Content uploaded by Saurabh Bhargava
Author content
All content in this area was uploaded by Saurabh Bhargava on Jun 10, 2016
Content may be subject to copyright.
American Economic Review 2015, 105(11): 3489–3529
http://dx.doi.org/10.1257/aer.20121493
3489
Psychological Frictions and the Incomplete Take-Up of
Social Benets: 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 benets with an IRS eld experiment. We speci-
cally assess the inuence 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-
plication, and the heightened salience of benets 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
benets 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).
1
The consequences of incomplete take-up
can be signicant. The typical EITC non-claimant forgoes an estimated $1,096,
1
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.
utexas.edu). This paper was originally circulated as Bhargava’s job market paper with the title “Why Are Benets
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
Kszegi, 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 http://dx.doi.org/10.1257/aer.20121493 to visit the article page for additional materials and author
disclosure statement(s).
3490 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
equivalent to 33 days of income.
2
These non-claimants sacrice 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”
3
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 benet—discourage applications from
those of low economic need, then such barriers may be efcient. 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
benets fail to claim.
Economic models have traditionally recognized three types of costs that might
deter take-up: the transaction costs of applying for a benet, 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 benets of claiming due to cognitive,
motivational, or emotional limits to decision-making. In the context of benet 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 Shar 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 signicant increase in the take-up of an
inuenza 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 reect a failure of policy to deliver benets
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
2
Estimates of expected benet 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.
3
Statement retrieved in 2014 from http://www.irs.gov/uac/Paulson,-IRS-Launch-Campaign-to-Help-Low-
Income-Taxpayers-Take-Advantage-of-Tax-Credit,-Free-Tax-Help.
3491
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 benets,
for many, are substantial. Specically, we strategically modied 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 dene 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 inuence
program take-up. All told, we informed individuals of $26 million in unclaimed
government benets, 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 dened, 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,
simplication, either through a visually more appealing notice, or a shorter work-
sheet in which select eligibility screens satised by all recipients are eliminated,
signicantly raised take-up from 0.14 (control mailing) to 0.23. Displaying the
3492 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
generic range of potential benets in the headline of the simplied notice further
improved take-up from 0.23 to 0.31. Intriguingly, the inuence of benet infor-
mation was not monotonically related to the magnitude of the benet 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 simplication 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 inuencing beliefs about eligibility and benet 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 signicant 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 reects
a failure to deliver benets to those who value the benets 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 benet 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 benet, is less likely to have a
qualied dependent, and is less likely to have used a tax preparer (Plueger 2009). To
3493
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 benet 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, identied several of the same
mechanisms implicated in our study—misperceptions of eligibility and confusion
about program rules.
Beyond the signicance of these results for policy, our ndings have implications
for the literature on benet take-up (see Currie 2006 for a review).
4
The outsized
inuence of small and largely noninformational changes to program mailings is
difcult to explain with economic models in which individuals are assumed to sen-
sibly weigh accurately perceived costs and benets 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 reect 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 Shar 2006), limits to self-control (e.g.,
O’Donoghue and Rabin 1999) or other cognitive resources (e.g., Mullainathan and
Shar 2013), or because of heuristic-choice strategies of the sort that have been
suggested as explaining inefcient 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.
5
We nd that the very basic, and consequential, decision
of claiming an owed benet 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
4
This literature has traditionally stressed the detrimental role of social stigma (e.g., Moftt 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 benet 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., Duo and Saez 2003).
5
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).
3494 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
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.”
6
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—specic to one’s number of qual-
ied dependents and ling status. Credit eligibility requires a valid Social Security
number, earned income below a specied threshold, minimal investment income,
and a failure to have been excluded from the program due to past negligence. Having
met these criteria, benet 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
qualied dependents—based on a complicated set of relationship, age, and resi-
dency tests—command larger credits of up to $5,667 (gures reect 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 benet 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 qualied dependents must
le a 1040(A/EZ) and indicate their benet amount or simply write “EIC” when
prompted. In the case of qualied dependents, eligible individuals must le a 1040(A)
along with a supplementary, one-page, tax addendum called the Schedule EIC.
7
The
rst two columns of Table 1 describe the average benet 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 qualied dependents and $259 for those without). This compares to a typical
estimated benet 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 qualied
dependent and 56 percent of single lers were female (Plueger 2009).
6
Quotation cited from a 1975 Senate Committee Report.
7
Claimants must le a tax return even if they fall below the ling requirement income threshold.
3495
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
US CA US CA
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 benet (if > $0)$2,185 $2,165 $412 $415 $511 $288 $838
Benet w/o qualied dependents $2,770 $1,870 $1,528 $1,535
Benet w/ qualied 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
jointly
0.26 0.30 0.26 0.25 0.27 — —
Filing status = head of
household
0.47 0.41 0.12 0.14 0.15 — —
Share with qualied
dependents
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
jointly
0.26 0.30 0.25 0.20 0.20 — —
Filing status = head of
household
0.47 0.41 0.07 0.08 0.09 — —
Share with qualied
dependents
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 benet across each
sample. Some of the gures are estimated from author calculations.
3496 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
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 difcult. The difculty stems
from the unknown rate of ineligible claiming, the presence of unobservable factors
that determine eligibility, such as qualied 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 condence interval of 73 percent to 77 percent), including 56 percent for those
without qualied dependents and 81 percent for those with at least one such depen-
dent (Plueger 2009).
8
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).
9
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 benet 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).
10
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.
11
However, Plueger (2009) points out that the lters
may also screen out some fraction of eligible ling non-claimants.
12
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
8
Plueger’s estimate is based on an exact match of tax records and census data. Specically 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.
9
As Plueger (2009) notes, the Scholz (1994) analysis was both for a period in which apparently eligible, ling
non-claimants were automatically mailed a benet by the IRS, and in which there was no credit for those without a
qualied dependent (a group with presumably lower take-up).
10
These gures are estimated for 2004 and are included in a 2007 Health and Human Services report to
Congress available at http://aspe.hhs.gov/hsp/indicators07/report.pdf.
11
“CP” refers to “Computer Paragraph” and denotes the varied missives that the IRS routinely sends to taxpay-
ers after a tax ling.
12
See Plueger (2009) for a discussion of the divide between eligible ling non-claimants and those receiving the
CP notication, and specically 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 veried). We obtained further details of this accounting from interviews with D. Plueger (August 2011).
3497
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
one-page (single or double-sided, depending on the inferred presence of qualied
children) worksheet conrms eligibility into the program with a series of screening
statements. Those who sign and return the worksheet, if approved, receive a benet
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.
13
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 benet ($511 versus
$2,185). This difference was due to a lower average benet 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 signicant difference in benet 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 benets for EITC claimants and non-claimants, estimated
from Plueger (2009), as well as for the experimental sample.
13
Author calculations from internal statistics from the IRS.
Claimants
Non-claimants
Experiment
Claimants
Non-claimants
Experiment
Claimants
Non-claimants
Experiment
Claimants
Non-claimants
Experiment
Claimants
Non-claimants
Experiment
0.0
0.1
0.2
0.3 0.31
0.21
0.14
0.05
0.15 0.12
0.05 0.04
0.12
0.04 0.04
0.05
0.25
0.62
0.81
0.4
0.5
0.6
0.7
0.8
0.9
1. 0
Percent share
$0
to $999
$1,000
to $1,999
$2,000
to $2,999
$3,000
to $3,999 >$4,000
F 1. B D EITC C E N-C
Notes: This gure compares the distribution of EITC benets 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.
3498 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
II. Research Design
A. Experimental Sample
The sample for the eld experiment consists of individuals from California who
satisfy the following conditions.
14
First, the taxpayer led a tax return for TY 2009
but failed to claim an EITC credit. Second, the taxpayer satised 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
14
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
3499
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-
et 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.
15
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.
16
The notice informed
the recipient of possible program eligibility, briey explained the purpose of the
15
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.
16
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
Eliminated
returns
Remaining
returns
Incremental steps
Step
share
Overall
share
Overall
share
Overall
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
address
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.
3500 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
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
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
3,676
Complexity (length)2. Complex worksheet Relative to simple worksheet, complex
worksheet includes additional,
nondiscriminatory, questions regarding
eligibility
10,979
Program information
Benet and cost
information
1. Benet display (low
and high)
Simple notice reports upper bound of
potential benet (up to “$457,” “$3,043,”
“$5,057,” or “$5,567”)
6,761
2. Transaction cost (low
and high)
Simple notice provides guidance as to
worksheet completion time (less than 10 or
60 minutes)
3,475
Penalty/audit
information
1. Indemnication
message
Bold message on worksheet indemnies
against penalty for unintentional error
17,027
General program
information
1. Envelope message Envelope message indicates that enclosure
communicates “good news”
17,044
2. Informational yer One page yer offers program information
and trapezoidal benet schedule
4,019
Stigma
Personal stigma
reduction
1. Emphasis on earned
income
Simple notice emphasizes that credit is
earned reward for hard work
1,844
Social stigma reduction 2. Social inuence Simple notice communicates that similarly
situated peers are also claiming
1,753
3501
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 simplied notice (“simple worksheet,” Appendix Figure,
panel B1).
17
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 satised. Specically, 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., simplied) 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-
ets of claiming inuenced take-up. First, we investigate the inuence of benet
information by prominently reporting the upper bound of one’s potential benet (we
did not receive permission to print the exact gure) in the headline of the simplied
control notice (“benet display”). Subjects in this treatment arm received a notice
indicating eligibility for a benet “… 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 benets, for subjects in this treatment
with either one or two dependents, we additionally randomized the amount reported
to either reect the maximum dependent specic benet (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 specic 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 (“indemnication
17
The simplied 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.
3502 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
message”): “Complete to the best of your ability—you will NOT be penalized for
unintentional errors.” (Appendix Figure, panel D2).
Fourth, to test the inuence 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 benet 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 benet 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-
ets”) (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 benet 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.
18
Stigma Interventions.—A nal set of interventions tests whether program stigma
inuences response. While early economic models of take-up featured the costs
of social stigma (Moftt 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 benet 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 benets
(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 dened 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
18
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.
3503
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
minimize experimental variance and produce more efcient 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 benet display notices were over-sampled
(×3) to power tests of differentiation across listed benet 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, benet
size, ling status, and past EITC claiming behavior (online Appendix Table A3).
19
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 benets 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 benet 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 benet 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. Specically,
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
19
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 benet levels, ling status, and past claiming. Overall, the analysis reported in the table suggests
that the treatments were successfully randomized (online Appendix Table A3).
3504 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
in-person to 1139 clients at several low-income tax clinics primarily in Chicago
from February to April 2011.
20
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 reected 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 qualied 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 benet 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 notication. The overall response to the mailing is 0.22
with an average disbursed benet 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
20
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
Response
Benet
size Deny Response
Benet
size Response
Benet
size
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
(Control)
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 benet size, and denial rate for the CA CP sample and
experimental samples of interest. To ensure a sufcient 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 specic response data is not available for the CP Notice.
3505
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
with a signicant increase in denied claims.
21
The estimated benet 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
benets. 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.
22
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 indemnication messages). The comparison suggests a large net positive
effect of simplication 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
21
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 notication
had been triggered, or if a qualied dependent was claimed by another party and such a claim altered the recipient’s
eligibility.
22
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
3,000
2,000
1,000
0
−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.
3506 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
additional response appears due to the modications reected in specic 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.
23
One
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.
24
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 coefcient 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 condence inter-
vals, as calculated from column 1. While the comparisons summarized in the table
were all preplanned, we note that the ve strongly signicant interventions reported
in the rst column survive a Bonferroni correction for multiple comparisons at a
family-wise alpha of 0.05.
23
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.
24
We were unable to obtain information on the rate of returned mail for either the initial notice or the experi-
mental mailings.
3507
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)
Full
sample Controls
No
dependents
with
dependents p-value
Full
sample Controls
(1) (2) (3) (4) (5) (6) (7)
[Simple notice, simple worksheet, plain envelope: excluded]
Complexity
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
Benet 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%]
Indemnication 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%]
Stigma
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 benet 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 signicance of
interventions in the specied categories. Errors are robust with standard errors clustered at each zip code.
*** Signicant at the 1 percent level.
** Signicant at the 5 percent level.
* Signicant at the 10 percent level.
3508 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
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 signicantly 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).
Complexity
Program information
Stigma
23%
−6%
−
4%
−
4%
−
4%
−
1% +0%
−
1%
−
1%
+8%
Response rate
Experimental intervention
Control mailing
Complex notice
Complex worksheet
Benet display
Transaction cost display
Indemnication
Informational yer
Envelope message
Personal stigma
Social stigma
0.35
0.30
0.25
0.20
0.15
0.10
0.05
0.00
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 reects response averaged across the envelope and indemnity treatments.
3509
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 benets 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 signicantly 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 signicantly 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 benets and costs
Intervention
Subjective
complexity
rating
(0–100)
Carefully
read?
(self-report)
(0 –100)
Compre-
hension
question
(1,0)
Perceived
eligibility
%
(0 –100)
Expected
benet
size
(ln $, if > 0)
WTP
preparer
($)
Respect
for
claimants?
(0 –100)
Perceived
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 benet 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 benet 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 benet 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 inuence 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.
*** Signicant at the 1 percent level.
** Signicant at the 5 percent level.
* Signicant at the 10 percent level.
3510 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
to which individuals attended to, and understood, program information. Beliefs
of program eligibility, in particular, appeared sensitive to the complexity of the
worksheet.
Informational Interventions.—Among treatments that provided information,
the display of benet information was the most potent. The inclusion of a benet
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 benet 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 benet
display was not tied to the benet 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
Benet display
(
with dependents
)
Baseline $457
Benet display
(
without dependents
)
0.45
0.40
0.35
0.30
0.25
0.20
0.15
0.10
0.05
0.00
+9%
27%
16%
+13%
+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 Benet 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,
respectively).
3511
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
$5,657 ( p < 0.01) displays. Those without dependents randomized into the benet
display treatment ($457) also exhibited a large and statistically signicant increase
in response, relative to the control, of 0.08 ( p < 0.01).
The remaining informational interventions did not signicantly 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 inuence
of the two cost displays (60 and 10 minutes) cannot be distinguished. The
one-page informational yer, which includes a benet 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 signicant effect on
behavior.
Mechanisms: Table 6 suggests at least two channels through which the benet
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 benets twice as large as the control con-
dition. Second, while the low display ($457) did not signicantly alter expecta-
tions of benet size, it did signicantly elevate belief of eligibility by 24 percent.
Given beliefs of benet size and eligibility are both sensitive to the benet 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 inu-
ence beliefs across these two margins (i.e., “If the benet 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 benets. 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 benet size. These patterns
raise the possibility that the yer signicantly 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 inuence on
3512 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
response in the eld could be due to the treatment not sufciently shifting recipient
beliefs.
25
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 inuence 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 signicant), 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
intervention.
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
25
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.
3513
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
t + 1, given the failure to take-up in period t.
26
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-
nicantly 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
26
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)
OLS IV
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 specied 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 benet size, and earned income. Errors are robust.
*** Signicant at the 1 percent level.
** Signicant at the 5 percent level.
* Signicant at the 10 percent level.
3514 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
claiming decision for the specied 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 identication 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 inuence 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. Benet and income
Expected benets: $0 to $499 0.24 26,988 0.25 23,618 0.15 3,370
Expected benets: $500 to $1,499 0.18 2,708 — — 0.18 2,708
Expected benets: $1,500 to $2,499 0.17 1,701 — — 0.17 1,701
Expected benets: $2,500 to $3,999 0.15 2,259 — — 0.15 2,259
Expected benets: ≥ $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 benet/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 benet size and earned income. Not all
subcategories sum to 35,050 due to either missing data or excluded subcategories.
3515
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 reects 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
$0
0.00
0.02
0.04
0.06
0.08
0.10
0.12
0.14
0.16
0.18
0.20
0.22
0.24
$5,000
$10,000
$15,000
$20,000
$25,000
$30,000
$35,000
$40,000
$45,000
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.
3516 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
F 7. R H B S, G, A
Notes: This gure shows heterogeneity in experimental response by estimated benet size, gender, and age. Each
panel reports marginal effects by intervention for the specied 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 signicant between-group differences, estimated separately from pooled
regressions.
Panel A. Response heterogeneity by benet size
(lers with dependents, low benet: < $678, high benet: >= $678)
Low High Low High Low High Low High Low High Low High Low High Low High Low High
−0.08
−0.06
−0.04
−0.02
0.00
0.02
0.04
0.06
0.08
Marginal effect on response
−0.04
−0.07
−0.04
−0.01
−0.02
−0.04
−0.02 −0.02
−0.05
−0.04
−0.01
0.00 0.00 0.00
0.00
0.01
0.07
0.06
Complex
notice
Complex
WS
Benet
display
Cost
display Flyer
Envelope
message
Indemnity
message
Personal
stigma
Social
inuence
p < 0.10
Male
Female
Male
Female
Male
Female
Male
Female
Male
Female
Male
Female
Male
Female
Male
Female
Male
Female
Complex
notice
Complex
WS
Benet
display
Cost
display Flyer
Envelope
message
Indemnity
message
Personal
stigma
Social
inuence
−0.08
−0.10
−0.06
−0.04
−0.02
0.00
0.02
0.04
0.06
0.08
0.10
Marginal effect on response
p < 0.05 p < 0.01
−0.09
−0.05
−0.07
−0.04
0.07
0.09
−0.03
0.00
−0.05
−0.04
−0.02
−0.01
0.01
0.00
−0.05
−0.06
−0.03
0.02
p < 0.05
Panel B. Response heterogeneity by gender (single lers only)
Young
Old
Young
Old
Young
Old
Young
Old
Young
Old
Young
Old
Young
Old
Young
Old
Young
Old
−0.10
−0.08
−0.06
−0.04
−0.02
0.00
0.02
0.04
0.06
0.08
0.10
Marginal effect on response
Complex
notice
Complex
WS
Benet
display
Cost
display Flyer
Envelope
message
Indemnity
message
Personal
stigma
Social
inuence
−0.06
−0.07
−0.05 −0.05
0.07
0.10
−0.02
−0.01 −0.01 −0.01 −0.01
−0.03
−0.05
0.01 0.01
0.00
−0.03
−0.05
Panel C. Response heterogeneity by age (single lers only, Young: < 39 years, Old: >= 39 years)
3517
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
with dependents in order to examine a wide range of recipient incomes.
27
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 beneted more from simplied notices
than did recipients with higher incomes. Specically, 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).
28
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 benet level, gender, and median age—and report
these in Figure 7. We conne the analysis of gender and age to single lers for the
purpose of identication. 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 benet 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.
29
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 signicant,
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.
30
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 reecting costs of claiming—that is, those associated with time, effort, stigma,
and potential penalties—which outweigh program benets. However, the responses
documented in the eld study, and mechanisms implied from the survey, are difcult
27
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.
28
We nd similar results when explicitly controlling for the cross-randomized envelope and worksheet inter-
ventions and demographic controls.
29
Specically, 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, benet, and demographic variables. θ
ˆ is the statistic of
interest.
30
Adapting the main response model by including an interaction between the messaged envelope and Hispanic
household density produces a statistically signicant and positive interaction coefcient, 0.030 ( p < 0.10). The
sum of the interaction coefcient and the coefcient for the envelope indicator is positive but insignicant.
3518 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
to rationalize in a traditional model of take-up in which eligible individuals balance
accurately perceived expectations of benets and costs, even allowing for the pos-
sibility of program stigma. In particular, the eld experiment afrms 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 simplied notice,
shortened worksheet, and even omission of the informational yer) or changes to
its salience (e.g., benet 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 inuenced decisions by heightening awareness and remedying confusion with
respect to eligibility and benet size (possibly by increasing the attention paid to the
mailings), but not by signicantly 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 benets of claiming, but suffer
from distorted beliefs as to the magnitudes of such costs and benets. However, the
relatively modest baseline assessments of claiming costs from the surveys, and the
further fact that the substantial inuence 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 insufcient for explaining the low
take-up observed in this setting.
31
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 Shar (2006), the framework explains how seemingly minor details can inu-
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
task.
32
With respect to program take-up, rather than deciding to claim after careful
evaluating expected costs and benets, 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 inuence 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 Grifn 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
31
Given survey respondents had inated beliefs of the likelihood of an audit, if the indemnication 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.
32
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.
3519
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
lead to signicant changes in behavior, the ndings of the study may also reect
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 Shar 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 difculty 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 decits in program awareness and misperceptions regarding pro-
gram benets 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.
33
The survey also provides novel evidence that individuals systematically
under-estimate eligibility and the magnitude of program benets. 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 benets was 0.8, 61 percent under-
estimated benet size, and 41 percent under-estimated benet 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
33
We did not elicit the full set of information required to determine exact eligibility and benet size such as
investment income or an invalid Social Security number. For the large majority of individuals, our inferences
regarding eligibility and benet size should be accurate.
3520 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
evidence that respondents viewed benet receipt as stigmatizing.
34
Overall the sec-
ond survey documents low program awareness, a signicant degree of under-esti-
mation of eligibility and benet 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 qualied dependents (57 percent) but
has higher income (median: ~$13,000). More tellingly, the sample includes a sig-
nicant 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 insufcient size of benets, 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.
34
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 benet, 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 benet. We interpret this as indicating a small to moderate share of individuals who
may nd the program to be stigmatizing.
3521
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 reect 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 benet 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 efcacious notice would yield 73,908
(simple mailing) to 99,615 (benet 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
nonrespondents
Revised rst mailing
all CP recipients
Revised rst mailing
all tax ling non-claimants
Mailing type Response Benet Observations
Response
(Δ take-up)
[$Benets]Observations
Response
(Δ take-up)
[$Benets]Observations
Response
(Δ take-up)
[$Benets]
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]
Benet 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]
Benet 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 reected by the given projection. We project results for the
simple mailing (i.e., simple notice and worksheet), the simple mailing with benet display (with simple worksheet),
and the benet display plus a second mailing (also a benet 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.
3522 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
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 benets.
35
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 benets) 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 (Benet 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 benets. We parenthetically report
the increase in overall program take-up implied by these projections. These calcu-
lations reveal a sizable benet 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 benets, to the
redesigned mailings.
B. Cost-Benet 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 benets 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
35
For example, we project the response to the simplied 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.
3523
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 signicant for the total cost of
the interventions to signicantly exceed the modest costs of administration.
Benets of the Program.—One could gauge the social benets 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 beneciaries. 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, simplied, notice. To achieve budget neutrality, we proportion-
ally reduce the benets 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 benets 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
50k
100k
150k
Projected claimants
0
0
Adjusted gross income
$10k $20k $30k $40k $50k0
50 m
40 m
30 m
20 m
10 m
0 0
0.05
0.1
0.15
Projected transfers
($millions)
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 simplied 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, simplied, 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).
3524 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
leveraged the ndings of the study, even under budget neutrality, would be likely to
improve welfare.
36
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 benets. 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 benet 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 decits 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 identication numbers were issued from 1999 to 2010—has
led to signicant 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 identied 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
36
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.
3525
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
need do not receive intended benets. Second, our evidence is not easily rational-
ized by a simple cost-benet 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 specic 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)
3526 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
Panel C1. Benet display (high)Panel C2. Benet display (low)
For IRS use only
–
Code
WS
4
.
.
.
.
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)
3528 THE AMERICAN ECONOMIC REVIEW NOVEMbER 2015
REFERENCES
Benzarti, Youssef. 2015. “How Taxing is Tax Filing? Leaving Money on the Table Because of Compli-
ance Costs.” http://ssrn.com/abstract=2412703.
Bertrand, Marianne, Dean Karlan, Sendhil Mullainathan, Eldar Shar, and Jonathan Zinman. 2010.
“What’s Advertising Content Worth? Evidence from a Consumer Credit Marketing Field Experi-
ment.” Quarterly Journal of Economics 125 (1): 263–306.
Bertrand, Marianne, Sendhil Mullainathan, and Eldar Shar. 2006. “Behavioral Economics and Mar-
keting in Aid of Decision Making among the Poor.” Journal of Public Policy and Marketing 25 (1):
8–23.
Berube, Alan. 2006. “The New Safety Net: How the Tax Code Helped Low-Income Working Families
During the Early 2000s.” The Brookings Institution Metropolitan Policy Program, Survey Series.
http://www.brookings.edu/metro/pubs/eitc/20060209_newsafety.pdf.
Beshears, John, James J. Choi, David Laibson, and Brigitte C. Madrian. 2013. “Simplication and
Saving.” Journal of Economic Behavior and Organization 95: 130–45.
Bettinger, Eric P., Bridget Terry Long, Philip Oreopoulos, and Lisa Sanbonmatsu. 2012. “The Role
of Application Assistance and Information in College Decisions: Results from the H&R Block
FAFSA Experiment.” Quarterly Journal of Economics 127 (3): 1205–42.
Bhargava, Saurabh, George Loewenstein, and Justin Sydnor. 2015. “Do Individuals Make Sensible
Health Insurance Decisions? Evidence from a Menu with Dominated Options.” National Bureau of
Economic Research Working Paper 21160.
Bhargava, Saurabh, and Dayanand Manoli. 2015. “Psychological Frictions and the Incomplete
Take-Up of Social Benets: Evidence from an IRS Field Experiment: Dataset.” American Eco-
nomic Review. http://dx.doi.org/10.1257/aer.20121493.
Blumenthal, Marsha, Brian Erard, and Chih-Chin Ho. 2005. “Participation and Compliance with the
Earned Income Tax Credit.” National Tax Journal 58 (2): 189–213.
Chetty, Raj, John N. Friedman, and Emmanuel Saez. 2013. “Using Differences in Knowledge across
Neighborhoods to Uncover the Impacts of the EITC on Earnings.” American Economic Review 103
(7): 2683–2721.
Chetty, Raj, Adam Looney, and Kory Kroft. 2009. “Salience and Taxation: Theory and Evidence.”
American Economic Review 99 (4): 1145–77.
Chetty, Raj, and Emmanuel Saez. 2013. “Teaching the Tax Code: Earnings Responses to an Experi-
ment with EITC Recipients.” American Economic Journal: Applied Economics 5 (1): 1–31.
Choi, James J., David Laibson, and Brigitte C. Madrian. 2009. “Reducing the Complexity Costs of
401(k) Participation through Quick Enrollment.” In Developments in the Economics of Aging,
edited by David A. Wise, 57–82. Chicago: University of Chicago Press.
Cialdini, Robert B. 1989. “Social Motivations to Comply: Norms, Values, and Principles.” In Taxpayer
Compliance, Vol. 2, edited by Jeffrey A. Roth and John T. Scholz, 200–27. Philadelphia: University
of Pennsylvania Press.
Cialdini, Robert B., and Noah J. Goldstein. 2004. “Social Inuence: Compliance and Conformity.”
Annual Review of Psychology 55: 591–621.
Crocker, Jennifer, Brenda Major, and Claude Steele. 1998. “Social Stigma.” In Handbook of Social
Psychology, Vol. 2, edited by Daniel T. Gilbert, Susan T. Fiske, and Gardner Lindzey, 504–53. Bos-
ton: McGraw-Hill.
Currie, Janet. 2006. “The Take-up of Social Benets.” In Public Policy and the Income Distribution,
edited by Alan J. Auerbach, David Card, and John M. Quigley, 80–148. New York: Russell Sage
Foundation.
Currie, Janet, and Jeffrey Grogger. 2001. “Explaining Recent Declines in Food Stamp Program Par-
ticipation.” In Brookings-Wharton Papers on Urban Affairs, edited by William G. Gale and Janet R.
Pack, 203–44. Washington, DC: Brookings Institution Press.
Dahl, Gordon B., and Lance Lochner. 2012. “The Impact of Family Income on Child Achievement:
Evidence from the Earned Income Tax Credit.” American Economic Review 102 (5): 1927–56.
Daponte, Beth Osborne, Seth Sanders, and Lowell Taylor. 1999. “Why Do Low-Income House-
holds Not Use Food Stamps? Evidence from an Experiment.” Journal of Human Resources
34 (3): 612–28.
Duo, Esther, and Emmanuel Saez. 2003. “The Role of Information and Social Interactions in Retire-
ment Plan Decisions: Evidence from a Randomized Experiment.” Quarterly Journal of Economics
118 (3): 815–42.
Ebenstein, Avraham, and Kevin Stange. 2010. “Does Inconvenience Explain Low Take-up? Evidence
from Unemployment Insurance.” Journal of Policy Analysis and Management 29 (1): 111–36.
3529
Bhargava and manoli: psychological frictions and take-up
vol. 105 no. 11
Eissa, Nada, and Hilary Hoynes. 2011. “Redistribution and Tax Expenditures: The Earned Income Tax
Credit.” National Tax Journal 64 (2): 689–729.
Engel, Eduardo M. R. A., and James R. Hines, Jr. 1999. “Understanding Tax Evasion Dynamics.”
National Bureau of Economic Research Working Paper 6903.
Ericson, Keith Marzilli, and Amanda Starc. 2012. “Heuristics and Heterogeneity in Health Insurance
Exchanges: Evidence from the Massachusetts Connector.” American Economic Review 102 (3):
493–97.
Finkelstein, Amy. 2009. “E-ZTax: Tax Salience and Tax Rates.” Quarterly Journal of Economics 124
(3): 969–1010.
Gilovich, Thomas D., and Dale W. Grifn. 2010. “Judgment and Decision Making.” In Handbook
of Social Psychology, Vol. 1, edited by Susan T. Fiske, Daniel T. Gilbert, and Gardner Lindzey,
542–88. Hoboken: John Wiley & Sons, Inc.
Hastings, Justine S., and Jeffrey M. Weinstein. 2008. “Information, School Choice, and Academic
Achievement: Evidence from Two Experiments.” Quarterly Journal of Economics 123 (4):
1373–1414.
Hoynes, Hilary, Doug Miller, and David Simon. 2015. “Income, the Earned Income Tax Credit, and
Infant Health.” American Economic Journal: Economic Policy 7 (1): 172–211.
Internal Revenue Service. 2003. Earned Income Tax Credit (EITC) Program Effectiveness and Pro-
gram Management FY 2002–FY 2003. Washington, DC: US Department of Treasury.
Jones, Damon. 2010. “Information, Preferences, and Public Benet Participation: Experimental Evi-
dence from the Advance EITC and 401(k) Savings.” American Economic Journal: Applied Eco-
nomics 2 (2): 147–63.
Karlan, Dean, Margaret McConnell, Sendhil Mullainathan, and Jonathan Zinman. 2015. “Getting to
the Top of Mind: How Reminders Increase Saving.” National Bureau of Economic Research Work-
ing Paper 16205.
Kling, Jeffrey R., Sendhil Mullainathan, Eldar Shar, Lee C. Vermeulen, and Marian V. Wrobel. 2012.
“Comparison Friction: Experimental Evidence from Medicare Drug Plans.” Quarterly Journal of
Economics 127 (1): 199–235.
Lewin, Kurt. 1951. Field Theory in Social Science: Selected Theoretical Papers. New York: Harper
and Row.
Liebman, Jeffrey B., and Erzo F. P. Luttmer. 2015. “Would People Behave Differently If They Bet-
ter Understood Social Security? Evidence from a Field Experiment.” American Economic Journal:
Economic Policy 7 (1): 275–99.
Liebman, Jeffrey B., and Richard J. Zeckhauser. 2004. “Schmeduling.” Unpublished.
Madrian, Brigitte C., and Dennis F. Shea. 2001. “The Power of Suggestion: Inertia in 401(k) Participa-
tion and Savings Behavior.” Quarterly Journal of Economics 116 (4): 1149–87.
Manchester, Colleen F., and Kevin J. Mumford. 2010. “How Costly is Welfare Stigma? Separating
Psychological Costs from Time Costs.” Purdue University, Krannert School of Management Work-
ing Paper 1229.
Milkman, Katherine L., John Beshears, James J. Choi, David Laibson, and Brigitte C. Madrian. 2011.
“Using Implementation Intentions Prompts to Enhance Inuenza Vaccination Rates.” Proceedings
of the National Academy of Sciences 108 (26): 10415–420.
Moftt, Robert. 1983. “An Economic Model of Welfare Stigma.” American Economic Review 73 (5):
1023–35.
Mullainathan, Sendhil, and Eldar Shar. 2013. Scarcity: The New Science of Having Less and How It
Denes Our Lives. New York: Picador.
O’Donoghue, Ted, and Matthew Rabin. 1999. “Doing It Now or Later.” American Economic Review
89 (1): 103–24.
Plueger, Dean. 2009. “Earned Income Tax Credit Participation Rate for Tax Year 2005.” Internal Reve-
nue Service Research Bulletin. http://www.irs.gov/pub/irs-soi/09resconeitcpart.pdf.
Saez, Emmanuel. 2009. “Details Matter: The Impact of Presentation and Information on the Take-Up
of Financial Incentives for Retirement Saving.” American Economic Journal: Economic Policy
1 (1): 204–28.
Scholz, John Karl. 1994. “The Earned Income Tax Credit: Participation, Compliance, and Antipoverty
Effectiveness.” National Tax Journal 47 (1): 63–87.
Smeeding, Timothy M., Katherin Ross Phillips, and Michael O’Connor. 2000. “The EITC: Expec-
tation, Knowledge, Use, and Economic and Social Mobility.” National Tax Journal 53 (4):
1187–1209.
