An Experiment on Time Preference and Misprediction

in Unpleasant Tasks∗

Ned Augenblick† and Matthew Rabin‡

March 21, 2015

Abstract

In this paper, we employ a new experimental design involving choices and predictionsabout completing work to investigate the time-inconsistent taste for immediate gratifica-tion, sophistication about that taste, and misprediction about future preferences. Over thecourse of seven weeks, 100 participants specified the number of unpleasant transcriptiontasks they desired to complete both immediately and at different future dates given variouswages. Participants exhibit a time-inconsistent taste for immediate gratification, prefer-ring to complete 10-12% fewer tasks in the present compared to any future date, whichleads to an estimated average quasi-hyperbolic discounting parameter of β ∈ [.81, .84].By comparing predictions about future immediate-work choices to actual choices, we findevidence against substantial sophistication about future present bias, generally estimat-ing an average sophistication parameter of βh ∈ [1.00, 1.01], although correlation betweenindividuals’present bias and predictions implies participants understand 9-18% of theirpresent bias. We explore how an unexpectedly strong motivation by participants to be-have consistently when presented with past predictions complicates the interpretationof sophistication. By varying the timing of elicitations, we find evidence of “projectionbias”: participants wished to complete 4-12% fewer tasks when predictions and choicewere elicited right after some effort was taken than before.

∗We have benefited from discussions with Aaron Bodoh-Creed, Stefano DellaVigna, David Laibson, TarsoMori Madeira, Ted O’Donoghue, Charles Spenger, and Joshua Schwartzstein, as well as seminar audiences atUniversities of California Berkeley and Santa Barbara. Tarso Mori Madeira and Wei Wu provided wonderfulresearch assistance.†Haas School of Business, University of California, Berkeley. ned@haas.berkeley.edu‡Department of Economics and Business School, Harvard University. matthewrabin@fas.harvard.edu

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1 Introduction

In this paper, we report the findings from an experiment investigating the presence and scale

of the time-inconsistent taste for immediate gratification, the awareness of this taste for im-

mediate gratification, and the effects of contemporaneous work burden on attitudes towards

later work. The experiment involved choices and predictions about performing the unpleasant

task of transcribing blurry foreign letters: over the course of seven weeks, participants specified

the number of tasks they were willing to complete for different piece-rate wages on different

days. Preferences were elicited from participants for both immediate work and future work,

and both before and after exerting some effort on the tasks. Participants were also asked to

make incentivized predictions about their future willingness to work.

Participants prefer 10-12% less immediate work than future work. Using different ap-

proaches and specifications, we generally estimate the standard now-vs.-future present-bias

parameter β between .81 and .84. Participants appear to have no time preference among future

dates anywhere from 4 and 30 days away, so that we estimate the exponential daily discounting

parameter δ consistently very close to 1. Participants’predictions of future immediate-work de-

cisions largely match their future-work preferences, and we estimate the present-bias sophistica-

tion parameter βh to be very close to 1. Yet a positive correlation between participants’severity

of present bias and their predictions suggests they understand 9-18% of their present bias. We

discuss how these conclusions about sophistication are complicated by participants’unexpect-

edly strong preference to behave consistently when reminded of their predictions. With less

statistical certainty, participants also appeared to exhibit the hypothesized “projection bias”:

they commit to and predict about 4-12% more work when asked before having exerted effort

than when asked after, when their current distaste for the task was clearly higher.

Section 2 presents our experimental design: we recruited 100 UC Berkeley Xlab participants,

who were required to participate for seven days over a subsequent six-week period: the first in

the experimental laboratory and the following six using an online interface. In the experiment,

we refer to these as "participation dates," which we shorten to "dates" throughout the paper.

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Each date, participants chose how many unpleasant transcription tasks (between 0 and 100)

that they wished to complete for 5 randomly chosen piece-rate wages (between $0.01 and $0.31)

in the present and on a selection of future dates. Participants were also required to complete

the tasks from one previous decision for the corresponding wage, which was chosen at random

from questions answered on past dates or immediately before. Participants were also asked

to make predictions about their future task decisions, which were rewarded with bonuses if

accurate within 5 tasks. Finally, participants were required to complete 10 mandatory tasks

each date regardless of decisions, which imposed fixed transaction costs across dates, gave

participants experience with the task, and– by randomizing whether the mandatory work was

completed before or after decisions– allowed us to test whether distaste for current effort led

to systematic changes in work choices. From here on in, we refer to these 10 mandatory

tasks as “mandatory work”, and to the non-mandatory tasks simply as “tasks.”Participants

who completed the entire project received $50 on top of the average of $60 performance-based

earnings. If a participant failed to show up for a date or complete the tasks, she was immediately

removed from the experiment, receiving previously-made earnings, but not the $50 completion

payment. All participants, whether they completed the full 6 weeks or not, were paid their

earnings one week after the full 6-week experiment ended.

Section 3 outlines the models we are investigating, as well as the empirical strategy we use to

identify qualitative features and estimate parameters. We assume the standard two-parameter

model of present bias from Strotz (1956) and Laibson (1997), where intertemporal discounting

embeds the taste for immediate gratification β and long-run discounting δ into intertemporal

utility U t = ut+∑∞

τ=t+1 βδτuτ , and we follow Strotz (1956) and O’Donoghue and Rabin (1999a,

2001) in modeling sophistication about future present bias with the parameter βh ∈ [β, 1]

whereby the person believes she will discount by βh in the future; the closer βh is to β, the more

sophisticated the agent is about her self-control problems.1 The experimental design was meant

to identify each of these biases based on willingness to work at different wages from different

1Beliefs about future present bias have typically been notated by β in the literature; we notate it as βh inthis paper to avoid confusion with the econometric estimate of β.

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perspectives. Given a convex effort-cost curve, the participant will choose the number of tasks

that equalizes the perceived (expected) marginal disutility of effort against the later monetary

payment. Present bias can be identified by systematic differences in committed decisions made

for immediate work vs. future work. If we give people a small reward for accurate predictions

of future work, βh can be identified from comparing predicted future immediate-work choices

to actual immediate-work choices. By asking these questions for multiple wages, it is possible

to estimate cost-curve parameters, which allows simultaneous estimation of the parameters

β, δ, and βh. Finally, by exogenously varying the timing of choices and predictions relative

to the mandatory work, we are able to investigate the presence of simple projection bias as

modeled by Loewenstein, O’Donoghue, and Rabin (2003), whereby a person in one state tends

to project current tastes onto future states where tastes will differ. Positing and showing that

the distaste for the tasks would be higher immediately following completion of mandatory work

than before, we provide a crude measure of projection bias, α, as the difference in effort choice

and predictions regarding the exact same scenarios before vs. after this mandatory work.2

An important feature of our design is the variation in bonuses for accurate predictions,

ranging from $0.25 to $8.25. While small prediction-accuracy bonuses allow full identifica-

tion in principle, one might worry that they provide little incentive for accuracy. Yet large

payments introduce potential distortions to our estimates of β and βh. The first distortion is

obvious: participants may change their immediate-work decisions to match earlier predictions

to receive the bonus. To get estimates independent of this distortion, we had 83% of immediate-

work decisions involve no previous prediction. More problematically, when the bonus is large,

sophisticated present-biased participants would recognize that prediction-accuracy payments

can be used as partial commitments, causing the would-be prediction to be higher than the

"straightforward prediction" given no bonus payment. Furthermore, as bonuses were given if

chosen tasks were within 5 of predicted tasks, the person would choose five tasks above this

2Although it was originally our intention to do so, upon reflection we lost confidence in our ability to estimatewith our data a tight theory-based estimate of the parameter α defined by Loewenstein, O’Donoghue, and Rabin(2003) to measure the degree of projection bias. We discuss different strategies of measuring projection bias inour experiment in Section 3.1.3 and Appendix Section A.4.

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desired amount. So long as participants treat prediction-accuracy bonuses in the same way as

wages, all the variation across bonuses and wages would in principle allow and even facilitate

structural identification of βh given how participants used the predictions for both accuracy

and as soft commitment devices. Yet (in addition to worries that a structural estimation of

this sort would push some functional-form assumptions too far) we anticipated a possibility

outside of formal models of present bias and commitment: that even people who understand

their future present bias might make straightforward predictions that do not optimally ex-

ploit the potential for commitment. Therefore, we further test if predictions are sensitive to

the prediction-accuracy bonus, and control for the use of accuracy-payments as commitments

accordingly.3

We analyze our results using simple reduced-form tests in Section 4 and (with highly con-

sistent results) using a structural model in Section 5. In both sections, we perform an aggregate

analysis in which all participants are assumed to have the same main parameters, and an indi-

vidual analysis in which parameters are allowed to fully vary across participants. As it happens,

only 72 of the 100 participants had enough observations, variation, and consistency in choices

to estimate individual parameters.4 In Section 5, for comparability we conduct the aggregate

analysis only with these 72 participants, but in the Appendix we show that the aggregate

analysis is robust to (among other things) the inclusion of all 100 participants.

Section 4 provides reduced-form evidence of our main findings. There is (strongly statisti-

cally significant) present bias in the aggregate, with participants choosing on average 5.7 fewer

immediate tasks than future tasks (43.5 vs. 49.1) overall, 5.3 fewer when controlling for fixed

effects for each wage, and 4.9 fewer when focusing only on decisions from the third date on–

where the data are reassuring that participants were not learning about the unpleasantness

3Given that designed the experiment to not draw participants’attention to the commitment potential ofpredictions, we do not see the design as a generalizable test of people’s willingness to use commitment devices.Rather, our goal was to see if sophistication could be identified separately from that willingness.

4We remove participants from analysis if the maximum likelihood routine could not converge or, in two cases,led to very extreme estimates. For example, multiple participants choose nearly the same interior task decisionregardless of wages while others choose very non-monotonically across wages, both behaviors which are diffi cultto rationalize with any standard economic model. It is not clear why the removal of these participants wouldbias our results, although we check for any effect (and find none) in the Appendix.

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of the task. The present bias is “quasi-hyperbolic”rather than hyperbolic: The difference in

preferences for work between 4 and 30 days into the future were small, insignificant, and un-

patterned. There is evidence for near-complete naivete in the aggregate: participants predict a

(statistically insignificant) average of 0.7 fewer immediate-work tasks in the future than their

current future-work choices, and a (statistically insignificant) average of 0.2 more immediate-

work tasks when analyzed using wage fixed effects or focusing on later dates. There is a large

amount of individual variation due either to individual preferences or noise, with 24% of indi-

viduals choosing more immediate than future work and 47% making higher predictions than

future work. We do find significant positive correlation (0.246) between the present-biased

taste for fewer immediate tasks and beliefs about such a taste in the future, suggesting some

level of sophistication. Finally, we find initial support for projection bias: participants chose an

average of 2.1 - 3.3 fewer tasks after completing the mandatory work than before. Although

the differences in these basic analyses are not statistically significant, the estimates are larger

and more statistically significant when we account for the 40% of censored task decisions at 0

or 100.

Section 5 reports the aggregate and individual structural identification of the parameters

β, δ, βh, and α by assuming a power cost function, a linear monetary utility function, and a

normally distributed error term added to the effort decision. These findings largely mirror the

reduced-form findings. Although we report a large array of regressions, given different fixed

effects, including and excluding the use of predictions as commitment devices, and focusing

on later decisions, our primary conclusion is quite stable: the null of β = 1 is always strongly

rejected, with the estimate of the present-bias parameter β ranges from 0.81 to 0.84 in the

aggregate analysis, and the average estimate of β ranges from 0.79 to 0.87 in the individual

analysis.5 Aggregate estimates of βh range from 1.00 to 1.01, and average individual estimates

5In 5 specifications, we find a daily discount factor δ of between 1.003-1.005, rejecting the null hypothesisof δ = 1 in one case with marginal rejection in two. The daily discount rates imply a weekly discount factor of1.02-1.03 and a yearly discount rate of 3-6. Our ex-post intuition of the positive discount factor is that, due touncertainty, participants are less willing to commit to large amounts of work farther in the future. Note thatthis effect would bias our estimate of β upward, which we discuss and estimate in Appendix Section A.2.

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range from .98 to .99.6 In each case, the null hypothesis of no perceived present bias (βh = 1)

cannot be rejected, and full awareness of the present bias (βh = β) is strongly rejected. But we

find significant correlation between individual estimates of β and βh indicating some degree of

sophistication: The regression of estimated perceptions about present bias 1− βh on estimates

of true present bias 1−β is positive and significant, ranging from 0.13 to 0.18 for all participants

and 0.19 to 0.23 for participants with estimates of βh < 1. The structural analysis provides

strong evidence for projection bias: with strong statistical significance, people chose 4.1 to 7.3

fewer tasks immediately following mandatory work than immediately before in the aggregate

analyses, and an average of 6.4 fewer in the individual analysis.

Section 6 compares our approach and findings to other recent empirical research. The

platform and task used most closely resembles Augenblick, Niederle, and Sprenger (forthcom-

ing), But more generally our findings of present bias accord with other recent experimental

and field data that have moved away from the common money-immediacy paradigm that has

dominated experimental investigations into time preference, to an approach that more directly

tests present bias as employed in economic theory and applications. Clear evidence about the

degree to which people are sophisticated about their present bias is rarer. Our approach differs

from most studies of sophistication in attempting to identify naivete from misprediction per

se rather than the taste for commitment, and we believe we are among the first papers to

use an experimental manipulation to directly estimate the βh parameter. We believe we are

also among the first to investigate projection bias over disutility of effort, with results that

seem consistent with the smaller experimental and ecological empirical literature showing how

random variation in the current state affects prediction of future tastes.

We conclude Section 6 and the paper with a discussion of some of the potentially worrisome

aspects of our identification strategy glossed over in the analysis of paper. We begin by noting

that our analyses may be underestimating the degree of both present bias and projection bias

by assuming that all the measured cost of doing the task is immediate unpleasantness, rather

6We estimate β < 1 for 69-78% and βh < 1 for 54-60% of participants.

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than financial or opportunity cost. Section 6 reports on various robustness checks supplied in

several appendices on the limitations of our primary analyses. We show, for instance, that while

there is evidence participants continue to learn about the unpleasantness of the task or improve

performance for the first couple of weeks, there seems little change after that; all analyses

basically hold when analyzed on later dates or when the cost function is allowed to vary over

time. There may of course be persistent uncertainty by participants about future costs on

particular days; in Section 6 and Appendix A.2, we argue that this is likely to underestimate

the severity of present bias and have an ambiguous effect on βh, and we also redo analysis

by estimating the empirical uncertainty from choice behavior. Section 6 and Appendix A.5

discusses robustness to various ways of handling the 28 participants who either exited the

experiment early or who did not respond to incentives in an interpretable way. The most

noteworthy caveat to the analysis in this paper arose from unexpected results indicating that

we (and all other formal analyses we know of!) missed an important preference or other

psychological component in predicting behavior: participants who were reminded of earlier

predictions exhibited an unexpectedly strong motivation to behave consistently with those

predictions– by either exactly matching the prediction or performing within 5 tasks virtually

no participant lost the bonus– in a way that cannot be explained by their pecuniary incentives.7

This complicates the interpretation of sophistication– in principle participants who predicted

this consistency taste may have been employing commitment devices after all. But we delineate

various reasons in Section 6 and Appendix A.3 why we think such sophisticated interpretation

is unlikely.

7Indeed, the patterns we observe are hard to explain even by simple dissonance stories we might have guessed;reminding a participant of their predictions for close-by wages, which might be expected to arouse participants’sense that they are being inconsistent or misbehaving, seemed not to influence behavior. Also, participantsoften violated their predictions in ways, simply not so much as to lose their bonus.

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2 Experimental Design

Our study examines participants’work decisions about the completion of unpleasant transcrip-

tion tasks over time. The experiment took place over seven days across six weeks, with the first

date occurring in the laboratory and the later dates requiring logging into a website accessi-

ble from any computer. Each date, participants stated work preferences and predictions, as

well as completing mandatory work and agreed-to tasks based on past decisions. Section 2.1

describes the task in more detail, Section 2.2 discusses choice of dates and payment details,

Section 2.3 walks through each of the components of participation dates, Section 2.4 describes

our randomization procedures, and Section 2.5 describes the sample characteristics generated,

including information about attrition.

2.1 Experimental Task

Each task consisted of a simple transcription of 35 blurry Greek letters through a computer

interface, using the mouse to point and click on the corresponding letters. The top panel of

Figure 1 is a screenshot from the interface. In order to maintain the full attention of the

participant throughout the task, an auditory “beep” sounded randomly every 5-15 seconds

throughout the transcription process, and the participant was required to press a button at the

bottom left of the screen after hearing this noise. If the participant did not press the button

within five seconds of the beeping noise, or pressed it when there was no beeping noise, all

work for the current transcription was erased.8 To be accepted as completing the task, we

required 80% accuracy, defined as an answer that required fewer than 7 insertions, deletions,

or character changes to match the target text.9 If the transcription was not accurate enough,

the participant was informed and could immediately correct the text.

8We are confident we succeeded in making the task unpleasant.9Although we did not record the number of (failed) submitted transcriptions which did not achieve 80%

accuracy on first attempt, more than 95% of transcriptions were more than 90% accurate when accepted,suggesting that participants were not minimizing effort to tightly match the accuracy cutoff.

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Figure 1: Screenshots of the transcription task (top), the decision interface for decisions aboutpresent work (middle) and predictions about future work (bottom).

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2.2 Participation Dates and Payment Logistics

When participants were recruited, they were told that the experiment required six addi-

tional days of participation over the ensuing six weeks, and were asked to choose these dates

prior to the first day of the experiment. The dates were required to be between 4 and 10

days apart, with the last date required to be completed within six weeks of the start of the

experiment. Participants were allowed (for a fee of $.25) to modify the dates over the course

of the experiment. We allowed this modification to insure participants against large scheduling

shocks, such as learning that a midterm occurred on a previously chosen date. To allow for such

date changes without permitting last-minute procrastination that would have confounded our

results, participants were allowed to modify a date only up to 5 p.m. of the prior day.10

Participants were paid $50 for completing the minimum requirements of the experiment

and paid additional amounts depending on their choices. If participants did not complete

all required components for some date, they were immediately removed from the study and

forfeited the $50 completion payment, but still received any previous earnings. Participants,

including those who were removed, received all payments associated with the experiment by

check exactly seven weeks from the start of the experiment. This later date was chosen for

payments to avoid any present bias associated with positive consumption from the payment.

Average earnings were about $110 for those who completed the entire experiment.

2.3 Experimental Components

Participation dates involved a set of experimental components that we describe below: complet-

ing mandatory work, stating preferences over future work, stating preferences over immediate

work, stating predictions about future decisions, observing the one supplemental work decision

that will be implemented for that date, and completing supplemental work in that decision.

All of these components were completed on each date except for the initial laboratory visit

10Date modification was rare: 12 participants modified dates once and 2 did so more than once. We did notintend to (and did not) analyze anything about participants’choices of or modifications of dates.

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(when there was not enough time to complete non-mandatory tasks) and the final date (when

we could not ask about future tasks).

On the first day of the experiment, participants were given instructions about the entire

experiment prior to making any decisions, including the logistics for all of the components

of the experiment and payment. Participants were informed of all points of randomization–

including payments, supplemental work determination, and ordering of components– although

they were not told of the exact distributions (discussed in next subsection) when complicated.

We explicitly told participants that all randomizations had been previously chosen by a random

number generator and therefore could not be affected by any of their decisions.

After the first day, participants received reminder emails with a link to the experimental

website both on the night prior to and the middle of each date. Once they clicked on the

experimental link, they saw an experimental timeline with all components of the experiment to

be completed during that day. While the instructions were always presented first, the ordering

of the rest of the components for online dates were determined by block randomization, which

allows us to test for ordering effects. After each component was completed, participants were

reminded of the timeline of the experimental day.

2.3.1 Completion of Mandatory Work

Each date, participants were required to complete mandatory work. These mandatory tasks

(1) gave the participants experience with the task, (2) required that the participants allocated

at least 10 minutes to each date, eliminating any fixed cost associated with completing some

rather than none of the tasks, and (3) allowed us to study whether contemporaneous distaste

for the task affected people’s willingness to do the task in the future.

2.3.2 Decision Type 1: Current and Future Work Decisions

Each date, participants were asked a sequence of questions concerning preferences about com-

pleting additional supplementary transcription tasks for five different wages on the present date,

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as well as for two future dates. The middle panel of Figure 1 shows the computer interface used

to elicit preferences for immediate work. For example, on the first line, a participant is asked

for the number of tasks she would like to complete immediately if given a wage of $.20/task,

using the slider bar to choose a number between 0 and 100.11 Once participants completed all

five decisions, they were allowed to submit the decisions. The computer interface used to elicit

preferences for future work is the same, with the exception of the timing description.

The five wages in each decision set were chosen randomly from wages from $0.01/task

to $0.31/task. This implies hourly wages of between $0.80/hour and $24.80/hour given the

average empirical completion rate of 45 seconds per task. The wide range of wages was used

to induce enough variation in participants’responses for estimation of effort parameters. To

ensure that participants paid full attention to the exact wage in each decision, and (for better

or worse) to avoid encouraging consistency across wages, the order of the five wage decisions

was random. The interface displayed hourly wage estimates and time-to-completion estimates

using a default task completion time of 55 seconds, with the option to enter different completion

times to generate different estimates. Each of the decisions had the potential to be randomly

chosen as the one decision-that-counts, in which case the participants were required to complete

the stated work for the specific wage on the relevant date.

2.3.3 Decision Type 2: Predictions of Future Work Decisions

In addition to making decisions about future work, participants were also asked to make predic-

tions about potential future immediate-work decisions given five randomly chosen wages. For

example, on November 12th, a participant might have been asked to predict the number of

tasks that they thought they would choose on November 18th when facing a wage of $0.15. For

each set of five wages, the participants were presented with a bonus that they would receive

on the future date if the given wage appeared in a immediate work decision chosen as the

11In order to minimize the extent to which the interface points a subject towards a default work decision, allslider points started in the middle position, slightly elevated from the slider bar with no assigned number. Oncethe slider point was clicked, it dropped to the slider bar and could be dragged.

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decision-that-counts and they choose a number of tasks within 5 tasks of their prediction. The

bonuses were randomly chosen from 14 bonus payments from $0.25-$8.25.12 The bonuses were

varied to later identify and control for the use of the accuracy payment to incentivize future

decisions. The computer interface that elicited these decisions is shown in the bottom panel of

Figure 1.

As participants were aware, if they faced a work decision later for which they had previously

made a prediction, they were reminded of the prediction with a visual cue on the work-decision

slider bar. Although the choice to provide prediction reminders potentially anchored the par-

ticipants on their prediction, we felt not reassuring them that we’d remind them would create

a potentially severe identification problem, since we could not know how likely it was that they

thought they would remember their predictions.

2.3.4 The “Decision-That-Counts”and Work Decisions

Participants were asked questions about their preferred number of tasks to complete on fu-

ture dates and the current date given different wages. Therefore, at the time of determining

the one decision-that-counts for a given date, participants would have made many past and

present decisions about work on that date.13 These decisions were all collected and displayed

to participants. Then, one decision was randomly chosen as the decision-that-counts.

Once the decision-that-counts was chosen, the participant was required to complete the

number of supplementary tasks chosen for the wage in the decision-that-counts. For example,

if the decision-that-counts involved a wage of $0.18/task, and the participant previously chose to

complete 40 tasks for that wage, the participant was then required to complete 40 supplementary

tasks for a supplementary payment of $7.20. If a participant did not complete these tasks, she

was immediately removed from the experiment and forfeited the $50 completion payment.

12The potential bonuses were .25, .40, .65, .85, 1.00, 1.25, 1.75, 2.25, 2.75, 3.25, 4.25, 5.25, 6.75, and 8.25.13Recall that participants could modify the timing of participation dates. Participants knew that if a date

was modified, then the decisions about that partictipation date were transfered to the new day.

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2.4 Randomization

The order, number, and types of decisions varied across dates and between participants. There

are a variety of ways in which the ordering and randomization deviated from purely independent

uniform draws. First, while the five wages in each decision set were drawn from a uniform

distribution across possible wages, we threw out sets with no wage lower than $.15 or no wage

higher than $.20. This was done to reduce the number of decision sets with too little variation

in decisions to comfortably identify effort costs. Second, wages for work decisions were chosen

to match either all, two, or none of the wages from previous prediction sets. This was done to

ensure that participants’predictions would potentially affect their payoff, while also allowing

for immediate work decisions that were uninfluenced by past predictions. On average, 11% of

predictions were for wages that later appeared for actual decisions. Third, to ensure enough

variation to identify the effects of bonuses, no participant received the same bonus for different

prediction sets. Finally, to ensure that participants’predictions and future work decisions were

evenly spread across future dates, the relevant date of participant’s predictions or decisions

were not randomly chosen. For example, on date 2, participants either made decisions about

future work on dates 3 and 5 or decisions about future work on dates 4 and 5. No participant

made a work decision for more than three dates in the future or a prediction decision more

than more dates in the future. On the first and sixth dates, participants made one set of future

work decisions and one set of future predictions. From the second to the fifth date, participants

made two sets of future work decisions and two sets of future predictions.

2.5 Sample

100 participants from the UC Berkeley Xlab subject pool were recruited into the experiment

across 4 experimental sessions on October 17-19, 2012.14 79 completed all seven weeks of

14We placed no restriction on participation except that we disallowed those who were subjects in Augenblick,Niederle, and Sprenger (2013).

15

the experiment and received the $50 completion payment.15 Participants who completed the

experiment made 130 decisions each. In total, participants made 11,405 decisions: 2,750 about

immediate work, 4,235 about future work, and 4,420 predictions.

For the individual analysis, we estimate individual time-discounting and cost parameters.

For 26 participants, it was impossible to estimate individual parameters using our main identi-

fication strategy. These participants have too few observations (due to early attrition), exhibit

too little variation in work decisions, and/or have so many non-monotonicities or inconsistent

work decisions that the baseline maximum likelihood routine does not run or does not con-

verge. As extreme examples of each of these issues, seven participants exited the experiment

after the first date, four participants completed the experiment but did not vary their task

decisions once across their 130 decisions, and six participants had non-monotonities in more

than a third of their decision sets. The remaining participants with no estimates had some

combination of these issues. In addition to these 26 participants, the irregular decisions of 2

participants lead the maximum likelihood routine to converge with estimated parameters that

are very clear outliers from all other participants.16 We therefore focus on the remaining 72

participants in the individual results section. For consistency, we estimate the aggregate results

with this restricted sample.

Appendices A.5-A.10 contain information about the attritors as well as a variety of robust-

ness checks on specification choices, participants sample, and choices sample. For example, we

replicate our main aggregate estimation table but including the entire sample of participants

and the entire sample minus attritors. The qualitative results are unchanged, although the

estimate of the present-bias parameter β is moderately lower when using these samples. Simi-

larly, we run the analysis given three different choice samples– such as removing decisions that

were very similar to recent decisions– and under a variety of alternative specifications using

different assumptions about the form of decision error. All of these robustness checks support

15Of the 21 subjects that did not complete the experiment, 7, 7, 1, 1, 4, and 1 subject(s) dropped out onparticipation date 2, 3, 4, 5, 6, and 7, respectively.16For example, the estimates of βh for these participants are both greater than 2. A Grubbs’test identifies

these observations as outliers with a p-value less than 10−5.

16

the qualitative conclusions from the main text.

The average completion time for a single transcription task over the course of the seven

dates was 56, 48, 44, 43, 42, 42, and 42 seconds, respectively. Because there appeared to be

some learning early in the experiment, our analysis and discussion below differentiates early and

late behavior when conceptually relevant. Furthermore, in the structural analysis, we explicitly

estimate and control for changes in cost function over time. In Appendix A.1, we demonstrate

that weekly parameter estimates remain stable over the course of the experiment.

3 Model and Identification Strategy

In this section, we outline a model of the experimental decisions and discuss the consequent iden-

tification of cost, time-preference, projection-bias, and sophistication parameters given these

decisions. Our design is geared mainly towards the identification of the present-bias parame-

ter, β, and the sophistication-about-present-bias parameter, βh. Loosely, comparing decisions

about future work with those about immediate work allows for the identification of β and the

other cost and discounting parameters. Similarly, comparing the decisions about future work

with predictions about future behavior given different bonus payments allow for the identifica-

tion of βh. The identification of βh depends on our assumptions about how participants make

predictions: we first discuss the model and identification of parameters under the assumption

of straightforward predictions and then assume that participants use prediction-accuracy pay-

ments as soft-commitment devices. Finally, we explain how the model can crudely test for

projection bias by comparing the difference in decisions before and after completion of the

mandatory work.

3.1 Theoretical Model

We begin by presenting the simple model that underlies our baseline identification strategy

of the parameters β, βh, and δ, first supposing that agents make straightforward predictions

17

and that they exhibit no projection bias. The model, in line with both existing literature and

our own ex-ante assumptions, focuses solely on the tradeoff between effort costs and monetary

reward, ignoring the apparent taste for following predictions we see in the data. We do not

include the realistic possibility of uncertainty about future preferences, although we extend the

model to include this possibility in Appendix A.2.

3.1.1 Baseline

For the effort decisions in our experiment, the agent chooses a number of tasks (an effort level)

e to complete at time k given a per-task wage w received at time T > k. At time k, the effort

level e from the decision-that-counts is chosen and the agent must complete the effort level e at

time k or receive a penalty P at time T . To match the experiment, we assume that the agent

is also required to complete 10 mandatory non-compensation tasks at time k or receive penalty

P at time T .

An agent with present-biased preferences making a decision at time t = k will choose

immediate effort

e∗(w; present) = arg maxe

β · δT−k · U(e · w)− C(e+ 10), (1)

where C(e) is a convex effort-cost disutility function, and U(m) is a (separable) concave utility

function that maps a future monetary payment m into future consumption utility.

The decision for an agent making a decision at time t for effort at time k is more complicated

than the immediate-effort case. In this case, the agent must first consider her own future actions

at time k if her effort choice e is chosen as the decision-that-counts given her present bias

perception βh. She will face the decision to complete e tasks or complete no effort and receive

a penalty P . In the experiment, we chose a relatively large penalty ($50) with the presumption

that it will force participants to complete previously chosen effort levels. Therefore, for the

model, we assume that P is large enough so that the agent will always choose to complete e

18

even when the effort is completed immediately.17 Knowing this, the agent at time 0 will choose

the effort that maximizes her current utility

e∗(w; future) = arg maxe

δT−k · U(e · w)− C(e+ 10). (2)

For the prediction decisions in our experiment, the agent predicts effort level p at time t < k

about her future decision e at time k given a per-task wage w received at time T, with a bonus

payment b received at time T if future chosen effort e is equal to p. We first assume that the

agent makes straightforward predictions, in that she simply truthfully reports her prediction

of her future work decision given no distortionary effect of the prediction-accuracy payment.

Under this assumption, the agent will predict

e∗(w; prediction) = arg maxe

βh · δT−k · U(e · w)− C(e+ 10). (3)

In anticipation of the identification section, we note that the parameters β and βh provide

the only difference between the maximization problems (1), (2) and (3).

3.1.2 Predictions-as-Commitment

In the model above assumes the agent made straightforward predictions. In removing this

simplifying assumption, an agent with βh < 1 will take two things in consideration that might

make her prediction differ than her beliefs about bonus-free behavior. First, she will “predict”

higher future immediate-effort choice as the bonus payment b rises, because the bonus can act

17This assumption appears reasonable given the estimated parameters in our main specification: an agentwould need to have βh < 0.1 to believe that, in the future, she would prefer to suffer the penalty rather thanwork. In the event, seven participants were removed from the experiment for not completing the tasks theyagreed to do. Reassuringly, six of these removals occured on the first at-home date, suggesting these participantsdiscovered something about the experiment immediately, rather than indicating any time inconsistency in theirvaluation of P.

19

as a soft commitment device. This leads the agent to make the prediction

e∗(w, b; prediction,soph) = maxe δT−k · U(e · w + b)− C(e+ 10)

such that:

βh · δT−k · U(e · w + b)− C(e+ 10) ≥

βh · δT−k · U(e∗(w; prediction) · w)− C(e∗(w; prediction) + 10)).

(4)

That is, the agent will predict the effort level closest to e∗(w;future) such that, when the future

arrives, the bonus will compel her to choose that effort level, rather than choosing her predicted

bonus-free level e∗(w;prediction). When b is extremely high, the agent will predict the uncon-

strained optimum e∗(w;future). As b falls, the agent’s predictions approach e∗(w;prediction) to

satisfy the constraint.

Recall that we equally rewarded predictions that were within five tasks of the chosen effort,

leading to the second distortion. When βh < 1, the agent believes that, in the future, she will

prefer a lower effort than she currently prefers. As she will be able to choose 5 fewer tasks

than the prediction and still receive the bonus when future arrives, the agent must adjust her

prediction to be 5 higher than her target level to incentive herself in the future to complete

these tasks, leading to the adjusted decision

e∗(w, b; prediction,soph,adj) = e∗(w, b; prediction,soph)+5.18 ,19 (5)

Given these two effects, an agent with βh < 1 who recognizes the incentive effects of

prediction-accuracy payments will made predictions that rise with the bonus amount rise and

level out at future effort choices plus five tasks. Conversely, straightforward predictions do not

vary with the bonus level b. When βh = 1, there is no difference between the predictions.

18Similarly, when βh > 1, the agent must adjust her prediction downward. When βh = 1, the agent istechnically indifferent between all choices within 5 of e∗(w;future)– this agent believes that she is time-consistentand will choose e∗(w;future) in the future regardless of the bonus.19Of course, the suggestion that the agent’s prediction will be exactly five tasks above e∗(w, b;

prediction,soph) ignores uncertainty. Unfortunately, the precise effect of uncertainty on the prediction de-pends heavily on the location and shape of the error term.

20

3.1.3 Projection Bias

The experiment is also designed to help examine “projection bias”in effort decisions. Building

from experimental and psychological evidence, Loewenstein, O’Donoghue, and Rabin (2003)

refer to projection bias as the tendency for a person to make decisions about the future as if her

tastes in the future will reflect her current tastes rather than predictable future tastes. In the

context of our experiment, a natural model of projection bias is that agent will (mistakenly)

project her current marginal disutility—the marginal cost from the next task she completes,

which we label C ′(ep) given she has just completed ep previous tasks—onto her marginal costs

from the eth task C ′(e). Under the simple parameterization in LOR (2003), where α ∈ (0, 1]

measures the severity of projection bias, her perceived marginal cost would be C ′(e) = (1−α) ·

C ′(e) + (1 − α) · C ′(ep).20 Consequently, a person who has completed more work (such as the

10 mandatory tasks) just before the time of decision will perceive that her marginal costs from

all subsequent tasks are higher, leading to lower work decisions for a given wage.21

3.2 Empirical Identification

In order to identify the parameters β, δ, βh,and α, we must make further structural assump-

tions about the monetary utility and effort cost functions. Specifically, we will assume that

the cost function takes a power form, with parameter γ > 1, and that the utility function in

money is linear with slope parameter ϕ > 0. Define 1(t = k) as an indicator function that

the decision occurs in the same period as the expenditure of effort and 1(p = 1) as an indica-

tor function that the decision is a prediction. We discuss identification given straightforward

predictions, identification given the use of predictions as soft commitments, and crude identifi-

20The influence of projection of this sort includes misprediction of immediate effort, not just future effort.Indeed our experiment involves testing of such continuation-effort projection. In this case, although the relevantmisprediction (of marginal disutility of effort) remains the same, the right overall utility function (for a ≥ a∗)utilities Ca∗(a) = C(a∗) + (1− α) · [C(a)− C(a∗)] + (1− α) · [C ′(a∗) · (a− a∗)].21There are other, potentially less natural, models which lead to similar qualitative predictions. For example,

imagine that a person who has just performed ep tasks perceives the cost from completing a fresh set of tasksas if she had already completed ep tasks. That is, with the linear parameterization: C(e) = (1−α) ·C(e)+ (1−α) · C(e+ ep).

21

cation of projection bias. In Section 5, we employ the identification strategy for aggregate and

individual analysis. For the aggregate analysis, we first assume that all participants share the

same parameters, and then assume that participants only differ in the slope parameters. For

the individual analysis, we use the same structure to separately estimate each parameter for

each participant.

3.2.1 Baseline

Given straightforward predictions and no projection bias, the equations that define the optimal

immediate-work decisions, future-work decisions, and predictions ((1), (2), and (3)) can be

written as

arg maxe

ϕ · β1(t=k) · β1(p=1)h · δ(T−k) · e · w − 1

γ(e+ 10)γ. (6)

Taking the first-order condition of (1) with respect to e and solving for e yields the predicted

choice e given parameters β, βh, δ, γ, ϕ and experimental variation in w, k, and the type of

decision:

e(w; present) = (ϕ · β · δ(T−k) · w)1

γ−1 − 10. (7)

e(w; future) = (ϕ · δ(T−k) · w)1

γ−1 − 10. (8)

e(w; prediction) = (ϕ · βh · δ(T−k) · w)1

γ−1 − 10. (9)

Assuming that observed effort is distributed around this predicted level of effort with a

normal error term ε with mean 0 and standard deviation σ yields to a likelihood of observation

i of a work decision ei of

L(ei|β, βh, δ, ϕ, γ) = φ(ei − eiσ

), (10)

22

where φ is the standard normal probability density function. Loosely, each parameter is iden-

tified by variation in the experimental variables. Variation in whether the decision occurs on

the day of effort (t = k) identifies β. That is, as β falls, participants will choose to complete

fewer tasks when effort occurs on the same day rather than in the future. Variation in whether

the decision is a prediction (p = 1) identifies βh. That is, as βh falls, participants will pre-

dict that they will choose fewer tasks when effort occurs on the same day than the number

of tasks they choose when effort occurs in the future. Variation in the distance-to-payment

(T − k) identifies δ.22 That is, as δ falls, participants will choose to complete fewer tasks as the

distance-to-payment rises. Variation in wages w identifies ϕ and γ. That is, changes in ϕ and

γ change the shape of tasks decisions given changes in wages. Variation in ei identifies σ. That

is, as σ rises, observed decisions ei differ more from ei.

To deal with the presence of corner solutions in effort decisions (where participants are

required to choose between 0 and 100), we follow the correction in a Tobit regression and

adjust the likelihood to account for the possibility that the tangency condition implied by (7)

does not hold with equality:

Ltobit(ei|β, βh, δ, ϕ, γ) = 1(ei < 100)φ(ei − eiσ

) + 1(ei = 100)Φ(ei − 100

σ), (11)

where Φ is the standard normal cumulative density function. For estimation of the parameters,

we maximize the sum of the logarithms of Ltobit using standard maximum-likelihood routines.

22Because participants choose participation dates, the distance between dates– used to estimate the standardexponential time discounting parameter δ– is endogenous. In Appendix A.12, we show that there is virtuallyno change in our estimates when we use the average distance between participation dates in our estimation.

23

3.2.2 Predictions-as-Commitment

Assuming that people are using predictions as soft commitments, as in equation (5), the optimal

prediction changes to

e(prediction,soph,adj) = arg maxe ϕ · βh · δ(T−k) · (e · w + b)− 1γ(e+ 10)γ + 5

such that:

ϕ · βh · δ(T−k) · (e · w + b)− 1γ(e+ 10)γ ≥

ϕ · βh · δ(T−k) · (e · w)− 1γ(e+ 10)γ,

where e = (ϕ · βh · δ(T−k) · w)1

γ−1 − 10,

(12)

when βh < 1, with an analogous adjustment of -5 when βh > 1. To avoid a discontinuity at

βh = 1 (where there is no adjustment of five tasks), we locally smooth the adjustment around

βh = 1. There is a unique solution to this maximization problem as the objective function

is concave under the assumption that γ > 1. For estimation, it is necessary to numerically

determine e(prediction,soph,adj) as there is no closed-form solution. Replacing e(prediction) with

e(prediction,soph) in equations (10) and (11) yields the full likelihood function.

3.2.3 Projection Bias

In Appendix A.4, we estimate two variants of the projection-bias models discussed in Section

3.1.3. In both cases, we estimate a statistically-significant parameter that lies within a rea-

sonable range for multiple specifications. We do not include this estimation in the main paper

and are skeptical of its meaning beyond its sign, largely because the estimate is identified off

of just two points on the cost curve and leans heavily on the functional form of the cost curve.

Consequently, we report a simple measure of projection bias that requires no structural or

functional-form assumptions: the change in the chosen number of tasks α due to the timing of

the mandatory work, which should be zero if participants have no projection bias. To do this,

we define 1(bm = 1) as an indicator that the decision is made before the mandatory work and

24

simply add 1(bm = 1)α to the equations in (7). Although our only analysis of the structural

projection-bias parameter is in Appendix A.4, in Section 5 below we estimate α in the context

of a structural estimation of the time-preference parameters.

4 Reduced-Form Analysis

Before estimating the parameters in our structural model, this section describes the data and

performs a set of simple non-parametric analyses of an aggregate and individual level. Recall

that the interpretation of participants’ predictions about future work decisions depends on

participants’recognition that predictions can be used as a soft commitment devices. We begin by

abstracting from this issue, and present data as if participants make straightforward predictions

about expected effort. We then show that there is little evidence of the two potential distortions

that would be expected if participants were using predictions as commitment devices. In Section

4.3, we show that allowing for such use has little effect on the structural results. Throughout

the paper, all reported or graphed standard errors are clustered at the participant level unless

otherwise noted.

4.1 Present Bias and Perceptions of Present Bias: Aggregate

To visualize the effect of wages on choices, the two graphs in Figure 2 show the average task

decisions given different wages for work decisions and predictions. For visual ease, observations

from the 31 wages are placed in 10 bins. Note that, for each type of decision, average task

decisions monotonically rise with offered wages, suggesting that the participants in our primary

sample understand the tradeoff between effort costs and monetary payoffs. In fact, on an

individual level, 66 of the 72 participants have fewer than 5 total non-monotonicities as wages

rise within a decision set (given a total of 104 violation opportunities in adjacent decisions for

the full experiment). Given that wages were randomly ordered and often very close to each

other, we take this as evidence that the participants in our primary sample understood the

25

Figure 2: Present vs. future decisions (left) and predictions vs. future decisions (right)

Note : Left graph: Comparison between decisions make about work in the future and decisionsmade about work in the present given different wages. The difference is a reduced-form measureof present bias. Right graph: Comparison between decisions make about work in the future andpredictions made about work in the future given different wages. The difference is a reduced-form measure of sophistication about present bias. For readability, wages are grouped into 10bins. Standard errors bars are clustered at the individual level.

main tradeoff in the experiment.23

Recall that present bias is intuitively identified by the comparison of decisions about future

work and decisions about immediate work. The left-hand graph compares these decisions for

difference wages. The task decisions for immediate work appear consistently lower than the

decisions for future work, particularly for higher wage levels, which matches the predictions of

the quasi-hyperbolic model. When making decisions about the immediate work, participants

choose an average of 5.7 (Z = 4.10, p < 0.001) fewer tasks than when making decisions about

future work.24

Our evidence would seem to speak fairly loudly about the quasi-hyperbolic specification of

present bias, where the departure from exponential discounting occurs only between “now”and

23Perhaps this is not surprising: large monotonicity violations would likely cause our individual estimationstrategy to fail and lead to the removal of the participant from the primary sample. However, even participantsremoved from the primary sample generally increase decisions with wages: only one participant has a cleardownward trend as shown in Appendix section A.5.24The difference remains similar at 5.3 (Z = 4.52, p < 0.001) when controlling for fixed effects for each wage

and 4.9 (Z = 3.05, p = 0.003) when focusing only on decisions after the second participation date.

26

Figure 3: Work decisions given different delays to the time of work

Note : Left graph: Work decisions given the number of participation dates until work occurs.Right graph: Work decisions given the number of calendar days until work occurs. The 2percent of decisions about work in 22 or more days are added to the final column. Standarderrors bars are clustered at the individual level.

“later.”The two graphs in Figure 3 show the average task decisions across all wages depending

on the number of participate dates (left graph) or calendar days (right graph) until the work

must be completed, with zero days representing decisions about immediate work. Because no

participant made a decision more than three dates into the future and dates were required to

lie between 4 and 10 days apart, future dates are all between 4 and 30 days into the future. For

readability, calendar days are combined into 4-day groups. The visual evidence that people are

present-biased but do not differentiate among is confirmed by statistical tests. Task decisions

about immediate work are 5.2, 6.7, and 5.7 lower than decisions for work in the following three

future dates, respectively, with p < 0.01.25 None of the decisions for work on future dates are

pairwise statistically significantly different (the highest statistic is Z = 0.89, p = 0.38). The

same basic results hold with calendar days.26

25The differences remain similar at 5.0, 5.5, and 5.5 (Z = 3.93, p < 0.001; Z = 3.92, p < 0.001; Z = 3.72,p < 0.001) when controlling for fixed effects for each wage and 4.8, 4.4, and 5.2 (Z = 2.77, p = 0.007; Z = 2.02,p = 0.048; Z = 2.30, p = 0.025) when focusing only on decisions after the second participation date.26Our conclusions are limited in one obvious way: the closest “later”we have by experimental design is 4

days later, so we cannot speak to potential discounting on 1- to 3-day delays. Kaur, Kremer, and Mullainathan(forthcoming), in fact, argue that the patterns of work ahead of deadlines suggest that people do differentiatebetween one-day and 3-day delays. If we understand correctly, this is inferred off an assumption that utility is

27

Figure 4: Histograms of participant-level differences between different types of decisions

Note : Right graph: Participant-level differences between decisions made about work in thefuture and decisions made about work in the present given different wages, a measure of presentbias. Left graph: Participant-level differences between work decisions in the future and predic-tions made about work in the future given different wages, a measure of sophistication aboutpresent bias. In each graph, there is a vertical line at one.

Assuming that participants are making straightforward predictions, the perception of

present bias is identified by the comparison of predictions with work decisions. Intuitively,

a completely sophisticated participant asked to predict immediate-work decisions in the future

will predict in line with her immediate-work preferences and a completely naive participant will

predict in line with her future-work preferences.

The right-hand graph of Figure 2 compares predictions and future work decisions for dif-

ference wages. It provides clear visual evidence for naivete: predictions about future work

are largely in line with future-work decisions. There is an average difference 0.7 (Z = 1.11,

p = 0.27) fewer tasks in predictions compared to future-work decisions.27 When comparing to

immediate-work decisions, predictions are 4.9 higher (Z = 3.48, p = 0.001) on average.28 At

the aggregate level, participants appear to have little sophistication about their own present

bias.

28

4.2 Present Bias and Perceptions of Present Bias: Individual

Figure 2 is based on aggregate data. To provide an assessment of decisions on an individual level,

Figure 4 presents a histogram of the measures discussed above within each individual. Fixed

effects for 10 wage bins are added due to the small number of observations for each individual.

The left-hand side presents the average difference between decisions about immediate work and

future work, a reduced-form measure of individual present bias. Following the results above,

the distribution is centered to the left of zero (suggesting a preference for less work in the

present), with 76% of individuals to the left of zero. The right-hand side presents the difference

between predictions and decisions about future work, a reduced-form measure of individual

sophistication. Following the results above, the distribution is centered near zero, with 53% of

individuals to the left of zero. Note that there is less variance in the individual differences in

the right-hand graph than in the left-hand graph (F (71, 71) = 11.77, p < 0.001). Individual

predictions about future work decisions are related to individual outcomes: the correlation

coeffi cient between the participants’distances in the left and right side of Figure 4 is 0.25,

which is statistically significant (Z = 2.09, p = 0.037).29

4.3 Prediction-as-Commitment

So far we have analyzed the data as if participants are not distorting their predictions as an

attempt to modify future incentives. This assumption would be valid insofar as participants

are fully naive about their present bias, or if they are (at least partially) sophisticated but

fail to think through the incentive effects of prediction-accuracy payments. As discussed in

Section 3, when this assumption is not satisfied, participants will predict 5 tasks above their

linear in weekly earnings.27This difference remains statistically insignificant regardless of controls, with participants choosing an average

of 0.2 (Z = 0.51, p = 0.61) more tasks for predictions when controlling for fixed effects for each wage and 0.2(Z = 0.20, p = 0.84) fewer when focusing only on decisions after the second participation date.28The difference that remains stable at 5.0 (Z = 3.27, p = 0.002) with wage fixed effects and 5.4 (Z = 4.78,

p < 0.001) focusing on later decisions.29The correlation rises slightly to 0.26 when restricting to those that predict fewer tasks in the future, although

this is no longer significant due to a smaller sample size (Z = 1.60, p = 0.110). The correlation rises 0.36 whenrestricting to those that choose fewer tasks in the present than in the future (Z = 2.65, p = 0.0079).

29

Figure 5: The variation of predictions given different bonus amounts

Note : Comparison between predictions made about work in the future and decisions madeabout work in the future. Predictions are shown when bonuses are relatively small or large. Forreadability, wages are grouped into 10 bins. Standard errors bars are clustered at the individuallevel.

current preferences for high bonus amounts and predict fewer tasks for lower bonus amounts.

We demonstrate that, for whatever reason, we do not find evidence for these behaviors in our

data.30

Figure 5 shows the average prediction given different wages under low and high bonus levels,

as well as future decisions about work, with medium bonuses omitted for visual ease.31 First,

there does not appear to be a connection between the bonus level and predictions at the

aggregate level, a conclusion is confirmed with a non-parametric analysis. Participants facing

low, medium, and high bonuses predicted an average of 0.1, 0.7, and 1.2 tasks fewer than future

work decisions. These differences are not statistically significant (Z = 0.11, p = 0.92; Z = 0.45,

30As planned, we explore changes in predictions given different bonus levels only at the aggregate level givena lack of power at the individual level: each participant faces 10 prediction sets and each set is associated withthe same bonus level.31The cutoffs were determined to attempt to equalize the number of observations in three bins of low, medium,

and high bonuses. Low and high bonuses lie between $0.25-$1.00 and $4.25-$8.25, respectively. The conclusionsare very robust to the number or borders of the bonus bins.

30

Figure 6: Comparison of decisions made before and after 10 mandatory tasks.

Note : For readability, wages are grouped into 10 bins. Standard errors bars are clustered atthe individual level.

p = 0.66; Z = 0.88, p = 0.38) from zero and not statistically different from each other (for high

and low bonuses, Z = .054, p = 0.59). Controlling for wage fixed effects and focusing on later

decisions, the effect of bonuses on predictions are non-monotonic and similarly not statistically

significant.32 Second, there is no evidence that participants choose anywhere near 5 tasks above

preferences for future work, regardless of the size of the bonus. Therefore, in aggregate, there

is little evidence that participants are using the prediction to manipulate the incentives of their

future selves.

31

4.4 Projection Bias

As discussed above, participants with projection bias should choose fewer total tasks after

having just completed more tasks. Figure 4.4 compares the average of task decisions for

different wages when made prior to completing the mandatory work to those made after

completion. While it does visually appear that participants generally choose less work after

completion of mandatory work, the difference is not dramatic. Participants reduce task deci-

sions by an average of 2.1 tasks after completing mandatory work, which is not statistically

significant (Z = 1.28, p = 0.20).33 The difference rises to 2.5 (Z = 1.55, p = 0.13) when

controlling for fixed effects for each wage and rises to a marginally statistically significant 3.3

(Z = 1.71, p = 0.09) when focusing only on decisions after the second participation date.

Our structural analysis below shows stronger and statistically significant effects of projection

bias. Much of the effect is due to our ability in the structural estimation to apply a Tobit-like

correction that accounts for the 40% of cases where in response to particular wages participants

chose 0 tasks or the maximum of 100 tasks. Using a Tobit to account for this censoring, the

statistics above rise to 3.8 (Z = 1.55, p = 0.12), 4.2 (Z = 1.78, p = 0.08) and 5.8 (Z = 1.94,

p = 0.052). Indeed, the effects of projection bias seem to show up clearly in the extreme choices:

18.6% of participants chose 0 tasks before the mandatory work, and 20.2% did after, whereas

24.0% chose 100 tasks before the mandatory work and 20.2% after.34 As throughout the paper,

the statistical significance reported for these 6 comparisons are from two-sided tests, which does

not take our ex ante, projection-bias-based directional prediction into account.

32The predictions for low, medium, and high bonuses are 0.6 higher (Z = 0.62, p = 0.54), 0.2 lower (Z = 0.19,p = 0.85), and 0.4 higher (Z = 0.32, p = 0.75) than future work decisions when controlling for fixed effects foreach wage are 0.8 higher (Z = 0.53, p = 0.60), 1.0 higher (Z = 0.51, p = 0.61), and 1.6 lower (Z = 1.00, p =0.32) when focusing only on decisions after the second participation date, with all pairs remaining statisticallyindistinguishable (for high and low bonuses: Z = 0.23, p = 0.82; Z = 1.00, p = 0.32).33Because projection bias applies in all three situations, we had no a priori reason to expect differences

across the situations, and did not plan to analyze them separately. Ex post we did, however, notice a strong(and perhaps surprising) differences: participants reduce present work by an average of 5.4 tasks (Z = 2.04,p = 0.045) after completing mandatory work, while reducing future work by an average of 1.8 tasks (Z = 0.88,p = 0.381) and predictions by 1.5 tasks (Z = 0.70, p = 0.463). (The statistics in parentheses are unadjusted forthe ex post nature of estimates.)34The differences would appear significant, with (Z = 2.05, p = 0.04) and (Z = 2.91, p < 0.01), but these

were not ex ante planned comparisons.

32

5 Structural Analysis

In this section, we estimate time-discounting, sophistication, cost, and projection-bias parame-

ters under our structural assumptions and identification strategy outlined in Section 3. The

qualitative conclusions of this section largely follow the conclusions of the non-parametric

analysis. We first estimate the parameters under the assumption of straightforward predic-

tions, which we relax with little effect on the estimates. As in the reduced-form section, all

referenced standard errors and standard error bars in graphs are clustered at the participant

level unless otherwise noted.

5.1 Present Bias and Perceptions of Present Bias: Aggregate

Table 1 estimates the main structural parameters through the maximization of the likelihood

in (11) for our primary sample of 72 participants. The first four columns present the estimation

results assuming that participants are making straightforward predictions. Column (1) presents

the estimation under the assumption of common parameters for each participant. Column (2)

adds participant fixed effects, effectively allowing the slope of the cost curve to vary arbitrarily

for each participant.35 Column (3) adds additional fixed effects for the date of decision, which

allows for the slope and curvature of the cost curve to change across time.36 Column (4) focuses

only on decisions made on or after the third date. We return shortly to column (5), which

includes the assumption that participants are manipulating predictions for incentive purposes,

briefly noting that it is largely similar to the other columns. When fixed effects are included

on a parameter, we report the average parameter across these fixed effects.

35Originally, we planned on using subject fixed effects on both the monetary slope ϕ and cost curvature γparameters. However, this specification does not converge when decision-date fixed effects are added (in thisestimation, there are 144 subject fixed effects and 14 date fixed effects). In Appendix Section A.8, we discuss theeffect of different combinations of date and subject fixed effects and show there is little impact on the results.36The fixed effects control for consistent changes in the cost curve as the date-of-decision changes, capturing

learning about the task over time. They do not control for consistent changes in the cost curve as the date-of-work in the decision changes. These changes could occur if, for example, all participants face a midterm on aspecific participation date, which would lead them to choose fewer tasks to be completed on that date regardlessof when the decision was made. In Appendix A.9, we account for these effects by adding work-date fixed effectsand find no change in our conclusions.

33

Table 1: Primary aggregate structural estimation

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.835 0.812 0.833 0.833 0.825(0.038) (0.042) (0.040) (0.041) (0.041)

Naive Pres. Bias βh 0.999 1.014 1.006 1.003 1.004(0.011) (0.011) (0.010) (0.009) (0.003)

Discount Factor δ 1.003 1.005 1.003 1.003 1.003(0.003) (0.002) (0.001) (0.002) (0.001)

Effort Cost γ 2.145 2.142 2.118 1.971 2.126(0.070) (0.084) (0.081) (0.075) (0.081)

Money Slope ϕ 724 710 687 367 720(252) (265) (244) (120) (258)

Proj Task Reduction α 7.304 5.257 5.269 4.066 5.207(2.597) (1.279) (1.290) (1.275) (1.269)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 8049 8049 8049 5539 8049Participants 72 72 72 64 72Log Likelihood -28412 -25079 -24838 -16522 -24837

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.93 p= 0.23 p= 0.58 p= 0.74 p= 0.11H0(α =0) p= 0.005 p<0.001 p<0.001 p= 0.001 p<0.001H0(δ =1) p= 0.37 p= 0.01 p= 0.06 p= 0.08 p= 0.07

Note: Our main aggregate structural estimations for our primary sample of 72 participants.Columns (1),(2),(3),(4) assume straightforward predictions. Column (1) presents the base-line estimation. Column (2) adds fixed effects for participants applied to the monetaryslope parameter. Column (3) adds fixed effects for decision dates applied to the effort costand monetary slope parameters. Column (4) matches column (3) but focuses on participa-tion dates three and later. Column (5) matches column (3) but assumes that participantsuse predictions-as-commitments. When fixed effects are added, the parameter presented isthe average of the fixed effects. In all specifications, standard errors are clustered at theparticipant level.

34

The aggregate estimate of the present-bias parameter β ranges from 0.812 to 0.835. In

each case, the null hypothesis of no present bias (β = 1) is firmly rejected. Estimates of the

perceived present-bias parameter βh range from 0.999 to 1.014. In each case, the null hypothesis

of no perceived present bias (βh = 1) cannot be rejected. Estimates of the standard daily time

discounting parameter estimates δ range from 1.003 to 1.005. The null hypothesis of no standard

discounting (β = 1) is only rejected in specification (2) under classic rejection criteria, although

the test statistic is borderline significant in all but column (1). A parameter δ greater than one

suggests that people prefer to complete less work as the temporal distance to work increases.

One explanation for this finding is that participants do not want to commit to more work farther

in the future because there is greater uncertainty about other obligations on these dates.

In all specifications, the aggregate effort-cost parameter estimates hovers near two, suggest-

ing near quadratic costs. Quadratic costs imply that the marginal cost of completing a task

rise linearly with the number of tasks completed. The monetary slope parameter is around 700

in the specifications, which allows costs to be converged into dollar amounts. For example,

in the first specification– where cost curves are assumed to be stable over time– the marginal

costs of the 25th, 50th, 75th and 100th future-work task are $0.055, $0.122, $0.194, and $0.270,

respectively. Although not shown in the table, the fixed effects specification in Column (3)

produces estimates of the cost curve for each date. For example, the marginal costs of the

50th tasks for the seven dates are estimated at $0.110, $0.110, $0.116, $0.123, $0.126, $0.129,

and $0.129, respectively. Although task time-to-completion drops over time, this finding sug-

gests that participants learn as the experiment progresses that the task causes slightly higher

disutility. Reassuringly, controlling for this learning into account does not noticeably change

the estimates of β, βh, δ, and α, implying that it is not spuriously driving our results. In

Appendix A.1, we further show that the main parameter estimates are stable over time, as well

as discussing the cost curve changes in more detail.

Following the discussion of the appropriateness of the quasi-hyperbolic discounting model

in the reduced-form analysis, we separately estimate the relative weight placed on the disutility

35

from tasks that must be completed on future dates in comparison to tasks that must be com-

pletely immediately. We find that the weights for tasks that must be completed one, two, and

three dates away are 17%, 20%, and 17% higher than the weight placed on immediate tasks.

All of these estimates are significantly different from 0 (χ2(1)=13.66, p<0.001; χ2(1)=13.69,

p<0.001; χ2(1)=9.85, p = 0.002).37

5.2 Present Bias and Perceptions of Present Bias: Individual

To analyze individual heterogeneity, we estimate participant-specific parameters using a variety

of specifications. We initially assuming that participants make straightforward predictions and

have no projection bias. The mean, median, and standard deviation of the main individual

parameters for all decisions, early decisions (on or before the third date), and late decisions

(on or after the fourth date) are shown in Columns (1)-(3) in Table 2. Note that, as we did

to create our primary sample of 72 participants, we remove participants when the maximum-

likelihood routine does not converge or produces estimates that are transparent outliers for each

specification.38 The results largely mirror the aggregate results, with the average estimate of

β ranging from 0.794-0.874, the average estimate of βh ranging from 0.978-0.988, the average

estimate of δ ranging from 1.006-1.016, and the average estimate of γ ranging from 2.044-2.160.

Figure 7 contains histograms of the individual estimates of β (left panel) and βh (right

panel) from the main specification in Column (1). Note that the histograms largely match the

corresponding histograms of reduced-form measures of present bias and sophistication calcu-

lated in Section 4.2 and shown in Figure 4. The correlation between the individual estimates of

37The weights remain similar when adding participant fixed effects at 17%, 20%, 23% (χ2(1)=10.41, p=0.001;χ2(1)=11.81, p<0.001; χ2(1)=11.95, p<0.001) and both participant and decision-date fixed effects at 17%, 17%,14% (χ2(1)=10.61, p=0.001; χ2(1)=9.74, p=0.002; χ2(1)=6.56, p=0.01). In all of these specifications, none ofthe weights on future participation dates are pairwise statistically significantly different from each other (thehighest statistic is χ2(1)=2.38, p=0.12 comparing one and three dates away in the second specification).38We remove outliers whose estimates are rejected by a Grubb’s outlier test with 99.99% confidence. Specifi-

cally, 4,2,7, and 4 outliers are removed from the "Early Decisions", "Later Decisions", "Proj. Bias", and "Pred.Soph." specifications, respectively. The largest source of outliers are very large βh parameters (βh ∈ [2, 33]) .When these outliers are included, the means of βh in Table 2 change to 1.07, 1.60, 0.97, 1.11, and 1.13, respec-tively, although the medians remain largely unchanged. Removing more outliers (by changing the confidencelevel to 99% or 95%) does not meaningfully change the means, except in the case of the estimates of βh in theestimation with sophistication, which swings between 0.90 and 1.02 depending on the cutoff.

36

Table 2: Summary statistics for individual structural estimates

(1) (2) (3) (4) (5)PrimaryEstimation

EarlyDecisions

LaterDecisions

Proj.Bias

Pred.Soph.

mean(βi) 0.794 0.853 0.874 0.772 0.773median(βi) 0.824 0.877 0.901 0.807 0.807sd(βi) (0.286) (0.340) (0.244) (0.280) (0.297)

mean( ˆβh,i) 0.984 0.988 0.978 0.985 0.943median( ˆβh,i) 0.988 0.988 0.984 0.997 1.003sd( ˆβh,i) (0.120) (0.154) (0.101) (0.118) (0.396)

mean(δi) 1.016 1.010 1.006 1.016 1.012median(δi) 1.008 1.005 1.004 1.008 1.008sd(δi) (0.035) (0.024) (0.024) (0.035) (0.026)

mean(γi) 2.138 2.160 2.044 2.245 2.134median(γi) 1.930 1.963 1.905 2.050 1.978sd(γi) (0.692) (0.756) (0.636) (0.727) (0.562)

mean(αi) 6.413median(αi) 3.238sd(αi) (11.288)

P[βi]<1 0.78 0.76 0.69 0.79 0.81P[ ˆβh,i]<1 0.54 0.56 0.60 0.51 0.46r(βi, ˆβh,i) 0.284 0.245 0.273 0.237 0.187p-value r(βi, ˆβh,i) 0.016 0.040 0.044 0.052 0.183

Observations 72 71 55 68 52

Note: Summary statistics of the individual parameter estimates. Participants for whomthe estimation does not converge or creates strongly-outling estimates are removed. sd(αi)is the standard deviation of the distribution of individual estimates (not the average stan-dard error). P[xi]<1 is the proportion of estimates below 1. r(βi, ˆβh,i) is the correlationcoeffi cient between βi and ˆβh,i. the p-value associated with the test this coeffi cient equals0 is also shown.

37

Figure 7: Histogram of individual estimates βi and ˆβh,i

Note : Right graph: distribution of individual estimates βi. Left graph: distribution of indi-vidual estimates ˆβh,i. These can be compared to the histograms in Figure 4. In each graph,there is a vertical line at one.

β and the measure of present bias is 0.6785 (p<.001). The correlation between the individual

estimates of βh and the measure of sophistication is 0.5935 (p<.001). This provides in-sample

validation of the maximum-likelihood parameter estimates.

The correlation between the estimates of β and the estimates of βh across participants ranges

from 0.245-0.284, which is always significant (p ≤ 0.05). Focusing only on the participants with

estimates of βh < 1, the correlation rises to 0.280-0.512, which is strongly statistically significant

(p<0.001). However, while the correlation suggests that participants are (on average) at least

partially aware of their own present bias, it does not quantify the level of awareness. To measure

the average level of sophistication, we regress the individual estimated perceived levels of present

bias (1 − βhi) on the individual estimated levels of present bias (1 − β) given the estimation

equation

(1− βi) = λ · (1− βhi) + εi. (13)

The parameter λ1 captures the participants’percentage of awareness about her present bias.

A person with β = .8 and βh = .9 would have λ = .5, as would a person with β = .9 and

βh = .95. The estimates for each specifications in Table 2 are shown in Table 3. The top two rows

use include participants from Table 2. Row 1 reports the results from estimating Equation (13)

using ordinary least squares (OLS) with robust standard errors. Because βhi is an estimated

38

Table 3: Relationship between individual estimates βi and ˆβh,i

(1) (2) (3) (4) (5)PrimaryEstimation

EarlyDecisions

LaterDecisions

ProjectionBias

WithSophistication

Primary SampleOLS : (1-β) 0.104* 0.106* 0.125** 0.085 0.251*

(0.061) (0.062) (0.054) (0.062) (0.129)GLS : (1-β) 0.133*** 0.176*** 0.142*** 0.106** 0.144

(0.043) (0.053) (0.050) (0.046) (0.129)

Observations 72 71 55 68 52

Primary Sample: ( ˆβh,i<1)OLS : (1-β) 0.278*** 0.197*** 0.185*** 0.274*** 0.081

(0.042) (0.073) (0.067) (0.045) (0.214)GLS : (1-β) 0.233*** 0.224*** 0.187*** 0.235*** 0.241

(0.040) (0.062) (0.071) (0.036) (0.227)

Observations 39 40 33 35 24

Note: These are the coeffi cients of the regression of (1- ˆβh,i) on (1-βi). The "GLS" uses in theinverse of the variance estimates for ˆβh,i provided by the individual estimation as weights.All specifications use robust standard errors. * p < 0.10, ** p < 0.05, *** p < 0.01.

parameter with estimated standard errors, Row 2 reports estimates using generalized least

squares (GLS) with weights equal to the inverse of the square of the estimated standard error.

Rows 3 and 4 report the results of OLS and GLS when the sample is restricted to participants

with estimates of βh < 1.

The estimated coeffi cient λ is statistically significant in all specification and highly significant

in the specifications in columns (1)-(3), confirming the conclusion that there is a relationship

between perceptions of present bias and observed present bias. In these columns, the OLS

coeffi cients range from 0.104-0.125, while the GLS coeffi cients range from 0.133-0.176. When

focusing only on participants that perceive that they are present biased (βh < 1), the OLS

coeffi cients range from 0.185-0.278, while the GLS coeffi cients range from 0.187-0.233.

39

5.3 Prediction-as-Commitment

The parametric estimates above are calculated under the assumption that participants make

straightforward predictions. Column (5) in Tables 1, 2 and 3 mirror the main estimations under

the assumption that participants optimally use predictions as soft commitment devices. There

is very little effect of this change, which is not surprising given that βh ≈ 1 in the estimates

with straightforward predictions.39

5.4 Projection Bias

Section 4.4 provided (borderline statistically significant) evidence for projection bias, noting

that participants reduce task decisions by an average of 2.1 - 3.3 tasks after completing the

mandatory work. When the censored nature of the data is taken into account, the figures rise

to between 3.8 and 5.8. We estimate this statistic, which we label α, in both the aggregate

and individual structural estimations. While this is not a structural estimate of the projection

bias parameter α along the lines we attempt in Appendix A.4, it includes all of the structural

assumptions about the shape of the cost curve, other parameters, and error term. In the

aggregate estimations (Table 1), α ranges from 4.1 to 7.3 and is always statistically significant

(p < 0.005), while the average individual estimate is 6.4.

6 Discussion and Conclusion

6.1 Related Literature on Present Bias and Projection Bias

Following millennia of folk wisdom and gradual incorporation of the idea, an explosion of

recent theoretical and empirical research (now too expansive to list fully) has incorporated

the idea that people have a taste for immediate gratification. Formal theory and economic

39Unlike in the other specifications, the means of the individual estimates in the sophistication specificationare particularly dependant on the rule to remove outliers. Under a slightly different rule, mean(βh,i) = 1.1 due

to inclusion of 3 estimates with βh,i > 3.

40

applications, such as Strotz (1956), Laibson (1997), O’Donoghue and Rabin (1999, 2001), has

directly considered the relevant components of present bias to be the flow of utility over time

rather than the timing of receiving money. Yet a long tradition of experimental research had

primarily examined preferred timing of money. Our design follows such papers as Read and

van Leeuwen (1998), Badger et al (2007), McClure et al (2007), Brown et al (2009), and

Augenblick, Niederle, and Sprenger (forthcoming) in moving away from this money-immediacy

paradigm to an approach that more directly tests present bias as employed in economic theory

and applications.40

There are a range of studies measuring β in both ecological and experimental data using

consumption choices. The closest to our experiment is Augenblick, Niederle, and Sprenger

(forthcoming), using a very similar task and with participants drawn from the same pool.41 ,42 ,43

Using our different elicitation structure– whereby participants always trade offmoney vs. work,

40For discussions of the problems and confusions associated with using monetary experiments to investigatethe theory of present bias, see Chabris, Laibson and Schuldt (2008), Cubitt and Read (2007), Augenblick,Niederle, and Sprenger (2013), and O’Donoghue and Rabin (2015). O’Donoghue and Rabin (1999b) illustratesthe difference in stark form: thet invoke present bias to explain delays in wealth accumulation: because theeffort associated with switching money (or traveling on a tight schedule to pick up and then cash experimen-tal earnings) generates immediate disutility, whereas the increase in wealth is a delayed benefit of increasedfuture consumption, present-bias theory predicts delayed wealth accumulation. Although many researchers(including O’Donoghue and Rabin (1999b), citing evidence in contradiction to their own approach) invokedmoney-immediacy evidence in support of the theory of present bias, the theory itself does not predict peoplewant money sooner in general. In particular (and important) circumstances, the timing of money receipt cancoincide with the timing of utility. This is the case, for instance, when there are plausible liquidity constraints.41The tasks were identical, except that– by requiring participants to concurrently identify a random noise

through headphones– we feel (we are proud to say) we made ours more irritating . While participants weredrawn from the same pool (Berkeley’s xlab), we asked the recruitment organizers not to permit the samespecific students to sign up. Much of the preliminary analysis in ANS was completed before all the details ofour experiment were finalized and the experiment was implemented. We do not believe (based on memory,records, and the nature of the design and adjustment issues) that results from ANS influenced any of the maincomponents of our design.42ANS is primarily concerned with comparing “present bias”in monetary payments– as traditionally studied

in experiments– to present bias in real effort– which is meant to capture discounting over utility as the theoryis developed for and as most applications assume. To this end, they use Andreoni and Sprenger’s (2012) convex-budget-set design, who show no taste for immediate money delivery when asked to trade off money at one timeversus another under different exchange rates. They replicate Andreoni and Sprenger’s (2012) finding of no tastefor the immediate delivery of money, but find present bias using the identical procedures where participantstrade off effort at different times.43Besides the papers discussed in the text, the only other paper we are familiar with that attempts to

experimentally measure present bias in the context of unpleasant effort is Bisin and Hyndman (2014). Theyrequire students to complete either one or three word-sorting tasks over time, allowing some of the studentsto create self-imposed deadlines. By assuming full sophistication and using a structural model of optimalstopping-time choice, the authors estimate β = .44 in one treatment and β = 1 in another.

41

without ever making any now vs. later choices within the work domain– we obtain a very similar

range of estimates for β. By asking participants to make a large number of work choices and

specific predictions over many weeks, we are better equipped estimate each parameter for all

individuals, analyze learning over time, and identify if preferences across different future work

dates are consistent with the quasi-hyperbolic discounting model.

Conversely, there exist few studies measuring βh from ecological data, and we know of

no previous studies attempting to use an experimental manipulation to directly estimate βh

from a tightly measured utility function.44 Much of the research on sophistication explores the

binary choice of whether or not to self-commit– where self-commitment suggests at least partial

awareness of present bias. To take just some of the examples, Ariely and Wertenbroch (2002)

document significant student demand for deadlines to complete classroom assignments– and

find that these deadlines improve performance. Ashraf, Karlan, and Yin (2006) show that in

the Philippines, where credit constraints create a tighter link between money and immediate

consumption, 30% of bank clients demand a savings commitment product.45 Kaur, Kremer, and

Mullainathan (forthcoming) find that Indian data-entry workers were willing to set positive–

although relatively small– work targets 36% of the time, even though missing the target was

penalized. Augenblick, Niederle, and Sprenger (forthcoming) find little willingness to pay for

commitment. They do, however, find that around half of subjects choose to commit when they

don’t have to pay, and that such commitment is correlated with individual structural estimates

of present-bias. Perhaps the most dramatic finding of a taste for commitment is Schilbach

(2015), who studies rickshaw drivers in India with drinking problems and finds that one-third

of the drivers were willing to sacrifice money to receive incentives to be sober. Acland and

Levy (2015), who follow Charness and Gneezy (2009) in paying students to attend the gym

and examining the development of habits, is the closest antecedent to a structural estimate of

44As an example of one of the few ecological estimates of βh, Skiba and Tobacman (2008) use initial borrowingand default timing from a large sample of payday loan borrowers to structurally estimate parameters of β ofaround .5 and βh of between .9 and 1. Although their data involved people chosing the timing of receivingmoney, the context was specifically for individuals who were presumed to highly credit-constrained individuals.45They also show that this demand is predicted (at the 10% level) by time-inconsistent behavior in hypothetical

monetary choices, although not with hypothetical decisions about rice or ice cream.

42

βh using experimental data. While they cannot separately identify β and βh, an earlier version

of the paper (Acland and Levy (2013)) structurally estimates (1 − βh) = 0.33 · (1 − β) using

the demand for commitment implied by valuations of future-behavior-contingent contracts.

We differ from these studies by attempting to identify sophistication from exploring how

closely predictions on future behavior align with the behavior exhibited for immediate choice.

In addition to helping more finely identify the level of sophistication, focusing on predictions

rather than demand for commitment devices can potentially separate sophistication from the

taste for commitment. One way to frame this separation is in the language of O’Donoghue

and Rabin (1999a), who characterize sophistication as influencing behavior in two ways: a

“pessimism effect”, whereby a person predicts her own future misbehavior and takes actions

now in light of that misbehavior, and an “incentive effect”, whereby she tries to manipulate

circumstances to minimize that misbehavior. Although the present-bias model predicts both

effects inseparably, our speculation was that the pessimism effect might be operative without

the incentive effect in the case of incentivized predictions, when the incentive effects might

be opaque to the participants. If our finding of little sophisticated pessimism replicates, and

studies such as Schilbach (2015) continue to find an apparent strong taste for self-commitment,

it might suggest the confusing result that people demand commitment without necessarily being

pessimistic about future behavior. That said, these differences might be due to sophistication

differing in different situations, particularly given that previous work in our environment–

Augenblick, Niederle, and Sprenger (forthcoming)– find little demand for commitment.

Finally, we know of relatively few papers with experimental or ecological estimates of the

degree of projection bias. Two exceptions from ecological data are Conlin, O’Donoghue, and

Vogelsang (2007), who estimate α ≈ .5 from consumers who mis-order weather-related clothing

based on the idiosyncratic weather conditions at the time they order, and Levy (2010), who

estimates α ∈ [.4, .5] from the failure of cigarette smokers to predict how habit forming smoking

will be. Some of the original (and best) evidence of projection bias comes from experiments–

Read and van Leeuwen (1998) find people order future food by current hunger state, and Badger

43

et al (2007) find addicts pay considerably more for future delivery of a heroin substitute when

they are current craving state is unusually high.46 But the only experimental estimate of α

we are familiar with is Acland and Levy (2013), who estimate α ≈ .9 based on participants’

underappreciation of how habit forming their exercise routines would be.

6.2 Limits to the Analysis

The analysis we present in the paper glosses over some potentially worrisome aspects of our

identification strategy and results. First, our results could be biased in the presence of uncer-

tainty. In Appendix A.2, we model a participant who faces random shocks to the convexity

of her cost curve, showing that foreseeable uncertainty would tend to make participants more

cautious about committing in the future, leading us to underestimate the severity of present

bias.47 Given our experimental design, the large number of participant choices allows us to both

estimate the level of this uncertainty (essentially comparing the variation in future decisions

with the variation in present decisions) and control for it, leading to an estimate of β of 0.77.

Second, as participants make multiple decision sets each day, it is possible that the answers on

earlier sets influence answers on later sets. Furthermore, participants making immediate-work

decisions for a given wage might be effected when reminded of past predictions about decisions

for a different wage. In Appendix A.6, we show that the results are robust to eliminating

later decision sets or decision sets with any prediction reminder. Third, as noted above, the

main analysis focuses on only 72 of the 100 participants whose decisions allow estimation of

individual parameters. While we have relatively little to say about the individual estimates of

the dropped participants (they were removed due to a lack of individual estimates), we show

that their average reduced-form statistics are very similar to our primary sample in Appendix

A.5 and demonstrate in Appendix A.6 that our aggregate results are consistent when including

46Both studies were also cited above for being seminal in identifiying present bias; each demonstrated bothprojection bias and present bias in a way that separately identified the two. Neither study measured the scalesof the biases, nor studied naivete about present bias.47Due to the more complicated relationship between the bet-induced incentives and the wage incentives, the

effect of uncertainty on the estimate of βh is both more complex and more ambiguous.

44

the data from all participants. Fourth, our results may be biased if participants learn about the

unpleasantness of the task or become more proficient at the task over time. While we observe

evidence of both of these effects– the immediate work choices and task completion time both

drop significantly in the first few dates– there is little change from the third decision date on-

ward. Our conclusions remain unchanged when focusing only on these later dates or allowing

the cost function to vary over decision dates. Furthermore, in Appendix A.1, we allow the

parameters β, βh, and α to vary on each decision date, and find that they remain stable over

time.48

Another possible worry concerns the timing of utility, which is diffi cult to control for in our

design. In our analysis and estimation, we assume that all costs associated with completing

tasks– captured in the function C(e)– correspond to immediate disutility. Insofar as some of

the cost function is something not associated with disutility– such as, say, foregone earnings

or other future benefits from an activity displaced by the task– then present bias will not lead

to differential treatment of immediate work in comparison to future work. To the degree such

factors contributed to the cost function, our estimates of β would be biased upwards, leading us

to underestimate the bias. Our measures of projection bias are likewise affected: if the source

of the convexity of the cost function is in part due to displacement of some alternative activity

with concave benefits that are not subject to taste misprediction– such as forms of cleaning

that have diminishing returns – then projection bias will not lead to the distortions, again

leading us to underestimating the bias.

The final (and perhaps most worrisome) issue arises as a result of an unanticipated empiri-

cal observation about participant decisions given past predictions. To understand the concern,

consider a participant who– following our estimates of βh ≈ 1 and β ≈ .83– is largely naive

about her moderate present bias. As we observe in the data, this participant would make

predictions that are an average of 5 tasks above her immediate-work preferences, with the de-

viation rising in wages. When the work date arrives, our model makes some basic predictions

48The one exception is hard to interpret: significant movement in the estimate of the parameter α during thelast two participation dates, dropping from 7.5 to 0.3, but then rising back to 11.5.

45

about the participant’s behavior when facing the previous prediction and the associated ac-

curacy payment. Three of the predictions are satisfied in the data: the participants are most

likely to choose at the bottom end of the prediction interval given an “internal prediction”–

predictions strictly between 0 and 100 tasks; the average work choice is significantly lower than

the associated prediction; and the average difference between choice and prediction rises with

wages. Two observations, however, are importantly inconsistent with our a priori model, in

which participants simply trade off disutility from effort and utility from money coming from

either wages and bonuses. First, the percentage of participants choosing to match their exact

prediction is nearly 30% for internal predictions, a behavior the model predicts is rare. Second,

participants choose outside the prediction interval less than 1% of the time, although rough

simulations given the model suggest that this should occur nearly 20% of the time, with the

large majority (80%) of these below the interval. Therefore, it appears that many participants

have an unmodeled preference to choose within the prediction interval (which avoids losing

the accuracy payment) and some have a desire to match previous predictions exactly. Perhaps

oddly, the consistency preference takes a very local form: participants’work decisions are not

effected by reminders of previous predictions for other similar wages. Consistency preferences

are potentially problematic for our conclusions about βh: sophisticated participants could use

their empirically-unobserved internal consistency rewards as a commitment device, which would

contaminate our estimate. However, this alternative cannot explain the three above observa-

tions, which are compatible with naivete. Furthermore, we suspect the fine-tuned sophistication

required to recognize and use these very particular consistency rewards as commitment devices

is unlikely. We discuss the reaction to bonuses further in Appendix A.3, and supply some addi-

tional data. All said, however, this unexpected and hard-to-interpret finding might reasonably

temper confidence in our conclusions about sophistication.

46

6.3 Final Thoughts on Implications and Future Directions

We conclude with three thoughts on directions of research in this area that are provoked by this

experiment. The first is clearest: to better understand the psychology of prediction and the

nature of commitments, we think further research elaborating how previous predictions affect

behavior, and the degree to which these effects are anticipated by participants, is important.

The second, based on the verification of our hypothesis that recent work effort affects future-

oriented choice, is that misprediction of future tastes may indeed be important in (the very

classical) domain where people face convex effort costs. We found non-trivial effects comparing

before and after an initial work load, and wonder if the how the effects would be changed if the

workload was much greater, the decisions took place over longer horizons, or the type of work

was more naturalistic. Finally, the experiment points to potential situations in which present

bias and projection bias are confounded. For example, in our experiment, if we had elicited

immediate-work preferences by having people complete tasks for a given wage and freely choose

when to stop working, both projection bias and present bias would lead fewer immediate task

completions. While most studies that we are familiar with do not face this confound, there

is a potential for researchers focused on discounting to misinterpret degrees of present bias by

ignoring projection bias.

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49

A Appendix

We now report a variety of robustness checks on specification choices, participant sample, and

data sample. Many of these robustness checks were designed ex-post, in response to suggestions

and our own realizations of problems. We do not report all specifications and robustness checks

due to space constraints, but have not omitted any analyses because they yielded “unfavorable”

conclusions.

A.1 Stability of parameters across the experiment

In our simple model, we assume that a participant’s parameters are stable across time, such

that participants make consistent decisions across time. However, in the main text, we note

that participants’cost of completing tasks appears to be increasing over the course of the exper-

iment, despite lowering task-completion times. In the left panel of Figure A.1, we confirm this

conclusion in the raw data by showing a downward trend in average wage-adjusted immediate-

work, future-work and prediction decisions as the date of the decision increases, particularly

in the first few dates. Recall that we control for this learning issue in the main analysis by

including participation-date fixed effects on both the monetary slope and cost curve parameters

in Columns (3)-(5).49 In the right panel, we display the estimated total-cost curves from the

specification in Column (3)– with darker colored lines representing later dates– affi rming that

we are capturing and controlling for these increasing costs.

While we allow the cost curve to vary in the main analysis, we do not let the main parameters

of interest– β, βh, and α– to vary over time. Yet as a robustness check, we ran specifications

in which these parameters too are allowed to vary across dates. We visually present the results

in Figure A.2. Our main parameter estimates remain largely stable, with one exception: The

value of α, which is relatively stable over several weeks, dips near zero for date 6 and rises to

over 10 for date 7—a result for which we have no explanation or interpretation.

49Changes in γ and in ϕ can be interpreted as learning about the curvature and the slope of the effort cost,respectively—not necessarily learning about the monetary slope.

50

Figure A.1: Choice data and estimated aggregate cost curves across participation dates

Note : Left panel: Average present-work, future-work, and prediction choices across partic-ipation dates, controlling for wages. There is a downward trend, particularly in the earlyparticipation dates, suggesting that participants’relative costs are increasing. Right panel: Incolumn (3) of Table (1), we use participation date fixed effects to allow the aggregate cost curveto vary over time. This graph shows the estimated cost curves for each participation date, withlater dates in darker colors.

Figure A.2: Aggregate parameter estimates across participation datesNote : In the main analysis, we assume that our main parameters (beta, beta-hat, and alpha)are constant across participation dates. This figure plots the parameter estimates across datesfrom another specification.

51

A.2 Robustness: Estimating the effect of uncertainty

The formal model that we estimate in the paper assumes no “structural”uncertainty, allowing

only for error terms as a reduced-form way to rationalize the mismatch between the best-fit

model predictions and observed noise. This error could correspond to measurement errors,

random errors, model uncertainty, or as a heuristic way to allow for unmodeled preference

heterogeneity. We implicitly assume that participants do not adjust their decisions to account

for future uncertainty, a potentially unrealistic assumption. For example, a participant might

be aware that she will sometimes feel unpredictably tired, while on other days, she will feel

unpredictably refreshed. Knowing this, she will choose future-work and prediction decisions to

maximize her expected utility given these shocks, leading to different decisions than suggested

by our model.

To study the effect of anticipated preference shocks on participants’decisions, we modify

our model such a participant faces zero-mean normally-distributed preference shocks ηγ with

standard deviation σγ(ηγ) to her cost-curve parameter γ. We focus on the effects of this change

on future-work decisions and the estimate of β; the effect on βh is ambiguous and depends

heavily on the precise form of the error term.50 The agent’s future-work decision at time t < k

given the anticipated preference shock maximizes expected utility is then

maxe

E[ ϕ · δ(T−k) · e · w − 1

γ + ηγ(e+ 10)γ+ηγ ], (14)

with γ representing the mean of the realized parameter γ. Simplifying and solving for the

first-order condition yields an implicit solution for observed effort

ϕ · δ(T−k) · w = E[(e+ 10)γ−1+ηγ ]. (15)

50We conjecture, but have not proven, that with convex costs adding uncertainty leads to lower predictions.Intuitively, positive shocks lead to smaller drops in chosen effort than the corresponding rises in chosen effortfrom equilivent negative shocks. Therefore, lower predictions lead to a higher probability of drawing a parameterthat leads to effort chosen within five tasks of the prediction. However, the bias on the estimate of βh fromnot accounting for this uncertainty is unclear: βh is identified in the comparison of predictions and future-workdecisions, and– as we show shortly– these decisions are also lower due to uncertainty.

52

Given convex costs and this symmetric error, anticipated preference shocks will lead to

a lower future-work decisions than in our baseline model, because the agent desires to insure

herself against positive shocks in effort costs. Not taking this effect into account biases our main

estimates of β upward, as β increases with the difference between future-work and immediate-

work decisions.

To demonstrate this effect empirically, we estimate our model taking this anticipated un-

certainty into account. Note that, as this anticipated error will not lead to any variation in

future-work decisions for a given wage, we still require a reduced-form way to account for the

mismatch between decisions and model predictions. We therefore include the reduced-form

error term εγ with standard deviation σγ(εγ) to both present and future decisions. Given this,

the likelihood of observing immediate-work decision i becomes:

L(ei|ϕ, β, γ, δ) =γpresent − γ

σγ(εγ) + σγ(ηγ)(16)

where γpresent =ln(ϕ·β1(t=k)·β1(p=1)h ·δ(T−k)·w)+ln(ei+10)

ln(ei+10). For reference, γpresent is derived in Equation

20 of Appendix Subsection A.10. The likelihood of observing future work decision i becomes:

L(ei|ϕ, β, γ, δ) = φ(γfuture(ηγ)− γ

σγ(εγ)) (17)

where: γfuture(ηγ) maximizes 14 given ηγ ∼ N(0, σ(ηγ)).

Column (1) of Table A.1 first presents the results of estimated this model with both antici-

pated and reduced-form error, but assuming that participants do not change their future work

decisions to take this error into account. The estimates σ(εγ) and σ(ηγ) are presented, showing

that there is additional dispersion in present effort decisions– captured in σ(ηγ)– compared to

future-effort decisions. Column (2) presents the same results under the assumption that par-

ticipants take this uncertainty into account when making future work decisions. As expected,

the estimate of β is lower when taking uncertainty into account.

53

Table A.1: Estimation given preference shock to parameter gamma with participants takingthis uncertainty into account in decisions

(1) (2)Error OnParameter γ

Preference ShockOn Parameter γ

Present Bias β 0.817 0.766(0.029) (0.036)

Effort Cost γ 2.420 2.330(0.054) (0.023)

Decision Error σ(εγ) 0.212 0.217(0.011) (0.013)

Preference Shock σ(ηγ) 0.131 0.123(0.016) (0.014)

Observations 8049 8049Participants 72 72Log Likelihood -641 -699

H0(β =1) p<0.001 p<0.001H0(δ =1) p= 0.09 p= 0.00

Note: These specifications assume that participants face preference shocks to the parametergamma on the day of work, in addition to a standard reduced-form error term to capture de-viations from model predictions and observed choices on all decisions. Column (1) assumesthat participants do not take preference shocks into account when making future-work de-cisions. Column (2) assumes that participants do optimally take these shocks into account.

54

A.3 Internal-Consistency Rewards

As we discuss in the paper, when making immediate-work decisions for which they previously

stated a prediction, participants act somewhat inconsistently with our simple model of mon-

etary payment utility and disutility from work. To understand the deviation, consider the

potential outcomes of a participant’s immediate-work decision given a previous prediction. If

her immediate work preference lies within the prediction interval, she will choose that level and

receive the bonus. The situation is more complicated when her work preference is outside the

interval. If the bonus is high enough, the participant will be choose the closest work level in the

interval (on one of the bounds) to receive the bonus. If the bonus is too low, however, she will

choose her preferred level and forgo the bonus. Therefore, we expect some portion of decisions

continuously spread across the decision interval, a large chunk of decisions at the lower bound,

and some decisions far outside the interval. Because β < 1, we expect current preferences

to fall below the prediction on average, leading the average immediate-work decision to be

lower than the associated prediction. Furthermore, the model predicts that the difference will

rises in wages. In the likely case that participants receive preference shocks to immediate-work

preferences, these general predictions continue to hold.

Before turning to the data, we note that this analysis is made more complicated by the

fact that we observe censored work decisions (between 0 and 100), which leads to censored

predictions. For example, if the participant predicts that she would choose 150 tasks without

constraints, she predicts that she will choose 100 tasks given the constraints. Then, if the

day of work arrives and the participant’s immediate-work preference is to complete 130 tasks,

she is forced to choose 100 tasks. In this case, even though her immediate-work preferences

differ from her unconstrained prediction, there is no observed difference due to censoring. This

problem is clear in the data: for predictions of either 0 or 100, nearly 95% of the resultant

work decisions perfectly match the prediction. As this effect is presumably due to censoring,

we focus on predictions strictly between 0 and 100, where this confound does not exist.

With these corner predictions removed, the histogram plotting the difference between the

55

Figure A.3: Analysis of immediate-work decisions given previous predictions

Note: This figure shows a histogram of the difference between immediate-work decisionsfollowing a previous prediction and the associated prediction. The prediction interval (+/-5 tasks) is shown in dotted lines. Observations above and below the prediction interval arecombined in the ">5" and "<-5" bins. The average of the data is shown in the verticalsolid line.

immediate-work decision and the associated prediction are shown in Figure A.3, with the pre-

diction interval represented by dotted lines and observations outside the interval combined to

the bins on the edges. As predicted, a significant chunk of the immediate-work decisions (35%)

lie on the lower bound of the prediction interval. Furthermore, the average difference between

immediate-work decisions– denoted on the histogram with a straight line– is negative (-1.68)

and significantly lower than zero (Z = 2.72, p < 0.001), clustering standard errors at the

participant-level. Finally, although not shown in the graph, this difference is significantly rising

in the wage level.

However, there are important deviations from the predictions of the model. First, for 28% of

the data, the immediate-work decisions perfectly matches the associated prediction. Based on

our model, this should be a rare event. Particularly, given the likelihood of shocks to immediate-

work preferences, as it is unlikely that a participant would end up preferring the exact work

56

level in the prediction. Second, there are virtually no cases in which participants choose outside

the prediction interval. Given our estimated parameters, the size of estimated immediate-work

preference shocks, the size of the bonuses, and an assumption that participants value the

monetary bonuses the same as monetary wages, rough simulations suggest that participants

should forego the bonus rather than work within five of their prediction 20% of time, leading to

15% of the prediction-effected immediate-work decisions lying below the prediction interval and

5% lying above. It appears that, instead, participants have (1) strong unmodeled preference to

choose within the prediction interval and receive the monetary bonus and (2) a weaker desire

to match previous predictions exactly.

Interestingly, these consistency preferences are surprisingly “local.”To understand this find-

ing, suppose that a participant previously made a prediction of 60 tasks given a wage $.20, but

only desires to do 40 tasks for this wage when she arrives on the work day. Suppose that this

participant desires to be consistent with her past preferences and consequently chooses 60 tasks

when shown her previous prediction. What will this participant do when faced with a wage of

$.18 (for which she prefers to do around 40 tasks)? One might imagine that the participant

would recognize that her previous prediction did not just imply doing 60 tasks for $.20, but

implied a general preference to do a higher level of work across other wages– for example, do-

ing around 60 tasks for $.18. This does not appear to be the case. Immediate-work decisions

with “similar”wages (but no past prediction for that wage) are between 6.7-9.0 tasks lower (Z

ranging from 1.98 − 2.73 and p from 0.001 − 0.05) than those with the prediction, depending

on the definition of “similar."

Potentially more pedestrian reasons might explain some of the behavior. For example,

in our dataset, participants commonly appear to round their decisions. For example, 48%

of non-corner predictions are divisible by 10 and 72% are divisible by 5. The tendency to

round decisions makes it is far more likely that immediate-work decisions will end up matching

predictions. Supporting this hypothesis, nearly twice the proportion of round predictions lead to

perfectly matching work choices in comparison to non-round decisions (38% vs. 20%), although

57

there is still some perfect matching with no rounding.

A.4 Projection Bias

We discuss two potential ways to model projection bias in Section 3.1.3. Tables A.2 and A.3

estimate these models using nine different specifications using different approaches of the sort

used elsewhere in the paper. The estimates of α are between .27 and .73, with seven of the

nine between 0.4 and 0.6. All but one are statistically significantly different than the full-

rationality value of α = 0, but worrisomely (and one of our reasons for our caution for the

structural estimation), one specification for the more theoretically grounded model of the two

is extremely noisy in ways that suggest convergence issues.

A.5 Participants Not Included in the Main Sample

In the main text, we focus on a primary sample of 72 participants for whom we are able to

estimate individual structural parameters. The removed participants have very similar averages

as the primary sample for the main reduced-form statistics discussed in the paper. When

making decisions about the immediate work, removed participants choose an average of 5.06

(Z = 2.07, p = 0.048) fewer tasks than when making decisions about future work. There

is an average difference of 0.25 (Z = 0.31, p = 0.76) fewer tasks in predictions compared

to future-work decisions. When comparing to immediate-work decisions, predictions are 5.31

higher (Z = 2.25, p = 0.03) on average.

In Figure A.4, we present the raw data of the 28 removed participants. The participants

are ordered by the coeffi cient obtained from a linear regression of decisions of wages, with

the estimated regression line shown in the plots. There is only one participant (ID:90, top

left of graph), who appears to have a clear negative relationship between wages and choices.

For a large set of the removed participants, there is very little variation in decisions given

different wages, including four participants with no variation. There are a few participants

with seemingly reasonable decisions, but for which the estimation routine did not converge for

58

Table A.2: Structural estimation of projection bias - based on marginal cost projection

(1) (2) (3) (4)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Present Bias β 0.833 0.811 0.833 0.833(0.036) (0.246) (0.040) (0.041)

Naive Pres. Bias βh 0.999 1.013 1.005 1.003(0.015) (0.171) (0.010) (0.009)

Discount Factor δ 1.003 1.006 1.003 1.003(0.003) (0.047) (0.001) (0.002)

Effort Cost γ 2.185 2.162 2.131 1.972(0.098) (0.860) (0.091) (0.080)

Money Slope ϕ 401 440 429 270(189) (265) (130) (86)

Proj Bias α 0.531 0.430 0.406 0.268(.) (1.270) (0.119) (0.067)

Participant FE X X X

Day FE X X

Prediction Soph.

Later Decisions X

Observations 8049 8049 8049 5539Participants 72 72 72 64Log Likelihood -28409 -25075 -24834 -16524

H0(β =1) p<0.001 p= 0.442 p<0.001 p<0.001H0(βh =1) p= 0.92 p= 0.94 p= 0.59 p= 0.73H0(α =0) p= . p= 0.735 p<0.001 p<0.001H0(δ =1) p= 0.39 p= 0.90 p= 0.06 p= 0.08

Note: Projection Bias 2

59

Table A.3: Structural estimation of projection bias - based on task level projection

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.835 0.812 0.833 0.833 0.825(0.038) (0.042) (0.040) (0.041) (0.041)

Naive Pres. Bias βh 0.999 1.014 1.006 1.003 1.004(0.011) (0.011) (0.010) (0.009) (0.003)

Discount Factor δ 1.003 1.005 1.003 1.003 1.003(0.003) (0.002) (0.001) (0.002) (0.001)

Effort Cost γ 2.145 2.142 2.118 1.971 2.126(0.070) (0.084) (0.081) (0.075) (0.081)

Money Slope ϕ 724 710 687 367 720(251) (267) (244) (120) (258)

Proj Bias α 0.730 0.526 0.527 0.407 0.521(0.260) (0.128) (0.129) (0.128) (0.127)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 8049 8049 8049 5539 8049Participants 72 72 72 64 72Log Likelihood -28412 -25079 -24838 -16522 -24837

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.93 p= 0.23 p= 0.58 p= 0.74 p= 0.11H0(α =0) p= 0.005 p<0.001 p<0.001 p= 0.001 p<0.001H0(δ =1) p= 0.37 p= 0.01 p= 0.06 p= 0.08 p= 0.07

Note: Projection Bias 1

60

whatever reason, potentially because the number of decisions was too small due to attrition.

Table A.4 replicates our main aggregate specification in Table 1 for the full 100 participant

sample. For completeness, Table A.5 replicates it for the full sample with attritors removed.

The qualitative results are unchanged, although the estimate of the present-bias parameter β

is moderately lower.

A.6 Sample Robustness

We check robustness of our results to eliminating choices that might be distorted for various

reasons. Recall that the main analysis does not include any immediate-work decisions for

which participants had made a previous prediction because prediction-accuracy payments might

distort these work decisions. In Table A.6, we additionally remove entire decision sets for

which a previous prediction was made for any wage in the set. Recall that we often asked

participants to make two future-work or prediction decision sets on one date. To remove any

consistency effects across these decision sets, Table A.7 removes the second decision set of a given

type. Finally, to remove consistency effects across decision sets of different types (immediate

work, future work, and predictions), Table A.8 only includes the first decision set made by the

participant on a given date. Our conclusions are largely stable, except for the non-statistically

significant β coeffi cient of 0.915 for the later dates in the most restrictive data sample. As a

result of the restrictions, this specification only uses 32% of the sample, leading to relatively

erratic estimates - for example, in this specification, βh is estimated at 1.09.

A.7 Predictions-As-Commitment

In the majority of our main estimation table (Table 1), we assume that participants make

straightforward predictions and do not use prediction-accuracy payments for soft commitments.

In Column (5), we show that assuming this use of predictions in the specification in Column

(3) does not change the results. In Table A.9, we perform this exercise for the first four columns

in Table 1 (consequently replicating Column (5) of Table 1 as Column (3) of Table A.9). There

61

Figure A.4: Scatter of all decisions of 28 removed participants

Note : In our main analysis, we focus on a primary sample of 72 participants. This graph showsscatter plots of task decisions (y-axis) given a wage (x-axis) of all of the removed participants,as well as the linear regression line. The plots are ordered by the regression slope coeffi cients."ID" is the assigned id of the participant and "[Left Early]" represents attrition. Present,future, and prediction decisions are represented by circles, diamonds, and triangle respectively.

62

Table A.4: Robustness: primary aggregate estimation using full sample

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.768 0.775 0.734 0.723 0.731(0.042) (0.043) (0.064) (0.068) (0.065)

Naive Pres. Bias βh 1.003 1.017 1.010 1.006 1.000(0.012) (0.013) (0.012) (0.013) (0.003)

Discount Factor δ 1.008 1.009 1.012 1.013 1.011(0.003) (0.003) (0.007) (0.008) (0.007)

Effort Cost γ 2.254 2.161 2.117 1.943 2.117(0.104) (0.113) (0.112) (0.111) (0.111)

Money Slope ϕ 995 758 609 304 612(492) (386) (300) (148) (302)

Proj Task Reduction α 8.123 5.716 5.217 4.908 5.213(2.847) (2.103) (2.174) (2.487) (2.167)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 10919 10919 10919 7489 10919Participants 100 100 100 86 100Log Likelihood -38025 -35661 -35524 -23707 -35525

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.83 p= 0.18 p= 0.42 p= 0.62 p= 1.00H0(α =0) p= 0.004 p= 0.007 p= 0.016 p= 0.048 p= 0.016H0(δ =1) p= 0.02 p= 0.00 p= 0.09 p= 0.09 p= 0.09

Note: This Table replicates Table 1 for the full sample of 100 subjects. Subject fixed effectsare only calculated for subjects in primary sample as the maximum likelihood routine doesnot converge otherwise.

63

Table A.5: Robustness: primary aggregate estimation using full sample minus attritors

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.761 0.783 0.730 0.721 0.729(0.045) (0.047) (0.071) (0.073) (0.072)

Naive Pres. Bias βh 1.006 1.022 1.012 1.006 0.998(0.013) (0.014) (0.013) (0.013) (0.004)

Discount Factor δ 1.010 1.009 1.013 1.014 1.013(0.004) (0.003) (0.008) (0.009) (0.008)

Effort Cost γ 2.318 2.188 2.141 1.962 2.137(0.124) (0.129) (0.127) (0.122) (0.126)

Money Slope ϕ 1311 949 744 344 734(764) (555) (417) (184) (410)

Proj Task Reduction α 8.910 6.069 5.326 4.812 5.354(3.091) (2.296) (2.347) (2.619) (2.342)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 9799 9799 9799 7044 9799Participants 79 79 79 79 79Log Likelihood -34012 -31959 -31834 -22452 -31834

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.65 p= 0.11 p= 0.34 p= 0.63 p= 0.58H0(α =0) p= 0.004 p= 0.008 p= 0.023 p= 0.066 p= 0.022H0(δ =1) p= 0.01 p= 0.00 p= 0.10 p= 0.10 p= 0.10

Note: This Table replicates Table 1 for the sample of 79 non-attritor subjects Subject fixedeffects are only calculated for subjects in primary sample as the maximum likelihood rou-tine does not converge otherwise.

64

Table A.6: Robustness: primary aggregate estimation using a restricted data sample

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.851 0.785 0.808 0.790 0.798(0.048) (0.051) (0.050) (0.058) (0.051)

Naive Pres. Bias βh 0.999 1.014 1.006 1.004 1.006(0.011) (0.011) (0.010) (0.009) (0.003)

Discount Factor δ 1.003 1.006 1.003 1.003 1.003(0.003) (0.002) (0.001) (0.002) (0.001)

Effort Cost γ 2.149 2.154 2.128 1.970 2.139(0.072) (0.086) (0.082) (0.075) (0.083)

Money Slope ϕ 733 744 713 366 758(259) (285) (257) (119) (277)

Proj Task Reduction α 6.835 5.137 5.099 3.615 5.016(2.729) (1.341) (1.345) (1.358) (1.320)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 7550 7550 7550 5040 7550Participants 72 72 72 64 72Log Likelihood -26675 -23562 -23335 -15026 -23333

H0(β =1) p= 0.002 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.93 p= 0.22 p= 0.53 p= 0.68 p= 0.05H0(α =0) p= 0.012 p<0.001 p<0.001 p= 0.008 p<0.001H0(δ =1) p= 0.40 p= 0.01 p= 0.06 p= 0.08 p= 0.08

Note: This Table replicates Table 1, but removes observations in which present-work decisionhave any prediction bonus in the decision set.

65

Table A.7: Robustness: primary aggregate estimation using a restricted data sample

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.842 0.829 0.858 0.853 0.849(0.037) (0.041) (0.039) (0.040) (0.040)

Naive Pres. Bias βh 1.004 1.021 1.010 1.002 1.003(0.019) (0.015) (0.013) (0.013) (0.003)

Discount Factor δ 1.003 1.006 1.002 1.002 1.002(0.003) (0.002) (0.002) (0.002) (0.002)

Effort Cost γ 2.129 2.116 2.083 1.931 2.089(0.071) (0.086) (0.082) (0.079) (0.081)

Money Slope ϕ 660 621 591 309 615(227) (236) (213) (106) (221)

Proj Task Reduction α 6.951 4.805 4.684 3.686 4.642(2.658) (1.330) (1.329) (1.286) (1.313)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 6559 6559 6559 4499 6559Participants 72 72 72 64 72Log Likelihood -23119 -20511 -20304 -13427 -20303

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.82 p= 0.17 p= 0.46 p= 0.89 p= 0.29H0(α =0) p= 0.009 p<0.001 p<0.001 p= 0.004 p<0.001H0(δ =1) p= 0.29 p= 0.01 p= 0.34 p= 0.27 p= 0.37

Note: This Table replicates Table 1, but removes the second future and prediction decisionsets made on a decision date.

66

Table A.8: Robustness: primary aggregate estimation using a restricted data sample

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.851 0.875 0.878 0.915 0.851(0.044) (0.053) (0.056) (0.063) (0.050)

Naive Pres. Bias βh 1.035 1.096 1.074 1.093 0.997(0.057) (0.059) (0.051) (0.052) (0.009)

Discount Factor δ 1.003 1.006 1.003 1.001 1.003(0.003) (0.002) (0.003) (0.004) (0.003)

Effort Cost γ 2.077 2.109 2.062 1.909 2.060(0.073) (0.093) (0.088) (0.084) (0.089)

Money Slope ϕ 519 572 517 271 527(182) (238) (206) (101) (215)

Proj Task Reduction α 5.111 4.990 4.738 4.380 4.812(2.765) (1.690) (1.734) (1.625) (1.741)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 3639 3639 3639 2559 3639Participants 72 72 72 64 72Log Likelihood -12712 -11388 -11250 -7608 -11254

H0(β =1) p<0.001 p= 0.018 p= 0.030 p= 0.175 p= 0.003H0(βh =1) p= 0.54 p= 0.10 p= 0.15 p= 0.07 p= 0.73H0(α =0) p= 0.065 p= 0.003 p= 0.006 p= 0.007 p= 0.006H0(δ =1) p= 0.31 p= 0.01 p= 0.31 p= 0.79 p= 0.31

Note: This Table replicates Table 1, but removes all but the first decision set of any kindmade on a decision date.

67

is very little quantitative change in the results.

A.8 Location of Fixed Effects

In our original analysis plan, we expected to display one specification in which we allowed the

monetary slope ϕ and cost curvature γ parameters to vary arbitrarily for each participant.

However, due to the large number of fixed effects, this specification does not converge when

decision-date fixed effects are also added. Consequently, in the main paper, we were required

to use an alternative specification: using participant fixed effects for the monetary slope ϕ

parameter. In Columns (1)-(6) of Table A.10, we show that the estimates are robust to other

possibilities. The parameters are largely consistent with two fixed-effects specifications in the

paper (Columns (2) and (3) of Table 1), with some estimates above and some below: however,

the specification which adds only decision-date fixed effects to the ϕ parameter (Column (3))

leads to a higher β estimate of 0.907, which is borderline statistically significant ( p = 0.073).

A.9 Date-of-Work Fixed Effects

In multiple specifications in the paper, we control for participant learning by including date-

of-decision fixed effects on cost curve parameters. However, these fixed effects do not control

for consistent changes in the cost curve for a given date-of-work. These changes might occur

if participants shared a common event on the same participation date, such as a midterm on

date four. Given that participants choose their own calendar dates for each of the final six

"participation dates," this coordination would be unexpected. However, as a formal check,

Table A.11 mirrors our main estimation Table, but includes date-of-work rather than date-of-

decision fixed effects where appropriate. There is little effect on the estimates.

A.10 Location of Error Term

Throughout the paper, we assume that observed effort choices e are composed of predicted effort

choice and an additive reduced-form normally-distributed error term ε. In this section, we show

68

Table A.9: Robustness: assuming predictions used for commitment

(1) (2) (3) (4)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Present Bias β 0.825 0.799 0.825 0.828(0.038) (0.043) (0.041) (0.043)

Naive Pres. Bias βh 1.006 1.005 1.004 1.003(0.004) (0.003) (0.003) (0.003)

Discount Factor δ 1.003 1.005 1.003 1.003(0.003) (0.002) (0.001) (0.002)

Effort Cost γ 2.156 2.151 2.126 1.976(0.069) (0.084) (0.081) (0.075)

Money Slope ϕ 769 752 720 377(261) (284) (257) (125)

Proj Task Reduction α 7.236 5.191 5.207 4.024(2.582) (1.254) (1.270) (1.242)

Participant FE X X X

Day FE X X

Prediction Soph. X X X X

Later Decisions X

Observations 8049 8049 8049 5539Participants 72 72 72 64Log Likelihood -28411 -25078 -24837 -16522

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.09 p= 0.08 p= 0.11 p= 0.33H0(α =0) p= 0.005 p<0.001 p<0.001 p= 0.001H0(δ =1) p= 0.38 p= 0.01 p= 0.07 p= 0.08

Note: Forcing sophistication.

69

Table A.10: Robustness: differing location of fixed effects

(1) (2) (3) (4) (5) (6)

Present Bias β 0.810 0.907 0.817 0.865 0.813 0.851(0.045) (0.052) (0.041) (0.047) (0.043) (0.043)

Naive Pres. Bias βh 1.013 1.005 1.010 1.007 1.009 0.997(0.012) (0.011) (0.011) (0.012) (0.012) (0.009)

Discount Factor δ 1.005 0.996 1.004 0.999 1.003 1.000(0.002) (0.003) (0.002) (0.002) (0.002) (0.002)

Effort Cost γ 2.239 2.162 2.135 2.235 2.231 2.266(0.098) (0.083) (0.085) (0.098) (0.099) (0.099)

Money Slope ϕ 873 930 702 954 852 11670(369) (356) (266) (408) (360) (15979)

Proj Bias α 5.910 5.754 4.777 5.720 5.384 6.538(1.381) (1.313) (1.282) (1.418) (1.409) (1.431)

γ Participant FE X X X X

ϕ Participant FE X X

γ Day FE X X X

ϕ Day FE X X X

Observations 8049 8049 8049 8049 8049 8049Participants 72 72 72 72 72 72Log Likelihood -25161 -24948 -25048 -25116 -25129 -24848

H0(β =1) p<0.001 p= 0.073 p<0.001 p= 0.004 p<0.001 p<0.001H0(βh =1) p= 0.30 p= 0.66 p= 0.38 p= 0.58 p= 0.47 p= 0.76H0(α =0) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(δ =1) p= 0.03 p= 0.12 p= 0.04 p= 0.65 p= 0.10 p= 0.99

Note: In the main Table in the paper, we run two fixed-effects specifications. In this table,we display the results given a variety of different locations for the fixed effects. Standarrderrors are clustered at the participant level.

70

Table A.11: Robustness: Using date-of-work rather than date-of-decision fixed effects

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.835 0.812 0.805 0.815 0.800(0.038) (0.042) (0.038) (0.044) (0.040)

Naive Pres. Bias βh 0.999 1.014 1.003 1.007 1.002(0.011) (0.011) (0.011) (0.009) (0.003)

Discount Factor δ 1.003 1.005 1.010 1.004 1.010(0.003) (0.002) (0.008) (0.005) (0.008)

Effort Cost γ 2.145 2.142 2.116 1.967 2.120(0.070) (0.084) (0.079) (0.076) (0.078)

Money Slope ϕ 724 710 576 361 589(252) (265) (225) (117) (237)

Proj Task Reduction α 7.304 5.257 4.700 3.857 4.682(2.597) (1.279) (1.238) (1.317) (1.224)

Participant FE X X X X

Work Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 8049 8049 8049 5539 8049Participants 72 72 72 64 72Log Likelihood -28412 -25079 -24937 -16545 -24936

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.93 p= 0.23 p= 0.77 p= 0.42 p= 0.42H0(α =0) p= 0.005 p<0.001 p<0.001 p= 0.003 p<0.001H0(δ =1) p= 0.37 p= 0.01 p= 0.20 p= 0.45 p= 0.22

Note: This Table replicates Table 1, but uses work-date rather than participation-date fixedeffects in Columns (3)-(5).

71

that our results are robust to different assumptions about the location and form of the error

term. First, we calculate the likelihood functions given three alternative error specifications

and then we structural estimate the relevant parameters given these specifications.

In our first alternative specification, we assume that the error term on effort choices is

distributed log-normally, rather than normally. In this case:

L(ei|ϕ, β, γ, δ) = φLN((ϕ · β1(t=k) · β1(p=1)h · δ(T−k) · w)

1γ−1 − ei

σ),

where φLN(·) is the log-normal probability distribution function.

In our second alternative specification, we assume that there is a normally-distributed error

which occurs on the parameter γ. In this case, observed effort would be equal to:

e = (ϕ · β1(t=k) · β1(p=1)h · δ(T−k) · w)1

γ+εγ−1 − 10, (18)

with εγ distributed normally with mean zero and standard deviation σγ. Given this,

ln(ϕ · β1(t=k) · β1(p=1)h · δ(T−k) · w) + ln(e+ 10)

ln(e+ 10)∼ N(γ, σ2γ), (19)

which leads the likelihood of observation i to become:

L(ei|ϕ, β, γ, δ) = φ(

ln(ϕ·β1(t=k)·β1(p=1)h ·δ(T−k)·w)+ln(ei+10)ln(ei+10)

− γσγ

). (20)

In our third alternative specification, we assume that there is a log-normally-distributed

error which occurs on the parameter ϕ. In this case, observed effort would equal to:

e = ((ϕ+ εϕ) · β1(t=k) · β1(p=1)h · δ(T−k) · w)1

γ−1 − 10, (21)

72

with εϕ distributed log-normally with mean zero and standard deviation σϕ.51 Given this,

(e+ 10)γ−1

β1(t=k) · β1(p=1)h · δ(T−k) · w∼ LogN(ϕ, σ2ϕ), (22)

which leads the likelihood of observation i to become:

L(ei|ϕ, β, γ, δ) = φLN(

(ei+10)γ−1

β1(t=k)·β1(p=1)h ·δ(T−k)·w− ϕ

σϕ). (23)

Replicating our main results given these three different specifications are presented in Tables

A.12,A.13, and A.14, respectively. Comparison of the columns suggests that the location of

the error term does not have a large effect on any of the coeffi cients, although the β parameter

in the Table A.14 is higher than in our main table (but still statistically significantly different

from one).

A.11 Effect of Tobit Estimation

In the estimations of the paper, we account for the censored nature of the data by correcting

the likelihood function following a standard Tobit specification. Table A.15 present the results

without using a Tobit, using a likelihood of Equation (10) rather than equation (11). The main

parameters are largely stable (with β slightly higher in the later specifications) and the main

conclusions continue to hold. The cost-curvature and monetary-slope parameters do increase,

presumably to account for the fact that participants’ tasks decisions level out at 100 tasks,

regardless of wage.

51It is possible to write down a model with a normally-distributed error term on φ, but this assumption ishard to rationalize with the observed data. In particular, there are many instances in the data where a personchooses to a large amount of work (for example, 100 tasks) for a very low wage (like $.01). Rationalizing thesedata points requires an extremely high φ parameter that is hard to justify given a normally-distributed erroron the φ parameter which is implied from the majority of the data. As a result, estimations with this form donot converge.

73

Table A.12: Robustness: error on the log of effort

(1) (2) (3) (4)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Present Bias β 0.806 0.766 0.816 0.823(0.040) (0.039) (0.038) (0.038)

Naive Pres. Bias βh 1.000 1.008 1.003 1.008(0.013) (0.012) (0.011) (0.010)

Discount Factor δ 1.004 1.011 1.005 1.003(0.003) (0.002) (0.002) (0.002)

Effort Cost γ 1.662 1.657 1.658 1.573(0.051) (0.067) (0.066) (0.063)

Money Slope ϕ 73 72 81 60(16) (18) (21) (15)

Proj Task Reduction α 3.187 3.042 3.076 2.442(1.048) (0.733) (0.746) (0.761)

Participant FE X X X X

Day FE X X

Prediction Soph.

Later Decisions X

Observations 8049 8049 8049 5539Participants 72 72 72 64Log Likelihood -9437 -6919 -6784 -4586

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 1.00 p= 0.49 p= 0.76 p= 0.44H0(α =0) p= 0.002 p<0.001 p<0.001 p= 0.001H0(δ =1) p= 0.22 p= 0.00 p= 0.00 p= 0.08

Note: The error term is on gamma

74

Table A.13: Robustness: error on parameter gamma

(1) (2) (3) (4)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Present Bias β 0.816 0.753 0.888 0.863(0.029) (0.031) (0.046) (0.053)

Naive Pres. Bias βh 0.994 1.006 0.999 1.009(0.020) (0.021) (0.021) (0.025)

Discount Factor δ 1.006 1.016 1.001 1.001(0.003) (0.002) (0.002) (0.003)

Effort Cost γ 2.420 2.673 2.711 2.757(0.054) (0.046) (0.046) (0.057)

Money Slope ϕ 1481 3511 5530 6370(336) (647) (1027) (1429)

Proj Task Reduction α 3.367 2.209 2.602 2.227(0.961) (0.587) (0.625) (0.587)

Participant FE X X X

Day FE X X

Prediction Soph.

Later Decisions X

Observations 8049 8049 8049 5539Participants 72 72 72 64Log Likelihood -666 908 1069 654

H0(β =1) p<0.001 p<0.001 p= 0.015 p= 0.009H0(βh =1) p= 0.77 p= 0.79 p= 0.95 p= 0.72H0(α =0) p<0.001 p<0.001 p<0.001 p<0.001H0(δ =1) p= 0.08 p= 0.00 p= 0.74 p= 0.71

Note: The error term is on gamma

75

Table A.14: Robustness: error on parameter phi

(1) (2) (3) (4)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Present Bias β 0.909 0.819 0.935 0.918(0.028) (0.027) (0.033) (0.037)

Naive Pres. Bias βh 1.007 1.009 1.002 1.015(0.016) (0.016) (0.015) (0.019)

Discount Factor δ 1.004 1.013 1.001 1.000(0.003) (0.002) (0.002) (0.002)

Effort Cost γ 2.155 2.472 2.513 2.543(0.068) (0.051) (0.050) (0.057)

Money Slope ϕ 518 1629 2483 2771(158) (351) (516) (663)

Proj Task Reduction α 2.897 0.919 0.426 0.570(1.252) (0.677) (0.659) (0.611)

Participant FE X X X

Day FE X X

Prediction Soph.

Later Decisions X

Observations 8049 8049 8049 5539Participants 72 72 72 64Log Likelihood -6501 -4960 -4816 -3178

H0(β =1) p= 0.001 p<0.001 p= 0.049 p= 0.026H0(βh =1) p= 0.66 p= 0.57 p= 0.88 p= 0.44H0(α =0) p= 0.021 p= 0.174 p= 0.518 p= 0.351H0(δ =1) p= 0.17 p= 0.00 p= 0.65 p= 0.98

Note: The error term is on gamma

76

Table A.15: Robustness: primary aggregate estimation without using a Tobit correction

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.826 0.836 0.888 0.887 0.883(0.038) (0.032) (0.030) (0.033) (0.030)

Naive Pres. Bias βh 1.000 1.013 1.006 1.011 1.001(0.011) (0.012) (0.011) (0.011) (0.001)

Discount Factor δ 1.003 1.007 1.001 1.000 1.001(0.003) (0.002) (0.001) (0.001) (0.001)

Effort Cost γ 2.606 2.713 2.697 2.589 2.701(0.095) (0.119) (0.115) (0.106) (0.116)

Money Slope ϕ 4552 6693 7039 4368 7208(2075) (3505) (3591) (2067) (3695)

Proj Task Reduction α 2.722 2.548 2.998 2.338 2.996(1.617) (0.700) (0.732) (0.744) (0.734)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 8049 8049 8049 5539 8049Participants 72 72 72 64 72Log Likelihood -38549 -35309 -35044 -23899 -35044

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.99 p= 0.25 p= 0.59 p= 0.30 p= 0.43H0(α =0) p= 0.092 p<0.001 p<0.001 p= 0.002 p<0.001H0(δ =1) p= 0.32 p= 0.00 p= 0.21 p= 0.79 p= 0.24

Note: This Table replicates Table 1, but without using a Tobit correction for the censorednature of the data

77

A.12 Endogeneity of Participation-Date Choice

Recall that we allowed participants to choose their own dates, with the restriction that each

participation date was within 4 to 10 days of the previous date and the final date occurred within

six weeks of the start of the experiment. This flexibility was designed to allow participants to

avoid dates with previous commitments, such as classes, exams, or social events. However, this

endogeneity could potentially bias our results: for example, if participants with high exponential

discount factors (δ = 1) choose their dates in close succession, while those with lower discount

factors choose to space their dates as far as possible, our estimate of δ might be potentially

biased, which could in turn bias our other estimates. Table A.16 replicates our main results

with the distance between each payment dates is forced to match the average distance between

payment dates across all participants. There is very little quantitative change between the

results in this table and that in the paper.

A.13 Experimental Instructions

Welcome:Thank you for participating in the study. We will begin shortly.

Eligibility for this study:To continue in this study, you need to meet these criteria: You must be willing to participate

for seven (7) separate days over the next six weeks. Each participation day will require at least

20 minutes of your time. You can choose participate for additional time each day to receive

supplementary payments. The first day (today) will occur in the xlab. All other days will occur

at any computer that has access to the Internet.

You must be willing to receive your payment from this study as one single payment by check

at the end of the study. Payments will be made seven weeks from today, on December 7th,

2012. You will return to the xlab to receive this payment.

If you do not meet these criteria, please inform us of this now.

78

Table A.16: Robustness: primary aggregate estimation using average participation date choice

(1) (2) (3) (4) (5)Initial

EstimationParticipant

FEDecisionDay FE

LaterDecisions

Pred.Soph.

Present Bias β 0.820 0.808 0.825 0.833 0.817(0.040) (0.043) (0.042) (0.044) (0.043)

Naive Pres. Bias βh 1.000 1.013 1.005 1.003 1.004(0.011) (0.012) (0.010) (0.009) (0.003)

Discount Factor δ 1.005 1.006 1.004 1.003 1.003(0.002) (0.002) (0.002) (0.002) (0.002)

Effort Cost γ 2.154 2.145 2.117 1.971 2.125(0.072) (0.084) (0.081) (0.075) (0.081)

Money Slope ϕ 710 710 676 367 708(244) (267) (238) (119) (252)

Proj Bias α 7.646 5.383 5.277 4.080 5.214(2.610) (1.293) (1.287) (1.280) (1.266)

Participant FE X X X X

Day FE X X X

Prediction Soph. X

Later Decisions X

Observations 8049 8049 8049 5539 8049Participants 72 72 72 64 72Log Likelihood -28396 -25070 -24837 -16523 -24836

H0(β =1) p<0.001 p<0.001 p<0.001 p<0.001 p<0.001H0(βh =1) p= 0.97 p= 0.26 p= 0.59 p= 0.77 p= 0.11H0(α =0) p= 0.003 p<0.001 p<0.001 p= 0.001 p<0.001H0(δ =1) p= 0.01 p= 0.01 p= 0.03 p= 0.11 p= 0.03

Note: SE clustered at subject level.

79

Informed ConsentPlaced in front of you is an informed consent form to protect your rights as a participant.

Please read it. If you would like to choose not to participate in the study you are free to leave

at this point. If you have any questions, we can address those now. We will pick up the forms

after the main points of the study are discussed.

AnonymityYour anonymity in this study is assured. Your name will never be recorded or connected to

any decision you make here today. Your email will be collected solely in order to send reminder

emails. After the study, your email information will be destroyed and will not be connected to

your responses in the study.

RulesPlease turn your cell phones off. Please put away any books, papers, computers, etc. If you

have a question at any point, just raise your hand. There will be a quiz once we have finished

with the instructions. If it is clear that you do not understand the instructions when we review

your answers, you will be emailed and removed from the study.

Your EarningsYou will be paid a one-time completion payment of $50 for completing the minimum require-

ments of the study. Furthermore, you will have the chance to earn a supplementary payment of

between $2-$25/hour for further participation. You will also have the chance to earn additional

bonuses.

It is very important for the study that you participate on your chosen participation

days. Therefore, as we discuss below, you will be allowed to your modify a participation

date if needed (up to 5pm the day before). You cannot modify participation dates after that

point. Unfortunately, if you do not modify a date and you miss one of your participation dates,

you will forgo the $50 completion payment and will be immediately removed from the study (you

will receive any supplementary payments and additional payments you have already earned).

There will be absolutely no exceptions to this rule, regardless of the reason.

80

All payments (completion, supplementary, bonus) will be made as one single payment by

check at the end of the study, regardless of if you are removed from the study. All payments

will be made seven weeks from today, on December 7th, 2012. You will return to the xlab to

receive this payment.

Choosing Future Participation DaysAs stated above, you will participate in the study for 7 days over the next 6 weeks. Today

is your first participation day. Today, you will choose a set of 6 future participation dates that

occur within the next 6 weeks. Participation dates must between 4 and 10 days apart. That

is, if you choose November 12th as you third participation date, your fourth participation date

must lie between November 16th and November 22nd.

For future participation dates, you will be emailed an online study link the day before your

participation date. This link will be active on 4am (Pacific Time) on the participation date. You

simply click on the link and follow the instructions. You must complete the study for that day in

one sitting by midnight. If you fail to complete the study for that day, you will be immediately

removed from the study and will forgo the $50 completion payment.

You will have the ability to modify your participation dates over the course of the study if

needed. For example, if chose November 12th as your third participation date, but later learn

that you will have a test on that day, you can change the third participation date to November

14th. There is a small fee of $.25 each time you modify your participation dates. You may

modify a participation date up to 5pm the day before the participation date. That is, if your

third participation date is November 12th, then you can modify this date anytime up to 5pm

on November 11th.

The StudyThis study examines people’s decisions about doing work for monetary payments. For the

study, we have designed a task (discussed below) that you can choose to do for different

wages. The task has no value to us beyond understanding these decisions.

We are interested in these work decisions at different points in time. For example, in the

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study, you might be asked on Monday how many tasks you want to do next Thursday for

different wages. Then, when next Thursday arrives, you be asked how many tasks you want to

do on that day for different wages. Note that the answers about work in the future may be the

same or may be different than the eventual answers about work when the day arrives. You will

actually have to do the tasks specified in one of the decisions, so it is in your interest to answer

truthfully.

We are also interested in people’s perceptions about their future work decisions. For example,

in the study, you might be asked on Monday how many tasks you think you will want to do

when you answer work questions next Thursday. That is, we want to know your prediction of

your future answers. Note that these predictions may be the same or may be different than

the answers about future work. You may be rewarded for accurate predictions, so it is in your

interest to answer truthfully.

Greek Transcription JobAs we just discussed, we have designed a task involving transcribing a line of blurry letters

from a greek text for this study.

We will now spend a few minutes practicing this job on the computer. Before we continue,

you will be asked to register using your email by clicking “register”once you open the computer

shortcut. Make sure that you enter a valid email address as this is the email we will use to contact

you about future participation days.

In the task, Greek text will appear in a Transcription Box on your screen. For each letter

you will need to find and select the corresponding letter and enter it into the Completion Box

on your screen. One task is one row of greek text. For the task to be complete your accuracy

must be 80% or better.

As part of the task, an auditory “beep”will sound randomly throughout the transcription

process. Please put on your headphones so that you can hear the beeping noise. After you hear

this beeping noise, you must press the “noise”button at the bottom left of the screen. If you do

not press the “noise”button within five seconds of hearing the beeping noise, your transcription

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will be reset. If you press the noise button erronously (when there was no beeping noise), your

transcription will be reset.

On average, people with some experience complete a task in about 52 seconds (about

70/hour).

Each day of participation, you will have to complete a 10 mandatory tasks (10 lines of

greek text). Furthermore, you will complete additional supplementary tasks for supplementary

payments. The number of supplementary tasks you must complete on each participation day

and the supplementary payment will depend on your choices in the study.

Participation Date: TimelineEach participation date will involve a series of steps, which we will discuss now. The order

of these steps might be different on different days. Today, we will complete only a subset of the

following steps. In future participation dates, you will complete all of the following steps.

Completion of Mandatory TasksRecall that you are required to complete 10 mandatory tasks on each participation

date. These mandatory tasks will ensure that you participate for at least 20 minutes for each

participation date.

Question Type 1: Work DecisionsRecall that we are interested in people’s decisions about doing work for monetary

payments. Therefore, you will be asked a series of questions concerning your preference about

completing additional supplementary tasks. Note that the supplementary tasks are in addition

to the 10 mandatory tasks.

We are interested in these work decisions at different points in time. Therefore, you will be

asked questions about how many tasks you want to do in the future as well as questions about

how many tasks you want to do today. For example, you might see the following screen on the

computer:

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In this screen, you are asked to choose the number of tasks that you want to complete on

November 12th, 2012 for five different wages. For example, on the first line, you are asked the

number of tasks you would like to complete for $.20/task. You will use the slider bar to choose

a number between 0 and 100. You will also do this for the other 4 wages.

As another example, you might see the following screen on the computer:

In this screen, you are asked to choose the number of supplementary tasks that you want

to complete today. For example, on the first line, you are asked the number of tasks you would

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like to complete for $.18/task. You will use the slider bar to choose a number between 0 and

100. You will also do this for the other 4 wages.

The hourly wage estimates and time-to-completion estimates have been calculated using a

task time of 55 seconds. Notice that the box in the bottom of the screen allows you to enter a

different task time if you want a different estimate of the hourly wage and time-to-completion.

The wages in each question have been chosen at random from a set of wages from $.01/task

to $.31/task. Your decisions cannot in any way affect the choice of future wages– the wages

for this study have already been randomly chosen by a random number generator.

Each one of these decisions could be randomly chosen as the decision-that-counts (the

process for choosing that decision-that-counts is discussed below). If a decision is chosen as

the decision-that-counts, you must complete that amount of supplementary tasks for the sup-

plementary wage. Therefore, it is in your own interest to answer honestly about your

work preferences, because you might actually have to complete the work you specify for the

given wage. For example, if given a wage of $.12/task, you would like to do 50 tasks (and make

an extra $6.00), you should answer “50."

Recall that you can modify participation dates. If you modify a date, then the decisions

about that date will be transfered to the new date. For example, if your third decision date is

November 12th and you change it to November 14th, all of the decisions you made about No-

vember 12th will then have the potential to be chosen as the decision-that-counts on November

14th.

Random Selection of the “Decision-That-Counts"You will be asked questions about how many tasks you want to do in the future and how

many tasks you want to do on that day. Therefore, when a given participation date arrives,

you will have answered many questions about work on that date. We will collect all of those

decisions and randomly choose one as the decision-that-counts. This is the screen that collects

all of the past decisions:

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When you press the “choose” button, one of these decisions will be randomly chosen as

the decision-that-counts. The decision-that-counts has already been chosen by a random

number generator in the computer. You cannot affect how the decision-that-counts is

chosen with your choices.

Completion of Supplementary WorkOnce the decision-that-counts is chosen, you must complete the amount of supplementary

tasks you chose for the wage in the decision-that-counts. For example, if you answered “40”to

the question: “For $.18/task, how many tasks do you want to complete TODAY?”, and this

decision is chosen as the decision-that-counts, you would complete 40 supplementary tasks and

make a supplementary payment of 40·$.18=$7.20.

Question Type 2: PredictionsRecall that we are also interested in people’s perceptions about their future work

decisions. Therefore, you will be asked a series of questions concerning your predictions about

how many tasks you think you will want to do when you answer work questions in the future.

For example, you might see the following screen on the computer:

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The first line asks for your prediction of your own answer on November 12th to a question

about the number of tasks you want to complete for a wage of $.19. For example, if you

predict that you would answer 62 to this question on November 12th, you should answer “62.”

Furthemore, the question gives a bonus amount if your answer is within 5 tasks of your eventual

answer on that day (in the example above, it is $3.44). Again, the wage and bonus have already

been chosen by a random number generator and you cannot affect this choice with your

decisions.

On November 12th, when you are in the step of the study that asks questions of type 1, there

is some chance that the computer will ask you the set of questions you made a prediction about,

such as “For $.19/task, how many tasks do you want to complete today?”. If this occurs, you

will be reminded about your previous predictions about your own answers (for example, “62”)

and be reminded about the bonus if you answer within 5 tasks of this amount. If you answer

such that your previous prediction is accurate (for example, you choose a number between

57-67) and this decision is chosen as the decision-that-counts, you will receive the bonus. If you

do not answer such that the previous prediction is correct (for example, you choose “10”) or

this decision is not chosen as the decision-that-counts, you will not receive any bonus.

As there is a chance that the question you are making predictions about will be asked and

chosen as the decision-that-counts, it is in your interest to make your predictions as

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accurate as possible.

Recap:

• This is a study about work decisions. We are interested in decisions about work for

different wages at different points in time. We are also interested in predictions about

future decisions.

• The study requires participation for seven days over the next six weeks. Today is the first

participation date.

• You will choose your participation dates today. They can be modified in the future for a

small fee. You cannot modify a date after 5pm the day before.

• You will be paid a one-time-completion payment of $50 for completing the minimum

requirements of the study on each day. Furthermore, you will have the chance to earn

anywhere from $2-$25/hour for further participation and the chance to earn additional

bonuses. You will return to the xlab on December 7th to receive your payment by check.

• If you choose to no longer participate, or do not complete the jobs you chose, you will

forgo the completion payment of $50 and be removed from the study. You will return to

the xlab on December 7th to receive your payment by check.

• You will be asked to complete tasks involving transcription of greek letters.

• Each week, you will be asked to complete a minimum requirement of tasks.

• Each week, you will be asked questions about how many supplementary tasks you would

like to complete for different wages on different days.

• Each week, one of the decisions you make about supplementary work will be randomly

chosen as the decision-that-counts and you will complete your chosen supplementary

number of tasks for the chosen supplementary wage.

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• Each week, you will make predictions about your future answers to questions about

supplementary tasks given different wages. If the question you make a prediction about

is chosen as the decision-that-counts and your prediction is accurate, you will receive a

bonus payment.

• On December 7th, you will receive a payment consisting of your completion payment of

$50, plus any supplementary earnings you made during the study, plus any bonuses made

during the study. You will return to the xlab to receive your payment by check.

ConsentNow that we have explained the study, you are free to leave if you would like to choose not

to participate in the study. Otherwise, please sign the consent form and we will pick these up

now.

Choosing DatesPlease choose 6 future participation dates using the calendar on the computer. Once you

choose a date today, it cannot be amended until tomorrow. Recall that participation dates must

between 4 and 10 days apart. You will have the ability to modify these dates over the course

of the study for a fee of $.25. You may modify a participation date up to 5pm the day before

the participation date.

Mandatory WorkNow you will complete your minimum work of 10 tasks for the first participation date. When

this is completed, please fill out the quiz at your table.

QuizOnce you have completed the minimumwork, you may answer the questions on the quiz. You

are free to consult these instructions when answering questions. Recall that if your answers

suggest that you do not understand the study, you will be emailed and removed from the

study. Please sit quietly once the quiz has been completed.

Question Type 1: Work Decisions

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You will answer questions about your preferences about work on your second participation

date. On the screen, you see five different wages, with five different sliders. For each wage,

choose the number of tasks that you want to do on that date.

Once you are done, you will answer questions about your preferences about work today. On

the screen, you see five different wages, with five different sliders. For each wage, choose the

number of tasks that you want to do today. Because we do not have time today to complete

the tasks, you will not have to complete these tasks. These questions are used solely for you to

get practice with the computer interface. This is the only set of practice questions in the entire

study.

Please stop when you have finished these decisions.

Question Type 2: PredictionsYou will now answer a set of five questions about your predictions about work decisions

on the third participation date. On the screen, you see five different wages, with five different

sliders. For each wage, choose the number of tasks that you predict you will want to do when

you answer questions on your third participation date.

Random Selection of the “Decision-That-Counts"The decision-that-counts will now be chosen. You have made five decisions about work

today. These decisions have been collected and one will be chosen randomly. Press “choose”to

randomly choose the decision-that-counts.

Completion of Supplementary WorkOn a normal day of the study, you would now have to complete the supplementary work

chosen in the decision-that-counts. As we do not have time today, you do not have to complete

these tasks. The computer has been set to require only one task. Please complete it now. On

future days, you will have to do the number of tasks chosen in the decision-that-counts for the

wage chosen.

Future Participation Dates

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You will receive an email the night before each participation date. This email contains a

personalized link to access the study. You will also receive a reminder email the night of each

participation date. If you have any questions, please email: experiment@haas.berkeley.edu.

Feel free to take these instructions for future reference. This concludes today’s portion of

the experiment.

QuizPlease complete the quiz in order to make sure that you understand the study.

Participant #:

Session Date and Time:

1. Including today, how many participation dates are required in the study?

2. How many mandatory tasks are you required to participate on each participation date?

3. When can you modify participation dates? What is the fee for modification?

4. You will make many decisions about how many tasks you want to do on a date. Only

one of the decisions will be chosen as the decision-that-counts. How is this decision chosen?

5. You will be paid a bonus if your prediction for a given wage is within tasks of your

eventual decision

6. True / False: The wages and decisions-that-count are chosen randomly. There is no way

that you can affect the random choice with your decisions.

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