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Psychological Frictions and the Incomplete Take-Up of Social Benefits: Evidence from an IRS Field Experiment †


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We address the role of "psychological frictions" in the incomplete take-up of EITC benefits with an IRS field experiment. We specifically assess the influence of program confusion, informational complexity, and stigma by evaluating response to experimental mailings distributed to 35,050 tax filers who failed to claim $26 million despite an initial notice. While the mere receipt of the mailing, simplification, and the heightened salience of benefits led to substantial additional claiming, attempts to reduce perceived costs of stigma, application, and audits did not. The study, and accompanying surveys, suggests that low program awareness/understanding and informational complexity contribute to the puzzle of low take-up.
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American Economic Review 2015, 105(11): 3489–3529
Psychological Frictions and the Incomplete Take-Up of
Social Benets: Evidence from an IRS Field Experiment
By S B  D M*
We address the role of “psychological frictions” in the incomplete
take-up of EITC benets with an IRS eld experiment. We speci-
cally assess the inuence of program confusion, informational com-
plexity, and stigma by evaluating response to experimental mailings
distributed to 35,050 tax lers who failed to claim $26 million
despite an initial notice. While the mere receipt of the mailing, sim-
plication, and the heightened salience of benets led to substantial
additional claiming, attempts to reduce perceived costs of stigma,
application, and audits did not. The study, and accompanying sur-
veys, suggests that low program awareness/understanding and
informational complexity contribute to the puzzle of low take-up.
(JEL C93, D03, H24, M38)
A well-documented, and perhaps surprising, feature of transfers to the eco-
nomically and socially disadvantaged is that many individuals fail to take-up the
benets for which they are eligible (Currie 2006). The earned income tax credit
(EITC), the nation’s largest means-tested cash transfer program, is a prime example,
with an estimated incomplete take-up rate of 25 percent, amounting to 6.7 million
non-claimants each year (Plueger 2009).
The consequences of incomplete take-up
can be signicant. The typical EITC non-claimant forgoes an estimated $1,096,
Throughout the paper we use “incomplete take-up” to describe the failure to fully, or partially, claim a credit
by an eligible individual.
* Bhargava: Carnegie Mellon University, 5000 Forbes Ave., Pittsburgh, PA 15213 (e-mail: sbhar@andrew.cmu.
edu); Manoli: University of Texas, Austin, Speedway Stop C3100, Austin, TX 78712 (e-mail: dsmanoli@austin. This paper was originally circulated as Bhargava’s job market paper with the title “Why Are Benets
Left on the Table? Assessing the Role of Information, Complexity, and Stigma on Take-up with an IRS Field
Experiment.” We especially thank Alan Auerbach, Linda Babcock, Dan Black, Raj Chetty, Stefano DellaVigna, Jon
Guryan, George Loewenstein, Jesse Shapiro, and Oleg Urminsky for their invaluable insight and support. We are
additionally indebted to Leila Agha, Joe Altonji, Marianne Bertrand, Jim Berry, David Card, Kerwin Charles, Amy
Finkelstein, Ray Fisman, John Friedman, Jeff Grogger, Jon Gruber, Erin Johnson, Damon Jones, Larry Katz, Botond
Kszegi, Kara Leibel, Brigitte Madrian, Bhash Mazumder, Bruce Meyer, Sendhil Mullainathan, Kevin Mumford,
Ted O’Donoghue, Matthew Rabin, Emmanuel Saez, Dick Thaler, Heidi Williams, Aman Vora, and George Wu for
comments. We also thank seminar participants at the Behavioral Economics Annual Meeting, Carnegie Mellon
University, Chicago Booth, Columbia University, Cornell University, the Harris School of Public Policy, Harvard
University, the NBER Public Finance Meeting, University of California-Berkeley, and the University of Wisconsin.
Finally, we are grateful to collaborators at the IRS of whom Ciyata Coleman, Dick Eggleston, Amy Pitter, and Dean
Plueger warrant special mention. Finally, we thank Christine Cheng, Gladys Nichols, and Rolando Palacios for
assistance with the surveys.
Go to to visit the article page for additional materials and author
disclosure statement(s).
equivalent to 33 days of income.
These non-claimants sacrice other advantages,
such as those related to health, education, or consumption, that may be linked to
transfers (Hoynes, Miller, and Simon 2015; Dahl and Lochner 2012; Smeeding,
Phillips, and O’Connor 2000). The problem of low take-up, according to many
accounts, is even more severe for other social programs beyond the EITC such as
food stamps, Social Security, and health insurance.
For many policymakers, improving the take-up of means-tested social pro-
grams such as the EITC is an unequivocal objective. In speaking of the program
in 2007, the acting IRS Commissioner declared that the agency “… wants all eligi-
ble taxpayers to claim the EITC”
However, the rationale for such improvement is
often less obvious to economists due to the ambiguous link between higher take-up
and welfare. If existing barriers to claiming a credit—such as the time and effort
required to learn about, and then apply for, a benet—discourage applications from
those of low economic need, then such barriers may be efcient. On the other hand,
if these barriers reduce claiming by those with high need, then policies eliminating
such barriers may enhance welfare. Critical for assessing the welfare implications
of low take-up is a deeper understanding of why exactly those who are eligible for
benets fail to claim.
Economic models have traditionally recognized three types of costs that might
deter take-up: the transaction costs of applying for a benet, the costs involved
with learning about eligibility and application rules, and the stigma associated with
enrollment (Currie 2006). Recent work, however, has challenged whether individ-
uals sensibly compare the expected costs and benets of claiming due to cognitive,
motivational, or emotional limits to decision-making. In the context of benet pro-
grams, these limits imply that the failure to claim may be a consequence of low
program awareness (e.g., Chetty, Friedman, and Saez 2013; Chetty and Saez 2013;
Smeeding, Phillips, and O’Connor 2000), confusion regarding program rules or
incentives (e.g., Liebman and Zeckhauser 2004), procrastination (e.g., Madrian and
Shea 2001), inattention (e.g., Karlan et al. 2015), or psychological aversion to pro-
gram complexity or the small “hassles” often involved in claiming (e.g., Bertrand,
Mullainathan, and Shar 2006). As an example of how alleviating a minor pro-
cedural hassle can lead to a larger change in behavior than that predicted by eco-
nomic costs alone, one study documented a signicant increase in the take-up of an
inuenza vaccination when a prompt, asking individuals to note the date of their
intended clinical visit, was added to an informational mailer (Milkman et al. 2011).
If existing barriers to claiming deter take-up, particularly among those of high
economic need, because of “psychological frictions” associated with low program
awareness, confusion, or an aversion to program complexity or hassles, then encour-
aging take-up by reducing these barriers would likely improve social welfare. In
such a scenario, low take-up would reect a failure of policy to deliver benets
to those who most need them, rather than an optimal use of application ordeals to
screen recipients by need. To the extent that policymakers view raising take-up as a
Estimates of expected benet size and income for eligible non-claimants are based on author calculations from
results reported in Plueger (2009) for tax year (TY) 2005. For the day of work equivalence, we assume 250 work
days each year.
Statement retrieved in 2014 from,-IRS-Launch-Campaign-to-Help-Low-
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
policy objective, clarifying the causes of non-claiming may also provide insight into
the design of policies aimed at groups not highly responsive to traditional incentives.
Despite the importance of understanding why eligible individuals do not claim, in
her seminal review of the topic, Currie (2006) characterized incomplete take-up as a
continuing puzzle and advanced experiments as the means to solve it.
In this paper, we report ndings from a large policy eld experiment, in col-
laboration with the IRS, designed to investigate the causes of low take-up of the
EITC. Our eld study focused on a setting where the failure to claim is especially
puzzling given that conventional costs of claiming appear to be low and the benets,
for many, are substantial. Specically, we strategically modied the content and
appearance of IRS tax mailings and distributed these to the universe of 35,050 tax
lers from California who failed to claim their 2009 Tax Year EITC credit despite
presumed eligibility and the receipt of a rst reminder notice. Each mailing, consist-
ing of a reminder notice, claiming worksheet, and a return envelope, communicated
program eligibility and offered recipients an additional opportunity to claim.
We use the differential response to these mailings to draw inferences about the
relative importance of three explanations for non-claiming: the misconstrual of pro-
gram incentives and/or lack of credit awareness (“Confusion”), the informational
complexity of claiming, and program stigma. We dene the latter as including both
the “social” stigma conventionally discussed by economists, as well as the more
identity-driven “personal” stigma recognized by psychologists as potentially import-
ant even in the absence of needing to claim the credit in public. To our knowledge,
our study represents the rst eld experiment, conducted with a federal govern-
ment agency, to investigate the psychological and economic factors that inuence
program take-up. All told, we informed individuals of $26 million in unclaimed
government benets, of which about $4 million was ultimately claimed due to
the mailings.
Two features of our setting make it appealing for study. First, because it is a
domain where we can precisely target a population of known statutory eligibility, we
need not worry that observed increases in enrollment are driven by ineligible appli-
cants. Second, our setting is one in which many of the traditional costs of take-up—
transaction costs of claiming, the costs of program learning, and social stigma—are
particularly low. Indeed, the mailing provides recipients with a short summary of
program and eligibility rules, and claiming a credit requires only that a recipient sign
and return a one-page worksheet in a provided stamped envelope. Moreover, social
stigma, as it is usually dened, is likely to be minimal. Given that a typical recip-
ient is owed a credit of over $500 and has an income of about $14,000, traditional
economic models would predict that recipients should claim unless such claiming
entails high unobserved costs (e.g., those involving time or stigma), or recipients
suffer from the decision-making frictions that our study was designed to test.
Overall, the experiment provides evidence that claiming is sensitive to the fre-
quency, salience, and simplicity with which information is provided. Merely receiv-
ing a second opportunity to claim, just months after the receipt of an initial notice
led 0.22 of the sample to take-up. Comparing across experimental interventions,
simplication, either through a visually more appealing notice, or a shorter work-
sheet in which select eligibility screens satised by all recipients are eliminated,
signicantly raised take-up from 0.14 (control mailing) to 0.23. Displaying the
generic range of potential benets in the headline of the simplied notice further
improved take-up from 0.23 to 0.31. Intriguingly, the inuence of benet infor-
mation was not monotonically related to the magnitude of the benet displayed in
the headline which, for some part of the sample, was randomized to show either
a medium ($3,043) or large ($5,657) amount. Attempts to lower program stigma
(social or otherwise), or to inform individuals about the low costs of claiming (i.e.,
time-costs of lling out the claiming worksheet, or penalties associated with errone-
ous claiming) did not impact take-up. Finally, an analysis of heterogeneity indicates
that simplication disproportionately helped low earners, among those with depen-
dents, and, females, among single lers, while language barriers may have reduced
take-up among Hispanic households.
To gain deeper insight into the mechanisms underlying response to the interven-
tions, we conducted a rst survey with approximately 3,000 low to moderate income
subjects online, many of whom were eligible for the EITC. Participants reviewed
one of the experimental interventions, after which we assessed beliefs about program
rules, incentives, and stigma. The survey suggests that interventions shaped behav-
ior by inuencing beliefs about eligibility and benet size, and increasing attention
paid to forms, but not by reducing perceptions of program stigma or the time and
penalty costs of claiming, which respondents judged to be fairly low. Together, the
ndings from the eld study and survey point to the conclusion that confusion, pro-
gram complexity, and lack of program awareness play a signicant role in the failure
to take-up, while stigma, and high perceived economic costs of claiming, do not.
The possibility that psychological frictions shape the take-up decision in this set-
ting has implications for welfare and policy. First, so long as the presence of such
frictions is not negatively correlated with economic need, low take-up likely reects
a failure to deliver benets to those who value the benets most highly. While we
cannot directly observe economic need, this interpretation is supported by the fact
that the poorest among our sample, a fairly poor group to begin with, were most
harmed by the complexity of program mailings. Second, the experimental ndings
suggest that inexpensive marketing interventions offer a scalable, and potentially
more effective, strategy for improving take-up among groups of policy interest than
traditional program incentives. Indeed, in our, admittedly unrepresentative, sam-
ple, we nd a low elasticity of response with respect to benet size. How might
our interventions practically impact overall program take-up? We estimate that the
most effective experimental treatments, if applied to the entire population of tax l-
ing non-claimants—approximately 35 percent of all non-claimants overall (Plueger
2009)—could reduce incomplete take-up from 10 percent to 7 percent, among tax
lers, and from 25 percent to 22 percent, overall. This would result in an estimated
increase in annual disbursements of $503 million.
While the welfare of the approximately 1.3 million non-claimants who le taxes
is of independent policy interest, our experimental sample differs from the broader
population of EITC non-claimants across a range of dimensions. Most notably, the
recipients of our mailings had two prior opportunities to claim their credit (e.g., at
the point of ling, and when they received a rst mailed reminder), and, as such,
might have especially high unobserved costs of claiming. In comparison to the typ-
ical claimant, our sample is owed a smaller average benet, is less likely to have a
qualied dependent, and is less likely to have used a tax preparer (Plueger 2009). To
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
explore the generalizability of our ndings, we report results from a second survey
of several hundred low-income subjects from tax preparation clinics who, on several
dimensions, more closely resembled the typical EITC eligible individual. The sur-
vey assessed program awareness as well as perceptions of program rules, incentives,
claiming costs, and stigma.
Jointly, the two surveys we administered, while each subject to its own limits,
suggests that a broad population of low-income individuals, including eligible
claimants and non-claimants, exhibit low program awareness, and a propensity to
underestimate eligibility and benet size. Respondents do not perceive the EITC
to be highly stigmatizing, nor do they perceive the claiming worksheets to be very
time-consuming to complete. We interpret the survey evidence as consistent with
the possibility that the ndings from the experiment extend to eligible non-claimants
beyond the experimental sample. Intriguingly, asking survey respondents directly
why eligible individuals might not claim a credit, identied several of the same
mechanisms implicated in our study—misperceptions of eligibility and confusion
about program rules.
Beyond the signicance of these results for policy, our ndings have implications
for the literature on benet take-up (see Currie 2006 for a review).
The outsized
inuence of small and largely noninformational changes to program mailings is
difcult to explain with economic models in which individuals are assumed to sen-
sibly weigh accurately perceived costs and benets of claiming. The evidence from
this study is instead more consistent with alternative models which not only per-
mit biased beliefs about eligibility and program incentives, but reect even sharper
departures from the standard framework. Such models predict that individuals might
avoid or postpone the take-up decision altogether due to psychologically aversive
“hassle costs” (Bertrand, Mullainathan, and Shar 2006), limits to self-control (e.g.,
O’Donoghue and Rabin 1999) or other cognitive resources (e.g., Mullainathan and
Shar 2013), or because of heuristic-choice strategies of the sort that have been
suggested as explaining inefcient health-plan decisions (Ericson and Starc 2012;
Bhargava, Loewenstein, and Sydnor 2015).
Our paper additionally builds upon and augments several other literatures includ-
ing that which investigates how information (e.g., Chetty and Saez 2013; Liebman
and Luttmer 2015; Karlan et al. 2015), as well as its salience (e.g., Chetty, Looney,
and Kroft 2009; Finkelstein 2009) and complexity (Hastings and Weinstein 2008;
Bettinger et al. 2012; Kling et al. 2012; Bhargava, Loewenstein, and Sydnor 2015)
affects economic decisions.
We nd that the very basic, and consequential, decision
of claiming an owed benet is highly sensitive to the manner, and frequency, with
which program information is presented. Methodologically, the closest analogue to
our eld experiment is a study in which direct mail varying the economic terms and
This literature has traditionally stressed the detrimental role of social stigma (e.g., Moftt 1983), concrete
transaction costs (e.g., Currie and Grogger 2001), and the lack of information (e.g., Daponte, Sanders, and Taylor
1999). More recent research implicates the role of nonmonetary factors on social and private benet take-up, such
as the transparency of information (e.g., Saez 2009; Jones 2010), costs of inconvenience (Ebenstein and Stange
2010), as well as the actions of one’s peers (e.g., Duo and Saez 2003).
Studies in the latter category have shown that the transparency and clarity of information may affect paren-
tal school choice (Hastings and Weinstein 2008), applications for college nancial aid and college enrollment
(Bettinger et al. 2012), health care choices (Kling et al. 2012; Bhargava, Loewenstein, and Sydnor 2015), and sav-
ings/investment decisions (e.g., Beshears et al. 2013; Madrian and Shea 2001; Choi, Laibson, and Madrian 2009).
the informational presentation of loan offers were randomized by a South African
lender (Bertrand et al. 2010).
I. Background on EITC and Take-Up
A. Program Structure and Summary
The EITC, (or the “earned income credit,” or EIC), was conceived in 1975 as a
small offset to payroll taxes and as “an added bonus or incentive for low-income
people to work.
As a result of ve subsequent expansions, notably in 1986, and
then again in the 1990s, by TY 2009 the EITC distributed $58 billion in refundable
credits to nearly 27 million working people of low to moderate income.
The program can be characterized by a small number of parameters—a nega-
tive phase-in tax rate, a plateau tax rate, the income at which the tax supplement is
phased-out, and the positive, phase-out tax rate—specic to one’s number of qual-
ied dependents and ling status. Credit eligibility requires a valid Social Security
number, earned income below a specied threshold, minimal investment income,
and a failure to have been excluded from the program due to past negligence. Having
met these criteria, benet size is determined by one’s income and family structure.
While a credit of up to $457 is available to earners with no dependents, those with
qualied dependents—based on a complicated set of relationship, age, and resi-
dency tests—command larger credits of up to $5,667 (gures reect TY 2009 unless
otherwise stated). The credit begins to diminish at an income of $21,500 (for a
family with 3 children), and is fully exhausted for earned incomes above $48,321
(see online Appendix Figure A1 for benet schedules). Individuals in 21 states, as
of 2011, could have accrued additional local credits from 3.5 percent to 43 percent
of the federal credit.
Critically for the present study, the EITC, unlike other anti-poverty programs,
is administered through the tax system. Those with no qualied dependents must
le a 1040(A/EZ) and indicate their benet amount or simply write “EIC” when
prompted. In the case of qualied dependents, eligible individuals must le a 1040(A)
along with a supplementary, one-page, tax addendum called the Schedule EIC.
rst two columns of Table 1 describe the average benet and demographic charac-
teristics of EITC recipients. In TY 2009, the typical recipient received $2,185 from
the EITC (13 percent of adjusted gross income, and amounting to $2,770 for those
with qualied dependents and $259 for those without). This compares to a typical
estimated benet of $1,096 (12 percent of adjusted gross income) for non-claimants
(calculated from Plueger 2009). Of claimants, 77 percent had at least one quali-
ed child, and only 34 percent of claimants prepared their own taxes. While less is
known of non-claimants, estimates suggest that 63 percent had at least one qualied
dependent and 56 percent of single lers were female (Plueger 2009).
Quotation cited from a 1975 Senate Committee Report.
Claimants must le a tax return even if they fall below the ling requirement income threshold.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
T 1—EITC S S  TY 2009
EITC claimants CP notice recipients Experimental sample
Variable name mean mean mean mean Mean Median SD
Panel A. Overall
Number 26,742,267 2,975,197 608,233 76,759 35,050
Response 0.41 0.22 —
Share paid 0.99 0.99 0.44 0.39 0.21
EITC benet (if > $0)$2,185 $2,165 $412 $415 $511 $288 $838
Benet w/o qualied dependents $2,770 $1,870 $1,528 $1,535
Benet w/ qualied dependents $259 $256 $262 $148
Total EITC paid $58.1b $6.4b $111m $13.0m $4.0m
Panel B. Descriptive and tax variables (all sample)
Descriptive variables
Age 43 22 13
Gender—male (primary ler)0.49 0.54 0.69 0.67 0.71
Gender—male if single FS 0.65
Filing status = single 0.26 0.30 0.62 0.60 0.58
Filing status = married ling
0.26 0.30 0.26 0.25 0.27
Filing status = head of
0.47 0.41 0.12 0.14 0.15
Share with qualied
0.77 0.76 0.24 0.33 —
Tax variables
Earned income $14,402 $9,568 $13,532
Adjusted gross income $17,002 $16,964 $10,448 $10,368 $15,852 $10,538 $14,044
Total taxes $368 $463 $312 $347 $352 $0 $842
Total taxes (if > 0)$810 $383 $1,124
Tax refund $4,080 $3,874 $1,338 $1,342 $1,246 $604 $3,182
Tax refund (if > 0)$1,471 $802 $3,409
Share—self-preparation 0.34 0.27 0.70 0.65 0.62
Share—self-employ inc. > 0 0.18 —
Past claim—TY 2008 0.16
Past claim—TY 2006 to 2008 0.29
Panel C. Descriptive and tax variables (claimants only)
Descriptive variables
Number 26,567,446 2,959,339 270,642 31,012 7,423
Gender—male (primary ler)0.49 0.54 0.64 0.61 0.65
Filing status = single 0.26 0.30 0.68 0.72 0.70
Filing status = married ling
0.26 0.30 0.25 0.20 0.20
Filing status = head of
0.47 0.41 0.07 0.08 0.09
Share with qualied
0.77 0.76 0.14 0.14 0.21
Tax variables
Share—self-preparation 0.34 0.27 0.78 0.77 0.76
Adjusted gross income $17,002 $16,964 $9,793 $9,083 $12,352 $9,179 $11,442
Total taxes $368 $463 $248 $252 $285 $0 $784
Tax refund $4,080 $3,874 $1,061 $974 $955 $504 $1,602
Notes: This table provides summary statistics for various subsets of EITC eligible based on data from the IRS
Central Data Warehouse. The data is extracted through end of 2010 except for the experimental data which is
through May 2011. The sets of columns report data for US EITC recipients, CA EITC recipients, US CP recipients,
CA CP recipients, and the experimental sample, respectively. Statistics from the rst four columns exclude response
from the experimental sample. Panel A reports overview statistics, panel B reports descriptive and tax variables for
the full sample, and panel C reports descriptive and tax variables for those who claim an EITC benet across each
sample. Some of the gures are estimated from author calculations.
B. Take-Up in the EITC
Despite considerable interest in the question, accurately measuring take-up of the
EITC (i.e., eligible claimants/eligible individuals) is difcult. The difculty stems
from the unknown rate of ineligible claiming, the presence of unobservable factors
that determine eligibility, such as qualied dependent status, and because one can-
not simply assume that eligible non-claimants and claimants, even conditioned on
observable characteristics, are otherwise similar (Berube 2006).
An analysis by the IRS based on data for TY 2005, which informs assumptions
used in this study, suggests an overall program take-up rate of 75 percent (with
a condence interval of 73 percent to 77 percent), including 56 percent for those
without qualied dependents and 81 percent for those with at least one such depen-
dent (Plueger 2009).
After accounting for changes in program eligibility over time,
namely the expansion of the credit to those without eligible dependents, Plueger’s
estimate is similar to that of Scholz (1994), whose take-up estimate of 80 percent
to 86 percent (TY 1990), is commonly cited by academics (1994).
Plueger esti-
mates that of the 25 percent who do not take-up, 16 percent do not le taxes while
9 percent le taxes but fail to claim a benet on their return, implying an overall rate
of take-up among eligible tax lers of 90 percent. Take-up appears to further vary
across demographic and tax characteristics with generally lower take-up for men,
and those with low income and education (e.g., Blumenthal, Erard, and Ho 2005).
The participation rate in the EITC compares favorably with other major transfer pro-
grams which has been estimated at 42 percent in Temporary Assistance for Needy
Families (TANF), 55 percent in the Supplemental Nutrition Assistance Program
(SNAP), and 46 percent in Supplemental Security Income (SSI).
The IRS mails reminder notices and claiming worksheets—the “CP09” is sent
to those with dependents, and the “CP27” is sent to those without—to anyone who
les a tax return and neglects to claim their EITC credit despite appearing eligible
based on administrative screens such as ling status, age, earned income, investment
income, and foreign income.
However, Plueger (2009) points out that the lters
may also screen out some fraction of eligible ling non-claimants.
CP reminder
notices consist of a one page (double-sided) letter summarizing the program, detail-
ing eligibility requirements and directing the reader to an attached worksheet. The
Plueger’s estimate is based on an exact match of tax records and census data. Specically he estimates eligible
claimants from the Survey of Income and Program Participation (SIPP), and IRS studies of EITC compliance, and
estimates the number of total eligible from the American Community Survey, SIPP, and the CPS Annual Social and
Economic Supplement.
As Plueger (2009) notes, the Scholz (1994) analysis was both for a period in which apparently eligible, ling
non-claimants were automatically mailed a benet by the IRS, and in which there was no credit for those without a
qualied dependent (a group with presumably lower take-up).
These gures are estimated for 2004 and are included in a 2007 Health and Human Services report to
Congress available at
“CP” refers to “Computer Paragraph” and denotes the varied missives that the IRS routinely sends to taxpay-
ers after a tax ling.
See Plueger (2009) for a discussion of the divide between eligible ling non-claimants and those receiving the
CP notication, and specically Table 10 of Plueger (2009) for an accounting of nationwide ling non-claimants for
TY 2005. In brief, some ling non-claimants do not receive a CP reminder notice due to a variety of factors includ-
ing the exclusion of various ling groups (e.g., taxpayers who le electronically but print and mail their returns, or
returns submitted after April 15th may not generate a notice), and a policy designed to avoid missives to anyone
with ambiguous eligibility (e.g., taxpayers with dependent children older than 18 whose school enrollment status
cannot be veried). We obtained further details of this accounting from interviews with D. Plueger (August 2011).
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
one-page (single or double-sided, depending on the inferred presence of qualied
children) worksheet conrms eligibility into the program with a series of screening
statements. Those who sign and return the worksheet, if approved, receive a benet
check within three months. The response to the CP mailings has ranged from 41 per-
cent to 52 percent nationally for TYs 2006 to 2009.
The experimental sample,
discussed below, comprises those who failed to respond to a rst CP mailing.
Table 1 suggests that the experimental sample, in comparison with EITC claimants
more generally, were characterized by a lower average EITC benet ($511 versus
$2,185). This difference was due to a lower average benet for those with depen-
dents ($1,870 versus $2,770) and a lower share of such claimants (33 percent versus
77 percent), but not by a signicant difference in benet for those without depen-
dents ($256 versus $259). Experimental subjects also had a lower average adjusted
gross income ($15,852 versus $17,002), and were more likely to have self-prepared
their returns (62 percent versus 34 percent) than claimants overall. Figure 1 plots the
distribution of expected benets for EITC claimants and non-claimants, estimated
from Plueger (2009), as well as for the experimental sample.
Author calculations from internal statistics from the IRS.
0.3 0.31
0.15 0.12
0.05 0.04
0.04 0.04
1. 0
Percent share
to $999
to $1,999
to $2,999
to $3,999 >$4,000
F 1. B D  EITC C  E N-C
Notes: This gure compares the distribution of EITC benets for claimants, eligible non-claimants, and the exper-
imental sample. Data for the former two groups is for TY 2005 and is estimated from Plueger (2009), while the
experimental data is for TY 2009.
II. Research Design
A. Experimental Sample
The sample for the eld experiment consists of individuals from California who
satisfy the following conditions.
First, the taxpayer led a tax return for TY 2009
but failed to claim an EITC credit. Second, the taxpayer satised a set of eligibility
screens, enumerated above, that resulted in the receipt of a CP09 or CP27, and
nally, the taxpayer neglected to respond to this CP notice. Figure 2 depicts the set
of screens that led to the experimental sample (panel A), while Table 2 describes
The choice of California as a setting for the study was dictated to us by the IRS.
Panel A. Screening timeline for experimental sample
Panel B. Organization of experimental treatments by mailing component
F 2. S S  P O  E T
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
the step-wise exclusions that generated the sample from the approximately 3.0 mil-
lion individuals eligible for the EITC in California for TY 2009 (gures in bold
are exact). Of those eligible, an estimated 263,000 led taxes but did not claim the
EITC, and 76,440 received a reminder notice indicating a possible unclaimed ben-
et of which 45,099 taxpayers failed to respond. A further 7,096 individuals were
excluded by the IRS, in part, because of an incorrect mailing address, and 2,953 were
excluded due to an inaccurate inference regarding the number of dependents during
the randomization stage.
The experimental sample featured the 35,050 remaining
individuals: 23,618 with no dependents, and 11,432 with at least one dependent.
B. Experimental Conditions
Structure of Mailings.—Subjects in the experiment were either sent a control or
one of several treatment mailings. Mailings consisted of three physical components:
a one page, two-sided notice; a one-page, two-sided eligibility worksheet, and an
envelope in which the notice and worksheet were contained.
The notice informed
the recipient of possible program eligibility, briey explained the purpose of the
During the randomization when interventions were assigned to each anonymized taxpayer, our inference of
dependents relied on the presence of a child Social Security number. We later obtained explicit data on number
of dependents and learned that our earlier inference was a noisy one. Of the 2,953 mischaracterizations, 2,324
are dependent-free individuals who received dependent worksheets, and 629 are individuals with dependents who
received a dependent free worksheet. We ignore these individuals in the remaining analysis.
Each mailing also included an addressed, stamped envelope so that the recipient could return the worksheet.
This did not vary across any of the mailings.
T 2—S-B-S A  G E S
Incremental steps
number Notes and assumptions
Start: Total CA EITC Eligible 1.00 3m 3.0m led; 26% noncompliance
(TIGTA 2011, TY 2009); 25% incom-
plete take-up (Plueger 2009, TY 2005)
1. Program participants 0.75 0.75 0.25 750,000
2. Non-ling non-claimaints 0.65 0.16 0.09 262,500 65% of non-claimaints did not le
taxes (Plueger 2009, TY 2005)
3. Did not receive CP 09/27 0.75 0.06 0.03 76,440 ~75% may not have received CP
(Plueger 2009) [76,440 is exact gure
as reported by IRS]
4. Respond to CP 09/27 0.41 0.01 0.015 45,099
6. Mistagged & exclusions 0.22 0.003 0.012 35,050 Exclude 2,953 due to mistagging of
dependents, and 7,096 due to incorrect
End: experimental sample 35,050
Notes: This table traces the generation of the experimental sample from an estimate of all EITC eligibles in California
for TY 2009. Bolded gures indicate exact gures. Remaining gures are estimated or inferred. Noncompliance
estimate assumes that all overclaiming is on the extensive margin (i.e., is by ineligible individuals).
Sources: The source for the noncompliance estimate (TIGTA 2011) is the report titled Treasury Inspector General
for Tax Administration, Ref. No. 2011-40-023. Filing and CP statistics are either from the IRS website or from inter-
nal IRS documents.
program, directed recipients to verify eligibility via the accompanying worksheet,
and offered instructions for additional assistance. The eligibility worksheet featured
a series of eligibility screening statements (e.g., “My Social Security card reads ‘Not
Valid for Employment’ ). For those with children, the worksheet additionally
asked recipients to report each child’s name and Social Security number. Eligible
recipients were asked to sign, date, and return the last page of the worksheet. Finally,
the notice and worksheet were enclosed in a standard number-10 sized envelope
(4.125 inches × 9.5 inches). Figure 2 summarizes the treatment conditions by phys-
ical component (panel B). Table 3 organizes the interventions by tested mecha-
nisms. Selected examples of notices, worksheets, and the envelope are depicted in
the Appendix.
Control Condition (Simplicity Interventions).—We created the control mailing
by simplifying the initial CP 09/27 notice and worksheet that subjects received just
months earlier. While the initial notice was a textually dense, two-sided document
that emphasized eligibility requirements repeated later in the worksheet, the new
notice was single-sided, featured a larger and more readable font (Frutiger), a prom-
inent headline, and did not repeat eligibility information (“simple notice,” Appendix
Figure, panel A1). Similarly, we redesigned the worksheet from the original CP
notice by eliminating repetition, changing the font, and using a cleaner layout. The
T 3—E I  M
Mechanism Intervention Description Sample
Complexity (design)1. Complex notice Relative to simple notice, complex notice
is two pages, features denser textual layout,
and repeats eligibility information included
in the worksheet
Complexity (length)2. Complex worksheet Relative to simple worksheet, complex
worksheet includes additional,
nondiscriminatory, questions regarding
Program information
Benet and cost
1. Benet display (low
and high)
Simple notice reports upper bound of
potential benet (up to “$457,” “$3,043,
“$5,057,” or “$5,567”)
2. Transaction cost (low
and high)
Simple notice provides guidance as to
worksheet completion time (less than 10 or
60 minutes)
1. Indemnication
Bold message on worksheet indemnies
against penalty for unintentional error
General program
1. Envelope message Envelope message indicates that enclosure
communicates “good news”
2. Informational yer One page yer offers program information
and trapezoidal benet schedule
Personal stigma
1. Emphasis on earned
Simple notice emphasizes that credit is
earned reward for hard work
Social stigma reduction 2. Social inuence Simple notice communicates that similarly
situated peers are also claiming
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
resulting single page worksheet (two-sided for those with dependents) carries a sim-
ilar design aesthetic to the simplied notice (“simple worksheet,” Appendix Figure,
panel B1).
Complexity Interventions.—An initial set of interventions tests whether infor-
mational complexity affects take-up. We manipulated complexity via two interven-
tions. Our rst intervention, the “complex notice,” was the original CP 09/27 notice
that subjects received earlier but with minor changes to standardize information
across conditions (Appendix Figure, panel A2). We expected that the difference in
response between the control notice (i.e., simple notice) and the complex notice
would indicate the role of design and text simplicity in shaping response.
Second, we test whether a modest increase in perceived worksheet complexity—
through an additional set of eligibility statements—would lower take-up (“complex
worksheet,” Appendix Figure, panel B2). Critically, the additional questions pertained
to EITC eligibility criteria which, by our observation of tax records, our recipients
had satised. Specically, in Step 1 of the worksheet, we presented additional screens
for earned income, foreign earned income, investment income, citizenship, and ling
status. For those with no dependents, the complex worksheet featured a new section
that elicited more detailed information on earned income for the recent tax year. We
expected that the difference in response between the control (i.e., simplied) notice and
the complex notice would indicate the role of worksheet length in shaping response.
Information Interventions.—A second set of interventions was designed to test
whether information regarding program existence, eligibility, and the costs and ben-
ets of claiming inuenced take-up. First, we investigate the inuence of benet
information by prominently reporting the upper bound of one’s potential benet (we
did not receive permission to print the exact gure) in the headline of the simplied
control notice (“benet display”). Subjects in this treatment arm received a notice
indicating eligibility for a benet “… of up to $457” in the case of no dependents
and “… of up to $5,657” in the case of three or more dependents. In order to gen-
erate variation in the magnitude of perceived benets, for subjects in this treatment
with either one or two dependents, we additionally randomized the amount reported
to either reect the maximum dependent specic benet (i.e., $3,043 for one depen-
dent, and $5,028 for two dependents) or for the program as a whole (i.e., $5,657)
(Appendix Figure, panels C1 and C2).
Second, we explore how perceptions of transaction costs affected response by
offering varying guidance as to the time required to complete and return the eligibil-
ity worksheet (“transaction cost display”). That is, we communicated in the notice
headline that worksheet completion required “… less than 60[10] minutes” where
the specic magnitude, (i.e., 60 or 10), was again randomized among those assigned
to this treatment (Appendix Figure, panel D1). Third, we test the importance of per-
ceived penalty costs (e.g., those relating to a possible audit) by assuring recipients,
with bold lettering displayed above one-half of worksheet headlines, that mistak-
enly reporting incorrect information would not result in a penalty (“indemnication
The simplied notice is adapted from a layout originally designed by a third party rm retained by the IRS
and pretested for “readability” in a test lab.
message”): “Complete to the best of your ability—you will NOT be penalized for
unintentional errors.(Appendix Figure, panel D2).
Fourth, to test the inuence of general program information on response, in one
condition, we attached a one-page yer, adapted from that used by Chetty and Saez
(2013), to baseline notices. The “informational yer” displayed benet information
and marginal incentives through an annotated graphical display (customized by esti-
mated number of dependents; gures are for single, as opposed to married, lers).
We believe that this is the rst instance in which the trapezoidal benet schedule has
been depicted on IRS documentation. The yer also contained a section enumerat-
ing program “myths and realities” intended to clarify potentially confusing aspects
of eligibility requirements (e.g., “I need to have a bank account to receive EIC ben-
ets”) (Appendix Figure, panel E1).
Finally, to assess whether inattention to the mailed information meaningfully con-
tributed to nonresponse, we displayed a prominent envelope message for the treat-
ment group, relative to an unmarked envelope control, indicating that the enclosed
contents may benet the recipient: “Important—Good News for You” (“envelope
message,” Appendix Figure, panel E2). By IRS request, the treatment envelopes
also included a parenthetical Spanish translation of the message.
Stigma Interventions.—A nal set of interventions tests whether program stigma
inuences response. While early economic models of take-up featured the costs
of social stigma (Moftt 1983), psychologists and recent economic research has
made the distinction between social stigma, and the related construct of personal
(or identity-driven) stigma (e.g., Crocker, Major, and Steele 1998; Manchester and
Mumford 2010). The latter occurs when an individual internalizes existing negative
beliefs or stereotypes that others hold toward the stigmatized target. We test the sen-
sitivity of response to personal stigma by modifying the notice headline to empha-
size that the benet was an earned consequence of hard work rather than a welfare
transfer: “You may have earned a refund due to your many hours of employment.
A second headline tests for the role of social stigma by invoking a, stigma-reducing,
descriptive social norm: “Usually, four out of every ve people claim their refund”
(e.g., Cialdini 1989; Cialdini and Goldstein 2004).
C. Experimental Randomization
We assigned subjects to a notice (including a condition with the control notice
plus the informational yer), worksheet, and envelope with three independent ran-
domized assignments. Conditioned on assignment to a notice displaying benets
(with at least 1 dependent), stigma, or claiming cost, we subsequently randomized
recipients into one of the sub-treatment variations. All randomizations were con-
ducted within blocks dened by zip code and the presence of eligible dependents
yielding a total of 3,483 blocks. In this way, our blocking design was intended to
Due to IRS rules governing messaging outside the envelope, we had little latitude in choosing the precise ver-
biage. We attempt to disentangle the effects of including Spanish language from the envelope messaging indirectly
by examining differential responses for subpopulations in the sample that vary in the inferred presence of Spanish
speaking households.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
minimize experimental variance and produce more efcient estimates than a simple
randomization. Treatments were randomized with equal sample weights with three
exceptions: The control notice was over-sampled 4) to heighten the statistical
power for pair-wise comparisons; the benet display notices were over-sampled
3) to power tests of differentiation across listed benet amounts; nally, at the
behest of the IRS, the lengthier complex worksheet was limited to 25 percent of
the sample (Table 3 reports sample sizes by intervention). Balancing tests, imple-
mented through a series of regressions, ensure that the treatment samples were sim-
ilar across key observables such as earned income, adjusted gross income, benet
size, ling status, and past EITC claiming behavior (online Appendix Table A3).
D. Survey Instruments
We supplement the eld experiment with two large-scale surveys of low to mod-
erate income samples. A rst survey was designed to offer a detailed psychomet-
ric assessment of how exposure to one of the experimental notices or worksheets
altered beliefs regarding the costs—associated with application, stigma, and poten-
tial audits—and benets of claiming. The approximately 10 minute survey was
administered to 2,800 subjects online through Amazon Mechanical Turk in the sum-
mer of 2011. Subjects in the sample were diverse across gender (62 percent female,
38 percent male), age (median age 27, standard deviation: 11), education (48 per-
cent college, 98 percent high school), earned income (median: ~$24,000, standard
deviation: ~$30,000), employment status (employed: 60 percent, unemployed at
time of survey: 18 percent, student: 17 percent, other: 5 percent), and inferred EITC
eligibility (~38 percent eligible).
A rst segment of the survey elicited basic income and demographic detail which
permitted inference of EITC eligibility and estimate benet size. A second segment
of the survey presented respondents with one of the experimental notices and/or
worksheets after which respondents were asked about their understanding of pro-
gram rules, beliefs regarding eligibility, and perceptions of benet size and a range
of claiming costs. Each version of the survey, to which respondents were randomly
assigned, featured a distinct experimental mailing (not all conditions were tested
due to sample constraints), so that we could attribute differences in program per-
ceptions and beliefs to differences in the content of the interventions. Specically,
respondents were asked to indicate perceptions of program complexity (1 to 100
scale), the carefulness with which they read the information (1 to 100 scale), intent
to complete and return the form (yes/no), willingness to pay a preparer to assist in
completing the forms (in dollars), and respect for those who decided to claim the
credit (1 to 100 scale), and were tested on their comprehension of program infor-
mation. The survey was distinguished by a near absence of item nonresponse due
to built-in forced response mechanisms. A second, paper survey, was administered
We implement the balancing tests with individual-level regressions of the following form:
Outcom e
nwe = α + φ n + γ w + θ e + ε nwe . Here, n indexes the notice, w indexes the worksheet, and e indexes the
envelope. Indicator variables mark assignment into each of the three components of the mailings and the excluded
category consists of the simple notice, simple worksheet, and plain envelope. The dependent variables relate to
income, expected benet levels, ling status, and past claiming. Overall, the analysis reported in the table suggests
that the treatments were successfully randomized (online Appendix Table A3).
in-person to 1139 clients at several low-income tax clinics primarily in Chicago
from February to April 2011.
The survey, which appeared to take about 15 to 25
minutes to complete during an “intake” period when clients waited for a tax pre-
parer, was designed to measure baseline levels of program awareness and literacy
in a population beyond the experimental sample. Subjects again reected a diverse
range of gender (56 percent female, 44 percent male), age (median: 44 years,
standard deviation: 16), earned income (median: ~$13,000, standard deviation:
~$11,000), and education (30 percent college, 90 percent high school). Of the sam-
ple, 65 percent of subjects were deemed eligible for the EITC of which 60 percent
were female, 41 percent had qualied dependents, and median income was approx-
imately $9,000. Credit eligible respondents resembled overall EITC claimants more
closely than the experimental sample in gender and the presence of dependents,
and, of course, nearly all used a tax preparer. Like the rst survey, the second survey
elicited income and demographic detail, and also gauged program awareness, beliefs
of eligibility and benet size, and perceptions of the various costs of claiming.
III. Results
A. Overall Response
Table 4 reports a rst key result of the eld experiment: the magnitude of the
overall response to a mailed notication. The overall response to the mailing is 0.22
with an average disbursed benet of $511 (0.25 response and $247 for those without
dependents, and 0.16 response and $1,531 for those with). Relative to the response
to the initial CP notice of 0.41, the experimental treatments augmented response by
32 percent (i.e., [0.22 × (1 0.41)]/0.41). The additional response is not associated
The survey was administered to low-income tax lers at ve Chicago tax centers, as well as one in San
Francisco, organized by local organizations (the Chicago sites were managed by the Center for Economic Progress
and Ladder-Up) to assist in tax preparation.
T 4—S  R  E M
All sample No dependents With dependents
size Deny Response
size Response
CP Notice (CA TY 2009)0.41 $570 0.02
Overall response 0.22 $511 0.01 0.25 $247 0.16 $1,531
Simple notice + simple worksheet
0.23 $514 0.01 0.27 $246 0.16 $1,616
Complex notice + complex worksheet 0.14 $546 0.01 0.17 $294 0.10 $1,570
Information notice + simple worksheet 0.28 $531 0.01 0.31 $242 0.21 $1,643
Stigma notice + simple worksheet 0.22 $452 0.01 0.25 $255 0.14 $1,330
Predicted language neutral response 0.25 $530 0.01 0.26 $245 0.21 $1,638
Notes: This table summarizes the response rate, non-zero benet size, and denial rate for the CA CP sample and
experimental samples of interest. To ensure a sufcient sample, gures in the table represent an average across the
envelope as well as the indemnity treatments. The adjustment for the Spanish speaking population is estimated with
a response model using zip code level data on the density of the Hispanic population and is further described in the
text. Dependent specic response data is not available for the CP Notice.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
with a signicant increase in denied claims.
The estimated benet size for nonre-
spondents was $788, including $247 for those without dependents, and $1,787 for
those with, suggesting that response was not driven by the magnitude of anticipated
benets. Figure 3, which plots the IRS processing date for returned worksheets—
including response to the initial CP mailings as well as the experimental notices—
indicating that the patterns summarized by Table 4 are almost certainly due to receipt
of the experimental notices rather than delayed response to older notices.
Beyond overall response, the table compares the 0.23 response rate associated
with the control condition—that is the mailing with the simple notice and work-
sheet—with the average response to mailings in each of the three treatment categories
(aggregating across the plain and messaged envelopes, and worksheets with and
without indemnication messages). The comparison suggests a large net positive
effect of simplication on response (from 0.14 to 0.23), as well as of information
(from 0.23 to 0.28), but not of the attempts to reduce stigma (from 0.23 to 0.22).
These treatment effects are roughly similar for those with and without dependents.
How is it that the mere receipt of a second notice, just months after the receipt of a
rst notice, could prompt such substantive additional response? While some of the
A mailed claim is rarely denied, likely because the sample was prescreened for statutory eligibility. Such a
denial might arise if the notice recipient led an amended return which altered eligibility after the CP notication
had been triggered, or if a qualied dependent was claimed by another party and such a claim altered the recipient’s
According to interviews with the IRS, there was a period in early January, 5 to 8 weeks after we mailed the
interventions, when the IRS did not process EITC claims.
Pre-experimental period
Experimental notices mailed
(mid November 2010)
Number of responses
Experimental period
Number of week relative to experiment launch
20 15 10 50 0 5 10 15
F 3. EITC C P B  A M  E N
(California CP notice recipients)
Notes: This gure depicts the number of TY 2009 EITC claiming worksheets, from California, processed by the
IRS, each week from July 2010 to March 2011.
Source: Data was provided to the authors from the IRS.
additional response appears due to the modications reected in specic interven-
tions, the complex mailing (notice and worksheet), arguably the closest analogue to
the initial mailing received by recipients, still resulted in a response of 0.14.
explanation as to why second exposure to the same information raised take-up is that
the experimental mailings helped to combat low program awareness, inattention, or
forgetfulness among recipients. Consistent with this explanation, in a subsequent
section, we discuss survey evidence indicating low program awareness among those
eligible for the EITC. Another alternative is that the receipt of the second notice
may have caused recipients to adjust inferences regarding eligibility or some other
program parameter. Finally, a small share of the response may be attributable to lost
or unopened mail that is, at least partially, stochastic in nature.
B. Response to Experimental Treatments
We summarize the effects of the individual interventions on response, as well as
denied claims, in Table 5. The rst column depicts treatment effects from a linear
probability model estimated as follows:
Pr( Respons e i = 1) = α +
θ j Notic e i j +
k Workshee t i k + ℓEn v i + πDe p i + e i ,
where indicator variables denoting experimental notice j ( Notic e i j ), worksheet
k ( Workshee t i k ), and the presence of a messaged envelope ( En v i ), predict an individ-
ual, i ’s, binary response, Respons e i . To permit clear pair-wise comparisons, effects
are estimated relative to the excluded control condition (i.e., simple notice, simple
worksheet, and the plain envelope). A dummy variable, De p i , controls for the pres-
ence of dependents. We report the change in response relative to the control mailing
in brackets.
The second column estimates the same model but with a rich set of income, bene-
t, tax, and demographic control variables. The insensitivity of the point estimates to
the inclusion of these additional controls speaks to the success of the randomization.
We exclude controls, apart from the variable indicating the presence of dependents,
in the subsequent analyses. Columns 3 and 4 report the estimated model, without
the dummy variable, for the sample with and without dependents while the follow-
ing column reports p-values testing for coefcient equality across the two groups
(estimated from a separate set of pooled regressions with an interaction term). The
nal two columns provide evidence that any disproportionate increase in denied
claims, due to the interventions, are too modest to account for the overall pattern of
response. Figure 4 summarizes treatment effects graphically, with condence inter-
vals, as calculated from column 1. While the comparisons summarized in the table
were all preplanned, we note that the ve strongly signicant interventions reported
in the rst column survive a Bonferroni correction for multiple comparisons at a
family-wise alpha of 0.05.
Importantly, none of the interventions in our study precisely duplicated the initial mailing received by recip-
ients. The complex notice was a near duplicate of the initial notice, and the complex worksheet featured more
screening questions than the initial worksheet but had a simpler design.
We were unable to obtain information on the rate of returned mail for either the initial notice or the experi-
mental mailings.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
T 5—R  D  E I
Dependent variable: (LPM)
Response (yes/no)Denial (yes/no)
sample Controls
dependents p-value
sample Controls
(1) (2) (3) (4) (5) (6) (7)
[Simple notice, simple worksheet, plain envelope: excluded]
Complex notice 0.061*** 0.060*** 0.062*** 0.060*** p = 0.90 0.0014 0.0014
(0.007) (0.007) (0.009) (0.010) (0.002) (0.002)
[−27%] [−26%] [−23%] [−38%]
Complex worksheet 0.040*** 0.040*** 0.054*** 0.012 p < 0.01 0.0011 0.0012
(0.005) (0.005) (0.006) (0.008) (0.001) (0.001)
[−17%] [−17%] [−20%] [−8%]
Program information
Benet display 0.077*** 0.078*** 0.082*** 0.066*** p = 0.23 0.0035** 0.0033**
(0.007) (0.006) (0.008) (0.010) (0.001) (0.001)
[+33%] [+34%] [+30%] [+41%]
Transaction cost display 0.013* 0.015* 0.015 0.008 p = 0.67 0.0025 0.0027
(0.008) (0.008) (0.010) (0.012) (0.002) (0.002)
[−6%] [−6%] [−6%] [−5%]
Indemnication message 0.004 0.005 0.003 0.007 p = 0.71 0.0010 0.0010
(0.004) (0.004) (0.006) (0.007) (0.001) (0.001)
[+2%] [+2%] [+1%] [+4%]
Informational yer 0.036*** 0.036*** 0.045*** 0.018 p = 0.07 0.0001 0.0001
(0.007) (0.007) (0.009) (0.011) (0.002) (0.002)
[−16%] [−16%] [−17%] [−11%]
Envelope message 0.007 0.006 0.009* 0.001 p = 0.37 0.0005 0.0005
(0.004) (0.004) (0.005) (0.007) (0.001) (0.001)
[−3%] [−3%] [−3%] [−1%]
Personal stigma reduction 0.007 0.009 0.011 0.001 p = 0.57 0.0033 0.0035
(0.010) (0.010) (0.013) (0.016) (0.003) (0.003)
[−3%] [−4%] [−4%] [+1%]
Social stigma reduction 0.042*** 0.042*** 0.045*** 0.037** p = 0.67 0.0023 0.0021
(0.010) (0.010) (0.013) (0.015) (0.002) (0.002)
[−18%] [−18%] [−17%] [−23%]
Dummy variable for dependents X X X X
Controls X X
Observations 35,050 35,050 23,618 11,432 35,050 35,050
R20.02 0.04 0.01 0.01 0.02 0.03
Response/deny rate for control
(simple N + WS)
0.23 0.23 0.27 0.16 0.01 0.01
p-value of F-test: complexity 0.00 0.00 0.00 0.00 0.19 0.18
p-value of F-test: program intervention 0.11 0.11 0.42 0.09 0.10 0.09
p-value of F-test: stigma 0.00 0.00 0.00 0.12 0.77 0.69
Notes: This table summarizes the marginal treatment effects on response and denial estimated from a linear proba-
bility model. The rst column presents the baseline response model, while the second column estimates the model
with a full set of controls. Control variables include indicators for ling status, past claiming behavior, mode of tax
preparation, gender, as well as expected benet size and income. The next two columns estimate the baseline model
for recipients with and without dependents. The nal columns estimate the baseline model of denials without and
then with controls. The relative size of the estimated effects compared to the response rate of the simple mailing
(i.e., the control) is reported in brackets. p-values report results of F-tests that check for the joint signicance of
interventions in the specied categories. Errors are robust with standard errors clustered at each zip code.
*** Signicant at the 1 percent level.
** Signicant at the 5 percent level.
* Signicant at the 10 percent level.
Complexity Interventions.—The rst set of interventions, as depicted in Figure 4,
indicates the stark effect of informational complexity on response. The complexity
notice decreased response by 0.06 ( p < 0.01), or 27 percent, relative to the 0.23
response of the control mailing, and the effect magnitude, in absolute terms, did
not differ signicantly across dependent status. The lengthened worksheet lowered
response by 0.04 ( p < 0.01) or 17 percent. The effect of worksheet complexity
appears to be driven largely by those without dependents possibly because the treat-
ment worksheet for this population is substantially “stronger” (due to the additional
section of questions) than the same intervention for those with dependents. A sepa-
rate estimate of the interaction of the two conditions reveals that the joint presence
of both complexity elements reduced response by 0.09 ( p < 0.01).
Program information
1% +0%
Response rate
Experimental intervention
Control mailing
Complex notice
Complex worksheet
Benet display
Transaction cost display
Informational yer
Envelope message
Personal stigma
Social stigma
F 4. R  M E  E I
Notes: This gure depicts the response rates, and marginal treatment effects, associated with experimental interven-
tions using estimates reported in column 1 of Table 4. The “Control mailing” refers to the simple notice and simple
worksheet and reects response averaged across the envelope and indemnity treatments.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
Mechanisms: We turn to the psychometric survey evidence for insight into why
modest, noninformative, changes in the appearance of the mailings lead to such
large changes in response. Table 6 presents a series of regressions estimating how
exposure to each of the mailing elements, randomized across survey respondents,
altered the attention recipients paid to the information as well as inferences made
with respect to the costs and benets of the program. Indicator variables represent
each intervention, with the control notice and worksheet excluded, and the model
controls for the presence of dependents.
As initial evidence for whether the interventions successfully manipulated per-
ceived complexity, the rst column of the table indicates that subjects rated the
complex notice, but not the lengthier worksheet, as signicantly more complex than
the control (notice: p < 0.01). That the latter doesn’t register as more complex on
this scale could be because, unlike the textually dense notice, the complex work-
sheet features a simple visual design. Overall, the survey suggests that the complex
notice and worksheet may have dampened response not by signicantly increasing
the perceived effort or time-costs of claiming, as proxied by the willingness to pay
a preparer to complete the worksheet (WTP Preparer), but by reducing the degree
T 6—P A  E I
Complexity Attention paid Inferences of program benets and costs
(0 –100)
(0 –100)
(ln $, if > 0)
(0 –100)
audit rate
(0 –100)
[Simple notice, simple worksheet: excluded]
Panel A. Complexity
Complex notice 6.12*** 4.31** 0.18*** 0.3 0.08 2.42 1.02 1.44
(1.926) (2.025) (0.036) (2.9) (0.08) (3.77) (1.75) (1.88)
Complex worksheet 0.36 1.26 0.03 6.99** 0.11 1.32 0.81 0.22
(1.925) (2.023) (0.036) (2.9) (0.08) (3.77) (1.75) (1.88)
Panel B. Program information (selected interventions)
$457 benet display 2.77 2.179 0.09 24.0*** 0.265 8.24 13.62*** 4.83
(4.152) (3.989) (0.077) (6.3) (0.18) (8.64) (3.80) (3.85)
$3,043 benet 7.01** 4.896* 0.066 2.0 0.981*** 1.46 1.89 3.59
display (3.011) (2.893) (0.056) (4.5) (0.13) (6.26) (2.75) (2.79)
$5,000 benet 5.30* 3.159 0.051 5.3 1.043*** 6.79 3.07 0.19
display (2.717) (2.611) (0.051) (4.1) (0.12) (5.65) (2.48) (2.52)
10 minute cost 0.07 1.742 0.11 4.3 0.023 14.04* 0.58 3.29
display (3.666) (3.522) (0.069) (5.5) (0.16) (7.65) (3.36) (3.41)
Flyer 3.58** 2.857* 0.048* 3.4 0.357*** 0.55 0.09 0.78
(1.421) (1.577) (0.026) (2.1) (0.05) (2.88) (1.24) (1.37)
Panel C. Stigma (selected interventions)
Social inuence 6.07 1.924 0.042 2.6 0.061 8.48 4.20 6.75*
(3.751) (3.604) (0.070) (5.7) (0.16) (7.80) (3.42) (3.48)
Average response 29.7 78.5 0.69 44.2 6.8 33.0 77.2 23.1
Notes: This table provides output from OLS regressions that capture psychometric assessments of select experi-
mental mailings from an online sample of respondents (Amazon M-turk, total N = 2,800). We restricted tests to
versions of the mailings without dependents. All regressions include a xed effect to control for whether the par-
ticipant had an eligible dependent. Please refer to the text for a description of the sample and design of the survey.
Errors are robust.
*** Signicant at the 1 percent level.
** Signicant at the 5 percent level.
* Signicant at the 10 percent level.
to which individuals attended to, and understood, program information. Beliefs
of program eligibility, in particular, appeared sensitive to the complexity of the
Informational Interventions.—Among treatments that provided information,
the display of benet information was the most potent. The inclusion of a benet
range heightened response by nearly 0.08 ( p < 0.01), or 33 percent, relative to the
control, and its effect was roughly equal for respondents with and without depen-
dents. Figure 5, which plots response separately for each benet display relative to
the appropriate control, investigates whether this increase in response was tied to
the magnitude of the displayed gure. For those with dependents, assigned to this
treatment arm, the gure reports response after exibly adjusting for the number of
dependents with dummy variables. The gure reveals that response to the benet
display was not tied to the benet magnitude. For those with dependents, random-
ized to receive either a high or low display, the low display ($3,043) actually pro-
duced the largest increase in response of 0.13. This represents an 81 percent increase
relative to the 0.16 response of the dependent control, and is statistically distin-
guishable from the 0.04 and 0.06 increases induced by the $5,028 ( p < 0.05) and
Response rate
Baseline 60min 10min
Cost display
Baseline $3,043 $5,028 $5,657
Benet display
with dependents
Baseline $457
Benet display
without dependents
+5% +6%
23% 1% 2%
F 5. R  M E  B  C D I
Notes: This gure depicts the response rates, and marginal treatment effects, associated with the Benet and Cost
Display Interventions. Baseline gures refer to the response to the control mailing (simple notice and simple work-
sheet) for the relevant sample (i.e., those without dependents, those with dependents, and the overall sample,
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
$5,657 ( p < 0.01) displays. Those without dependents randomized into the benet
display treatment ($457) also exhibited a large and statistically signicant increase
in response, relative to the control, of 0.08 ( p < 0.01).
The remaining informational interventions did not signicantly improve
response. Figure 4 indicates that the inclusion of transaction cost information
reduced response by 0.01 ( p < 0.10), while Figure 5 indicates that the inuence
of the two cost displays (60 and 10 minutes) cannot be distinguished. The
one-page informational yer, which includes a benet schedule as well as
information regarding eligibility and enrollment, actually dampened response by
0.04 ( p < 0.01), while the nal two informational interventions—the envelope
message and the indemnity message—had no statistically signicant effect on
Mechanisms: Table 6 suggests at least two channels through which the benet
display may have altered behavior (the two $5,000 interventions were coupled to
increase power). First, respondents observing notices with the high and middle
displays (~$5,000, $3,043) expected benets twice as large as the control con-
dition. Second, while the low display ($457) did not signicantly alter expecta-
tions of benet size, it did signicantly elevate belief of eligibility by 24 percent.
Given beliefs of benet size and eligibility are both sensitive to the benet dis-
play, a possible explanation for the stronger response to the smaller magnitudes
in the experiment may lie in the comparative degree to which the notices inu-
ence beliefs across these two margins (i.e., “If the benet is that large, I must
have known of it therefore, I must not be eligible”). The nonpositive effect of
the transaction cost notice on take-up is consistent with survey evidence indicat-
ing that respondents did not view the claiming worksheets as overly burdensome
to complete. The mean willingness to pay a third party to complete the work-
sheet was $33 (median: $20) while the median expected completion time was
15 minutes (unreported in the table) which suggests perceived economic costs of
claiming that were modest in comparison to expected benets. Consistent with
studies of tax salience (e.g., Chetty, Looney, and Kroft 2009), judging from an
increased willingness to pay a preparer, the transaction cost notice may actually
have heightened the salience of worksheet completion costs and, through this
channel, reduced response. Intriguingly, survey respondents saw the informational
yer as more complex, relative to just the baseline notice. The yer also lowered
comprehension and actually decreased expectations of benet size. These patterns
raise the possibility that the yer signicantly lowered response in the eld due
to its perceived complexity. Finally, while neither the envelope or indemnity mes-
sages were tested in the psychometric instrument, the nonpositive reaction to the
envelope, coupled with the relatively high share of survey respondents who claim
they would open IRS mail (85 percent, not reported in the table) suggests that
ignoring mail may not be an important determinant of low take-up in this context.
Alternatively, our envelope message may have simply failed to increase the rate
at which individuals open mail. The ineffectiveness of the indemnity message
in raising response is surprising given survey respondents vastly overestimated
the likelihood of an audit (mean belief of 23 percent relative to actual audit rate
for EITC claimants of about 2 percent). Again, the lack of observed inuence on
response in the eld could be due to the treatment not sufciently shifting recipient
Stigma Interventions.—Finally, we consider the two interventions intended to
reduce program stigma. The attempt to reduce personal stigma (emphasizing the
role of “hard work”) did not affect response, while the social inuence treatment,
highlighting take-up of peers, surprisingly decreased response by 0.04, or 18 percent
relative to the control ( p < 0.01).
Mechanisms: The nonpositive impact of attempts to reduce stigma is consistent
with survey results suggesting that claiming the EITC may not be highly stigmatiz-
ing. To assess perceived stigma, we asked respondents to indicate agreement with
the statement “I respect anyone who decides to claim the earned income credit”
(scale ranging from 0, strongly disagree, to 100, strongly agree). The mean response
was 77 and less than 4 percent of respondents disagreed with the statement, sig-
naled by a score below 50. We can only speculate as to why the social stigma inter-
vention actually decreased response in light of its successful use in other contexts.
One possibility, suggested by the psychometric surveys, is that while the interven-
tion marginally increased respect for claimants (not signicant), it also direction-
ally increased perceived complexity and belief in the likelihood of an audit. The
increase in recipient confusion, coupled with the already low baseline levels of per-
ceived stigma, may have prompted recipients to react negatively to the social stigma
C. Persistence and Inertia of Take-Up
Policymakers would be remiss not to ask whether a one-time intervention leads
to a continued pattern of increased take-up. The persistence of the interventions
featured in this study also may offer insight into whether the effects are driven by
information acquisition and learning as opposed to more transient mechanisms
(e.g., attention-based or persuasion effects). We assess persistence with two distinct
approaches that attempt to capture the effect of receiving a mailing on subsequent
claiming and the “inertial” effect of take-up in one period on future take-up.
First, we estimate the effect of the mere receipt of an experimental mailing on
subsequent year claiming. Despite the absence of a “hold-out” group, randomized
not to receive any mailing, in the experimental sample, we can still project a coun-
terfactual rate of TY 2010 take-up by examining the rate of EITC claiming in the
years prior to the experiment under straightforward assumptions. Conditioned on
ling but not claiming in time t, if claiming in proximal years is a white noise out-
come, then in expectation, claiming in t 1 and t + 1 should be equivalent. The
most plausible violations to this assumption, such as learning over time or shocks
that persist across periods, should actually lead to lower relative claiming in period
Another intriguing possibility is offered by Engel and Hines (1999) who note that tax behavior may be sen-
sitive to expectations regarding audit rates in the future as well as the present.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
t + 1, given the failure to take-up in period t.
In this sense, if claiming is not
independent across years, our estimate is likely to be a lower-bound of persistence.
Table 7 compares the rate of claiming for TY 2007 through TY 2010 for the
experimental sample. Claiming in the year following the experiment, 0.245, is sig-
nicantly higher than in the year preceding the experiment, 0.158 ( p < 0.01). In
support of the identifying assumption, TY 2008 and TY 2007 claiming are not sta-
tistically distinguishable ( p = 0.15). To account for the possibility that dependents
may age a ler out of a credit, we replicate the results on a sample excluding anyone
with a dependent at the age threshold in TY 2009. Overall, relative to the TY 2008
claiming rate, the table implies that the mailings led to a subsequent increase in
claiming of 55 percent.
Next, we attempt to estimate the causal effect of higher claiming in one period
on subsequent claiming. This exercise aspires to capture an “inertial” parame-
ter which may be of more general interest for policy and welfare. We express
the empirical relationship of interest with the following cross-sectional model:
Claim 2010
i = α + γ Claim 2009
i + X β + ε
i where Clai m i represents the binary
There is the possibility that a secular increase in take-up over this period, unrelated to the one-time shock
which might have prompted non-claiming in TY 2009, could lead to the spurious appearance of persistence.
However, overall take-up rates, reported by the IRS, (and available on the EITC website), suggest that claiming
actually decreased in California in 2010 relative to 2008.
T 7—P  T  T-U I
Claiming rate by year
TY 2007 TY 2008 TY 2010
Panel A. Pre and post experiment claiming
Experimental sample 0.162 0.158 0.245
(0.369) (0.365) (0.430)
p-value of claiming equivalence (t = t 1) [0.149] [0.000]
Adjusted for dependent age out 0.16 0.156 0.245
(0.366) (0.363) (0.430)
p-value of claiming equivalence (t = t 1) [0.228] [0.000]
Dependent variable: TY 2010 claiming (1,0)
Panel B. Inertial effect of TY 2009 claiming
Claiming 2009 (yes/no)0.108*** 0.090*
(0.006) (0.049)
Observations 35,050 35,050
R20.04 0.02
Notes: This table summarizes analysis of persistence of the experimental interventions as well as take-up inertia.
Panel A compares EITC claiming in years prior to and following 2009. Bracketed gures indicate p-values from a
t-test of the null hypothesis that current year claiming is equivalent to that of the prior year. Panel B reports results
of an OLS and IV regression of TY 2010 claiming on TY 2009 claiming as specied in the text. Regressions include
exible controls for the number of dependents, as well as controls for gender, ling status, past claiming, prepara-
tion mode, expected benet size, and earned income. Errors are robust.
*** Signicant at the 1 percent level.
** Signicant at the 5 percent level.
* Signicant at the 10 percent level.
claiming decision for the specied tax year of person i , X represents a vector of
available demographic and tax variable controls, and γ is the parameter of interest.
An obvious concern in this estimation, with simple OLS, is the endogeneity intro-
duced both by serial correlation in claiming due to stable preferences and beliefs,
as well as the possibility of shocks that jointly affect TY 2009 and TY 2010. We
overcome this identication problem by using the experimental interventions as an
instrument for claiming in TY 2009. The resulting two-stage estimate recovers the
LATE of higher take-up in TY 2009, induced by variation across the experimental
interventions (rst stage), on TY 2010 take-up (second stage). If the excludability
assumption is violated—that is, the effect of the experimental mailings on subse-
quent take-up does not act only through changes in contemporaneous take-up—our
estimates would capture both the direct effect of the interventions and the inertial
effect, and should be interpreted as an upper bound of the inertial parameter. Panel B
of Table 7 reports both the OLS and IV estimates of γ
ˆ for this model. OLS suggests
that induced claiming in one year results in a 0.11 higher likelihood of claiming
the subsequent year (i.e., or 44 percent relative to the 0.25 baseline claiming rate in
TY 2010). The less precise IV estimate produces a similar effect magnitude of 0.09
(37 percent relative to baseline).
Overall, the analyses point to some persistence in the inuence of the experimen-
tal mailings on take-up the following year. This is especially notable given that the
T 8—S S  E
All sample No dependents With dependents
Variable name Response Observations Response Observations Response Observations
Experimental sample 0.22 35,050 0.25 23,618 0.16 11,432
Panel A. Demographic variables
Female, age < 35 0.29 3,738 0.30 2,061 0.21 677
Female, age 35 0.25 6,544 0.28 4,445 0.18 2,099
Male, age < 35 0.23 7,329 0.25 5,731 0.18 1,598
Male, age 35 0.19 17,424 0.22 10,375 0.15 7,049
Panel B. Tax variables
Self-preparation 0.26 21,890 0.27 18,363 0.23 3,527
Paid preparation 0.16 13,136 0.20 5,235 0.13 7,901
Past claim from TY 2006 to TY 2008 0.23 10,165 0.27 5,870 0.17 4,295
Past claim + self prep 0.29 5,007 0.30 2,936 0.25 1,071
Past claim + paid prep 0.17 5,149 0.21 1,927 0.15 3,222
Self employment income > $0 0.19 6,427 0.19 4,656 0.18 1,771
Filing status = single 0.26 20,317 0.26 20,317
Filing status = MFJ 0.18 9,522 0.21 3,134 0.16 6,388
Filing status = HOH 0.16 5,196 0.13 167 0.16 5,029
Panel C. Benet and income
Expected benets: $0 to $499 0.24 26,988 0.25 23,618 0.15 3,370
Expected benets: $500 to $1,499 0.18 2,708 0.18 2,708
Expected benets: $1,500 to $2,499 0.17 1,701 0.17 1,701
Expected benets: $2,500 to $3,999 0.15 2,259 0.15 2,259
Expected benets: $4,000 0.14 1,394 0.14 1,394
Earned income: $1 to $4,999 0.24 9,759 0.24 9,230 0.22 529
Earned income: $5,000 to $9,999 0.26 8,490 0.26 7,988 0.18 502
Earned income: $10,000 to $19,999 0.23 7,895 0.25 6,400 0.16 1,495
Earned income: $20,000 to $29,999 0.15 2,275 0.15 2,275
Earned income: $30,000 0.16 6,631 0.16 6,631
Notes: This table summarizes response statistics by demographic, tax, and benet/income variables for vari-
ous subsets of the experimental sample. Panel A reports response statistics by age and gender, panel B reports
response by various tax variables, and panel C reports response by expected benet size and earned income. Not all
subcategories sum to 35,050 due to either missing data or excluded subcategories.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
domain in which TY 2010 take-up occurs (i.e., on one’s tax return at the time of l-
ing), is very different from that of TY 2009 (i.e., the return of a notice and worksheet
mailed in November). This partial persistence speaks both to the possibility that
respondents acquire and retain program information from the experimental mailings
or to possible habit formation in claiming.
D. Heterogeneity in Response
We explore the heterogeneity in experimental response for potential insights of
both theoretical and policy relevance. Looking rst at differences in overall response
by demographic and tax variables, Table 8 indicates a higher response rate for
females, young recipients, and self-preparers for those with and without dependents.
The apparent heterogeneity in response by earned income actually reects differ-
ential response by dependent status. However, one must interpret the table with
caution since the experimental population is the product of substantial selection that
likely differs across the examined subpopulations.
We can more cleanly investigate heterogeneity in the relative response to treat-
ment as compared to control mailings. Our main analysis investigates the sensitivity
of response to informational complexity across recipient income. We focus on those
Earned income
$5,000 bins
Response rate
Simple notice
Complex notice
F 6. H  R  S  E I
( For recipients with dependents)
Notes: This gure displays the response associated with the simple and complex notice by earned income for recip-
ients with dependents. Response for each notice is averaged across the envelope and worksheet variants.
F 7. R H  B S, G,  A
Notes: This gure shows heterogeneity in experimental response by estimated benet size, gender, and age. Each
panel reports marginal effects by intervention for the specied sample. The sample for panel A is restricted to those
with dependents, while the samples for panels B and C are restricted to single lers. The gure additionally reports
p-values corresponding to statistically signicant between-group differences, estimated separately from pooled
Panel A. Response heterogeneity by benet size
(lers with dependents, low benet: < $678, high benet: >= $678)
Low High Low High Low High Low High Low High Low High Low High Low High Low High
Marginal effect on response
0.02 0.02
0.00 0.00 0.00
display Flyer
p < 0.10
display Flyer
Marginal effect on response
p < 0.05 p < 0.01
p < 0.05
Panel B. Response heterogeneity by gender (single lers only)
Marginal effect on response
display Flyer
0.05 0.05
0.01 0.01 0.01 0.01
0.01 0.01
Panel C. Response heterogeneity by age (single lers only, Young: < 39 years, Old: >= 39 years)
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
with dependents in order to examine a wide range of recipient incomes.
Figure 6
compares the average response by earned income bins of $5,000 for those receiving
either the complex or simple notice. To expand the comparison sample, we average
response across the cross-randomized envelope and worksheet variants. The gure
indicates that recipients with lower incomes beneted more from simplied notices
than did recipients with higher incomes. Specically, the differential increase in
response for those below median income (b = 0.084) was more than twice that of
recipients above median income (b = 0.036) ( p < 0.05).
Even among a sample
of relatively low earners, informational complexity disproportionately affected the
very poor.
We examine heterogeneity in relative response to each treatment across other
dimensions of interest—median benet level, gender, and median age—and report
these in Figure 7. We conne the analysis of gender and age to single lers for the
purpose of identication. Overall, relative to the control condition, females were
more deterred by complexity (notice: p < 0.05, worksheet: p < 0.01) as well as the
attempt to reduce personal stigma ( p < 0.05), than were men. We do not nd clear
heterogeneity in response with respect to benet size or recipient age.
Our results additionally speak to the possibility that language may serve as a bar-
rier to take-up. While we did not experimentally test non-English language notices,
we can estimate a language-neutral take-up rate by modeling overall response to the
mailings across regions using zip code level census data from 2010.
Assuming that
differences in response, conditional on covariates, across regions of varying density
of Hispanic households can be attributed to language, the estimates, as reported
in Table 4, imply that overall take-up would rise from 0.22 to 0.25 in the absence
of language barriers. While unobserved cultural factors might also account for
the observed patterns, the disproportionately positive, and statistically signicant,
response in Hispanic regions to the messaged envelopes, which included a Spanish
translation, also points to language as a meaningful predictor of overall take-up.
IV. Rationalizing and Generalizing Findings
A. Implication of Findings for Models of Take-up
One may have initially interpreted incomplete take-up of the EITC among tax l-
ers as reecting costs of claiming—that is, those associated with time, effort, stigma,
and potential penalties—which outweigh program benets. However, the responses
documented in the eld study, and mechanisms implied from the survey, are difcult
For those without dependents, the interquartile range in income is $2,964 to $10,307. Even for this group, we
nd that the complex notice is, at least directionally, more detrimental for subjects below (b = 0.067), as com-
pared to above (b = 0.057), median earnings.
We nd similar results when explicitly controlling for the cross-randomized envelope and worksheet inter-
ventions and demographic controls.
Specically, we estimate the regression Respons e
ij = α + θHispDen s
j + X β + ε
ij where Respons e
ij is a
binary indicator of a returned worksheet for person i in zip code j , HispDen s
j is the fraction of Hispanic households
in zip code j , and X is a vector of controls including tax, benet, and demographic variables. θ
ˆ is the statistic of
Adapting the main response model by including an interaction between the messaged envelope and Hispanic
household density produces a statistically signicant and positive interaction coefcient, 0.030 ( p < 0.10). The
sum of the interaction coefcient and the coefcient for the envelope indicator is positive but insignicant.
to rationalize in a traditional model of take-up in which eligible individuals balance
accurately perceived expectations of benets and costs, even allowing for the pos-
sibility of program stigma. In particular, the eld experiment afrms the sensitiv-
ity of take-up to repeated exposure to program information (i.e., simply receiving
a second notice), reductions in its complexity (i.e., through the simplied notice,
shortened worksheet, and even omission of the informational yer) or changes to
its salience (e.g., benet display), but not attempts to lower perceptions of program
stigma or expectations of the time-costs of claiming. Consistent with this pattern
of behavior, the accompanying survey suggests that successful interventions may
have inuenced decisions by heightening awareness and remedying confusion with
respect to eligibility and benet size (possibly by increasing the attention paid to the
mailings), but not by signicantly reducing expectations of the economic costs of
claiming—which respondents reasonably judged to be low.
The present ndings seem more consistent with alternative models of behavior in
which psychological frictions play an important role. One candidate model is one
in which individuals rationally weigh the costs and benets of claiming, but suffer
from distorted beliefs as to the magnitudes of such costs and benets. However, the
relatively modest baseline assessments of claiming costs from the surveys, and the
further fact that the substantial inuence of complexity on experimental response
is not driven by increases in the perceived economic costs of claiming (Table 6),
suggest that informational frictions alone may be insufcient for explaining the low
take-up observed in this setting.
Other models, which depart more sharply from
conventional models of take-up, may have more success in rationalizing the accu-
mulated evidence. One such example are those models which incorporate the pres-
ence of “hassle costs.” First introduced by psychologist Kurt Lewin (1951) and later
discussed in the context of nancial decisions of the poor by Bertrand, Mullainathan,
and Shar (2006), the framework explains how seemingly minor details can inu-
ence behavior to a degree larger than that predicted by economic costs alone by
facilitating, or hindering, the psychologically important initial steps of a multi-step
With respect to program take-up, rather than deciding to claim after careful
evaluating expected costs and benets, individuals may instead avoid, or postpone,
claiming due to the psychological burden imposed by complicated forms, confusion
about program rules, or even a small degree of uncertainty with respect to eligibility.
The potential inuence of hassle costs on important decisions is consistent with the
success of automatic defaults in reshaping retirement savings and organ donation, as
well as studies demonstrating the surprisingly large importance of minor logistical
detail in improving medical adherence (e.g., Gilovich and Grifn 2010; Milkman
et al. 2011). A recent study documented how tax complexity could serve as a psy-
chological hassle in nding that taxpayer aversion for itemizing returns amounted to
individuals valuing the time-costs of itemization 4.2 times more than the time-costs
associated with other tasks (Benzarti 2015). While the recognition of hassle costs
offers one promising account for how minor changes in the decision-setting might
Given survey respondents had inated beliefs of the likelihood of an audit, if the indemnication intervention
was not effective in assuaging audit concerns, it is possible that a model of take-up with distorted beliefs of penalty
costs could explain low take-up in this context.
Lewin’s work spoke about the role of small situational forces, or “channel factors,” which caused individuals
to move strongly toward, or away from, a particular goal.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
lead to signicant changes in behavior, the ndings of the study may also reect
other models of behavior including those which involve limits to attention (Karlan
et al. 2015), self-control (e.g., O’Donoghue and Rabin 1999), or other cognitive
resources (Mullainathan and Shar 2013).
B. Generalizing Findings with a Survey of Low-Income Tax Filers
A potential drawback of the present study is that because it pertains to a sample
which failed to claim the credit on two prior occasions and is also observably differ-
ent from the overall population of EITC claimants—the typical experimental sub-
ject is more likely to be without a dependent, male, and to have self-prepared—the
ndings may not generalize. One difculty in assessing generalizability is that while
Table 2 reports available characteristics of EITC claimants and non-claiming tax
lers, we cannot directly observe the characteristics of non-claimants. Nevertheless,
to examine the potential role of psychological frictions in explaining non-claiming
in the EITC more generally, we report the results of a second survey, along with
additional ndings from the rst, in order to better understand program awareness
and literacy, and perceptions of program stigma, beyond the experiment. The sec-
ond survey, administered primarily at volunteer tax clinics in Chicago, comprises a
diverse sample of 1,139 low to moderate income tax lers. While the survey is itself
narrowly limited to subjects who le with preparer assistance, the use of preparers
is commonplace among EITC claimants with 66 percent of TY 2009 claims having
been led in this manner. Given estimates from Plueger (2009) indicating an aver-
age income of $8,900 for non-claimants, and further, that a majority of non-claim-
ants had a qualifying dependent (63 percent) and, among single lers, were female
(56 percent), eligible survey respondents ($9,000 median income; 41 percent with
dependents; 60 percent female) more closely resemble eligible non-claimants across
these dimensions.
The results of the survey, summarized in Table A1 of the online Appendix, indi-
cate widespread decits in program awareness and misperceptions regarding pro-
gram benets and the costs of claiming. Only 54 percent of the sample, including
56 percent of the 65 percent deemed eligible for the program, reported awareness of
the EITC.
The survey also provides novel evidence that individuals systematically
under-estimate eligibility and the magnitude of program benets. After reading pro-
vided program information, one-third of those eligible for the credit did not believe
themselves to be eligible (this compares to 12 percent of sample which believed
themselves to be eligible when they were not). Among those who correctly judged
eligibility, the median ratio of expected to actual benets was 0.8, 61 percent under-
estimated benet size, and 41 percent under-estimated benet size by 50 percent
or more. Echoing conclusions from the rst survey, respondents did not perceive
claiming as overly time-consuming, but did substantially overestimate the likeli-
hood of an audit with a median estimate of 15 percent (more than eight times the
actual audit rate for EITC claimants). Finally, the table reports, low to moderate
We did not elicit the full set of information required to determine exact eligibility and benet size such as
investment income or an invalid Social Security number. For the large majority of individuals, our inferences
regarding eligibility and benet size should be accurate.
evidence that respondents viewed benet receipt as stigmatizing.
Overall the sec-
ond survey documents low program awareness, a signicant degree of under-esti-
mation of eligibility and benet size, reasonably well-calibrated beliefs about the
time-costs of claiming, but high costs associated with potential penalties, and low to
moderate perceptions of stigma.
Given concerns that the second survey is unrepresentative, we also report pro-
gram awareness and literacy from respondents of the original psychometric sur-
vey. The 38 percent of this sample which appears eligible for the credit once again
resemble non-claimants more closely than the experimental sample with respect to
gender (64 percent female) and the share with qualied dependents (57 percent) but
has higher income (median: ~$13,000). More tellingly, the sample includes a sig-
nicant fraction of eligible non-claimants (i.e., of those deemed eligible, 68 percent
applied for the EITC, while 17 percent did not, and 15 percent didn’t remember).
Taken together, the two survey instruments canvass several thousand low-income
respondents—including eligible claimants and non-claimants—and document low
levels of program awareness, confusion with respect to program incentives, and
low to moderate degrees of perceived stigma. While one must cautiously interpret
the ndings from these samples, the surveys imply that the psychological frictions
implicated in the eld study may extend to broader groups of EITC non-claimants.
Lay Theories for Incomplete Take-Up.—An alternative strategy through which
to understand the factors responsible for low take-up is to directly ask the target
population why they, or their peers, might not claim an EITC credit. The introspec-
tions of the surveyed sample, including those eligible for the credit, parallel our
other ndings in attributing the failure to claim to confusion regarding eligibility
and program rules, but not the insufcient size of benets, low need of government
assistance (possibly capturing perceptions of program stigma), or fear of penalties
for inappropriate claiming (Table A2 of the online Appendix).
V. Policy Implications
In the introduction we noted that the welfare implications of low take-up hinged on
whether the presence of psychological frictions, among those of high need, deterred
claiming. The ndings of the study, including the observation that the lowest earners
in the sample were disproportionately harmed by informational complexity, sup-
ports the view, adopted by those who administer the EITC, that improving take-up
is normatively desirable. Allowing for the possibility that these ndings generalize
to all tax ling non-claimants, we can project how the experimental interventions
might affect overall program take-up with a series of calibrations.
The surveys indicate that 14 percent of subjects strongly disagree, and another 18 percent simply disagree,
with a statement declaring that people generally “respect” anyone who receives a benet, while 11 percent strongly
disagree, and another 29 percent simply disagree, with a statement stating that an individual “would not care” if
their friends were aware of the benet. We interpret this as indicating a small to moderate share of individuals who
may nd the program to be stigmatizing.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
A. Projected Effect of Interventions on Overall Take-Up
We can estimate the effect of scaling-up our interventions on overall take-up, as
well as disbursements, by projecting the increase in response under various sce-
narios involving wider distribution of the experimental mailings. Table 9 reports
the estimated impact of select experimental mailings on various subsets of ling
non-claimants for TY 2009 (bolded gures reect exact data). For tractability, we
interpret the complex mailing, in the rst row of the table, as a proxy for repeat
distribution of the initial CP 09/27 mailing even though the two mailings feature
differences in the worksheet design (as the original CP worksheet was not tested).
The rst set of columns reports the average response rates and benet levels
directly from the eld experiment while the second set of columns extrapolates the
additional response one would expect if experimental mailings were distributed to
the national population of 321,340 ling non-claimants who failed to respond to
the initial CP mailing. For example, we estimate that the mere distribution of a sec-
ond mailing, approximately similar to the rst reminder notice, would result in an
additional 44,988 claimants, whereas a more efcacious notice would yield 73,908
(simple mailing) to 99,615 (benet display) additional claimants. In the third set of
columns, rather than assuming a second round of notices, we project the outcome
T 9—P P I  E  A EITC T F N-C
Policy intervention and target population
Second mailing
experimental sample
Second mailing all CP
Revised rst mailing
all CP recipients
Revised rst mailing
all tax ling non-claimants
Mailing type Response Benet Observations
Complex mailing 0.14 $461 +44,988 0.14 321,340 0.47 1,128,000 0.47
(also proxy for (0.00) (0.00) (0.01) (0.05)
initial CP mailing) [+$2.3m] [+$24m] [$121m] [$520m]
Simple mailing 0.23 $514 +73,908 0.23 +54,981 0.56 +216,000 0.56
(0.00) (0.00) (0.00) (0.01)
[+$4.1m] [+$38m] [+$28m] [+$111m]
Benet display 0.31 $544 +99,615 0.31 +103,854 0.64 +408,000 0.64
(0.00) (0.00) (0.00) (0.02)
[+$5.9m] [+$54m] [+$56m] [+$222m]
Benet display +172,031 0.75 +675,840 0.75
+ second mailing (0.01) (0.03)
[+$128m] [+$503m]
Actual population
levels (TY 2009)
35,050 321,340 610,904 ~2.4m
Notes: This table projects how expanding the distribution of the experimental mailings to broader populations of l-
ing non-claimants would change overall program take-up and disbursements under the stated assumptions and using
gures from TY 2009. Bolded gures are exact and are from IRS while other gures are estimated. Parenthetically,
we report the percent change in overall program take-up reected by the given projection. We project results for the
simple mailing (i.e., simple notice and worksheet), the simple mailing with benet display (with simple worksheet),
and the benet display plus a second mailing (also a benet display) sent to nonrespondents of the rst mailing. The
rst set of columns reports response for the experimental sample. The second set of columns projects the response
of a second mailing distributed to all CP nonrespondents. The third set of columns projects take-up assuming that
the original CP notice was replaced by the experimental mailings. The nal set of columns projects response in a
scenario in which an initial notice, whose design is replaced by an experimental mailing, is distributed to the entire
population of non-ling non-claimants rather than just those who received the initial CP notice. The number of total
non-ling non-claimants is estimated using take-up rates from Plueger (2009) and assumes 27 million individuals
were eligible for the EITC in TY 2009.
of replacing the initial CP notices, distributed to 610,904, with the experimental
designs. Conservatively assuming that experimental response rates relate additively,
rather than proportionally, to the initial CP response, we estimate that an updated
mailing would yield an estimated 54,981 to 103,854 in additional responses, amount-
ing to $28 million to $56 million in additional disbursed benets.
The fourth set of columns projects the additional claiming that would result
from replacing the initial mailings with the experimental mailings across all l-
ing non-claimants—that is, both existing CP recipients as well as the estimated
1.8 million individuals who may not have received a CP notice. Notably, expand-
ing the notice program to all ling non-claimants, even using the original notice,
would result in a substantial improvement in take-up. The extrapolation suggests
that adopting the experimental mailing designs could yield an additional 216,000
to 408,000 claimants ($111 million to $222 million in additional benets) beyond
those brought in from the expanded distribution. Finally, the last row of the table
projects response given a combination of a redesigned rst notice (Benet Display)
and an identical second notice. This policy intervention, even if targeted only at the
existing population of CP recipients, would yield, according to our estimates, an
additional 172,000 claimants and $128 million in benets. We parenthetically report
the increase in overall program take-up implied by these projections. These calcu-
lations reveal a sizable benet from expanding the original population of mailing
recipients (+0.05) beyond that achieved through the contextual changes explored
in the experiment (+0.03). All told, we estimate that expanding the population of
recipients, redesigning documents, and instituting a second mailing to initial non-
respondents, could improve take-up from 0.75 to 0.83. Of this projected increase,
we attribute a rise in take-up of 0.03, involving $503m in additional benets, to the
redesigned mailings.
B. Cost-Benet Analysis
While we interpret the ndings of our study to suggest that higher take-up would
raise individual, and collective, welfare, a full normative analysis is beyond the scope
of this paper. Nevertheless, we can gain insight into the economic consequences of a
policy involving simpler and more psychologically informed mailings by sketching
out the anticipated costs and benets of expanding the tested interventions.
Costs of the Policy.—Our experimental interventions are not likely to be costly.
While we lack explicit data on costs, we can organize such costs as those relating
to (i) administration (i.e., printing, distributing, and processing the mailings); (ii)
noncompliance (i.e., ineligible claiming); and other (iii) negative externalities (e.g.,
disutility of receiving IRS mail). Administrative costs are likely minimal if they
resemble the current 0.5 percent expense ratio of the EITC (IRS 2003) which is
less than the 16 percent expense ratio of other transfer programs (Eissa and Hoynes
For example, we project the response to the simplied baseline notice as 56 percent amongst the CP pop-
ulation, given the response of 47 percent to the original notice, and the 9 percent additive response generated by
the simple mailing (as compared to 77 percent under an assumption of proportionality). Estimated increases in
disbursements are bracketed in the table.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
2011). Noncompliance costs are also likely to be minimal given that statutory eligi-
bility can be, at least noisily, inferred from administrative records. Moreover, there
is no evidence that the experiment led to an increased rate of ineligible claiming, rel-
ative to all program claimants, judging from the relative rates of disallowed claims
(0.93 percent in the experiment, versus 0.72 percent nationally) and audits (1.41
percent versus 1.91 percent, respectively). Externalities associated with the mail-
ings—such as those which might be incurred if the mailings reduced attention to
other important communications—would need to be signicant for the total cost of
the interventions to signicantly exceed the modest costs of administration.
Benets of the Program.—One could gauge the social benets of higher take-up
from the revealed preference of policymakers—e.g., congress appropriated $716 mil-
lion in 1997 over ve years for EITC outreach and enforcement—or, alternatively,
by forecasting how our interventions, if scaled to broader populations, would shift
the income distribution of beneciaries. Under the conservative assumption of EITC
budget neutrality, we can compare the preexperimental income distribution of CP
notice recipients (TY 2008 data) to the projected income distribution under a regime
featuring a second, simplied, notice. To achieve budget neutrality, we proportion-
ally reduce the benets of all EITC claimants to fund new enrollees.
Figure 8 indicates that the majority of new claimants would fall in the left of the
existing income distribution of CP claimants, and further, that the typical CP claim-
ant is poorer than the typical overall EITC claimant (data is from Eissa and Hoynes
2011 who tabulate returns from 2004 Statistics of Income (SOI) les). The exer-
cise implies that redistributing benets among existing EITC claimants to fund new
claimants, through interventions like those used in the experiment, would result in a
transfer of incomes to the very poor. Given the modest costs of administration, non-
compliance, and externalities, assuming some curvature in a policymaker’s social
welfare function, the analysis echoes our earlier interpretation that a policy which
Adjusted gross income
$10k $20k $30k $40k $50k
Projected claimants
Adjusted gross income
$10k $20k $30k $40k $50k0
50 m
40 m
30 m
20 m
10 m
0 0
Projected transfers
Density of EITC disbursements
CP notice and repeat mailing
CP notice
CP notice and
repeat mailing
EITC disbursements
CP notice
F 8. P C  D  S M  I
( Assumes a second simplied mailing to CP nonrespondents)
Notes: This gure depicts the projected shift in the distribution of claimants and disbursements by adjusted gross
income attributable to a second, simplied, reminder notice distributed to nonrespondents of the initial CP notice.
Distributional data for the CP notice are from TY 2008 (the year prior to the experiment) while projected distribu-
tions are extrapolated from the experimental data. The distribution of overall EITC disbursements in the right panel
is estimated from TY 2004 data reported by Eissa and Hoynes (2011).
leveraged the ndings of the study, even under budget neutrality, would be likely to
improve welfare.
VI. Conclusions
In this paper we use a eld experiment, in collaboration with the IRS, to bet-
ter understand the factors that give rise to the incomplete take-up of economically
consequential government benets. Our study demonstrates that the mere receipt
of an informational notice and claiming worksheet, just months after the receipt of
a very similar mailing, led to higher take-up. More strikingly, the complexity, and
salience, of the information in the mailings shaped the likelihood of claiming, but
attempts to reduce stigma or perceptions of economic claiming costs did not. We
sought to understand the mechanisms underlying the differential responses to the
interventions with an accompanying survey. The survey suggested that successful
mailings heightened program awareness, improved accuracy of beliefs regarding eli-
gibility and benet size, and increased attention paid to the notices, and, consistent
with the ndings from the experiment, did not substantially reduce the perceived
costs of claiming. We explored the generalizability of our ndings with a second
survey of low-income individuals. Together, the two surveys point to decits in pro-
gram awareness and understanding that extend beyond the experimental sample.
Our focus on understanding the behavior of non-claimants ignores the potentially
critical role of the tax preparers. Given the share of EITC claimants who rely on pre-
parers, an open question is why such preparers would fail to claim the credit for their
clients (particularly since many paid preparers may have incentives to le claims)?
While the composition of the experimental sample implies prepared claims are less
likely to forego an eligible credit as compared to self-prepared claims, one possible
explanation, raised during informal discussions with the preparer community, is that
the sheer size of the preparer population and the ease of application—reportedly
over 1 million preparer identication numbers were issued from 1999 to 2010—has
led to signicant variation in preparer quality. Given the complexity of the EITC and
other credits for which a typical EITC claimant may also be eligible, it is plausible
that even a reasonably competent preparer might neglect to claim a credit on behalf
of a client who is herself unaware.
Our study has important limitations. Chief among these is that because our experi-
mental and survey samples are nonrepresentative, our ndings may not generalize to
other non-claiming populations even within the EITC. A second limitation concerns
the scalability of the identied strategies for improving take-up. As an illustration,
sending a hypothetical bright red letter to individuals may yield an immediate rise
in response, but whether such a letter would remain effectual if deployed repeatedly
over time, or simultaneously across programs, is a question for future work.
These limitations not withstanding, we see three primary implications of this work.
First, in this setting, and perhaps more broadly, the ndings suggest that incomplete
take-up should be viewed as a “policy problem” in which those of high economic
We do note that, in this exercise, the redistribution of marginal dollars from households typically with chil-
dren to those typically without children may have more complicated implications for welfare. We thank an anony-
mous referee for this observation.
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
need do not receive intended benets. Second, our evidence is not easily rational-
ized by a simple cost-benet model of take-up, even one which allows for stigma,
but instead seems consistent with models in which small changes to the frequency,
appearance, and complexity of information matters. We hope that future research will
clarify which of these models best describe take-up in the presence of psychologi-
cal frictions. A nal, practical, implication is that we see our study as identifying a
set of specic interventions, and a more general set of principles, that highlight the
role of nontraditional policy levers in engaging populations that may not be highly
responsive to traditional incentives. To the extent that even the most sensible policy
implementation may not overcome decision-making frictions, like those associated
with program complexity, there may be a rationale for policies, such as the automatic
distribution of payments, that move beyond merely simplifying program information
to simplifying the rules and incentives governing such programs.
A: S E I
Panel A1. Simple notice (control)Panel A2. Complex notice (page 1of 2)
Panel C1. Benet display (high)Panel C2. Benet display (low)
For IRS use only
 
Notice EIC0927
Tax Year 2009
Notice Date November 2010
Social Security Number 999-99-9999
To Contact Us 1-800-829-1040
Page 3 of 4
Panel B1. Simple worksheet (no dependents)
Notice EIC0927
Tax Year 2009
Notice Date November 2010
Social Security Number 999-99-9999
To Contact Us 1-800-829-1040
Page 3 of 4
Panel B2. Complex worksheet (no dependents)
(page 1 of 2)
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
Panel D1. Transaction cost notice Panel D2. Indemnication worksheet
(no dependents)
Panel E1. Informational yer Panel E2. Envelope message
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I use a quasi-experimental design to estimate the burden of complying with the tax code. Employing a sample of US income tax returns, I observe the preferences of taxpayers when choosing between itemizing deductions and claiming the standard deduction. Taxpayers forego tax savings to avoid the hassle cost of itemizing, resulting in an average burden of itemizing of $617, with substantial heterogeneity. A revealed preference argument implies that itemizing deductions is as painful as working 19 hours. The burden of compliance is larger for richer households, consistent with the fact that the value of time increases with income. I explore two explanations for the result. First, it could be due to an extreme aversion to filing taxes. Such aversion implies that itemizing deductions imposes an aggregate compliance cost of 0.20% of GDP and back-of-the-envelope extrapolations to filing federal taxes yields an overall compliance cost of 1.25% of GDP. Second, if taxpayers are time inconsistent the revealed preference argument fails, introducing a wedge between foregone benefits and compliance costs. Being present-biased leads taxpayers to forego large benefits even when compliance costs are relatively small. I provide evidence of taxpayers being present-biased. Both explanations – whether driven by preferences or mistakes – suggest that the burden imposed by tax compliance is significantly larger than previously estimated. I discuss policy implications of the result.
Findings An analysis of IRS data on low-income working families who received the Earned Income Tax Credit (EITC) between tax years 2000 and 2003 reveals that: ■ The number of taxpayers receiving the EITC rose to 21.4 million in 2003, up 14 percent from 2000. Changing economic conditions helped fuel a rise in the proportion of all taxpayers receiving the EITC, from 15 percent to 17 percent. Of 122 large cities studied, 113 experienced at least a one-half percentage point rise in the share of their taxpayers earning the credit. ■ In 2003, the average EITC recipient earned a credit of $1,788, and EITC dollars accounted for 68 percent of recipients' net tax refunds. The extension of a portion of the Child Tax Credit to lower-income working families beginning in 2001 increased total tax refunds for EITC recipients. Among cities, the average EITC ranged from just over $1,200 in Cambridge, MA, to nearly $2,300 in McAllen, TX. ■ The proportion of EITC recipients who filed their returns through paid tax prepar-ers increased from 65 percent in 2000 to 71 percent in 2003. Cities and suburbs in the New York area experienced a dramatic 15 percentage point rise in the average share of their EITC earners using paid preparers. By contrast, fewer than 2 percent of EITC recipients nationwide accessed a free volunteer return preparation program to file their taxes in 2003, although programs in Tulsa, OK; Albuquerque, NM; Minneapolis-St. Paul, MN; and other cities reached higher proportions of recipients.
The daunting complexity of important financial decisions can lead to procrastination. We evaluate a low-cost intervention that substantially simplifies the retirement savings plan participation decision. Individuals received an opportunity to enroll in a retirement savings plan at a pre-selected contribution rate and asset allocation, allowing them to collapse a multidimensional problem into a binary choice between the status quo and the pre-selected alternative. The intervention increases plan enrollment rates by 10 to 20 percentage points. We find that a similar intervention can be used to increase contribution rates among employees who are already participating in a savings plan.