & \Omega_{VV}
\end{bmatrix}.
\]
Therefore, the joint limiting distribution of $\widehat{\boldsymbol{\theta}}_1$ and $\widehat{\boldsymbol{\theta}}_0$ is given by
\[
\begin{bmatrix}
\sqrt{G}(\widehat{\boldsymbol{\theta}}_1 - \boldsymbol{\theta}_1)\\
\sqrt{G}(\widehat{\boldsymbol{\theta}}_0 - \boldsymbol{\theta}_0)
\end{bmatrix} \rightarrow_d
\begin{bmatrix}
\mathbf{Q}_1^{-1} & \mathbf{0} \\
\mathbf{0} & \mathbf{Q}_0^{-1} 
\end{bmatrix}
\begin{bmatrix}
\boldsymbol{\xi}_U \\ \boldsymbol{\xi}_V 
\end{bmatrix}, \quad
\begin{bmatrix}
\boldsymbol{\xi}_U \\ \boldsymbol{\xi}_V 
\end{bmatrix} \sim \text{N}\left(\begin{bmatrix} \mathbf{0} \\ \mathbf{0}\end{bmatrix},
\begin{bmatrix}
\Omega_{UU} & \Omega_{UV} \\
\Omega_{VU} & \Omega_{VV}
\end{bmatrix}\right)
\]
from which it follows by the continuous mapping theorem that
\[
\sqrt{G}\left[ (\widehat{\boldsymbol{\theta}}_1 - \widehat{\boldsymbol{\theta}}_0 ) - (\boldsymbol{\theta}_1 - \boldsymbol{\theta}_0)\right] 
\rightarrow_d
\begin{bmatrix}
\mathbf{Q}_1^{-1} & -\mathbf{Q}_0^{-1}
\end{bmatrix}
\begin{bmatrix}
\boldsymbol{\xi}_U \\ \boldsymbol{\xi}_V 
\end{bmatrix}.
\]
To use this result in practice, we estimate the standard errors of  $(\widehat{\boldsymbol{\theta}}_1 - \widehat{\boldsymbol{\theta}}_0)$ as the square root of the diagonal elements of the matrix
\[
\widehat{\text{Avar}}(\widehat{\boldsymbol{\theta}}_1 - \widehat{\boldsymbol{\theta}}_0) 
= \begin{bmatrix}
\left(\mathbf{W}'\mathbf{X}_1\right)^{-1} &
-\left(\mathbf{W}'\mathbf{X}_0\right)^{-1} 
\end{bmatrix}
\begin{bmatrix}
\mathbf{S}_{UU}& \mathbf{S}_{UV}\\
\mathbf{S}_{VU}& \mathbf{S}_{VV}
\end{bmatrix} 
\begin{bmatrix}
\left(\mathbf{X}_1'\mathbf{W}\right)^{-1} \\
-\left(\mathbf{X}_0'\mathbf{W}\right)^{-1} 
\end{bmatrix}
\]
where
\[
\mathbf{S}_{UU} \equiv \sum_{g=1}^G \mathbf{W}_g' \widehat{\mathbf{U}}_g \widehat{\mathbf{U}}_g' \mathbf{W}_g, \quad
\mathbf{S}_{UV} \equiv \sum_{g=1}^G \mathbf{W}_g' \widehat{\mathbf{U}}_g \widehat{\mathbf{V}}_g' \mathbf{W}_g, \quad
\mathbf{S}_{VU} \equiv \mathbf{S}_{UV}', \quad
\mathbf{S}_{VV} \equiv \sum_{g=1}^G \mathbf{W}_g' \widehat{\mathbf{V}}_g \widehat{\mathbf{V}}_g' \mathbf{W}_g
\]
and we define the IV residuals
\[
\widehat{\mathbf{U}}_g \equiv \mathbf{Y}_g - \mathbf{X}_{1,g}\widehat{\boldsymbol{\theta}}_1, \quad
\widehat{\mathbf{V}}_g \equiv \mathbf{Y}_g - \mathbf{X}_{0,g}\widehat{\boldsymbol{\theta}}_0.
\]
In our application the number of clusters, $G$, is large.
If desired, an \emph{ad hoc} degrees of freedom correction can be applied by multiplying the standard errors by $\sqrt{G/(G-1)}$.


\section{Testing the Exclusion Restriction}
\label{append:exclusion}

\normalsize
\linespread{1.05}
%Really force it to normal size and linespread
\normalsize
\linespread{1.05}

This section describes the testable implications of our exclusion restrictions: \eqref{eq:exclusion0} and \eqref{eq:exclusion1} from Section \ref{sec:potentialOutcomes}. 
To consider possible violations of these conditions, it is helpful to introduce some additional notation.
As above, let $Y_0 \equiv Y(d=0,z=0)$ and $Y_1 \equiv Y(d=1,z=1)$ denote the potential outcomes under \emph{forced treatment}: $Y_0$ is the potential outcome when forced into the status quo contract and $Y_1$ when forced into the commitment contract. 
Further let $Y_{0,2} \equiv Y(d=0,z=2)$ and $Y_{1,2} \equiv Y(d=1,z=2)$ denote the potential outcomes under \emph{free choice of treatment}: $Y_{0,2}$ is the potential outcome when choosing the status quo contract and $Y_{1,2}$ when choosing the commitment contract. 
Using this notation, \eqref{eq:exclusion0} becomes $Y_0 = Y_{0,2}$ and while \eqref{eq:exclusion1} becomes $Y_1 = Y_{1,2}$.
Without imposing these, part (iii) of Assumption \ref{assump:randchoice} becomes 
\[
Y = \mathbbm{1}(Z =0) Y_{0} + \mathbbm{1}(Z = 1)  Y_{1}  + \mathbbm{1}(Z = 2) \left[(1 - C) Y_{0,2} + C Y_{1,2} \right]
\]
but parts (i) and (ii) continue to hold.
Accordingly, parts (i)--(iii) of Lemma \ref{lem_randchoice} are unchanged, while parts (iv) and (v) become
\[
\mathbbm{E}(Y|D=0,Z=2) = \mathbbm{E}(Y_{0,2}|C=0), \quad
\mathbbm{E}(Y|D=1,Z=2) = \mathbbm{E}(Y_{0,1}|C=1).
\]
Using these expressions, the testable restrictions we consider here are as follows:
\begin{align}
\label{eq:exclusion_append0}
\mathbbm{E}(Y_0|C=0) &= \mathbbm{E}(Y_{0,2}|C=0) \\
\label{eq:exclusion_append1}
\mathbbm{E}(Y_1|C=1) &= \mathbbm{E}(Y_{1,2}|C=1).
\end{align}
Equation \ref{eq:exclusion_append0} 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 \emph{would} choose the control condition when given a choice, experiences the same potential outcome, on average, when \emph{assigned} to the control condition.
Equation \ref{eq:exclusion_append1} is a restriction on the average potential outcomes of choosers that we use to point identify the TOT effect.
It says that someone who \emph{would} choose the commitment contract when given a choice, experiences the same potential outcome, on average, when \emph{assigned} to this condition.
Because they refer to different groups of people, either of \eqref{eq:exclusion_append0}  and \eqref{eq:exclusion_append1} could hold when the other is violated.
For this reason we consider each in turn.
Our approach is closely related to arguments from \cite{huber_mellace} and \cite{BinaryRegressor}, among others.
%As such, the following is a heuristic explanation rather than a fully-rigorous proof.
%See the aforementioned papers for more details of how to make this argument fully rigorous.

Consider first \eqref{eq:exclusion_append0}.
Let $p \equiv \mathbbm{P}(C=1) = \mathbbm{P}(D=1|Z=2)$ denote the share of choosers 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 $Y_0|C=0$ and $Y_0|C=1$ with mixing weights $(1-p)$ and $p$.
This allows us to construct a pair of bounds for $\mathbb{E}(Y_0|C=0)$ as follows.
The non-choosers must lie \emph{somewhere} in the distribution of $Y|Z=0$.
Consider the two most extreme possibilities: they could occupy the bottom $(1-p)\times 100\%$ of the distribution or the top $(1-p)\times 100\%$ of the distribution.
For this reason, computing the average of the \emph{truncated} distribution of $Y|Z=0$, cutting out the top $p\times 100\%$, provides a lower bound for the average of $Y_0$ among non-choosers.
Similarly, cutting out the bottom $p \times 100\%$ provides an upper bound.
Let $y^0_{1-p}$ denote the $(1-p)$ quantile of $Y|Z=0$ and $y^0_{p}$ denote the $p$ quantile of the same distribution.
Using this notation, the bounds are given by
\[
\mathbb{E}\left(Y|Z=0, Y\leq y^0_{1-p}\right)\leq \mathbb{E}(Y_0|C=0) \leq \mathbb{E}\left(Y|Z=0, Y \geq y^0_p\right) 
\]
These bounds do not rely on the exclusion restriction.
Under Equation \ref{eq:exclusion_append0}, however, we know that $\mathbb{E}(Y_0|C=0)=\mathbb{E}(Y|D=0,Z=2)$.
Therefore, if the exclusion restriction for non-choosers holds, we must have
\begin{equation}
\mathbb{E}\left(Y|Z=0, Y\leq y^0_{1-p}\right)\leq \mathbb{E}(Y|D=0,Z=2) \leq \mathbb{E}\left(Y|Z=0, Y \geq y^0_p\right).
\label{eq:testable0}
\end{equation}
Equation \ref{eq:testable0} provides a pair of testable implications of \eqref{eq:exclusion_append0}.
If either inequality is violated, then the exclusion restriction for non-choosers fails.
In our experiment, $\widehat{p} = \widehat{\mathbbm{P}}(D=1|Z=2) = 0.11$. For the APR outcome we estimate
\[
\widehat{\mathbbm{E}}(Y_\text{APR}|Z=0,Y_\text{APR}\leq y^0_{0.89}) = 0.48, \quad
\widehat{\mathbbm{E}}(Y_\text{APR}|Z=0, Y_\text{APR}\geq y^0_{0.11}) = 0.62.
\]
Since $\widehat{\mathbbm{E}}(Y_\text{APR}|D=0,Z=2) = 0.58$ falls between these bounds, we find no evidence against the exclusion restriction for non-choosers. 
Repeating this exercise for the financial cost outcome, we see that $\widehat{\mathbbm{E}}(Y_\text{FC}|D=0,Z=2) = 973$ likewise falls between 
\[
\widehat{\mathbbm{E}}(Y_\text{FC}|Z=0,Y_\text{FC}\leq y^0_{0.89}) = 626, \quad
\widehat{\mathbbm{E}}(Y_\text{FC}|Z=0, Y_\text{FC}\geq y^0_{0.11}) = 1046 
\]
so we again find no evidence against the exclusion restriction for non-choosers.

We can use an analogous approach to construct testable implications for \ref{eq:exclusion_append1}. 
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 $Y_1|C=1$ and $Y_1|C=0$ with mixing weights $p$ and $1 -p$.
The participants with $C = 1$ must lie \emph{somewhere} in the distribution of $Y_0|Z=1$ so again consider the two most extreme cases: they could occupy the bottom or the top $p\times 100\%$ of the distribution. 
Hence,
\[
\mathbbm{E}\left(Y|Z=1,Y\leq y^1_{p}\right) \leq \mathbbm{E}(Y_1|C=1) \leq \mathbbm{E}\left(Y|Z=1,Y \geq y^1_{1-p}\right)
\]
where $y^1_p$ and $y^1_{1-p}$ are the $p$ and $1 - p$ quantiles of the distribution of $Y|Z=1$.
As above, these bounds do not rely on the exclusion restriction.
If Equation \ref{eq:exclusion_append1} holds, however, we know that $\mathbb{E}(Y|D=1,Z=2) = \mathbb{E}(Y_1|C=1)$, yielding the following testable implications for choosers
\begin{equation}
\mathbbm{E}\left(Y|Z=1,Y\leq y^1_{p}\right) \leq \mathbbm{E}(Y|D=1,Z=2) \leq \mathbbm{E}\left(Y|Z=1,Y \geq y^1_{1-p}\right).
\label{eq:testable1}
\end{equation}
If either inequality is violated, then the exclusion restriction from Equation \ref{eq:exclusion_append1} fails.
Again, in our experiment $\widehat{p}=0.11$. For the APR outcome we estimate
\[
\widehat{\mathbbm{E}}(Y|Z=1,Y\leq y^1_{0.11}) = 0.06, \quad
\widehat{\mathbbm{E}}(Y|Z=1,Y\geq y^1_{0.89}) = 1.28
\]
Since $\widehat{\mathbbm{E}}(Y_\text{APR}|D=1,Z=2) = 0.43$ falls between these bounds, we find no evidence against the exclusion restriction for the choosers. 
Repeating this exercise for the financial cost outcome, we see  that $\widehat{\mathbbm{E}}(Y_\text{FC}|D=1,Z=2)= 570$ likewise falls between
\[
\widehat{\mathbbm{E}}(Y|Z=1,Y\leq y^1_{0.11}) = 53, \quad
\widehat{\mathbbm{E}}(Y|Z=1,Y\geq y^1_{0.89}) = 2934
\]
so we again find no evidence against the exclusion restriction for the choosers.

The aforementioned bounds for $\mathbbm{E}(Y_0|C=0)$ and $\mathbbm{E}(Y_1|C=1)$ 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 \ref{append:randchoice} fall \emph{outside} the partial identification bounds, this is equivalent to finding a violation of \ref{eq:testable0} or \ref{eq:testable1}. We implement these bounds for the TOT and TUT in our companion STATA package.



\section{ Causal Random Forest, HTE, and `mistakes'}



\begin{comment}

    \begin{figure}[H]
        \caption{Conditional Average Treatment Effect from Random Forest}
        \label{CATE}
        \begin{center}
\includegraphics[width=0.6\textwidth]{Figuras/he_dist_apr_pro_2.pdf}
\end{center}
     \scriptsize This Figure plots the densities of the CATE emerging from the Athey et al. (2019) random forest, along with the upper and lower confidence bounds.  
        \end{figure}
\end{comment}



% \subsection{Example of a Causal Tree}

% \vspace{.3in}
% \begin{figure}[H]
%         \caption{Example Causal Tree}
%     \label{causal_tree1}
%     \begin{center}
%         \centering
%         \includegraphics[width=\textwidth]{Figuras/crf_apr.pdf}
%     \end{center}
%     \footnotesize 
%     This figure shows an example of one of the regression trees used to compute the causal forest estimates described in Section \ref{sec:RF}. Each tree is constructed from a sequence of recursive binary partitions of the covariate space, with a splitting rule that is targeted to the causal quantity of interest, following the methodology of \cite{atheygrf}.
%     %This is one(it is chosen such that it minimizes the pruned cost, that is it is the tree with the smallest root-node impurity) of the honest causal trees in the random forest we use for the estimation of the heterogeneous treatment effect of the fee-forcing contract. It is meant only as an example of how these trees look like. The forest was such that there are as many estimated treatment effects as there are clients.
%      %\footnotesize{ \textit{RScript: }  \texttt{grf.R}
% \end{figure}


\subsection{Conditional ATE estimates}

\begin{figure}[H]
    \begin{center}
  \caption{Cumulative Distribution Function of Conditional ATE Estimates}
  \includegraphics[width=0.6\textwidth]{Figuras/cdf_CATE.pdf} 
    \label{fig:CATEsurvival}
    \end{center}
    
    \scriptsize This figure shows the share of borrowers who benefit from forced commitment, where ``benefit'' is defined as having an estimated conditional average treatment effect (ATE) above a specified threshold value. Results are based on the causal forest model from Section \ref{sec:RF}. The solid line equals $1 - F_\text{ATE}(\delta)$ where $F_\text{ATE}(\delta)$ denotes the CDF corresponding to the density of conditional ATE estimates from Figure \ref{heterogeneous_effects}. The blue shaded regions are associated 95\% confidence intervals. We estimate that at least 90\% of borrowers have a positive conditional ATE. 
%\textit{Do file: }  \texttt{cdf_CATE.do}
\end{figure}
 




\begin{figure}[H]
    \caption{Conditional ATEs from ``wide'' and ``narrow'' covariate sets}
    \label{wide_narrow_forests}
    \vspace{-2em}
    \begin{center}
    \begin{subfigure}{0.65\textwidth}
        \centering
        \includegraphics[width=\textwidth]{Figuras/scatter_hist_wide_narrow.pdf}
    \end{subfigure}
    \end{center}
    \vspace{-1em}
      \scriptsize  This figure plots the relationship between the causal forest conditional ATE estimates from Section \ref{sec:RF} 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, with the ``wide'' covariate set on the horizontal axis and the ``narrow'' set on the vertical axis. The density plots on each 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.

%\textit{Do file: } \texttt{wide_narrow_forests.do}       
\end{figure}



\subsection{Targeting rule comparisons}

Figure \ref{targeting_rules} compares the in-sample performance of targeting rules against universal forced commitment. The plot presents the estimated proportion of borrowers 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 of universal forced commitment. The fraction of the whole sample incorrectly targeted when moving from universal forced commitment to targeting based on the narrow RF falls only from 9.78\% to 9.59\%. Logit targeting makes things marginally worse. 


\begin{figure}
    \caption{Targeting rules}
    \label{targeting_rules}
    \begin{center}
    \begin{subfigure}{0.6\textwidth}
        \centering
        \includegraphics[width=\textwidth]{Figuras/wide_narrow_rule.pdf}
    \end{subfigure}
    \end{center}
    %\vspace{-2em}
      %\scriptsize   This figure plots the percentage of borrowers who would benefit from a program in which commitment is targeted using 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 in blue, 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 from the ``wide'' random forest model is positive. Each of the classification models produces an estimated probability of a positive CATE. For each, the assignment rule ranks borrowers by this estimated probability, and assigns the highest 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 performance of logit and RF-based targeting. 
      
      %, the top \hl{XXX\%} of Both targeted Both of the targeted assignment rules are assigned by a the ``narrow'' causal forest in green, and targeting based on the logit model in red. The causal forest rule assigns a borrower to commitment if her estimated conditional ATE from the ``narrow'' covariate set is positive; the logistic regression rule assigns her to commitment if the estimated probability that her conditional effect is positive is greater than 0.5. 
      %\todo[inline]{@Issac: Have I described this correctly? Also, is this an out-of-sample exercise. In other words, are we using a holdout sample to make these comparisons?}

      %This figure plots the (reversed) cumulative densities of the estimated benefits from the casual forest for three different rules.  The blue line plots the HTEs from the `wide' random forest for the Forcing arm, which we take as the ground truth for actual impacts.  The green line plots HTEs if we first target individuals using the variables in the `narrow' forest, and only assign individuals to commitment if they are on a leaf whose predicted forcing benefit is positive.  The red line uses a logit regression to predict which individuals benefit from treatment, and assigns all individuals to the arm predicted to be best for them.

\end{figure}



%We use \cite{atheygrf} \texttt{causal\_forest} of the \texttt{grf} library in $R$. The parameters used were:
%\scriptsize{\textit{causal\_forest(
%  X, 
%  Y, 
%  W, 
%  Y.hat = NULL,
%    W.hat = NULL,
%    clusters = NULL,
%    num.trees = 5000,
%    sample.weights = NULL,
%    equalize.cluster.weights = FALSE,
%    sample.fraction = 0.5,
%    mtry = min(ceiling(sqrt(ncol(X)) + 20), ncol(X)),
%    min.node.size = 5,
%    honesty = TRUE,
%    honesty.fraction = 0.5,
%    honesty.prune.leaves = TRUE,
%    alpha = 0.05,
%    imbalance.penalty = 0,
%    stabilize.splits = TRUE,
%    ci.group.size = 2,
%    tune.parameters = c("alpha", "imbalance.penalty"),
%    tune.num.trees = 500,
%    tune.num.reps = 200,
%    tune.num.draws = 2000,
%    compute.oob.predictions = TRUE,
%    num.threads = NULL,
%    seed = 1)}}


\begin{comment}

\begin{figure}[H]
        \caption{Single causal tree for the Forced-commitment contract heterogeneous treatment effects}
    \label{causal_tree2}
    \begin{center}
        \centering
        \includegraphics[width=\textwidth]{Figuras/ct_pro_2_apr.pdf}
    \end{center}
    \footnotesize 
   
     %\footnotesize{ \textit{RScript: }  \texttt{grf.R}
\end{figure}
\end{comment}




%\begin{figure}[H]
%    \caption{Choice of contracts and treatment effects}
%    \label{choose_wrong}
%    \begin{center}
%        \begin{subfigure}{0.45\textwidth}
%        \caption{Mistakes in choice arm}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/line_cw_apr_te_cf.pdf}
        
%   \end{subfigure}
%        \begin{subfigure}{0.45\textwidth}
%        \caption{Financial value of mistake}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/money_cw_apr_te_cf.pdf}

%    \bigskip
        
%    \end{subfigure}
%        \begin{subfigure}{0.45\textwidth}
%        \caption{\% better when forced to forced commitment}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/line_better_forceall_apr_te_cf.pdf}
%        
%    \end{subfigure}
    %     \begin{subfigure}{0.45\textwidth}
    %     \caption{\footnotesize{Effect of CATE benefit vs predicted take-up}}
    %     \centering
    %     \includegraphics[width=\textwidth]{Figuras/benefit_choice.pdf}% takeuppr_def.pdf 
    % \end{subfigure}
    
%    \end{center}
%        \scriptsize
%        In Panel (a) we estimate what the treatment effect of the commitment contract \textit{would have been} for all subjects in the choice arm if they had been forced into the fee-commitment contract. To do this we proceed in two steps. First, we estimate treatment effects in the forcing arm by comparing the Forced Commitment arm against the status quo arm. We let these effects be heterogeneous as a function of our $x$'s using \cite{atheygrf}'s methodology of causal forests. Second, we extrapolate these treatment effects based on the choice arm using the same $x$'s. Once we have personalized counterfactual treatment effects in the choice arm we calculate what fraction of subjects in the choice arm incurred in financial costs that are  $> z$\% than if they had chosen the opposite contract of what they actually chose, were $z$\% is defined as a fraction of the loan. $z$\% is a level of tolerance we can vary and we plot it in the X-axis. The left Y-axis measures the fraction of subjects that would have been better by a margin of $z$\% if they changed their choice, and the right Y-axis measures the amount of money ``left on the table''. We use bootstrap to tighten the confidence intervals (CIs). \cite{atheygrf}'s heterogeneous treatment effect using GRF is asymptotically normal. We compute the HTE ($\mu$) together with standard errors ($\sigma$) . For every pledge, we draw a random effect from a normal distribution with parameters ($\mu$,$\sigma^2$), and compute via bootstrap the percentage that choose wrong, along normal-approximation CIs (results are robust if we use instead percentile CIs or bias-corrected CIs) . This allows us to estimate a distribution for the upper and lower bound CIs, which we then use to obtain a 95\% CI. Panel (b) is analogous to Panel (a) except that it does the exercise separately for clients we classified as overconfident ($OC_i:=\mathbbm{1}(P^s_i-\widehat{P_i(X_i)}>0))$ and those we classified as not overconfident. Panel (c) simulates what percentage would be better by at least $z$ if we forced everybody of those in the Commitment Choice arm into the fee-commitment contract.
        % Panel (d) asks whether it is the case that people with larger causal benefits from the Forced Commitment contract would be more likely to select that contract. To do this we proceed in two steps as well. First we estimate a flexible model of take-up of the fee commitment contract \textit{in the choice arm} using random forests, and from this model obtain a probability $P(x_i)$ of choosing the Forced Commitment contract for a client with characteristics $x_i$. We extrapolate this model to clients in the Forced Commitment arm to estimate what would they have chosen if we had given them choice. 
        % Figure (d) plots $\widehat{P(x_i)}$ in the X-axis using a binscatter that splits the X-axis in 100 percentile bins. The Y-axis plots the heterogeneous treatment effects of the fee forcing contract on the probability of losing the pawns (more negative means then more likely to recover it), averaged for the respective x-axis bin. Positive assortative selection would mean a negative relationship: those who benefit more by treatment and lose the pawn less are \emph{less} likely to choose it.  Using all bins we estimate a slope of zero in the relationship. Using the 80 right most points, we estimate a \textit{positive} relationship.
        %\textit{Do file: }  \texttt{choose\_wrong\_quant\_wrong.do, choose\_wrong\_quant\_wrong\_decomposition.do}
%\end{figure}


\vspace{.3in}

\cleardoublepage




\vspace{.4in}

\begin{comment}
    
\subsection{Take up}


\begin{table}[H]
    \caption{\textcolor{red}{DELETE--Predicting Take-up: Goodness-of-Fit}}
    \label{Table_compliance}
    %\begin{subtable}{1\textwidth}
    % \centering
    %    \caption{Take up}
    %    \scriptsize{\input{./Tables/oos_pago_frec_vol.tex}}
    %\end{subtable}%
    
    %\bigskip
     \begin{subtable}{1\textwidth}
      \centering
        \caption{Take up: Choice-fee Arm}
        \scriptsize{\input{./Tables/oos_pago_frec_vol_fee.tex}}
    \end{subtable}
    
      \bigskip
    \begin{subtable}{1\textwidth}
      \centering
        \caption{Take up: Choice-promise Arm}
        \scriptsize{\input{./Tables/oos_pago_frec_vol_promise.tex}}
    \end{subtable}
            \scriptsize
           \\
           \\
           \\
    
     %\textit{Scripts: } \texttt{pred\_take\_up.do, pfv\_pred.R}
\end{table}




\vspace{.1in}
\begin{figure}[H]
    \caption{\textcolor{red}{DELETE--Out of sample ROC curve}}
    \label{roc_curve}
    \begin{center}
    \begin{subfigure}{0.45\textwidth}
        \caption{Take-up in Fee Arm}
        \centering
        \includegraphics[width=\textwidth]{Figuras/Boost/ROC_curve_outsample_pago_frec_vol_fee.pdf}
    \end{subfigure}
    \begin{subfigure}{0.45\textwidth}
        \caption{Take-up in Promise Arm}
        \centering
        \includegraphics[width=\textwidth]{Figuras/Boost/ROC_curve_outsample_pago_frec_vol_promise.pdf}
    \end{subfigure}
    \end{center}
     \scriptsize 
  %\footnotesize{ \textit{Do file: }  \texttt{pred\_take\_up.do}}
\end{figure}



\vspace{.3in}
\begin{figure}[H]
    \caption{\textcolor{red}{\hl{ARE THESE MADE OBSOLETE BY THE NEXT FIGURE? } Predictors of commitment contract take-up}}
    \label{interactions_takeup}
    \begin{center}
    \begin{subfigure}{0.7\textwidth}
        \caption{PLM}
        \centering
        \includegraphics[width=\textwidth]{Figuras/determinants_takeup_reg.pdf}
    \end{subfigure}
    \begin{subfigure}{0.7\textwidth}
        \caption{Logit}
        \centering
        \includegraphics[width=\textwidth]{Figuras/determinants_takeup_logit.pdf}
    \end{subfigure}
    \end{center}
     \scriptsize
      %\footnotesize{ \textit{Do file: }  \texttt{determinants_takeup.do}}
\end{figure}


\scriptsize 
\noindent This figure reports bivariate (and multivariate) regressions of the form $TakeUp = \alpha + \beta \: X_i + \epsilon_i$. The figure reports the $\beta$ coefficients for different $X_i$'s along with 95\% confidence intervals. Panel (a) uses a linear model. Panel (b) specifies a logit model.

\end{comment}




%\subsection{Selection on gains}

%\begin{figure}[H]
%    \caption{Determinants of treatment effects}
%    \label{determinants_cate}
%    \begin{center}
%    \begin{subfigure}{0.65\textwidth}
%        \caption{Determinants of CATE}
%        \centering
%        \includegraphics[width=\textwidth]{Figuras/blp_cate_apr.pdf}
%    \end{subfigure}
  
%    \end{center}
%     \scriptsize   This figure estimates bivariate \& multivariate double-robust regressions of the estimated CATE of forcing.
     
%\end{figure}
%\todo[inline]{This is a figure that is not referenced yet in the paper, but there is a line highlighted in yellow that could use this information. While there appears to not be any effect, let's remember that the RF is considering nonlinear interactions between variables, as well as using information of missingness of some survey questions.}


\normalsize

%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%
%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%

% APPENDIX B
\begin{comment}
    

\newpage
\section{ Mechanisms }


\subsection{Optimism, Over-Optimism, and the Failure of Self-Commitment}
\label{overconfidence}

\textcolor{red}{Need to decide whether we want to try to plant our feet on Confidence/Overconfidence as the core `why' of the previous result
.}
%\subsubsection{Behavioral: overconfident borrowers demand less (but benefit more)} \label{behavioral}

The leading behavioral explanation in the literature for low demand for commitment is present biased preferences with naivete (e.g. \cite{Rabin2018}, \cite{John}, \cite{Laibson2018})  \cite{Laibson2015} shows that the lost flexibility resulting from a commitment contract can limit take-up especially severely when agents are (partially) naive about their self control problem. In our context if consumers are (partially) naive about their present bias, they would plan to save more (or spend less) than what they actually end up saving, thus making it be harder to recover their pawn. This under-saving will be mitigated in the fee forcing contract since the fee makes them save money to pay part of the loan periodically. \ref{appendix_c} formalizes this in a model. Another behavioral explanation is that clients may underestimate the likelihood and severity of negative income shocks. Both of these explanations predict that clients will be overconfident about their likelihood of pawn recovery. Recall that in the control group the client's subjective probability of recovery is on average 93\%, while actual recovery is just 44\%. A further piece of evidence consistent with underestimating negative income shocks and with present bias with partial naivete is that a large number of people (25\%) in the control group pay a positive amount toward pawn recovery but end up losing their pawn anyway.


So, overconfidence of recovering the pawn is implied by both present bias preferences with naivete and upward bias in their income expectations. But does overconfidence actually predict low demand for commitment empirically? It does. We define as overconfidence as the reported subjective probability of recovery minus the predicted probability based on the client's characteristics, $P^s_i-\widehat{P_i(X_i)}$.\footnote{We predict $\widehat{P_i(X_i)}$ in two steps. In step one we use Lasso with cross validation to tune the regularization parameter to select the most predictive variables $X$. The typical present bias question as in \cite{Ashraf} was eliminated in this step. In the second step we estimate $\widehat{P_i(X_i)}$ using those variables in a logit model. The Lasso selected variables were type of pawn, female, age, has pawned before, has savings, participates in rotating savings, often feels tempted to change plans, would like to have a reminder to pay, and an economic vulnerability index. We are careful not to include these variables as controls in Table  \ref{oc_reg}.} There is a large amount of overconfidence in our context. Figure \ref{oc_hist} plots a histogram of $OC_i$ and shows that the overwhelming majority display overconfidence, and a large fraction overestimate recovery by more than 50 percentage points. Our measure of overconfidence is useful especially when there is limited time for a detailed survey.\footnote{It may be more useful than a simple elicitation of present bias as in \cite{Ashraf}. We find that 15\% of clients are classified as present biased using this measure of preference reversal. This level is similar to the number \cite{Ashraf} find but small to explain no take-up of commitment for 90\% of clients. This measure was not correlated with take up of commitment in our sample.} First it is very prevalent, which makes it promising to explain the overwhelming prevalence of low take up. Second, it is easy to measure. Third, it is predictive of take-up in an intuitive way. Finally, overconfidence in recovery is implied by present bias with (partial) naivete but also by biased expectations of negative income shocks, thus capturing both kinds of bias.\footnote{\textcolor{red}{Another indication of overconfidence is that in our data, of those who renew, 83\% lose the pawn anyway. Our measure of overconfidence has a correlation of \hl{xxx}\% with a dummy for renewing and losing the pawn. }} 

\cite{Sprenger} have argued that it is critical to understand the link between beliefs and demand for commitment, yet the evidence is scarce. Table \ref{oc_reg} does this: it regresses an indicator of take up of the monthly payment contract against an indicator for overconfidence $OC_i:=\mathbbm{1}(P^s_i-\widehat{P_i(X_i)}>0)$ and controls. Controls $Z$ include branch and day of the week dummies, schooling, whether the client does a monthly budget plan, among others. We are careful not to include controls that were used in $\widehat{P_i(X_i)}$. % and a measure of intertemporal preference reversal analogous to that of \cite{Ashraf} as controls.\
In the choice-fee arm, being overconfident decreases the likelihood of demanding commitment by 12 percentage points a result that this is robust to including controls  (columns 1 and 2). While overconfidence predicts lower take up in the Commitment Choice arm, this is not the case in the promise-choice arm (columns 3 and 4).  One interpretation of the results is that the overconfident borrowers think they do not need commitment, and their demand decreases sharply as soon as there is even a small fee, and at the same time they perceive the promise as a low cost option. This provides evidence for \cite{Sprenger}'s conjecture that ``tepid demand for commitment outside controlled experimental settings is consistent with broad unawareness [of biases]''. 

How does overconfidence map to cost outcomes? Theory predicts that the more overconfident (naive) may be at the same time those that benefit more from commitment. Extrapolating individual treatment effects of the Forced Commitment contract vs the status quo one to the choice arm (see below for more detail), and using them as a dependent variable we find that overconfident borrowers benefit \textit{more} from the commitment contract, with {24.8}\% (=\${30}/\${121}) more savings (columns 5 and 6). Thus while we predict the overconfident benefit more from commitment, they demand less of it. 




\subsubsection{Neoclassical Alternatives} \label{neoclasical}

\vspace{.1in}
\noindent \textbf{Risk aversion.} We do not have measures of risk aversion in our short survey, which makes it hard to assess the hypothesis that risk aversion limits take-up of the fee frequent payment contract. One way to proceed is to take the empirical distribution of financing cost ---$F_{fee}(FC)$--- as one the client would have faced had she chosen the the fee-commitment contract. We could then ask what would risk aversion have to be in order to justify the client choosing the fee-commitment contract distribution of costs over the distribution associated with the status quo contract, $F_{sq}(FC)$. Framed as a choice among cost distributions, we can calculate what risk aversion is needed to rationalize the overwhelming choice of the status quo contract over the fee-commitment contract. This exercise of course assumes --as is common in economics-- that clients know the distribution of financial cost, that the distribution is common across consumers (although this can be relaxed), and that this cost distribution is the only difference among contracts. 

Fortunately for us, it turns out that one distribution first-order-stochastically dominates the other, obviating the need to calibrate a specific utility function or use a parametric distribution function in order to rank them in terms of expected utility. We use the fact that if the utility $u(FC)$ is decreasing in $FC$ (i.e. clients dislike paying higher financing cost) and $F_{fee}(FC) \geq F_{sq}(FC)$ for all $FC$, which we actually verify in our data, then $E_{fee}[u(FC)] \geq E_{sq}[u(FC)]$, that is any expected utility maximizing client risk averse consumer should choose the Forced Commitment contract as a result of the distribution of cost payoffs.\footnote{See the Appendix for the proof. Figure \ref{ecdf_fc} in the Appendix shows that indeed $F_{fee}(FC) \geq F_{sq}(FC)$. Table \ref{stochastic_dominance} shows that this holds also for sub-populations of different characteristics.}. Thus, risk aversion cannot explain the low demand for commitment under the assumptions of this exercise.   


\vspace{.1in}
\noindent \textbf{Lost flexibility.} A second explanation for low take up is lost flexibility. That is, the fee-commitment contract may provide too much commitment which is costly because the client may be forced to incur in late payment fees if he experiences a negative income shock.\footnote{Note that income shocks that affect the ability to pay the entire loan are a worry for both the Forced Commitment contract and the status quo one, and should not make one contract more favorable than the other.} While we cannot rule out that income shocks combined with lost flexibility of the contract explain the low demand, we think it is unlikely. First, we showed above that clients report a subjective probability of recovery of 93\% on average, which suggests they are not too worried about income shocks. Second, the fear of incurring fees is quantitatively not enough of a concern when compared to the savings they are experiencing. %Note that fees for late payment are not that high. In an average loan of 2,000 pesos the monthly payment is close to 700 pesos, and a fee of 2\% of that is 14 pesos (less than \$1 dollar). This is about gr{1\%} of monthly per capita income of the first 3 deciles of Mexican {household's} income distribution. %This compares favorably to the gr{\$11.6 + \$62.3)} pesos transportation / transaction cost of one. 

To make this concrete, we calculated what the financing cost of the fee-commitment contract would be if \textit{all} its clients incurred in \textit{all} potential fees (while keeping payment profiles and pawn recovery constant) and added these fictitious fees to financing cost for those in the Forced Commitment arm, thus artificially inflating their cost. We then re-estimated the quantile treatment effects analogous to Figure \ref{fc_pro2}(b) with this inflated financial cost. %\footnote{Of course behavior may not be constant, but we believe this is a reasonable fist approximation. %It could be that having this small fee added to the balance discourages them to pay or makes it harder to pay back the loan. But the contrary may also happen, with the fee making them more determined to pay early. We would need a structural model of client behavior to estimate a full counterfactual. We suspect that such small fees would not generate large changes in behavior in a simple neoclassical model.}). 
Figure \ref{fc_allfee} presents the results. We find that even in this extreme scenario, tilted against the Forced Commitment contract, the estimated effect still implies cost savings from the Forced Commitment contract at the mean, 25$^{th}$, 50$^{th}$, and 75$^{th}$ percentiles.\footnote{Recall that the differences in financing cost already takes into account the fact that clients in the fee forcing contract sink more pre-payments than those in the status quo contract, and that those prepayments are lost if the loan is not fully paid back.}  Although these arguments are not definitive, they suggest that low demand for commitment may be driven by more than the anticipation of lost flexibility implied by a small fee.

\vspace{.1in}
\noindent \textbf{High time discounting.} We mentioned above that clients in the status quo contract tend to wait until the last moment to pay to recover their pawns. Even among those that recover their pawn, only 40\% pay before the 90$^{th}$ day. Table \ref{mechanisms} shows that clients assigned to the fee-commitment contract front load their payments, starting their first payment earlier and finishing paying earlier too. However, clients may dislike front loading payments if their time preference discount rate is high. They may be willing to trade off a higher probability of losing their pawn for more \textit{back} loaded payments.  

What would discount rates have to be in order for back loaded payments to offset the reductions in financial cost effects we observe? %We can calculate this number by looping across a grid of discount rates, incorporating this higher discount rate in the definition of financial cost, and reestimating equation \ref{basic_reg} with this modified financial cost measure as the dependent variable in equation 1, searching for the discount rate that makes $\beta$ equal zero. We did this and obtained 
We calculate that the discount rate that is necessary to compensate for the savings in financial cost (i.e. that makes the estimated $\beta$ in equation \ref{basic_reg} equal to zero when financing cost --using different $r$'s-- is the dependent variable) is a staggering 8,190 percent per year. We find this discount rate implausibly high even for this credit constrained population\footnote{For comparison, \cite{Levin} find that a discount rate of 1,415 per year for subprime borrowers in the US is too high to be believable.}, casting doubt on high discount rates as explanation for low demand for commitment. %\footnote{In the baseline survey we give respondents a hypothetical choice between $100$ pesos tomorrow or $150$ pesos in one month (an implicit yearly interest rate of {12,800\%}) and only 30\% chose the later one.} 


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% APPENDIX C

\newpage
\section{ A simple model}
\label{appendix_c}
\vspace{.2in}
\normalsize
\linespread{1.05}

Although the empirical results are striking and stand alone, this section refers to the model of \cite{John} to interpret our empirical results. The model is stylized but incorporates important features of our context. It allows for negative income shocks which we think are prevalent in this population. %The shock generates a cost of committing to monthly payments and could potentially be a reason for low take up. 
It also features clients with present biased time preferences --allowing for partial naivete-- choosing to save to pay for an expense, and with the opportunity to make a commitment to save and pay. These two features parsimoniously explain several facts about the context --like overconfidence in recovering the pawn--, and about the results --e.g. that forcing commitment seems to help. We intend the model only as a very stylized approximation to our context, and we use it only to help us organize the interpretation of the empirical results, not as a literal description of reality. %Third, it allows for a simple way to model commitment afforded by late payment fees. %Nonetheless, the model abstracts from several details of the context. Even with these abstraction it allows us to explain our six main results listed in Section \ref{explanations_recap} below.

We use the model of \cite{John} and refer the reader to that paper for more detail, justification of assumptions and some of the proofs. The model has three periods and linear utility.\footnote{This does not map perfectly to our 3 period contract, but it is enough to generate the results we need. We also assume that the amount of the loan is used up to pay for the emergency. \cite{John_theory} provides a more general treatment.} Period $t=0$ is a planning period where the client is either allocated to the status quo, the fee-forcing contract, or a choice between the two. Period $t=1$ is the saving-for-the-monthly-payment  period, and $t=2$ in the pawn recovery (loan payment) period. In period 1 the client receives her income $y_1=1$, or gets zero with probability $\lambda$. She can consume ($c_1$) or save ($s_1$) part that income. In period 2 the client gets her savings from period 1, and again receives income of either $y_2=1$, or zero with independent probability $\lambda$. In this last period, she decides whether to use income and savings for consumption $c_2$ and/or for paying back the loan of size $p \in(1,2)$ to recover the pawned piece valued at $b>p$. In this simple set up we model the fee-commitment contract as a contract that imposes a fee of size $F$ if the client fails at $t=1$ to save $s_1=p-1$ pesos, which is what is needed to pay the loan back when there are no shocks. In period $t=0$ she evaluates her welfare as $E[c_1+c_2]$, were for simplicity we have set the time discount to one. We also assume the interest rate is one. We introduce present biased preferences by assuming the following utility function $U_t=c_t+\beta \: \sum_{k=t+1}^{2} E[c_k]$, with $\beta<1$ indicating present bias. A naive client perceives she is not so present biased and instead of $\beta$ uses $\hat{\beta} \in (\beta,1]$. 

Note that under these assumptions it is efficient at $t=0$ to recover the loan since $b>p$ and since there is no discounting at $t=0$. Because $b>1$, paying back the loan requires that there is no negative shock in any period and that $s_1>0$. Because $\beta<1$ at $t=1$ the client will not send savings in excess of what is needed to recover the loan: $s_1=p-1$. This parsimonious model implies the following results:

\vspace{.2in}
\noindent \textbf{Result 1: Present biased clients default more.} Under the status-quo contract, absent shock realizations, present biased clients (sophisticated or naive) with $\beta<\beta_{SQ}<1$ will lose their pawn, while clients with no present bias will not.\footnote{$\beta_{SQ}=\frac{p-1}{\lambda(p-1)+(1-\lambda)(b-1)}$. See Proposition 1 in \cite{John}.} 

\vspace{.1in}
\noindent \textbf{Result 2: Forcing present-biased clients into the fee-commitment contract reduces default.} Imposing a fee $F>0$ for late payments weakly decreases default (for present biased clients only). It strictly decreases default if $F>F_{min}(\beta):=(p-1)-\beta[\lambda(p-1)+(1-\lambda)(b-1)]$. The larger the present bias the larger the $F$ required to induce pawn recovery.\footnote{$F_{min}(\beta)$ is derived from the incentive compatibility constraint needed to generate savings at $t=1$ to recover the pawn can be written as $1-(p-1)+\beta[\lambda(p-1)+(1-\lambda)(b-1)] \geq 1-F+\beta(1-\lambda)$.}

\vspace{.1in}
\noindent \textbf{Result 3: Demand for commitment.} Given $F>0$, (a) Neoclassical clients will never demand commitment. (b) Present-biased sophisticated clients will prefer the fee-forcing contract over the status quo contract $\iff$  $\lambda \: F<(1-\lambda)^2(b-p)$ and $F>F_{min}(\beta)$, that is $\iff$  $\beta \in [\beta_{min},\beta_{SQ}]$.\footnote{$\beta_{SQ}$ was determined in Result 1. $\beta_{min}$ is such that $F=F_{min}(\beta_{min})$.} (c) Analogously, naive clients will demand commitment $\iff$ $\hat{\beta} \in [\widehat{\beta_{min}},\beta_{SQ}]$, where $\widehat{\beta_{min}}<\beta_{min}$. So strongly naive clients will on the one hand demand more commitment than sophisticated clients since they believe (incorrectly) that a smaller fee will motivate them to pay. On the other hand they may demand less commitment since they think they can save and pay on their own. Whether they demand more or less than sophisticated clients depends on the empirical distribution of $\beta$ and $\hat{\beta}$. 

\vspace{.1in}
\noindent \textbf{Result 4: Overconfidence.} Only naive clients will be overconfident about the probability of recovery. This will be true whether they have the status quo or the fee-forcing contract. Overconfidence is increasing in $\hat{\beta}$.

\vspace{.1in}
\noindent \textbf{Result 5: Welfare.} (a) Neoclassical consumers' welfare strictly decreases when we force clients into the fee-commitment contract instead of the status quo contract because of the risk of them not being able to pay for the installment, and does not change when we offer a choice between them. (b) The welfare of sophisticated present biased consumers weakly increases when we give them choice, and it strictly increases  $\iff$  $\beta \in [\beta_{min},\beta_{SQ}]$, that is when they would choose the fee-commitment contract themselves. Forcing them into the fee-commitment contract increases welfare $\iff$  $\beta \in [\beta_{min},\beta_{SQ}]$, otherwise it strictly decreases it. So choice is better than forcing for sophisticates. (c) Forcing can be welfare improving for the naive. Indeed if $\hat{\beta}>\beta_{SQ}>\beta$ then forcing the fee-commitment contract increases welfare, and if $\hat{\beta} \in (\widehat{\beta_{min}},\beta_{min})$ then forcing the status quo contract increases welfare.\footnote{This result is different from that in \cite{John}. Her context has individuals choosing the size of the fee. In that context naive clients will \textit{always} chose the wrong fee size and default later, therefore choice is always decreasing for the naive. In our context $F$ is fixed at 2\% of the balance due, and this implies that choice could be welfare improving for some naifs.} We want to highlight that only under certain parameters will forcing installment payments improve welfare, and that welfare will likely decrease for those with no present bias and the sophisticated present biased consumers. 

\vspace{.1in}
\noindent \textbf{Result 6: Welfare and ex-post observed behavior.} If for a naive client $i$ the fee-forcing contract causes higher pawn recovery, then we know the fee $F$ made her IC constraint binding, and therefore that $\hat{\beta}_i>\widehat{\beta}_{min}$. If in addition if it was the case that $\beta_i<\beta_{SQ}$. %\footnote{\hl{Isaac, aqui tengo dos pregutas: (1) si es $\beta$ y no $\hat{\beta}$ verdad?  (2) Para que una persona naive empenie en el status quo tiene que ser que cree que va a recuperar no? Es decir tiene que ser $\hat{\beta}>\beta_{SQ}$ correcto?}} 
then the fee-forcing contract would have increased welfare for the naive. That is, our finding that the fee-forcing contract increases pawn recovery is a sign of higher welfare (although not a sufficient condition).\footnote{It is not sufficient since ex-ante the commitment $F$ may have been too expensive given the income shocks, i.e. if $\lambda \: F>(1-\lambda)^2(b-p)$.}




\subsection{Interpretation}

The model is very parsimonious but powerful and it can potentially explain all our empirical findings qualitatively.\footnote{The model is sufficiently stylized that we think we would not gain much from estimating it. Furthermore we have no data on income shocks which figure prominently in the model. \cite{Ted} and \cite{Aprajit} are two very recent models that combine a field experiment with commitment contracts and estimation of present bias parameters.} First, it can explain why default is high in the status-quo contract, namely that clients are present biased and have no commitment devices. Second, it can explain why clients are overconfident in our data, namely by virtue of naivete about present bias. Under the model naivete is necessary to explain this. Third, it can also explain why the fee forcing contract induces lower default, but not for everyone: namely that it makes the incentive compatibility constraint for payment binding for the present biased, while it was not binding in the status quo contract. Fourth, it can also explain why there is low demand for commitment even if it seems to improve welfare: namely that there is a small share of neoclassical and sophisticated clients, and at the same time naifs have a present biased parameters values in the region in which they think they can save on their own. Fifth, it explains non-zero demand for commitment for a set of clients. Sixth, it can explain why clients exposed to the Forced Commitment contract are more likely to come back namely those naifs whose welfare increased as a result of being forced into the fee-commitment contract.\footnote{Those with $\hat{\beta_i}>\beta_{SQ}>\beta$.}


\subsection{Other potential explanations: recap} \label{explanations_recap}

There may be other interpretations of the empirical findings, but the bar is high. An alternative explanation will need to explain the 6 facts below:

\begin{enumerate}
\itemsep0em 
\item High (although ex-post inefficient) default in status quo contract.
\item Overconfidence about pawn recovery.
\item Forcing commitment increases pawn recovery.
\item Small demand for commitment...
\item ...but positive demand for commitment.
\item Forcing commitment makes clients more likely to come back.
\end{enumerate}


Let us consider alternative explanations in isolation (i.e. just considering one change or feature at a time with respect to a neoclassical model):

\vspace{.1in}
\noindent \textbf{Alternative 1: Strong prevalence of income shocks.} This could explain (4) and (1), but not why forcing helps, (3) and (6), nor why there is overconfidence, (1). It would also not explain why clients come to pawn in the first place and then default, (2), as they would weight in on the high chance of losing the pawn. 

\vspace{.1in}
\noindent \textbf{Alternative 2: High time discounting}. This could not explain (1) nor (5) nor (6). It could qualitatively explain (4), but as we say in section \ref{sec:demand} quantitatively it would require unbelievably high discount rates.


\vspace{.1in}
\noindent \textbf{Alternative 3: Risk aversion.} We already discussed and rejected risk aversion in section \ref{sec:demand}, although using strong assumptions in the process. Risk or ambiguity aversion could still play a role in explaining 4 and should be investigated in future research. However it would hardly explain (1), (2), (5), or (6).

\vspace{.1in}
\noindent \textbf{Alternative 4: Misunderstanding the contracts.}\footnote{This is a potential criticism of \textit{any} paper offering choice, and one that is non-falsifiable if the critic has free reign to propose how the contracts are perceived in the subject's mind.} We were very aware of the importance of clients understanding the contract in order to infer preferences from choice. That is why we made a strong effort for clients to understand the contracts (see subsection \ref{implementation}). Note however that while clients making purely random mistakes could explain why 10\% demand commitment ---i.e. (4) and (5)--- it would not explain the rest of the findings, nor why the Soft Commitment (see below) had more take up that the fee-commitment, or why we can statistically predict take-up with significant accuracy (see Figure \ref{interactions_takeup} and Table \ref{Table_compliance}).


\vspace{.1in}
\noindent \textbf{Alternative 5 (behavioral): Forgetting to pay/salience.} Frequent payments may act as a reminder to save and recover the pawn. This would try to explain (1) by appealing to people forgetting to pay, and (3), (5), and (6) by appealing to frequent payment acting as reminders (i.e. there being demand for reminders). It would not explain (2) or (4) which are critical in the paper. However even for (1) it seems to us a stretch to explain people losing a valuable pawn by forgetting to pay it. Since the Soft Commitment installment contract did not change behavior (as shown below) this explanation would also require us to posit that only fees acts as reminders, not promises.

\vspace{.1in}
\noindent \textbf{Alternative 6 (behavioral): Income shocks overconfidence}. One could also easily introduce in the overconfidence about income shocks in the model of \ref{appendix_c}\footnote{Say with $\widehat{\lambda} <\lambda$. The effect on demand for commitment is uncertain since on the one hand it decreases $\beta_{SQ}$ decreasing demand, but on the other a smaller $F$ is needed to make the IC binding, making commitment less costly.}. This would leave default unchanged in both the status quo and the fee forcing contract thus would not explain (3), %since $F_{min}(\beta,\widehat{\lambda})<F_{min}(\beta,\lambda)$. 
% $\widehat{\lambda} <\lambda$ alone 
It would not explain (5) or (6) either as demand for commitment would be zero without present bias. 


\vspace{.1in}
We do not claim that the model in the Appendix is the only possible explanation of our empirical findings, but it is a parsimonious explanation of all of them.

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