Welfare stigma in the lab: Evidence of social signaling∗
Jana Friedrichsen
Tobias König
Renke Schmacker
November 24, 2016
Abstract
A puzzle of the modern welfare state is that a large fraction of social benefits is not
taken up. Using a laboratory experiment, we present evidence that stigmatization through
public exposure causally reduces the take-up of a redistributive transfer by 30 percentage points. We build a theoretical model that interprets welfare stigma as unfavorable
inferences about the claimant’s type. Our design exogenously varies the informativeness
of the take-up decision by varying whether transfer eligibility is based on ability or luck.
We find that subjects avoid the inference both of being low-skilled and of being willing to
live off others. Contrary to conventional wisdom, stigma may thus also contribute to low
take-up if eligibility is not linked to economic performance.
JEL-codes: D03, H31, I38, C91
Keywords: stigma, signaling, redistribution, non take-up, welfare program
∗
We thank Dirk Engelmann, Dorothea Kübler and seminar participants in Berlin for helpful comments.
The paper has also profited from discussion with conference participants at ESA 2016 (Bergen) and the “Arne
Ryde Workshop on Identity, Image and Economic Behavior, Image” (Lund). We gratefully acknowledge financial support from the Deutsche Forschungsgemeinschaft (DFG) through SFB 649.
Friedrichsen: DIW and Humboldt-Universität zu Berlin, jana.friedrichsen[at]hu-berlin[dot]de; König:
WZB and Humboldt-Universität zu Berlin, tobias.koenig[at]hu-berlin[dot]de; Schmacker: DIW,
rschmacker[at]diw[dot]de
1
1
Introduction
A puzzling observation in modern welfare states is that a large fraction of welfare benefits
is not taken up. For a number of important welfare programs, such as income transfers,
nutritional assistance, and social housing, many eligible individuals fail to claim their benefits
– even if this comes with severe negative consequences for present and long-term life outcomes
(e.g., Currie, 2006). Social scientists and policymakers regularly relate incomplete welfare
take-up to the negative attitudes that society may have toward welfare-claimants – an idea
that has been incorporated into many economic models, including prescriptive and normative
analyses of public policy (Besley and Coate, 1992; Yaniv, 1997; Lindbeck et al., 2003; Blumkin
et al., 2015).
Despite the wide usage of the term, evidence of the effects of welfare stigma on take-up
behavior is very scarce (for surveys see, e.g., Andrade, 2002; Currie, 2006). One reason it is
difficult to analyze stigma in a natural setting is data availability. In particular, it is hard
to know who is eligible but is not claiming a transfer, and even if such individuals can be
identified information about their motivations is typically scarce. Without such information,
stigma can typically not be disentangled from information or transaction costs so that the
“stigma hypothesis” is difficult to refute even though other deterrents of take-up have been
identified.1
This paper is the first to investigate the stigma hypothesis in a controlled laboratory
experiment. It shows that stigma causally reduces the take-up rate of a redistributive transfer.
Moreover, we identify the channels underlying the stigma and show that the effect is not
only related to inferences about the claimants’ ability or eligibility but it also has a moral
component that may also explain why programs that are not means-tested, and thus do not
signal anything about claimants’ earnings opportunities or wealth, suffer from low take-up
rates. Our results complement recent field experimental evidence showing that information
and transaction costs partially explain low take-up rates (Bhargava and Manoli, 2015) by
demonstrating a substantial negative effect of stigma on take-up rates in the laboratory.
Incomplete take-up of welfare benefits is a well-documented phenomenon in modern welfare states (see Hernanz et al., 2004, for OECD countries). The Department of Health and
Human Services (2016) estimated that in the United States in 2013 about 69 percent of eligible individuals did not claim Temporary Assistance for Needy Families (TANF) and 37.7
percent did not claim Supplemental Security Income (SSI). For Germany, recent estimates of
non-take-up rates of social assistance lie between 40 and 50 percent, which means that for
every three welfare recipients there are two to three individuals who are eligible but do not
claim their transfers (Bruckmeier and Wiemers, 2012). Non-take-up is a problem because
welfare policies typically intend to reduce poverty or mitigate its effects on the well-being of
people. These policy objectives are impeded if eligible individuals are not reached. Moreover,
incomplete take-up may be related to individual characteristics and may therefore lead to a
reinforcement of existing inequalities. Finally, incomplete take-up may depress transfer levels,
which are calculated based on the population on non-takers (Becker, 2007). Improving the
take-up rate in means-tested welfare programs is an important policy objective, but doing so
requires an understanding of what is driving non-take-up.
1
A recent field experiment on the Earned Income Tax Credit program in the US suggests that psychological
frictions, such as low program awareness/understanding and informational complexity, contribute significantly
to the puzzle of low take-up (Bhargava and Manoli, 2015).
2
Eligibility for social assistance like food stamps, social housing, medical aid or supplementary public benefits, is often based on market income and thus depends on individuals’
performance in a competitive environment. Furthermore, these benefits are typically redistributive, that is, they transfer money from the upper and middle classes to the poor. This
may give rise to two sources of social stigmatization, which have been discussed, for instance,
by Goffman (1963) and Besley and Coate (1992): first, claiming social benefits may be a
signal of low income or ability (ability signaling), and second, it may signal that the claimant
is willing to live off others (moral signaling).2 In both cases, an eligible individual may refrain from claiming a transfer because she is afraid of how society will treat her based on the
signal. As shown in the seminal contribution by Moffitt (1983), welfare stigma need not be
related to public exposure but we argue that public exposure will likely intensify any existing
stigmatization.3 While many welfare programs require some degree of exposure in the form
of periodic check-ups or reporting requirements, there are clearly differences in exposure and
thus stigmatization across programs, which may contribute to differential take-up rates.
The empirical literature does not provide conclusive evidence regarding the role of stigma
in welfare take-up. While Andrade (2002) concludes from a review of the literature that
welfare stigma “is probably the main determinant of low take-up rates,” Currie (2006) comes
to the opposite conclusion, namely, that stigmatization is only of minor importance. The
latter position is supported by recent field experimental evidence on the take-up of earned
income tax credit (EITC) benefits in the US (Bhargava and Manoli, 2015). Interventions
targeting informational barriers to take-up and transaction costs significantly increased the
take-up rate but experimental treatments that intended to affect the perceived stigma were
ineffective. However, this may have been due to the fact that EITC is associated with relatively little stigma. Receiving an income tax credit usually remains unrecognized by social
peers, quite in contrast to more visible and stigmatized assistance such as food stamps or
public housing. Indeed, a post-experimental survey revealed that participants perceived the
stigma associated with EITC benefits to be fairly low (Bhargava and Manoli, 2015).
To complement these field studies, we designed a laboratory experiment that allows us
to explicitly affect the degree of stigmatization and provides complete information about
eligibility and take-up. Based on a simple theoretical model of welfare stigma, we propose
an empirical strategy that takes advantage of the link between welfare stigma and public
inference: we exogenously vary stigmatization by varying the degree of public exposure. If
participants decide whether to take up a transfer in private such that nobody learns about
their decision, stigmatization can only be due to self-image concerns, whereas the participant
is subject to social stigmatization if he takes up a transfer in public. In addition, we assess
the relative importance of ability and moral signaling for the total effect of welfare stigma
by varying whether transfer eligibility is related to performance in a knowledge quiz or at
random.
Our results reveal a significant and surprisingly strong stigma effect: subjects are 30
2
While the match is not perfect, our notion of ability signaling relates more closely to Besley and Coate
(1992)’ statistical stigma and our notion of moral signaling bears similarity with their concept of taxpayer
resentment. Relatedly, Stuber and Schlesinger (2006) discuss identity-related stigma as opposed to treatment
stigma. See also Rainwater (1982).
3
Yaniv (1997) argues that stigma in the form of disapproval or statistical discrimination requires public
exposure. This view may be too stark as individuals may internalize an outside spectator’s inference and feel
stigmatized even without an audience. However, it is plausible that even then stigma is higher and take-up
lower the more visible the receipt of benefits is.
3
percentage points less likely to take a public as compared to a private transfer, even though the
transfer amounts to a 50 percent increase in their payoff. When we reduce the informational
content of take-up by letting eligibility depend on luck instead of quiz performance, we still
observe a sizable and significant stigma effect. However, it is significantly lower than in the
quiz treatment, suggesting that both moral and ability signaling concerns contribute to the
observed stigma effect. Using a further treatment, where taking up transfers does not reduce
other participants’ income, we exclude possible confounds in the form of meritocratic beliefs
and transaction costs. We conclude that the observed stigma effect in our setting is driven
by approximately one-third by ability signaling and two-thirds by moral signaling.
We also address individuals’ preferences for whether the transfer should be publicly visible
by letting participants vote. Interestingly, more than half of the “taxpayers” vote against the
public transfer. This suggests that stigma effects not only affect the take-up decisions, but are
also reflected in the voting decisions: not all taxpayers want to use stigma to lower their tax
payments. Our analysis adds to a recent strand of the literature that uses incentivized laboratory experiments to investigate preferences for redistribution and taxation and their potential
interplay with social motives (see, e.g., Tyran and Sausgruber, 2006; Durante et al., 2014;
Agranov and Palfrey, 2015). In contrast to these papers, we do not investigate what determines the preference for the level of redistribution. Taking the redistributive scheme as given,
our paper provides first evidence that preferences may be sensitive to the way redistribution
is implemented, in particular, whether the transfer is paid publicly or in private.4
Our results imply that welfare stigma in the form of social signaling concerns may lead
to inefficient take-up of social assistance even if take-up is unrelated to ability or economic
performance. We provide the first causal evidence that welfare stigma indeed reduces the
take-up of welfare transfers by eligible individuals. Furthermore, we find that moral signaling
accounts for more than half of the observed effect. This suggests that welfare stigma may
also affect the take-up of universal benefits, even though the literature has so far denied the
existence of stigmatization for such schemes.5 We show that individuals may not claim a
randomly allocated benefit to avoid being perceived as social free-riders. If complete takeup of a particular social benefit is intended by the policymaker, our results suggest this
benefit should be claimed and paid out discretely. This could, for instance, mean redesigning
public waiting rooms with long waiting times, the location of public offices or the way public
letters are marked. Our results also inform the ongoing controversy about cash versus in-kind
benefits.
Governments may exploit social stigmatization to reduce the extent of welfare fraud if
individuals who are not eligible for a transfer react more sensitively to stigmatization than
those who are truly in need.6 But if the needy react more sensitively to stigmatization, as
found, e.g., in Stuber and Schlesinger (2006), a higher degree of public scrutiny may also
worsen the targeting of welfare benefits. Note also that stigmatization as found in our paper
reduces total expenditure on welfare benefits and reducing stigma may therefore increase
public expenditure.
4
As the take-up rate systematically differs between private and public, our participants indirectly decide
on the level of redistribution that is realized. Note that they have no influence on eligibility and size of the
transfer.
5
It has typically been assumed that welfare stigma is only an issue with means-tested programs, where
personal traits may be signaled to the public (Currie, 2006), but clear empirical evidence has been lacking.
6
This idea has been raised by Besley and Coate (1992) and was taken up by Blumkin et al. (2015).
4
The paper proceeds as follows. To fix our conceptual framework, section 2 develops
a theoretical model of the decision to take up a welfare transfer if social stigma is taken
into account. Based on this model, we discuss our experimental design in section 3 and
develop several testable predictions. We present our results with respect to individual take-up
decisions in section 4 and discuss individual voting behavior in section 5. Section 6 concludes.
2
A model of welfare take-up and social stigma
Suppose an individuals’ utility is given by
u(c, t, s, δ) = c + δt − δ(s + α)
where c is the level of consumption without a transfer, t is the transfer, δ ∈ {0, 1} denotes the
decision whether or not to take up a transfer if eligible, s denotes the stigma costs associated
with taking up the transfer, and α is the moral disutility associated with receiving a transfer.
This disutility may reflect attitudes with respect to earned entitlements and redistribution.
Assumption 1. Assume that α is distributed according to a distribution function F which is
continuous, differentiable, and strictly increasing over its support [0, A]. Denote the associated
density by f (·).
The stigma costs s = aRA + bRM are increasing in the extent that a take-up of the
transfer is associated with ability or moral stigma, RA ≥ 0 or RM ≥ 0,7 and the parameters
a > 0 and b > 0 are the marginal disutilities associated with ability stigma and moral stigma,
respectively.8
The ability stigma term RA captures the idea that individuals may feel stigmatized because
taking up a transfer reveals that they are less able, i.e., the decision to take up the transfer
may signal inferior ability because only less able individuals are eligible for the transfer. The
moral stigma term RM accounts for the fact that individuals may feel stigmatized because
taking up the transfer reveals that they are willing to live off others’, i.e., the take-up decision
reveals something about an individual’s moral attitude toward receiving money from others
as measured by α. We specify these stigma terms as depending on the expected deviation
from the unconditional expectation of an individual’s ability θ after observing the take-up
decision in case of ability stigma, and as a function of the difference between the unconditional
expectation of α and the expectation of an individual’s moral attitude α conditional on the
take-up decision in case of moral stigma. Both stigmata also depend on the degree of public
exposure λ. We assume there are two functions h1 (·) and h2 (·), increasing in both arguments,
such that
RA (δ, λ) = h1 (E[θ] − E[θ|δ = 1], λ)
and
RM (δ, λ) = h2 (E[α] − E[α|δ = 1], λ)
We assume that an individual will not experience stigma if she decides not to take up the
transfer or if the take-up decision remains private (λ = 0) so that RA (0, ·) = RA (·, 0) =
RM (0, ·) = RM (·, 0) = 0. Note that her private moral concerns α may still lead her to not
7
By definition, the stigma terms are always positive if some but not all individuals decide to take up the
transfer. They are null if nobody or everyone is taking the transfer.
8
Our modeling of social stigma follows the same logic as models of social image concerns in the context of
pro-social behavior: see, for instance, Benabou and Tirole (2006).
5
take up a transfer of size t in a private situation if t < α. On the other hand, take-up behavior
is informative of an individual’s ability θ and her moral attitude α if the take-up decisions are
public so that stigma exists in a public situation. As RA and RM are increasing in λ, higher
public scrutiny intensifies the feeling of being stigmatized.9
The decision of an individual with moral attitude α to take up the transfer (δ = 1) or not
(δ = 0) depends on the trade-off in utilities, and the individual will take the transfer if this
yields at least the same utility as not taking it. Denote consumption without the transfer
by c and the transfer by t. Then, for everyone claiming the transfer it must be true that
u(c + t, s, δ = 1) ≥ u(c, s, δ = 0). This is equivalent to
(1)
t ≥ aRA (λ) + bRM (λ) + α
If equation 1 is fulfilled for all α, all individuals claim the transfer independent of their
moral attitude. Similarly, if there is no α for which 1 holds, no individual will claim the
transfer. To focus on the interesting cases, we assume that the tradeoff is negative for some
α and positive for others.10 Define G(α) = t − aRA (λ) − bRM (λ) − α. We make two technical
assumptions.
Assumption 2. Assume that there exist α, α0 ∈ [0, A] such that G(α) < 0 < G(α0 ).
Assumption 3. Assume that the distribution of moral attitudes fulfills f (α) < (bα)−1 for all
α ∈ [0, A].11
Assumption 2 implies that an individual with moral attitude α̃ exists who is just indifferent
between taking up the transfer and not taking it. Assumption 3, ensures that the threshold
value determined by equation 1 is unique. Then, the trade-off in equation 1 defines a unique
cutoff value α̃ such that all individuals with α ≤ α̃ claim the transfer and those with α > α̃
do not claim the transfer.12 The implied take-up rate is given by the fraction of individuals
with a moral attitude below the threshold, i.e., F (α̃).
Proposition 1. Individual behavior is characterized by a cutoff strategy. For a cutoff value
α̃ implicitly defined by G(α̃) = 0, individuals with α < α̃ take the transfer, and individuals
with α > α̃ do not take the transfer. The take-up rate is given by F (α̃).
Proof. Suppose assumptions 2 and 3 hold. As we have also assumed that the distribution of
α is continuous, we know that the moral stigma expression is continuous, and therefore G(α)
is continuous. By Assumption 2, we find α, α0 ∈ [0, A] such that G(α) < 0 < G(α0 ). As G(α)
is defined on the closed interval [0, A], the intermediate value theorem tells us that a value
d
α̃ exists for which G(α̃) = 0. By Assumption 3, we have dα
(t − aRA (λ) − bRM (λ) − α) =
9
At this point, we do not take a stance on whether this depends on the signal about an individual’s type
from the take-up decision becoming more precise or because stigmatization is felt more intensely. In our
experimental design, we control the informativeness of the take-up decision so that publicity works exclusively
through the way individuals feel stigmatized for a given signal.
10
This is also consistent with our experimental results which show that take-up is neither zero nor complete.
See the results section below.
11
This assumption is, for instance, fulfilled if moral attitudes are uniformly distributed on [0, 1] and the
marginal utility from moral stigma is less than one, b < 1.
12
We assume that the transfer is taken up in case of indifference but, as we have assumed a continuous
distribution of types, this is immaterial to our results.
6
−b∂RM (λ)/∂α − 1 = bαf (α) − 1 < 0. Thus, the trade-off defined in equation 1 only holds
for equality at most once, and α̃ with G(α̃) = 0 is unique.
Comparative statics Using implicit differentiation, we analyze how the threshold value
and thus the take-up rate changes in response to changes in the economic trade-off. This is
the basis for our design and yields testable predictions for the analysis.
First, we find that the threshold decreases if the take-up decision is more publicly exposed.13
0 (λ)
aR0 (λ) + bRM
dα̃
=− A
<0
dλ
b∂RM (λ)/∂ α̃ + 1
Intuitively, if claiming the transfer is more exposed, the disutility from the associated stigma
weighs more heavily so that only individuals with low moral concern claim the transfer. This
threshold translates directly into the rate of take-up so that we obtain the following result
with respect to the effect of making the take-up decision public:
Corollary 1. Take-up of the transfer is lower if the decision to take up the transfer is made
public than if it is private.
Second, we find that conditional on the take-up decision being public, the threshold decreases if the decision to take-up the transfer leads to a more negative signal about the
individual’s ability, i.e., if RA (λ) (which is weakly positive) increases. Intuitively, with a
higher ability stigma, only individuals with low moral concern take the transfer so that the
moral stigma associated with take-up becomes larger.
dα̃
a
=−
<0
dRA (λ)
b∂RM (λ)/∂ α̃ + 1
This derivative is unambiguously negative because the moral stigma associated with taking
up the transfer is decreasing with α̃. The more individuals that take the transfer, the higher
the conditional expectation of their moral concern, thus, on average, the welfare claimant is
more moral and less stigmatized. If all take the transfer, the claimant does not differ in his
or her moral concern from the average population and the moral stigma is zero. Thus, we
find that the stigma effect of publicity is larger if the take-up eligibility is related to ability.
Corollary 2. The stigma effect is larger if the rank is determined by the quiz than if participants are ranked at random.
Third, some individuals may be reluctant to claim a transfer in public because they do not
want to appear to be taking other people’s money. This moral stigma, denoted by RM in the
model, depends on how morally appropriate individuals think it is that an individual who is
formally entitled to claim a transfer actually does so. We argue that the moral appropriateness
of a transfer may change with its type of financing (in particular, the degree of redistribution
involved) and with perceptions of entitlement that will differ if income differences are based on
different performance or are random. Changes in the appropriateness of taking up a transfer
are reflected in a changing distribution of α so that the take-up rate changes for a given
α̃. Denote by γ the degree of redistribution involved and by ξ the extent to which income
differences are related to performance differences. We make the following assumption:
13
The denominator is positive by Assumption 3.
7
private
public
Description
quiz
7 sessions
rank based on
quiz performance
random
7 sessions
rank determined
randomly
Description
payment automatically
contains transfer if
claimed
claimant must pick up
a yellow note at
experimenter’s desk
Table 1: Experimental design. Overview of main treatments
Assumption 4. Assume that Fγ 0 (α) ≤ Fγ (α) for all α whenever γ 0 ≥ γ.
Consider γ 0 > γ. Then for a given threshold α̃, it holds that
Fγ 0 (α̃) ≤ Fγ (α̃)
because of the first-order stochastic dominance shift in the distribution of moral concerns.
Thus, if the financing becomes more redistributive, individuals become, on average, more
morally concerned and therefore fewer individuals will claim the transfer. This also affects
the stigma effect because individuals do not want to be seen to be redistributing money to
their own advantage.
Corollary 3. The stigma effect is larger if the transfer is redistributive than if it is a subsidy.
3
Experimental design and hypotheses
In light of our theoretical model, we developed a 2 by 2 design to cleanly test whether
stigma contributes to low take-up rates, and to disentangle possible sources of stigma in the
laboratory (see Table 1). We implement possible stigmatization within-subject by varying
whether the take-up of a transfer is public or private. Furthermore, we vary the informational
content of take-up by letting eligibility depend on either ability or pure luck between-subjects.
The experiment consisted of three stages: (1) a general knowledge quiz, (2) the decision
whether to claim a transfer if eligible for both a private and a public scheme, (3) a vote
about whether the transfer should be paid out in private or in public. This design allows us
to cleanly test several hypotheses that we develop below and that are based on the model
developed in section 2.
We implement the take-up decision using the strategy method so that we obtain a decision
from each participant as to whether they ended up being eligible or not. Therefore, feedback
about the ranking was given to participants only after they had made their take-up decisions.
To be able to analyze whether take-up decisions are systematically related to expectations
about own performance or eligibility, we elicited beliefs about each participant’s performance
in the quiz directly after the quiz. Figure 1 shows the timeline of the experiment.
First, all participants took part in a multiple choice quiz with 18 general knowledge
questions. The questions were identical in all sessions.14 Participants had six minutes to
14
The translated quiz is contained as a screenshot in the appendix.
8
rank
1
2
3
A
B
16 Euro
11 Euro
6 Euro
14 Euro
10 Euro
9 Euro
Table 2: Payoffs in main treatments
deliberate their answers and could not proceed to the next stage of the experiment before
all participants had confirmed their choices. Each correctly answered question was rewarded
with one point, wrongly answered questions and no answers received zero points.
Main treatments Before taking the quiz, participants learned that they would be matched
in groups of three and that their final payoff depended on the rank within their group according
to Table 2. They were informed that it would be decided at a later stage which payment
schedule would apply.15 We implemented two treatments that varied how participants were
allocated their ranks, the quiz treatment, and the random treatment.
Participants in the quiz treatment were informed that their ranks would be determined
by the number of points achieved in the quiz. In each group, the participant with the highest
number of points was ranked first, the one with the second highest number of points second,
and the one with the lowest number third. Ties were broken randomly. Participants in the
random treatment were informed that performance in the quiz would not affect their ranks.
Instead, each participant’s rank would be (and was) determined at random.16
Participants in the quiz treatment were asked which rank they expected based on their
performance, and participants in the random treatment were asked which rank they would
expect if the ranking was based on performance (which it is not in this treatment). We did not
incentivize this belief elicitation. Participants did not receive feedback on their performance
or their rank immediately after taking the quiz but only after take-up decisions in stage 2
had been made.
treatment
quiz/random
(1)
quiz
no rank
feedback
but elicit
expected rank
(2)
rank
feedback
take-up decision
private/public
(3)
payoffs
voting
Figure 1: Timeline of the experiment.
15
The instructions for this part of the experiment did not include details regarding the second and third
stage of the experiment but only mentioned that further instructions would follow later.
16
Participants worked on the knowledge quiz irrespective of being in the quiz and random treatment. This
was to ensure that all sessions lasted the same amount of time and potential outcome differences are not driven
by differences in opportunity costs of time.
9
After the quiz, the participants received instructions for stages 2 and 3 of the experiment.
Using the strategy method, we asked each participant whether he or she wanted to claim
the transfer if they were ranked third. Whether the private or the public treatment would
be payoff-relevant was determined by one round of random-dictator voting in stage 3 of the
experiment, and participants were informed of the exact procedure in the instructions.17 The
instructions emphasized that the take-up decision was binding, i.e., in case the participant
was actually ranked at third place, the previously made decision would be executed. All
participants took two decisions; they decided sequentially, on two separate screens, whether
they wanted to claim the transfer if it was paid out in private and if it had to be claimed
publicly. The order of decisions was randomized at the group level to control for possible
order effects. When subjects decided on take-up in case of a public transfer they did not
know that there would also be a decision for a private transfer, and vice versa.18
After having decided on their take-up of the transfer conditional on being ranked third
in their group, the participants were informed of their actual rank, and thereby their actual
eligibility for the transfer payment. Then, each participant voted for their preferred payment
method, i.e., either the private or the public setting. In each group, the decision of one group
member was drawn at random and was implemented for the respective group.
Finally, our participants received feedback on their payoff, taking into account the group’s
decision about the payment method (private/public) and the take-up decision of the lowestranked group member. In groups in which the transfer was determined to be claimed in
public, and in which the member in the third rank wanted to take up the transfer in the
public setting, this particular participant had to walk through the lab to pick up a slip of
paper at the experimenter’s desk. This paper slip entitled her to receive the transfer when
receiving her experimental payment. Each participant in the third rank was informed on the
screen whether she had to pick up a paper slip or not. We ensured that all subjects who
decided to take up the transfer publicly really did so by asking for a number that was written
on the slip of paper, and the session could only continue once all public transfer claimants
had entered this number.19
Based on the previous literature and our theoretical model, we expect that public exposure
influences take-up decisions because individuals feel stigmatized if they have to publicly reveal
that they intend to claim a transfer (cf. corollary 1).
Prediction 1 (Stigma effect). Take-up rates are higher in the private setting than if the
take-up is public.20
We call the decrease in the take-up rate from private to public the stigma effect. Using
the fact that the take-up is informative of an individual’s ability only in the quiz treatment,
we predict that this treatment induces a more severe stigmatization (cf. corollary 2).
Prediction 2 (Ability signaling). The stigma effect is larger in the quiz treatment than in
the random treatment.21
17
The instructions (translated into English) and screenshots of the take-up decisions can be found in the
Appendix.
18
We do not find evidence of order effects in the take-up rates, and therefore refute the hypothesis that our
results are only driven by a demand effect. We discuss this in more detail in section 4.4.
19
In the same session, claiming the transfer could be public for some groups but private for others.
20
This means that at least one of the marginal utilities a and b in our model is positive.
21
This means that the marginal utility a of the ability signal is positive.
10
However, based on our model that includes an element of moral signaling (RM ), we expect
that a stigma effect persists even without an ability signal because individuals do not want
to be perceived as taking money from others.
Prediction 3 (Moral signaling I). A stigma effect persists in the random treatment.22
Finally, we can use the difference in the income-generating process between the quiz
and the random treatment to assess whether individuals are meritocratic. We say that an
individual has a meritocratic attitude if she honors earned entitlements, i.e., if she finds it
more morally acceptable to claim a transfer if the income is based on luck than if it is based
on performance. In terms of our model, meritocratic attitudes at the population level are
reflected by the distribution of α shifting to lower values when income is random instead of
performance-based, so that Frandom (α) ≥ Fquiz (α) for every α.
Prediction 4 (Meritocratic attitudes I). If individuals have meritocratic attitudes, the takeup rate in the quiz treatment is higher than the take-up rate in the random treatment if the
take-up is private and the transfer is redistributive.
Further treatments In our main treatments, the transfer is a re-distributive payment,
i.e., the payments to all participants in a group depend on the welfare take-up decision of the
lowest ranked group member as shown in Table 2. This means that a participant claiming
the transfer takes away money from other participants. As discussed above, participants
may not want to be perceived as someone who takes other people’s money or live off others’.
This moral signaling effect is present both in the quiz and the random treatment presented
above and, in particular, the stigma effect observed in the random treatment is a measure
of moral signaling because ability stigma cannot play a role. But when we change from
quiz to random, we do not only change what can be inferred about an individual’s ability
from taking the transfer. In addition, the income-generating mechanism is different and it
may be that the moral appropriateness of a transfer changes, too. In particular, individuals
may perceive redistribution as more appropriate if the income is random than if it is based
on performance, and they may want to signal that they honor entitlements that have been
earned in a competitive environment (meritocratic attitude). If this is the case, our previous
estimate of the ability-related stigma effect would be biased upwards.
To control for a possible effect of meritocratic attitudes, we implement two further treatments that exclude explanations related to entitlements. These two treatment are analogous
to the quiz and random treatments described above but instead of a redistributive transfer,
we let the transfer be a subsidy from the experimenter to the transfer claimant as shown in
Table 3. The instructions for stage (1) and the control questions were adjusted accordingly
but everything else remained unchanged.
Comparing take-up rates in these subsidized treatments yields an alternative estimate of
the relative importance of ability and moral signaling for the overall stigma effect (cf. corollary
3).
Prediction 5 (Moral signaling II). If the transfer is a subsidy, a stigma effect persists in the
quiz treatment but it is smaller than in the quiz redistribution treatment.
22
This follows directly from our theoretical set-up if the marginal disutility from moral stigma is positive,
b > 0.
11
rank
1
2
3
A
B
16 Euro
11 Euro
6 Euro
16 Euro
11 Euro
9 Euro
Table 3: Payoffs in further treatments
Furthermore, the subsidized random treatment provides us with a placebo test for the
importance of social signaling. If income is random and the transfer a subsidy, according to
our theory neither ability nor moral signaling should have a bite so that we predict no stigma
effect.
Prediction 6 (Placebo test). If the transfer is a subsidy and income is random, the stigma
effect disappears.
However, if some individuals dislike public exposure or if they have a preference for privacy
(summarized as transaction costs), take-up will be lower in public than in private even if ranks
are drawn randomly and the transfer is a subsidy. This would potentially bias our previous
estimate of the stigma effect. The subsidized random treatment therefore allows us to a) test
whether transaction costs play a role and b) correct our experimental measures of stigma
effects for the pure effect of privacy preferences or transaction costs if this is the case.
By comparing the observed stigma effects in the two redistribution treatments with those
in the two subsidy treatments, we can also test whether signaling of meritocratic attitudes
plays a role.
Prediction 7 (Meritocratic attitudes II). If individuals desire to signal a meritocratic attitude, the difference in the stigma effects between quiz and random is smaller in the subsidized
treatments than in the redistribution treatments.
The first statement relates only to a change in the distribution of moral attitudes. If
individuals are meritocratic more individuals claim a transfer if it is not redistributive for a
given benefit level. The second statement brings in social inferences. Even if an individual’s
moral attitude is unchanged, she may anticipate that others will find it more appropriate to
claim a transfer that is subsidized so that the associated stigma is less severe. If this is the
case, our measure of moral signaling based on the redistribution treatment would be upward
biased through the effect of meritocratic attitudes.
Procedures The experiments were carried out at the Technical University Berlin between
November 2015 and June 2016. The experimental software was programmed using z-Tree
(Fischbacher, 2007) and subjects were recruited using ORSEE (Greiner, 2015). In total, 441
subjects took part in 14 sessions of 24 subjects and five sessions of 21 subjects. Table 4
illustrates the number of subjects per treatment. Sessions lasted 45 to 60 minutes each and
participants earned, on average, 11.24 Euros.
Upon entering the laboratory, subjects were randomly allocated a cubicle and asked to
carefully read the experimental instructions for stage (1), the quiz, of the experiment. After
the quiz had ended, participants received instructions for stages (2) and (3) of the experiment,
including a set of control questions. The experiment only started once everyone had correctly
12
answered all questions. After the end of the experiment, we administered a post-experiment
questionnaire while preparing for payment. Payments were made individually in a separate
room.
4
Experimental results
Subjects answered an average of 9.57 questions in the quiz correctly where the minimal score
was 3, i.e., all subjects worked on the task. The quiz task was able to differentiate well
between the ranks: in the quiz treatment subjects in rank 1 answered with 11.82 significantly
more questions correctly than those in rank 2 with 9.52 questions (t(154) = 8.375, p < 0.001)
who themselves answered more correctly than those in rank 3 with 7.44 questions (t(154) =
7.859, p < 0.001). There are no statistical differences to the random treatment with respect
to the number of questions answered correctly, although in this treatment subjects were told
that ranks did not depend on quiz performance. Moreover, the participants did not differ
across treatments with respect to any demographic characteristics that we elicited.23
For our main analysis, we investigate the take-up behavior as elicited by the strategy
method so that the actual number of claimants is not relevant for the analysis.24 We first
show that public exposure significantly reduces the take-up rate of a redistributive transfer
when eligibility is based on quiz performance. Having established the existence of a sizable
stigma effect, we decompose it into effects related to ability signaling and to moral signaling
by looking at a treatment where eligibility is based on a randomly drawn rank. Then, we
present results from the subsidized treatment that allows us to separate ability and moral
signaling from other possible explanations like meritocratic considerations and transaction
costs.
4.1
Evidence of welfare stigma
In the main quiz treatment, income is based on quiz performance and transfers come at a cost
to other participants in the same experiment. This captures two crucial features of a welfare
program. First, eligibility for social benefits is typically based on criteria that are informative
about the claimant’s performance in a competitive environment. Second, welfare benefits
quiz
random
total
redistribution
subsidized
total
165
159
324
69
48
117
234
207
441
Table 4: Number of subjects per treatment
23
Table 10 in the Appendix displays descriptive statistics of the sample. Fifty-nine percent of subjects are
male, subjects are an average of 24 years old, nearly all of them are studying, almost thirty percent are also
working. Twenty-four percent are enrolled in a subject related to economics (economics, business, industrial
engineering) and none had ever participated in more than three experiments.
24
In 126 out of 147 groups a transfer was claimed, where 35 transfers were given out under the stigma
regime and 91 under the private regime. In all but two sessions there was at least one claimant who received
a public transfer.
13
Figure 2: Take-up rate by transfer regime in quiz (n=165)
must be financed: they reduce consumption possibilities of other society members and often
involve redistributing money from upper and middle class individuals (taxes) to poorer ones
(benefits).
Figure 2 illustrates the take-up rates under the private and public transfer regime in our
benchmark treatment. The left bar shows that 87.9 percent of subjects decided to take up the
transfer if it was private, whereas only 57.6 percent would do so in the public treatment (right
bar). The resulting public-private gap of 30.3 percentage points is statistically significant
(t(164) = 7.998, p < 0.001) and relevant in magnitude; the take-up rate goes down by a third.
This large effect is remarkable because forgoing the transfer is very costly: not taking the
transfer means passing up a 50 percent increase in the experimental earnings when ranked
third, 6 Euros instead of 9 Euros. In line with our theoretical model, we interpret the decrease
in the take-up rate due to public exposure as a stigma effect.
Recall that by comparing public and private, we net out all potential determinants that
might affect the take-up behavior but that are invariant to the visibility of the welfare takeup decision. This may include, for instance, self-signaling concerns or internalized shame.
Similarly, other psychological frictions (e.g., decision errors) that may explain why the takeup rate deviates from 100 percent, which would be the prediction of a neoclassical model
of welfare take-up behavior, cannot explain the stigma effect. Under the assumption that
transaction costs and privacy concerns are not relevant, the only thing that varies is the
visibility of the take-up decision.25 Hence, the treatment effect can only be attributed to
a participant’s anticipation of the inferences the public (i.e., the other participants in the
laboratory) will make upon observing her taking up the transfer. This confirms Prediction 1.
Result 1. Welfare stigma matters. The take-up rate in the quiz redistribution treatment is
significantly lower in public than in private (both statistically and economically).
25
Using the subsidized treatments that we discuss in section 4.3, we show that transaction costs related
to public setting or privacy preferences do not explain or even contribute to the observed effect. See also
Prediction 6 and Result 5.
14
Figure 3: Take-up rate by treatment and transfer regime (n=159)
4.2
Ability and moral signaling as determinants of welfare stigma
Our theoretical model distinguishes between ability and moral signaling. To assess which of
these motives drives the observed stigma effect in take-up rates, we run a further treatment
random redistribution, where a subject’s rank, and therefore also eligibility to claim a transfer,
is determined randomly. If rank is based on luck alone, then taking up the transfer does not
allow the public to draw any inference about the claimant’s ability or skills. But, as transfers
are redistributive, the decision to publicly claim a transfer is informative about the claimant’s
moral attitude. If the stigma effect goes to zero when transfer eligibility is random, the stigma
effect described above must be driven by ability signaling alone. If we find a stigma effect of
similar size, we would conclude that moral signaling is the only relevant factor. If it decreases
but remains significantly positive, both ability and moral signaling are at play (cf. Predictions
2 and 3).
Figure 3 depicts the take-up rate, again divided into public and private. We indeed also
observe a difference in the take-up rates when rank is assigned by chance: here, the stigma
effect amounts to 18.9 percentage points, i.e., making the take-up of the transfer public
reduces the take-up rate by roughly 22 percent from the take-up rate in private. Individuals
still dislike being seen by others when taking the public transfer, leading to the conclusion
that a concern for moral signaling is a relevant factor in our setting, which confirms Prediction
3.
Result 2. Moral signaling matters. The take-up rate in the random redistribution treatment
is significantly lower in public than in private.
However, the stigma effect is reduced if income is determined randomly (0.189 vs. 0.303).
To statistically test for differences between random and quiz, we run the following differencein-differences estimation:
(2)
Take-upi = α + β1 Quizi + β2 Publici + β3 (Quiz x Public)i + i ,
using standard errors clustered on the subject level. The estimated interaction effect β3 and
its standard error are reported in the bottom-right cell in Table 5. As can be seen, the diff-in15
diff of 0.114 is significant at the 5 percent level, suggesting that ability signaling does indeed
matter. This lends support to our Prediction 2.
Result 3. Ability signaling matters. The stigma effect is significantly higher in the quiz
redistribution treatment than in the random redistribution treatment.
Table 5 summarizes the take-up rates of the treatments discussed so far and the estimated differences between them. The horizontal within-subject differences are calculated
using paired t-tests, and the vertical between-subject differences are assessed using unpaired
t-tests. Interestingly, when the transfer is private, we find virtually no difference in the takeup rates between quiz and random (first column of Table 5). This is in line with our idea that
there is neither room for ability nor moral social signaling when the transfer is private.26
Furthermore, the data indicates that individuals do not perceive it to be more morally
appropriate to claim a transfer if income is based on luck than if it is based on performance.
In contrast to Hypothesis 4, the take-up rates in private do not differ significantly between
the quiz and random treatments.
Result 4. Take-up rates in private are inconsistent with meritocratic attitudes. Take-up is
not significantly lower when income is based on ability than when it is based on luck.
In contrast, the take-up rate of the public transfer is 9.7 percentage points lower when
ranks are based on quiz rather than on luck (a decrease by 14.4 percent in the take-up
rate). Taken together, we conclude that both ability and moral signaling are relevant for the
observed public-private gap but meritocratic attitudes can be ignored. The public-private
gap of 30.3 percentage points in the main quiz treatment is reduced by 11.4 percentage points
when shutting down the ability signaling channel. This suggests that roughly one-third of the
total effect is due to ability signaling.
Table 5: Take-up rates in respective treatment
Task
Private transfer
Public transfer
Difference (paired)
Quiz
0.879
(0.025)
[165]
0.862
(0.027)
[159]
0.017
(0.037)
[324]
0.576
(0.039)
[165]
0.673
(0.037)
[159]
-0.097+
(0.054)
[324]
0.303∗∗∗
(0.038)
[165]
0.189∗∗∗
(0.032)
[159]
DiD=0.114∗
(0.050)
[324]
Random
Difference
(unpaired)
Notes: Standard errors in parentheses, number of observations in square brackets.
+
p < 0.10,
∗
p < 0.05,
∗∗
p < 0.01,
∗∗∗
p < 0.001
26
Although our design is not explicitly set up to address this question, our data suggests that self-signaling
(at least when it comes to ability) plays no role.
16
4.3
Robustness: Excluding meritocratic beliefs and transactions costs as
confounds
The results presented so far indicate that there is a significant interaction effect between the
public transfer regime and the quiz treatment. Under the assumption that moral signaling
concerns do not vary between the random and the quiz treatments, this interaction effect
identifies concerns for ability signaling. However, one might object that this assumption is not
valid. Specifically, moral concerns may be stronger in the quiz treatment than in the random
treatment because taking away income from group members is morally more objectionable
when income is based on performance rather than on luck because earned entitlements have to
be honored. Such a “meritocratic effect” could also result in the non-zero diff-in-diff described
above.27
To test whether our previous estimates are biased by meritocratic considerations, we run
a robustness treatment where the transfer is no longer redistributive. Transfers are now paid
(= subsidized) by the experimenter so that taking up the transfer does not affect the earned
incomes of others. First, this allows us to disentangle ability signaling and the meritocratic
component. Second, we can assess whether the take-up decision depends on the transfer being
redistributive or not and thereby obtain an alternative measure of the ability and the moral
signaling effects (cf. Prediction 5). Third, we can address further issues, such as whether
transaction costs (such as privacy or the physical costs of having to stand up and walk to the
experimenter desk) are relevant. To fix ideas, consider the resulting treatment structure:
ability+moral+meritocratic
ability
moral
z
}|
{ z
}|
{ z
}|
{
DiDiD = [(tpriv,quiz − tpub,quiz ) −(tpriv,rand − tpub,rand )] −[(tpriv,quiz − tpub,quiz ) −(tpriv,rand − tpub,rand )]
|
{z
}|
{z
}
redistribution
subsidized
where t denotes the take-up rate in the respective treatment combination. Until now, we
have considered the first diff-in-diff with redistribution. Now, consider the second diff-in-diff.
The public-private-gap in the subsidized quiz treatment captures ability signaling without
moral signaling and, thus, without the meritocratic component. Moreover, the public-privategap in the subsidized random treatment isolates other explanations like transaction costs and
shyness since there is no scope for signaling motives.
Table 6 summarizes the results of the subsidized treatments. If income is based on quiz,
the take-up rates of the private and public transfer differ significantly by 17.4 percentage
points, public exposure leads to a decrease of 18.5 percent in relation to the take-up rate in
private: individuals have a lower inclination to take a visible welfare benefit, even when doing
so would not affect the payout of other group members. The random treatment reported in
the second row of Table 6 allows us to hold constant any other channel that would produce
a positive public-private gap. As can be seen, the public-private gap sharply drops. While
the point estimate of 0.021 is still positive, this is not statistically different from zero at
27
We call this the meritocratic component, as quiz performance reflects ability or skills and income differences are therefore justified. See, for instance, Alesina and Angeletos (2005) who point out that whether
inequality is based on luck or ability determines demand for redistribution. In fact, we find an indication of this
reasoning in our post-experimental questionnaire, e.g., subjects in the quiz treatment agree to the statement
“The subject in rank three is entitled to receive a transfer” to a significantly lower degree than in the random
treatment according to a Wilcoxon rank-sum test (z = 4.435, p < 0.001).
17
Table 6: Take-up rates in respective treatment (subsidized)
Task
Private transfer
Public transfer
Difference (paired)
Quiz
0.942
(0.028)
[69]
0.917
(0.040)
[48]
0.025
(0.048)
[117]
0.768
(0.051)
[69]
0.896
(0.045)
[48]
-0.128+
(0.071)
[117]
0.174∗∗
(0.054)
[69]
0.021
(0.047)
[48]
DiDs =0.153∗
(0.076)
[117]
Random
Difference
(unpaired)
Notes: Standard errors in parentheses, number of observations in square brackets.
+
p < 0.10,
∗
p < 0.05,
∗∗
p < 0.01,
∗∗∗
p < 0.001
conventional statistical levels, suggesting that transaction costs or privacy concerns are not
of major concern in our experiment (cf. Prediction 6). This is reassuring as it suggests that
the observed stigma effect is in fact driven by social signaling concerns.
Result 5. Transaction costs do not play a significant role.
Furthermore, we show that neither meritocratic attitudes nor the desire to signal a meritocratic attitude have a significant effect. Differencing the two public-private gaps of the
subsidized treatment, we obtain a clean estimate of the stigma effect related to the ability
signaling of 0.153. This difference-in-differences effect is slightly higher than that of 0.114
estimated under redistribution in the previous section. This contradicts the hypothesis that
individuals want to signal their meritocratic attitudes which would predict a difference in
the opposite direction (cf. Prediction 7). To test for statistical differences between the two
difference-in-differences, we estimate the DiDiD from above by pooling the observations from
all treatments presented so far:
(3) public-private gapi = α + β1 Quizi + β2 Redistributioni + β3 (Quiz x Redistribution)i + i
Here, we regress the public-private gap, i.e., the within-subject difference (tpub −tpriv ) between
the public and the private transfer regime, on treatment dummies for quiz and redistribution
and their interaction. Formally, β3 is a triple difference estimator (DiDiD) that identifies the
meritocratic component.
As can be seen from Table 7, the interaction effect β3 is insignificant, suggesting that there
is no significant difference between the two differences. This rejects the hypothesis underlying
Prediction 7 that individuals want to appear to be honoring earned income more than random
income.
Result 6. The desire to signal meritocratic attitudes does not significantly affect the take-up
behavior.
Moreover, this result implies that the ability effect estimated in our previous section was
not driven by signaling meritocratic considerations. This confirms that ability signaling is
indeed an important driver of the take-up decision in our experiment and suggests that the
18
Table 7: Regression of the public-private gap on treatment characteristics (model 3)
(1)
public-private gap
0.153∗
(0.072)
0.168∗∗
(0.057)
-0.039
(0.087)
0.021
(0.047)
0.031
441
Quiz
Redistribution
Quiz x Redistribution
Constant
Adj. R2
N
Robust standard errors in parentheses.
+
p < 0.10,
∗
p < 0.05,
∗∗
p < 0.01,
∗∗∗
p < 0.001
observed gap between take-up rates in public and in private is explained by moral and ability
signaling.
Furthermore, we can use our data to assess the relative importance of the two effects,
adjusted for possible confounding factors. β1 isolates the ability signaling effect independent
from potential interactions with moral signaling as well as transaction costs. It amounts
to 0.153, which is equal to the diff-in-diff of Table 6. β2 , estimated to 0.168, identifies the
moral signaling effect, net of potential transaction costs. The estimate provides a formal
test of Prediction 5, and we conclude that the public-private gap is larger if the transfer is
redistributive. This confirms that moral signaling is indeed relevant for the observed stigma
effect.28
Result 7. Moral signaling relates to redistribution. If the take-up is public and eligibility is
random, take-up rates are significantly higher for the subsidy treatment than for the redistribution treatment.
Finally, it is noteworthy that we find no evidence that take-up behavior exhibits anomalies
not related to public exposure or moral concerns. As predicted by our model (and by any
neoclassical model) of take-up behavior, almost everyone takes up the transfer in private if
it is paid for by the experimenter. In this case, neither individual moral concerns nor social
inferences play a role. Based on Fisher’s exact test, the private take-up rate is not different
from 100 percent in any individual session within the subsidy treatment and is just borderline
significant with a p-value of 0.059 (0.06) in a one-sided Fisher’s exact test when pooling all
subsidy sessions in the random (quiz) treatment.
Result 8. Private take-up rates are close to 100 percent in the subsidy treatment.
4.4
Further Robustness: Experimenter demand effect and strategy method
First, we show that the results are unlikely to be driven by an experimenter demand effect.
One could be concerned about a potential experimenter demand effect due to the withinsubject design using the strategy method. As subjects are asked to make their take-up
decision for both the public and the private transfer regime, they might feel inclined to give
28
Note that we do not find evidence of moral signaling in the random subsidy treatment at all (cf. Result
5).
19
systematically different responses across setting.29 We mitigate such tendencies by presenting
both transfer regimes not at the same time but in randomized order on separate screens.
When subjects are asked about their take-up decision for the private transfer, they do not
know that there will also be a decision for a public transfer, and vice versa. If there was an
experimenter-demand effect we would expect that subjects who learn on the second screen
that there is both a public and a private transfer have lower public take-up rates (when
private is presented first) and higher private take-up rates (when public is presented first).
Instead, we observe that pooled over all treatments the mean take-up rate of the public
(private) transfer is 0.675 (0.886) if the private transfer is presented first and 0.677 (0.887) if
the public transfer is presented first. Thus, there are no systematic differences in line with
an experimenter demand effect. Similarly, there are no significant differences in the take-up
rates when comparing order effects by treatment.
Second, we check whether the take-up decision is associated with the expectation about
ones own rank when income is based on quiz performance. If the stigma effect is different
between those who are confident being in rank 1 and those who suspect that they should be
in rank 3, the strategy method might not be appropriate. It is therefore reassuring that there
are no significant differences in the take-up by expected rank as Figure 4 illustrates.
Third, we provide evidence that our treatments actually result in measurable variations
in the extent of ability and moral signaling. A Wilcoxon rank-sum test reveals that there is
greater approval to the statement “The participant in rank 3 has poor knowledge” in the quiz
treatment than in the random treatment (z = −8.706, p < 0.001). Moreover, significantly
more subjects in the random treatment than in the quiz treatment believe that the person
in rank 3 had bad luck (z = 5.292, p < 0.001). This supports our identification of ability
signaling, which rests on the assumption that subjects perceive taking up a transfer in the quiz
task as sending a negative signal about their ability. However, as can be seen in Table 8 there
are still many subjects who do consider quiz performance to be a matter of luck. While our
quiz treatment is subject to a higher degree of ability signaling than the random treatment, we
Figure 4: Take-up rate by expected rank (n=234)
29
A demand effect in the sense that individuals respond feeling pressured to answer consistently across
public and private conditions would only work against finding a stigma effect.
20
Table 8: Post-experimental questionnaire responses regarding voting
Statement
Rel. Frequency
Quiz
Random
“The participant in rank 3 has poor knowledge”
Strongly Disagree 0
28.17
1
29.58
2
19.72
3
19.25
Strongly Agree
4
3.29
N
213
75.47
10.69
10.06
3.14
0.63
159
“The participant in rank 3 had bad luck”
Strongly Disagree 0
7.69
1
14.96
2
26.50
3
37.18
Strongly Agree
4
13.68
N
234
14.49
5.80
13.53
14.98
51.21
207
Notes: The number of observation differs since the first question was not included in the first three
sessions.
conclude that our experimental measure of ability-related welfare stigma probably represents
a lower bound of this effect. The survey answers suggest that an income source which is more
strongly associated with ability (e.g., IQ test, school grades) might produce an even larger
stigma effect.
5
Preferences for transfer regime
So far we have analyzed how stigmatization affected individual decision to take up a welfare
transfer. In this section, we present results from the second part of our experiment, where we
used a random dictator decision rule to elicit individuals’ preferences for the public or private
transfer mode.
Figure 5 illustrates the fraction of participants who voted in favor of the public transfer
regime, divided by rank and income source. As subjects already know their rank at this
stage we have to differentiate between those who presumably benefit from the public transfer
regime (ranks 1 and 2) and those who are harmed by it due to stigmatization (rank 3). As
expected, only very few subjects at rank 3 vote in favor of the public transfer regimes, and in
all treatments they are less likely to vote for the public regime than those with ranks 1 and
2. Moreover, Figure 5 shows that there are more subjects at rank 1 who vote for the public
transfer regime in the quiz treatment but none of the treatment differences are significant.30
30
One reason why the support for the public transfer payment may be higher in the quiz than in the random
treatment could be that participants are curious about who performed poorly in the quiz and are not ashamed
of admitting this and of asking for redistribution. This would only add to the neoclassical motives pushing for
a high share voting in favor of the public payment and it cannot explain why support for the public regime is
so low.
21
Figure 5: Share voting for public transfer by rank and task, only redistribution (n=324)
However, keeping in mind that the take-up rate is much lower under the public transfer
regime it is striking that there are relatively few rank 1 and rank 2 subjects voting for it. If we
assume that subjects take the stigma effect into account – and we find a strong indication of
this in the post-experimental questionnaire31 – we would expect all payoff-maximizing agents
in rank 1 and 2 to vote in favor of the public transfer.
In order to investigate the reasons for this voting pattern, Table 9 takes a closer look at
the voting motives that were stated by the subjects in the post-experimental questionnaire.
We see that a majority of subjects in ranks 1 and 2 who voted for the public transfer agreed
to the statement “I want to reduce the take-up probability to raise my payout.” However,
they are rather indifferent to the statement “Free-riders should be identified as such.” In
contrast, 82.0 percent of those who voted against the public transfer agreed to the statement
“I don’t want the claimant to be ashamed.” This means that there are, on the one hand, many
subjects who anticipate the existence of a stigma effect and vote for the public transfer to
reduce the take-up probability. On the other hand, many subjects acknowledge the existence
of the welfare stigma but have social preferences toward the subject in rank 3. They vote
against the public transfer to spare them the shame of getting stigmatized.32
In summary, the voting patterns from the second part of the experiment provide further
evidence of the existence of welfare stigma in line with our theoretical model (e.g., Prediction
1). While exploratory in nature, these findings indicate that we should not only investigate
preferences for redistribution but we need to take into account that individuals have preferences with respect to the way that redistributive payments are paid out. Specifically, our
data suggests that even many of those individuals who are net payers dislike stigmatization.
31
75.3 percent of subjects on rank 1 and 2 agree to the statement “It is discomforting for the claimant when
the transfer is public” and 70.8 percent agree to the statement “Public transfers reduce take-up probability”.
32
Nevertheless, there are a few subjects who appear not to be responsive to stigma. Among those who
are in rank 3 and vote in favor of the public transfer regime 6 out of 11 disagree with the statement “It is
discomforting for the claimant when the transfer is public.”
22
Table 9: Post-experimental questionnaire responses regarding voting
Statement
Rel. Frequency
Pro Public
Contra Public
“Free-riders should be identified as such”
Strongly Disagree 0
10.64
1
23.40
2
29.79
3
21.28
Strongly Agree
4
14.89
N
94
34.43
27.87
24.59
8.20
4.92
122
“I want to reduce the take-up probability to raise my payout”
Strongly Disagree 0
9.57
27.87
1
11.70
20.49
2
23.40
31.15
3
28.72
13.11
Strongly Agree
4
26.60
7.38
N
94
122
“I don’t want the claimant to be ashamed”
Strongly Disagree 0
18.09
1
24.47
2
39.36
3
8.51
Strongly Agree
4
9.57
N
94
2.46
4.92
10.66
22.13
59.84
122
Notes: Only subjects in ranks 1 and 2 are considered.
6
Conclusion
This paper complements the empirical literature on welfare stigma with a laboratory experiment. Based on a theoretical model that understands welfare stigma as the disutility
associated with the anticipation of social inferences upon taking up a welfare transfer in public, we vary the degree of welfare stigma through public exposure or scrutiny by changing
the visibility of taking up a redistributive transfer. Furthermore, we investigate whether the
take-up decision is affected by the ability signal that is contained in public take-up or by
the associated moral stigma of living off others’ means. By design and based on a control
treatment, we can rule out other explanations for low take-up as, for example, transaction
costs or privacy concerns and cleanly identify the effect of ability and moral signaling.
There are three key results: First, making take-up public reduces the take-up rate significantly by approximately 30 percentage points. Second, we use our theoretical framework
and experimental design to decompose the overall stigma effect into an effect related to inferences about ability and inferences about moral attitudes. We estimate that in our experiment
ability signaling reduces take-up by 15.3 percentage points and moral signaling by 16.8 percentage points, that is, moral signaling is at least as important as ability signaling. Third,
when subjects are asked to vote on one of the two transfer regimes, more than half of the net
payers (i.e., individuals ranked 1 or 2) vote against the public transfer regime even though
23
this implies that they have to pay the transfer with higher probability. We find suggestive
evidence that net payers who vote against the public transfer have social preferences as they
vote for the private regime in order to spare claimants the shame of being stigmatized.
Our study complements the field experiment by Bhargava and Manoli (2015) who find no
evidence of welfare stigma in the context of EITC benefits. We believe that their intervention
did not effectively reduce stigmatization in a welfare program that is anyway subject to a low
degree of stigmatization. In contrast, our experiment induced substantial stigmatization and
showed that it is behaviorally relevant for the decision to claim a privately beneficial transfer
payment.
References
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25
A
Data and descriptives
Table 10: Descriptive statistics
Male
Age
Studying
Working
Subject related to Econ
Experimental Experience
Correct answers in quiz
B
n
Mean
Std. Dev.
Minimum
Maximum
441
441
441
441
441
441
441
0.592
23.900
0.952
0.297
0.243
1.889
9.574
0.492
4.234
0.213
0.457
0.429
0.995
2.591
0
16
0
0
0
0
3
1
48
1
1
1
3
17
Instructions (translated into English)
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Welcome to our experiment!
During the experiment you are not allowed to use electronic devices or communicate with
other participants. Please do only use the programs and functions provided for the
experiment. Please do not talk to other participants. If you have a question, please raise your
hand. We will come to you and will quietly answer your question. Please never ask your
questions aloud. If the question is relevant for all participants, we will repeat it and answer it
loudly. If you do violate these rules, we must exclude you from the experiment and the
payoff.
The following instructions describe the process of the experiment and are equal for all
participants. You can earn money in this experiment. The level of your payout depends on
your decisions, on the decisions of other participants and on chance. Please carefully read
the instructions. You can leave the experiment at any time. If you want to do so, please raise
your hand. You will only be paid off if you stay until the end of the experiment.
Quiz
In this experiment, you and two other participants will form a group. The group will remain
the same for the entire experiment. All participants will first answer a quiz.
You receive 18 questions on different domains of general knowledge. There are four possible
answers to each question, of which exactly one is correct. You will obtain one point for each
question answered correctly. You do not receive any point for questions that were not
answered or incorrectly answered.
You have six minutes to work on the quiz. After that, all given responses will be submitted.
[Quiz: Your pay-off depends on how well you solve your tasks in comparison to the other
two group members. The member of the group who has collected the biggest amount of
points after six minutes receives the first rank, the member of the group with the second
biggest amount of points receives the second rank and the member of the group with the
third biggest amount of points receives the third rank. If two or three members of the group
have the same amount of points, it will be determined randomly who gets the higher rank.]
[Random: Independently of the amount of collected points, each group member will be
randomly assigned to a rank, which is relevant for the rest of the experiment. Your rank does
in no way depend on your performance in the quiz.]
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Pay-Off
The payoff to one participant depends on her rank. There are two possible modes of payoff:
payoff mode A and payoff mode B.
[Redistribution:]
Rank
1st
2nd
3rd
Mode A
16 Euro
11 Euro
6 Euro
Mode B
14 Euro
10 Euro
9 Euro
Mode A
16 Euro
11 Euro
6 Euro
Mode B
16 Euro
11 Euro
9 Euro
[Subsidized:]
Rank
1st
2nd
3rd
[Redistribution: Mode A differs from mode B in that the participant on the third rank
receives a transfer from the participants on the first and second ranks.]
[Subsidized: Mode A differs from mode B in that the participant on the third rank receives a
transfer].
Which of these payoff modes will be applied depends on your decisions and the decisions of
the other participants in the second part of the experiment. You will receive the instructions
for the second part upon completing the first part.
28
Second part of the experiment
The second part of the experiment will decide which of the two payoff modes will be
applied. In each group, this depends on the decisions of the group member on the third
rank. If the group member on the third rank decides to take the transfer, payoff mode B will
be applied. If the group member on the third rank decides not to take the transfer, payoff
mode A will be applied.
Stage 1
You now must make a binding decision on whether you would like to take the transfer in the
case of being placed on the third rank. You will only find out about your rank in stage 2. If
you end up on the third rank, the decision that you now make will be applied.
On two consecutive screens, you will now receive information on the conditions under which
you can receive the transfer. On each of these screens, you have to decide on whether you
would take the transfer under the given conditions and in case you end up on the third rank.
Which of these conditions will be applied is determined in stage 2.
Please consider that your decision is binding and irreversible for the rest of the
experiment.
Stage 2
[Quiz: After making your decision in stage 1, you will find out about the rank you achieved in
your group]. [Random: After taking your decision in stage 1, you will find out about the rank
you were randomly assigned to]. For each group it will now be decided which of the
conditions shown in stage 1 will be applied.
Out of the two possible conditions, each member of the group will now pick the one that
should be applied according to his/her opinion. In each group, one participant will be
randomly picked and her decision will be applied in her group.
Payoff
Remember: the pay-off depends on the rank. Whether payoff mode A or B will be applied
depends on the group member on the third rank. If that member decided to take the
transfer, mode B will be applied. If that member decided against the transfer, mode A will be
applied to the pay-off. It is now relevant how the group member on the third rank decided
under the conditions picked by the group.
29
[Redistribution:]
Rank
1st
2nd
3rd
Mode A
16 Euro
11 Euro
6 Euro
Mode B
14 Euro
10 Euro
9 Euro
Mode A
16 Euro
11 Euro
6 Euro
Mode B
16 Euro
11 Euro
9 Euro
[Subsidized:]
Rank
1st
2nd
3rd
Please answer the attached control questions and raise your hand when you are done. An
experimenter will then come to you to check your answers.
If you have any questions, please raise your hand.
Questionnaire
1.
Does your rank depend on your performance in the quiz?
O Yes
O No
2.
[Quiz: Assume you scored the second highest number of points in your group]. [Random:
You were randomly assigned to the second rank]. In the first stage, the two other group
members decided to take the transfer under both conditions.
a) What is your payoff? ___
b) What is the payoff of the group member on rank 1? ___
3.
Assume that you decided for a certain condition in stage 2. The two other group members
decided for the other condition. Which condition is relevant for payoff?
a) The condition that I chose.
b) The condition that the other two group members chose.
c) Both conditions are possible.
30
O
O
O
C
Screenshots
Figure 6: Take-up conditions presented on-screen in randomized order (translated into English)
31
32
Figure 7: Screenshot of quiz (translated into English)