an experiment on time preference and misprediction in ... · an experiment on time preference and...
TRANSCRIPT
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. [email protected]‡Department of Economics and Business School, Harvard University. [email protected]
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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.
9
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.
14
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.
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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.
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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.
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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: [email protected].
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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